Essays on Public Economics and Criminal

Justice

Steven Mello

A Dissertation

Presented to the Faculty

of Princeton University

in Candidacy for the Degree

of Doctor of Philosophy

Recommended for Acceptance

by the Department of

Economics

Advisers: Alexandre Mas and Ilyana Kuziemko

June 2019

© Copyright by Steven Mello, 2019.

All rights reserved.

Abstract

A theme throughout this dissertation is the application of questions in the field of public

economics to the context of policing and the criminal justice system. Another common theme

is the use of large datasets and quasi-experimental research designs for policy evaluation.

A third theme is the consideration of the equity or distributional implications of criminal

justice policies.

The first chapter studies the ability of low-income individuals to cope with expense

shocks. Using administrative data on traffic citations in Florida linked to high-frequency

credit reports and leveraging variation in the timing of traffic stops with event study and

difference-in-differences research designs, I study the impacts of fines for traffic violations on

the financial situations of Florida drivers. I find that, following a traffic stop, the poorest

quartile of drivers experience reductions in job stability and declines in financial health

which are outsized relative to the typical fine amount. I conclude by estimating welfare

losses associated with traffic fines and discussing implications for optimal policing.

The second chapter, co-authored with Felipe Goncalves, estimates the degree to which

individual police officers practice racial discrimination. Using a bunching estimation design,

we document that nonwhite drivers are less likely than white drivers to benefit from lenience

on the part of Florida Highway Patrol officers in the form of a reduced speeding charge.

We further find that about forty percent of officers explain the entirety of the aggregate

discrimination. We use our estimates of officer-level racial bias to explore the effectiveness

of various personnel policies aimed at mitigating aggregate racial disparities.

The third chapter exploits a natural experiment to estimate the causal effect of police

hiring on local crime. I leverage quasi-random variation in the receipt of COPS hiring grants

in 2009 by comparing the change over time in police and crimes for cities whose applications

for funding were accepted and rejected. I find that police employment increased by 3.2

percent and cost-weighted crime fell by 3.5 percent in funded cities relative to unfunded

iii

cities. Crime declines associated with additional police were more pronounced in areas most

affected by the Great Recession.

iv

Acknowledgements

I am extremely grateful to my advisers for their incredible mentorship, guidance, support,

and encouragement. I thank Alex Mas for insightful advising centered around conveying

important messages clearly and transparently. Alex has taught me to balance on focus on

broad, fundamental questions with creative thinking and the pursuit of unique interests. I

thank Ilyana Kuziemko for enthusiastic advising with an emphasis on applying clear economic

thinking to important, policy-relevant questions. Ilyana’s generous mentorship has taught

me to think more deeply about all aspects of the research process. I thank Will Dobbie for

detailed and constructive advising which has combined a willingness to engage with the most

subtle issues and a constant focus on the big-picture. Will has taught me not only countless

practical lessons, but also how to ask better and more meaningful questions. All three have

brought remarkable generosity, positivity, and dedication to their advising. I could not be

more grateful.

My development as an economist has also benefited greatly from the advice of many other

members of the Princeton faculty, particularly Leah Boustan, Janet Currie, Hank Farber,

Henrik Kleven, Alan Krueger, Jonathan Mummolo, Christopher Nielson, Mica Sviatschi, and

Owen Zidar. I am especially grateful to David Lee, not only for his thoughtful mentorship

and advice, but also for his tireless help with obtaining the data used in the first chapter

of this dissertation. I additionally benefited from the help of Laura Hedden and Stephen

Redding, especially during the job market.

The Industrial Relations Sections has been a stimulating and nurturing academic home

for the past three years. I am thankful for the unyielding aid and support of Linda Belfield,

Valerie Ching, Lori Mitrano, Jeannie Moore, and Patti Tracey, as well as the many others

who have contributed to the caring and gratifying intellectual and social life of the Section.

I am also grateful for the financial support provided by the Graduate School at Princeton

University, the Industrial Relations Section, the Fellowship of the Woodrow Wilson Scholars,

and the Charlotte Elizabeth Procter Honorific Fellowship.

v

I have been fortunate to meet many amazing people at Princeton and am thankful for the

support and friendship of Fabiola Alba, David Arnold, Jessica Brown, Mingyu Chen, David

Cho, Michael Dobrew, Ted Enamorado, Ben Eskin, Julia Fonseca, Felipe Goncalves, Daniel

Herbst, Elisa Jacome, Stephanie Kestelman, Andrew Langan, Luisa Langan, Mathilde Le

Moigne, Graham McKee, Terry Moon, and Neel Sukhatme. I am especially indebted to

Jessica Brown and Julia Fonseca, without whose help I would never have passed my first-

year courses, to Mingyu Chen and Andrew Langan for seven years of friendship, and to Elisa

Jacome for constantly raising my spirits. I owe a huge debt of gratitude to Felipe Goncalves,

a coathor of one of my disseration chapters, who is not only a fantastic collaborator but also

a great mentor and friend.

I thank the many teachers, coaches, and professors who have guided me prior to graduate

school, especially Emily Conover, Elizabeth Jensen, and Stephen Wu. Their mentorship and

support helped me cultivate an interest in economics and I would never have pursued grad-

uate school without their encouragement. John Donohue, who taught me how meaningful

empirical research can be in the real world, has also been an invaluable mentor.

My family has been a source of inspiration and love throughout my graduate studies.

My mother Kathy’s kind and nurturing spirit has provided comfort and given me the confi-

dence to keep pushing. My brother, Ted, and sister, Kate, have given me countless laughs,

fun times, and sincere friendship. Whitney Rosenbaum deserves ten pages of acknowledge-

ments to herself. Her generosity and inquisitive nature have inspired me, her support and

encouragement have comforted me, and her love has been a constant source of joy.

Finally, I would like to dedicate this dissertation to the memory of my father, Steven

Mello, who passed away on March 7, 2019. He taught me to aim high and never give up. I

aspire to his grit and determination every day.

vi

Contents

Abstract . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . iii

Acknowledgements . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . v

List of Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . ix

List of Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xii

1 Speed Trap or Poverty Trap? Fines, Fees, and Financial Wellbeing 1

1.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1

1.2 Traffic Enforcement in Florida . . . . . . . . . . . . . . . . . . . . . . . . . . 8

1.3 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 11

1.4 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 16

1.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 23

1.6 Estimating Welfare Effects . . . . . . . . . . . . . . . . . . . . . . . . . . . . 37

1.7 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 42

Appendices 64

.1 Appendix Figures and Tables . . . . . . . . . . . . . . . . . . . . . . . . . . 65

.2 Becker-Style Model . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 84

.3 Effects of Payroll-Job Separations . . . . . . . . . . . . . . . . . . . . . . . . 93

2 A Few Bad Apples? Racial Bias in Policing 98

2.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 98

2.2 Institutional Background and Data . . . . . . . . . . . . . . . . . . . . . . . 105

vii

2.3 Conceptual Framework . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 110

2.4 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 112

2.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 116

2.6 Robustness Checks and Alternative Explanations . . . . . . . . . . . . . . . 119

2.7 Applications of Officer Heterogeneity . . . . . . . . . . . . . . . . . . . . . . 124

2.8 Model and Counterfactuals . . . . . . . . . . . . . . . . . . . . . . . . . . . . 128

2.9 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 135

Appendices 156

.1 Data Appendix . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 157

.2 Accounting for Stopping Margin Selection . . . . . . . . . . . . . . . . . . . 158

.3 Testing for Statistical Discrimination . . . . . . . . . . . . . . . . . . . . . . 161

.4 Notes on Model Estimation . . . . . . . . . . . . . . . . . . . . . . . . . . . 165

3 More COPS, Less Crime 183

3.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 183

3.2 Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 186

3.3 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 193

3.4 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 199

3.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 203

3.6 Cost-Benefit Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 216

3.7 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 218

Appendices 238

.1 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 239

.2 Power Calculations . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 241

.3 Appendix Figures and Tables . . . . . . . . . . . . . . . . . . . . . . . . . . 244

Bibliography 263

viii

List of Tables

1 Summary Statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 54

2 Impact of Citations on Financial Strain . . . . . . . . . . . . . . . . . . . . . 55

3 Impacts of Citations on Financial Strain by Driver Income . . . . . . . . . . 56

4 Impact of Citations on Employment and Borrowing . . . . . . . . . . . . . . 57

5 Impacts of Citations on Employment and Borrowing by Driver Income . . . 58

6 Treatment Effects Across Studies . . . . . . . . . . . . . . . . . . . . . . . . 59

7 Income Changes Predicting Financial Strain Impacts . . . . . . . . . . . . . 60

8 Heterogeneous Impacts by Baseline Financial Situation . . . . . . . . . . . . 61

9 Treatment Effects of Payers and Traffic School Attendees . . . . . . . . . . . 62

10 Event Study Estimates of Impact of License Suspensions . . . . . . . . . . . 63

A-1 Credit File Match Rate by Driver Characteristics . . . . . . . . . . . . . . . 79

A-2 Summary Statistics for Matching Candidates and Matches . . . . . . . . . . 80

A-3 Difference in Difference Estimates for Other Outcomes . . . . . . . . . . . . 81

A-4 Difference-in-Differences Estimates for Employment and Earnings . . . . . . 82

A-5 Sensitivity of 12 Month Effects to Imputation . . . . . . . . . . . . . . . . . 83

C-1 Summary Statistics for Job Separations Sample . . . . . . . . . . . . . . . . 95

1 Summary Statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 137

2 Characteristics of Cited Drivers Relative to Other Data Sources . . . . . . . 138

3 Officer Lenience Randomization Check . . . . . . . . . . . . . . . . . . . . . 139

4 Difference-in-Difference Results . . . . . . . . . . . . . . . . . . . . . . . . . 140

ix

5 Alternative Difference-in-Differences Specifications . . . . . . . . . . . . . . 141

6 Alternative Interpretations . . . . . . . . . . . . . . . . . . . . . . . . . . . 142

7 Alternative Interpretations, Section 2.6.3 . . . . . . . . . . . . . . . . . . . . 143

8 Predicting Officer Bias . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 144

9 Early Discrimination . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 145

10 Discounting Gap Decomposition . . . . . . . . . . . . . . . . . . . . . . . . 146

11 Model Counterfactuals . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 147

A.1 Racial Disparity in Speeding . . . . . . . . . . . . . . . . . . . . . . . . . . 170

A.2 Racial Disparity in Discounting . . . . . . . . . . . . . . . . . . . . . . . . . 171

A.3 Racial Disparity in Speeding, Non-lenient Officers . . . . . . . . . . . . . . . 172

A.4 Officer Lenience Randomization Check . . . . . . . . . . . . . . . . . . . . . 173

A.5 Difference-in-Differences Officer-Level Results . . . . . . . . . . . . . . . . . 174

A.6 Officer Discrimination Randomization Check . . . . . . . . . . . . . . . . . 175

A.7 Predicting Officer Complaints/Force . . . . . . . . . . . . . . . . . . . . . . 176

A.8 Model Parameter Estimates . . . . . . . . . . . . . . . . . . . . . . . . . . . 177

A.9 Speed Gap Decomposition . . . . . . . . . . . . . . . . . . . . . . . . . . . . 178

1 Summary Statistics for Applicant Cities . . . . . . . . . . . . . . . . . . . . 230

2 Difference in Differences Estimates . . . . . . . . . . . . . . . . . . . . . . . 231

3 Accounting for Differential Recession Exposure . . . . . . . . . . . . . . . . 232

4 Accounting for Other ARRA Spending . . . . . . . . . . . . . . . . . . . . . 233

5 IV Estimates by Crime Type . . . . . . . . . . . . . . . . . . . . . . . . . . 234

6 IV Estimates, Crimes and Arrests . . . . . . . . . . . . . . . . . . . . . . . 235

7 Dynamic TOT Effects of Grant Offers on Police . . . . . . . . . . . . . . . . 236

8 Testing for Asymmetric Treatment Effects . . . . . . . . . . . . . . . . . . . 237

A-1 Sample Police Departments . . . . . . . . . . . . . . . . . . . . . . . . . . . 255

A-2 Relationship Between Application Scores and Baseline Characteristics . . . 256

A-3 Regression Discontinuity Power Calculations . . . . . . . . . . . . . . . . . . 257

x

A-4 Dynamic Difference in Differences Estimates . . . . . . . . . . . . . . . . . . 258

A-5 Sensitivity of IV Estimates to Controls . . . . . . . . . . . . . . . . . . . . . 259

A-6 Sensitivity of IV Estimates to Data Cleaning . . . . . . . . . . . . . . . . . 260

A-7 Reduced Form Estimates by Crime Type . . . . . . . . . . . . . . . . . . . 261

A-8 IV Estimates by Crime Type (Logs) . . . . . . . . . . . . . . . . . . . . . . 262

xi

List of Figures

1.1 Ticketing Frequency and Neighborhood Per Capita Income in Florida . . . . 44

1.2 Timeline for Matching . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 45

1.3 Event Study Estimates for Financial Strain Outcomes . . . . . . . . . . . . . 46

1.4 Event Study Estimates for (Payroll) Employment . . . . . . . . . . . . . . . 47

1.5 Event Study Estimates for Borrowing Outcomes . . . . . . . . . . . . . . . . 48

1.6 Outcomes Around Traffic Stop for Matched DD Sample (Raw Data) . . . . . 49

1.7 Impacts on Financial Strain by Baseline Characteristics . . . . . . . . . . . . 50

1.8 Impacts on Employment by Baseline Characteristics . . . . . . . . . . . . . . 51

1.9 Treatment Effects on Strain by Baseline Financial Distress . . . . . . . . . . 52

1.10 License Suspension Event Studies . . . . . . . . . . . . . . . . . . . . . . . . 53

A-1 Local Policing Intensity and Per Capita Income in the U.S. . . . . . . . . . . 65

A-2 Reliance on Fines and Fees and Per Capita Income in the U.S. . . . . . . . . 66

A-3 Credit File Match Rate by Zip Code Per Capita Income . . . . . . . . . . . 67

A-4 Correlation Between Estimated Income and Payroll Earnings . . . . . . . . . 68

A-5 Age Profiles for Select Outcomes . . . . . . . . . . . . . . . . . . . . . . . . 69

A-6 Event Study Estimates without Individual Trends . . . . . . . . . . . . . . . 70

A-7 Event Study Estimates for Monthly Earnings . . . . . . . . . . . . . . . . . . 71

A-8 Fully Non-Parametric Matched Difference-in-Differences Estimates . . . . . . 72

A-9 Employment Effects by Baseline Employment Status . . . . . . . . . . . . . 73

A-10 Means Around Traffic Stop Date for Other Outomes (Raw Data) . . . . . . . 74

xii

A-11 Outcome Means Using All Match Candidates . . . . . . . . . . . . . . . . . 75

A-12 Imputed Fine Gradients . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 76

A-13 Effects by Common Violation Types . . . . . . . . . . . . . . . . . . . . . . 77

A-14 License Suspension Event Studies for Other Outcomes . . . . . . . . . . . . 78

B-1 Welfare Effects by Risk Aversion and Excess Burden . . . . . . . . . . . . . 91

C-1 Effect of Payroll Separations on Financial Strain . . . . . . . . . . . . . . . . 96

C-2 Effect of Payroll Separations on Credit Cards . . . . . . . . . . . . . . . . . 97

2.1 Distribution of Charged Speeds and Fine Schedule . . . . . . . . . . . . . . . 148

2.2 Charged Speed Distributions by Driver Race . . . . . . . . . . . . . . . . . . 149

2.3 Evidence of Officer Lenience . . . . . . . . . . . . . . . . . . . . . . . . . . . 150

2.4 Difference-in-Difference Raw Data Plot . . . . . . . . . . . . . . . . . . . . . 151

2.5 Officer Lenience and Stop Characteristics . . . . . . . . . . . . . . . . . . . . 152

2.6 Difference-in-Difference Results . . . . . . . . . . . . . . . . . . . . . . . . . 153

2.7 Difference-in-Differences Officer-Level Results . . . . . . . . . . . . . . . . . 154

2.8 Officer-Level Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 155

A.1 Distribution of Charged Speeds for Radar Gun Sample . . . . . . . . . . . . 179

A.2 Model Estimates: Officer Lenience by Race . . . . . . . . . . . . . . . . . . . 180

A.3 Model Estimates: Percentiles of Officer Lenience . . . . . . . . . . . . . . . . 180

A.4 Model Estimates: Speed Distribution . . . . . . . . . . . . . . . . . . . . . . 181

A.5 Model Estimates: Racial Discrimination by Officer . . . . . . . . . . . . . . . 181

A.6 Model Diagnostic Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . 182

3.1 COPS Hiring Program Funding Over Time . . . . . . . . . . . . . . . . . . . 220

3.2 Distribution of Application Scores and Funding Probability . . . . . . . . . . 221

3.3 Baseline Characteristics by Application Score . . . . . . . . . . . . . . . . . 222

3.4 Trends in Police and Crime by Treatment Status (Raw Data) . . . . . . . . . 223

3.5 Effect of Exceeding the Threshold on Police and Crime . . . . . . . . . . . . 224

xiii

3.6 Sensitivity of First Stage and Reduced Form Estimates . . . . . . . . . . . . 225

3.7 Effect of Exceeding the Threshold on Violent and Property Crimes . . . . . 226

3.8 Testing for Geographic Spillovers . . . . . . . . . . . . . . . . . . . . . . . . 227

3.9 Heterogeneous Effects by Recession Exposure . . . . . . . . . . . . . . . . . 228

3.10 Trends in Police for Predicted Firers and Hirers (Raw Data) . . . . . . . . . 229

A-1 Probability of Sample Inclusion by Application Score . . . . . . . . . . . . . 244

A-2 Data Imputation by Treatment Status . . . . . . . . . . . . . . . . . . . . . 245

A-3 Changes in Police and Crime by Application Score (2008–2009) . . . . . . . 246

A-4 Application and Funding Rates by 2009 Treatment Status . . . . . . . . . . 247

A-5 First Stage Placebo Tests . . . . . . . . . . . . . . . . . . . . . . . . . . . . 248

A-6 Dynamic Estimates with and without City Trends . . . . . . . . . . . . . . . 249

A-7 Total ARRA Funding By Source, 2009–2013. . . . . . . . . . . . . . . . . . . 250

A-8 IV Estimates and ARRA Funding Differences by Bandwidth . . . . . . . . . 251

A-9 Dynamic TOT Estimates of Effect of Grants on Police . . . . . . . . . . . . 252

A-10 Heterogeneous Effects by City Size . . . . . . . . . . . . . . . . . . . . . . . 253

A-11 Relationship Between Predicted Hiring and Recession Exposure . . . . . . . 254

xiv

Chapter 1

Speed Trap or Poverty Trap? Fines,

Fees, and Financial Wellbeing 1

1.1 Introduction

The ability of households to cope with adverse shocks has important implications for taxa-

tion and social insurance policies (e.g., Baily 1978, Chetty 2006a). Despite the prediction of

canonical models that liquidity-constrained households anticipate income volatility by accu-

mulating buffer stock savings (Deaton 1991, Carroll 1992, Carroll 1997), recent evidence has

highlighted the lack of precautionary savings in the United States (Beshears et al., 2018).

Half of all households accumulated no savings in 2010 (Lusardi, 2011) and forty percent

of Americans indicated an inability to cover an emergency $400 expense in 2017 (Board

of Governors of the Federal Reserve System, 2018). The widespread dearth of rainy-day

1I am grateful to Will Dobbie, Ilyana Kuziemko, David Lee, and Alex Mas for unrelenting ad-vice and encouragement on this project. Mark Aguiar, David Arnold, Reyhan Ayas, Leah Boustan,Jessica Brown, Mingyu Chen, David Cho, Felipe Goncalves, Elisa Jacome, Henrik Kleven, AndrewLangan, Atif Mian, Jack Mountjoy, Jonathan Mummolo, Chris Neilson, Scott Nelson, WhitneyRosenbaum, Mallika Thomas, Owen Zidar, and seminar participants at Princeton University pro-vided helpful comments. I thank Beth Allman for providing the citations data and for severalhelpful conversations, as well as numerous individuals at the data-providing credit bureau for ex-ceptional assistance with accessing and working with the data. I benefitted from generous financialsupport from the Industrial Relations Section at Princeton University, the Fellowship of WoodrowWilson Scholars, and the Charlotte Elizabeth Procter Fellowship. Any errors are my own.

1

funds, termed financial fragility, has spurred concern among scholars and policymakers in

recent years because fragile households may be particularly vulnerable to unexpected shocks

(Lusardi et al., 2011).

While ethnographic studies such as Shipler (2005) and Desmond (2016) are rife with

accounts of disadvantaged individuals whose fortunes are altered by unplanned expenses,

causal evidence on the impacts of transitory, negative shocks on household finances is scarce.

An important obstacle to such an empirical analysis is the lack of usable variation in small

income shocks, especially for poor households. Existing studies have examined consumption

responses to small positive shocks such as tax refunds (e.g., Parker 2017) or significant

negative shocks such as hospital admissions (Dobkin et al., 2018) or job loss (Stephens

2001, Keys 2018). The literature’s reliance on policy variation generated by tax rebates or

mortgage programs and on credit card or bankruptcy filings data has left the bottom end of

the income distribution relatively understudied.

In this paper, I examine the impacts of fines for traffic infractions on financial wellbeing.

Over forty million traffic citations are issued each year for speed limit violations alone, making

traffic fines a common unplanned expense for the driving population. Further, policing

activity disproportionately affects poor communities, whose residents may have an especially

limited capacity to absorb fines. As shown in Figure 1.1, residents of the most disadvantaged

zip codes receive traffic citations at nearly twice the rate of residents of rich zip codes.2 While

most traffic fines are nominally small, typically between $100 and $400, they could induce

financial distress in several ways. For individuals lacking financial slack, coping mechanisms

such as forgoing basic needs, missing bills, or borrowing at high interest rates may impact

future financial stability (e.g., Skiba and Tobacman 2011). Nonpayment of fines results in

2The correlation between neighborhood income and ticketing rates is consistent with a wealthof evidence suggesting that low-income and nonwhite communities tend to be the most policed. Forexample, poorer cities employ more police officers per capita (Figure A-1) and rely more heavilyon revenue from criminal justice fines and fees (Figure A-2).

2

the revocation of driving privileges, which may jeopardize employment arrangements or put

individuals at risk of a misdemeanor charge for driving without a valid license.

An analysis of the impacts of fines is particularly interesting given the current public

concern regarding the unintended consequences of criminal justice policies (e.g., Ang 2018).

While a large literature has examined the public safety benefits of policing (Chalfin and

McCrary, 2017) in the spirit of deterrence models such as Becker (1968), the social costs of

policing have historically received less attention. A host of recent events such as the 2014

riots in Ferguson, Missouri have vaulted the potential negative implications of policing to the

forefront of public consciousness. Prompted by the Ferguson Report ’s findings that a focus

on revenue generation shaped the city’s policing practices and that nonwhite and low-income

citizens disproportionately received citations (Department of Justice Civil Rights Division,

2015), media outlets and advocates have offered accounts of individuals suffering cycles of

debt and involvement with the criminal justice system stemming from fines and fees.3 While

compelling, such evidence is both anecdotal and correlational. To date, there has been no

rigorous empirical analysis of the causal effects of fines on economic wellbeing.

To estimate the impacts of fines, I link administrative data on the universe of traffic

citations issued in Florida over 2011–2015 to monthly credit reports and payroll records for

ticketed drivers. The citations data provide nearly complete coverage of the state’s traffic

offenders and my analysis sample represents about five percent of Florida’s driving-age popu-

lation. Credit reports offer a detailed account of an individual’s financial situation, including

information on delinquencies, adverse financial events such as charge-offs and repossessions,

and unpaid bills in collection. The payroll records report monthly earnings for individuals

working at large employers. About sixteen percent of the analysis sample is employed in a

payroll-covered job in the year prior to receiving a citation.

3For examples, see Adams (2015), Lopez (2016), Grabar (2017), or Sanchez and Kambhampati(2018). In 2015, John Oliver devoted a segment of his popular HBO show, Last Week Tonight,to municipal violations, providing several anecdotes and noting that “if you don’t have enoughmoney to pay a fine immediately, tickets can ruin your life.” See http://time.com/3754023/

john-oliver-municipal-violations/.

3

The high-frequency nature of the credit report and payroll data allows for the use of event

study and difference-in-differences research designs that leverage variation in the timing of

traffic stops for identification. My primary difference-in-differences approach compares the

evolution of outcomes for drivers around the time of a traffic stop with a matched control

group of comparable individuals who receive citations two to four years later. This empirical

strategy relies on the identifying assumption that fined drivers would have trended similarly

to control individuals in the absence of a traffic ticket, which I validate by showing that the

two groups of drivers follow parallel pre-citation trends on a host of outcomes.

First, I examine the impact of traffic fines on several measures of financial distress. In the

first year after a traffic stop, individuals experience a three percent increase in collections, a

four percent increase in collections balances, and two percent increases in delinquencies and

incidences of derogatory events. Collections activity related to an unpaid citation typically

will not appear on a credit report, so the observed increases in collections most likely reflect

increases in unpaid utility or medical bills (Avery et al., 2003). Estimated impacts persist,

and in most cases continue to grow, two years out from the traffic stop date.

For the majority of strain outcomes, treatment effects are two to five times larger for

the poorest quartile of drivers than for the richest quartile. While non-zero effect sizes for

the richest subset of drivers may seem surprising, there is evidence of widespread hand-to-

mouth behavior and binding liquidity constraints even among wealthy households (Chetty

and Szeidl 2007, Kaplan et al. 2014). To help interpret the estimated magnitudes, I rely

on the cross-sectional relationship between payroll earnings and financial strain outcomes

to construct income-equivalent effect sizes — the change in income that would predict the

observed change in distress. For low-income drivers, the two-year increase in financial strain

is observationally similar to what would be predicted by a $950, or five percent, drop in

earnings.

Next, I study effects on payroll outcomes. Traffic citations could affect employment status

through their impacts on financial distress, which may reduce labor supply (Dobbie and Song,

4

2015) or job-finding rates (Bartik and Nelson, 2017), or through their impacts on the costs

of driving. Unpaid citations result in driver license suspensions, and many tickets result

in driver license “points” which might increase auto insurance premiums. I find that one

year (two years) out from a ticket date, individuals are about three (five) percent less likely

to have any reported payroll earnings. Citations both reduce the likelihood of a transition

into a payroll-covered job and increase the likelihood of a transition out of the payroll data.

As with the financial strain outcomes, employment effects are most pronounced for poor

drivers. The estimated impact on payroll employment for the richest quartile of the sample

is quite small, while the poorest quartile of drivers experience nearly a ten percent decline

in the likelihood of positive reported earnings. For individuals remaining in the payroll data

following a citation, there is no effect on earnings on average, but suggestive evidence of a

two percent decline in earnings for low-income drivers.

I also examine the impact of traffic tickets on measures of borrowing and consumption. An

unplanned expense may increase demand for credit, but financial distress or unemployment

could restrict credit availability. I find small declines in the number of credit cards, credit

card balances, and the likelihood of car and home ownership, proxied by the presence of an

open auto loan and mortgage on a credit report, following a traffic stop. Reductions are

more pronounced in the long-run than the short-run, suggesting that diminished access to

credit following the accumulation of unpaid bills and delinquencies could be an important

mechanism. The pattern of heterogeneity in the borrowing effects is less stark, likely because

the poorest quartile of drivers exhibit tenuous borrowing at baseline.

After presenting the main results, I consider the relative importance of competing mech-

anisms in explaining the estimated effects. In particular, traffic tickets represent unplanned

expense shocks but also can affect insurance costs or driving privileges. Using information

on traffic ticket dispositions available for a subset of drivers, I show that treatment effects for

those whose dispositions indicate payment, and therefore typically will not incur a suspended

license, are similar to the sample-wide average effects. Impacts are smaller for individuals

5

making payment and electing to attend an optional traffic school that suppresses points

from accruing on the driver’s license. One the one hand, the reduced treatment effects for

school attendees suggest that the negative consequences of traffic tickets are in part due to

license suspensions or increased insurance costs (individuals making payment can still face

suspensions if payment is late or if they have accrued many past citations). On the other

hand, impacts are still present for school attendees and the treatment effect disparities are

largely eroded when accounting for observable differences between the two groups of drivers.

Further, a separate analysis reveals that the causal effects of license suspensions are large,

but not outsized compared to the main citation effects. On net, it appears that both the

pure expense shock and potential effects on driving costs are important mechanisms.

I conclude by quantifying the welfare losses associated with traffic tickets and discussing

policy implications. Using back-of-the-envelope calculations and a standard willingness-to-

pay framework, a conservative estimate of the welfare cost associated with the average ticket

is about $500. Intuitively, this quantity has a policy-relevant interpretation. To the extent

that welfare costs are greater than the revenue raised and public safety produced by an

additional traffic citation, there is deadweight loss associated with ticketing. Governments

who do not consider the outsized welfare costs of citations will generally choose to over-

police. I then use a simple Becker-style model to consider the welfare implications of moving

to an income-based fine system.4 In a stylized environment where individuals earn either

$20,000 or $40,000 per year and the multiplying welfare effects of fines for poor individuals

are taken into account, a $10 increase (decrease) in the fine for rich (poor) drivers yields a

welfare benefit of between $3 and $10 dollars per citation. At current ticketing levels, this

policy offers a total social benefit as high as $20 million per year, eroding about one percent

of the total welfare cost of annual citations in Florida ($500 × 2 million tickets).

4Finland employs an income-based fine schedule for speeding. Countries such as Sweden andDenmark also use income-dependent fines in some form. See https://www.theatlantic.com/

business/archive/2015/03/finland-home-of-the-103000-speeding-ticket/387484/.

6

My paper makes two important contributions. First, the empirical results highlight that

many individuals are not fully insured against even small economic shocks. Faced with a

$175 traffic ticket, individuals accrue unpaid bills and delinquencies on their credit reports

while also reducing consumption, suggesting an inability to cover the unexpected expense.

While the increases in unpaid bills and declines in consumption are smaller than the fine itself

for rich drivers, traffic tickets appear to have a multiplying effect on financial health for poor

drivers, who exhibit increases in financial distress observationally similar to a $950 income

loss following a $175 ticket. Results are even starker for individuals with unpaid bills at

baseline, who experience the largest increases in distress and largest declines in employment

and borrowing. This pattern of results is consistent with a poverty trap (e.g., Banerjee and

Duflo 2011, Barrett et al., eds 2019), whereby small shocks have minor consequences for

financially stable individuals but deleterious effects for the already distressed population.

These findings have potentially important implications for social insurance programs as

optimal policy formulas typically depend heavily on the ability of households to smooth

across states of the world. Further, the empirical analysis contributes to a large literature

studying how households are affected by economic shocks by providing some of the first

causal evidence on the effects of small, negative shocks for low-income individuals.5

Second, this paper adds to the current public debate over the use of fines and fees in the

criminal justice system. While scholarly work has found that increases in speeding tickets

improve road safety (Makowsky and Stratmann 2011, DeAngelo and Hansen 2014, Luca

2015), critics have argued that the ability of police departments to raise municipal revenue

through citations distorts policing incentives (Goldstein et al., 2018). Advocates and media

outlets (e.g., Adams 2015, Lopez 2016, Grabar 2017) have argued that flat fine schedules

and more intensive policing in low-income communities result in an unfair burden of fine

systems on the poor. Others have called the harsh punishments imposed for nonpayment

of fines an effective “criminalization of poverty” (Balko, 2018). My findings illustrate the

5Beshears et al. (2018) provides a thorough and recent review of the literature.

7

outsized impacts of fines on the financial well-being of low-income individuals, a fact that

has potentially important implications for both the optimal level of policing and the design

of fine-and-fee systems.

The remainder of the paper is organized as follows. Section 2 explains the institutional

details of traffic enforcement in Florida. I describe the data in Section 3 and the empirical

strategy in Section 4. Results are presented in Section 5. I briefly discuss welfare and policy

implications in Section 6 and conclude in Section 7.

1.2 Traffic Enforcement in Florida

The context of the present study is traffic enforcement in Florida. The vast majority of traffic

laws, such as speed limits, are enforced with fines for violators. Patrolling police officers, or in

some cases automated systems such as red light or toll cameras, issue citations to offenders.

Traffic tickets are very common. Over 4.5 million individual Florida drivers received at least

one traffic citation between 2011 and 2015, with between 1.1 and 1.4 million licensed Florida

drivers cited each year. As of the 2010 census, the age 18 and over population of Florida was

14.8 million, implying that around thirty percent of the driving age population received a

citation over 2011–2015 and about seven to ten percent of the driving age population receives

a citation each year. As has been shown in other contexts, traffic enforcement appears to

disproportionately affect low-income individuals. Figure 1.1 illustrates a clear correlation

between the zip code ticketing rate (number of citations issued to zip code residents divided

by the zip code population) and zip code per capita income, computed from the IRS public

use files.6 A ten percent decline in neighborhood per capita income is associated with a four

percent increase in the citation rate.

Traffic citations specify the offense and a fine to be paid, which is determined by the

violation code and the county of the offense. For reference, the most common single violation

6The IRS public use data are available from the IRS website at https://www.irs.gov/

statistics/soi-tax-stats-individual-income-tax-statistics-zip-code-data-soi.

8

codes over 2011–2015 were speeding (20 percent), red light camera violations (8.5 percent),

lacking proper insurance (7.5 percent), driver not seat-belted (6 percent), and failure to pay

toll (6 percent), which account for nearly half of all citations over the period. Statutory

fines vary widely across offense types and counties. For example, in Miami-Dade county,

low-level equipment violations such as broken tail lights carry a fine of $109, while the fine

for speeding 30+ miles per hour above the posted limit in a construction or school zone

is $619. Punishments for very rare criminal, rather than civil, traffic offenses can exceed

$1,000 and in some instances may include jail time. Unfortunately, the citations database

does not include a reliable measure of the statutory fine associated with each offense. Using

an imputation procedure, I estimate that the average statutory fine faced by drivers in the

main sample is about $175, but this is likely an underestimate.

Citations can be associated with additional costs beyond the statutory fine. Traffic

violations result in points on a driver’s license. Insurance companies typically consider driver-

license points when setting premiums, so individuals may face increases in car insurance

prices following a citation (Gorzelany, 2012). A rough back of the envelope calculation

suggests the typical speeding ticket could increase monthly car insurance premiums by $10.

State law dictates that drivers accruing 12 points in 12 months (18 points in 18 months; 24

points in 36 months) have their driver license suspended for 30 days (3 months; one year).

Most common offenses are associated with three points, but certain violations carry up to 6

points.7 Individuals cited for equipment violations such as broken taillights are ordered to

make repairs or face the risk of quickly becoming repeat offenders.

Once a citation has been issued, a driver can either submit payment to the county clerk

or request a court date to contest a ticket. For those contesting their ticket in court, a

judge or hearing officer ultimately will decide to either uphold the original citation, reduce

the punishment, or dismiss the charge. For individuals who do not request a court date,

payment is due 30 days from the citation date. At the time of payment, a driver may also

7See the FLDHSMV website at https://www.flhsmv.gov/driver-licenses-id-cards/

driver-license-suspensions-revocations/points-point-suspensions/.

9

elect to attend traffic school. A voluntary traffic school election (and completion) coupled

with an on-time fine payment prevents the license points associated with the citation from

accruing on the individual’s DL.8 If the county clerk has not received payment in-full within

30 days, the individual is considered delinquent and their license is suspended effective

immediately. Knowingly driving with a suspended license is a low-level misdemeanor offense

and typically results in a fine of $300-500 with the possibility of jail time and punishments

increasing drastically for second and third offenses.

If a citation remains unpaid after 90 days, county clerks add a late fee to the original

amount owed and send the debt to a collections agency, who then solicit payment for the

citation. Collections agencies are authorized by state law to, and therefore typically will, add

a 40 percent collection fee to the original debt.9 Relevant for the empirical analysis is whether

collections originating from unpaid citations will appear directly in the credit bureau data.

Not all collections agencies report their activity to credit bureaus and reporting behavior

varies across both agencies and clients. I compiled a list of collections agencies used by the

five largest counties in Florida by examining county clerk webpages and contacted each one

directly to inquire about their reporting behavior.10 While most signaled an ability to report

to credit bureaus on their webpage, the two agencies that responded directly to my inquiry

indicated that they did not report citation-related collections.

An important takeaway from a close examination of the institutional details is that

a traffic ticket represents a possibly multi-faceted treatment. The exact treatment for a

given individual may depend on driving history and ex post decisions, neither of which are

8Individuals seeking to prevent point accrual following standard non-criminal moving violationstake the Basic Driver Improvement Course. The course is four hours of instruction, cannot becompleted in one sitting, and typically costs about $25.00. Many providers allow the course to betaken online. Individuals can only complete traffic school once in any twelve-month period and fivetimes total.

9See Adams (2015) and corroborating evidence on the Miami-Dade County Clerk of Courtswebsite at http://www.miami-dadeclerk.com/parking_collections.asp.

10Most counties use some combination of (1) Linebarger, Goggan, Blair and Sampson, LLP,(2) Penn Credit, and (3) AllianceOne, with some also using Law Enforcement Systems, Inc. andMunicipal Services Bureau (MSB).

10

perfectly observed in the data. We should primarily think of the treatment as receiving a

bill for, on average, $175, where the punishment for nonpayment is a revocation of driving

privileges. However, the treatment could entail time in court for contesters and increases in

insurance premiums as well. I focus on estimating reduced form, or intent-to-treat, effects

of traffic tickets, but rely on analysis of heterogeneous treatment effects and an independent

examination of license suspensions to provide some insights about which components of

treatment are particularly relevant.

1.3 Data

1.3.1 Traffic Citations

The Florida Clerks and Comptrollers Office (FCC) provided administrative records of all

traffic citations issued in Florida from 2005 through 2015 in response to a sunshine law

(FOIA) request. The records were culled from the Clerk’s Uniform Traffic Citation (UTC)

database, which preserve an electronic record of each ticket transcribed from the paper

citation written by the ticketing officer. Each record includes the data and county of the

citation, as well as the violation code and information listed on the offender’s driver license,

such as DL number, name, date of birth and address. My analysis makes use of subsets of

citations issued in 2011–2015 due to the availability of credit report data, discussed below.

1.3.2 Credit Reports

Access to monthly credit reports from January 2010 through December 2017 was provided

by a major credit bureau.11 I provided the credit bureau with a list of 4.5 million Florida

residents issued a traffic citation between January 2011 and December 2015. Via a propri-

etary linking algorithm, the driver information was matched with the credit file using name,

11My data sharing agreement precludes me from sharing the name of the Credit Bureau.

11

date of birth, and home address reported on the citation.12 The linking process matched 3.7

million drivers for an 82 percent match rate. Brevoort et al. (2015) find that about eleven

percent of adults, and as many as 30 percent in the lowest income areas, have no credit

record. Additionally, in most cases, names and addresses were written by hand, undoubt-

edly leading to some mistakes in transcription. Hence, 82 percent is a reasonable match

rate.

Consistent with Brevoort et al. (2015), the credit file match rate is higher for residents of

the richest zip codes (∼86 percent) than for the poorest zip codes (∼78 percent), as shown

in Figure A-3. Table A-1 examines a more complete set of predictors of a credit file match.

The regressions confirm a strong relationship between neighborhood income and a successful

match, but also highlight differences across demographics groups. Female, white, and older

drivers are more likely to be matched. We should think of the matching process as slightly

eroding the negative selection into the citations data. Individuals receiving traffic tickets

are more disadvantaged than average as shown in Figure 1.1, but among cited individuals,

there appears to be positive selection in terms of being matched to the credit file. To the

extent that the treatment effect is larger for the most disadvantaged individuals, the selection

induced by the credit file matching process ought to bias estimates toward zero.

After matching the data, the credit bureau removed the citations data of all personally

identifiable information such as driver names, addresses, birth dates, driver license numbers,

and exact citation dates, preserving only the year and month of each citation. I was then

allowed access, through a secure server, to the anonymized citations data and monthly credit

reports each with a scrambled individual identifier for linking across the two datasets.

The credit bureau data represent a snapshot of an individual’s credit report taken on the

last Tuesday of each month. The data include information reported by financial institutions,

such as credit accounts and account balances, information reported by collections agencies,

information culled from public records such as bankruptcy filings, and information computed

12Note that the credit bureau preserves a list of previous addresses for individuals on file. Hence,the address at the time of the traffic ticket need not be current to achieve a match.

12

directly by the credit bureau such as credit scores.13 The data also include an estimated

income measure, which is based on a proprietary model that predicts an individual’s income,

rounded to the nearest thousand, using information in the credit file. Estimated income is

highly, but not perfectly, correlated with payroll earnings (described below), as shown in

Figure A-4. While I do not use estimated income as a primary outcome because I cannot

replicate its computation, I make use of the measure both in constructing the matched control

group (discussed below in Section 4) and in splitting the sample to examine heterogeneous

effects by income.

Credit bureau data provide a wealth of information on an individual’s financial situation.

The challenge in working with such data is to focus on a parsimonious set of outcomes with

a relatively clear welfare interpretation. I focus my analysis on two types of outcomes –

measures of financial strain and measures of credit usage. Following Dobbie et al. (2017),

I use collections, delinquencies, and incidences of major derogatory events as measures of

financial strain. Collections represent unpaid bills that have been sent out to third-party

collections agencies. I use the number of accounts ever at least 90 days past due as my

primary measure of delinquency, but also consider total balance currently past due, summed

across all accounts. Major derogatory events are incidences of repossessions, charge-offs

(where a creditor declares a debt unlikely to be paid), foreclosures, bankruptcies, or internal

collections. The credit bureau computes the number of accounts on file with any major

derogatory event to date, and I use this as an additional outcome measuring financial strain.

Collections and collections balances are an especially useful measure of stress in my con-

text because unpaid bills need not be related to borrowing accounts. According to Avery et

al. (2003) and Federal Reserve Bank of New York (2018), only a small fraction of collections

are related to credit accounts, with the majority associated with medical and utility bills.

13The provided credit score is the VantageScore® 3.0. For more information, see https://www.

vantagescore.com. The innovation of the VantageScore 3.0, which is also an advantage for myanalysis, is an improved ability to score individuals with thin credit files. The Credit Bureausestimate that about 30M previously unscoreable consumers can be assigned a VantageScore 3.0.

13

Credit usage is sporadic among a sizable subset of cited drivers. Almost 20 percent of in-

dividuals in the primary sample have no open account at baseline. Collections can capture

increases in financial strain even among individuals with tenuous credit usage, while individ-

uals need to maintain open borrowing accounts in order to exhibit delinquency, for example,

in the credit file.

My primary measures of credit usage are the number of open revolving accounts and

revolving account balances. Revolving accounts are accounts that provide a borrowing limit

and no set maturity date. The majority of revolving accounts are credit cards and store

cards. I also examine whether individuals have any open auto loan or mortgage to study

durable good consumption.

All fields in the credit report data are pre-topcoded. Fields measuring counts, for exam-

ple the number of collections or number of revolving accounts, are topcoded at 92. Balances

are topcoded at $9,999,992. Credit report information can be missing either because an in-

dividual lacks a credit report in a given month or for reasons such as insufficient information

to compute a field. For example, the field for number of open accounts may be missing be-

cause the credit bureau cannot ascertain whether certain accounts qualify as open. Balances

corresponding to non-existent accounts, e.g. collections balances for a person-month with

zero collections, are typically coded as missing. Both for simplicity and to be conservative,

I impute missing fields as zero in the main specification. After imputing where account

numbers are zero, balances are frequently zero, and I therefore winsorize balance measures

at the 99th percentile rather than taking logs.14

14For reference, the 99th percentile of collections balances is about $35,000 while the maximumis about $750,000. For revolving balances, the 99th percentile and maximum are about $225,000and $9,500,000. In the appendix, I present results retaining missing values, with point estimatesnearly identical to those shown in the main text.

14

1.3.3 Payroll Data

The provider of the credit report data also maintains a database of payroll records that are

shared directly with the credit bureau. The payroll data are relatively thin, but include

information on the number of payroll accounts, i.e. number of jobs, and annualized earn-

ings for individuals in a given month. In terms of coverage, employers reporting payroll

information are mostly larger businesses, with about 85 percent of Fortune 500 companies

covered in the payroll data. Coverage appears more sparse in the citations sample than for

the nation as a whole. According to the credit bureau, around 30 percent of the individuals

in the credit file are covered in the payroll data. In my main analysis sample of over 600,000

individuals, 16 percent are employed and 11 percent have nonmissing earnings at baseline in

January 2010.

The primary outcome from the payroll data used in my analysis is employment, measured

either as having an active account or having positive earnings in a given month. While non-

presence in the payroll data does not indicate unemployment, transitions out of the payroll

data indicate transitions into unemployment or to a new job. Further, there is reason

to think that those covered in the payroll data represent relatively good and high-paying

jobs. Existing research by Cardiff-Hicks et al. (2015) and Brown and Medoff (1989) has

noted that large employers tend to pay higher wages and provide more generous benefits.

For individuals covered in the payroll data at baseline, median earnings were over $35,000.

Median earnings in Florida in the 2010 American Community Survey were about $27,000.

Given the relatively young age distribution in the cited driver sample, and the fact that

payroll earnings is a lower bound on total earnings, the evidence suggests that jobs covered

in the payroll data are higher-paying than average.15

15Appendix .3 presents further validation of the payroll employment measure. Specifically, Iestimate the effect of separations from payroll-covered jobs occurring several months before a trafficstop on credit report outcomes using an event-study approach. I find that unpaid bills increaseby about 5 percent and credit card balances decrease by about 5 percent in the year following aseparation, suggesting a deterioration in financial health. See Appendix .3 for more detail.

15

1.4 Empirical Strategy

1.4.1 Event Study

The goal of the empirical analysis is to estimate the reduced form impacts of traffic tickets.

Given that only cited drivers are matched to the credit file, the natural source of variation

provided by the data is the timing of citations among ticketed drivers, which lends itself to

an event study approach. Specifically, I estimate regressions of the form:

Yit =∑τ

ατ + f(ageit) + φi + κt + γi(t) + εit (1.1)

where φi and κt are individual and time, i.e. year × month, fixed effects. Here, τ indexes

event time, or months since citation, and the coefficients on the event time indicators ατ

are the object of interest. Identification of the event-time effects relies on variation in the

timing of traffic stops – deviations in y are compared for individuals at the same calendar

time but different event time. To flexibly control for lifecycle dynamics in the credit bureau

outcomes, I include a quartic in age. A causal interpretation of the post-event coefficients

rests on the assumption that, among cited drivers, the precise timing of a traffic stop is as

good as random.

Coefficients for τ < 0 are typically viewed as a test of the identifying assumption. Pre-

event trends may suggest that changes in y predict the timing of the event. Several of

the outcomes under study exhibit a slight pre-trend but a trend break around the time of

traffic stop, so I also include person-specific linear time trends, γi(t) in my main estimates of

equation (1.1).16 When linear trends are included, the α’s are identified off deviations from

trend and the identifying assumption is that the traffic stop’s timing is random conditional

on a secular pre-event trend.

16I show estimates without individual trends in the appendix. Results are qualitatively similar inall cases, with some outcomes displaying more of a trend-break then a simple increase or decreasearound the time of a traffic stop.

16

Estimates of equation (1.1) using all available data are computationally infeasible because

I cannot invert a matrix larger than 60 million rows with the computing tools available for

analyzing the credit report data. Therefore, I rely on a 25 percent random sample of drivers

in the event study analysis. To construct the sample, I first identify the set of drivers who are

present in the credit report data in January of the year prior to their first observed citation

in 2011–2015, then select individuals ages 18-64 as of that month. There are 2.8 million

such drivers, and I draw a 25 percent random sample resulting in 710,486 individuals. I

include each individual in the data for four years beginning in the aforementioned January,

which reduces the dimensionality of the dataset but retains at least 12 months of pre-citation

and 24 months of post-citation data for each driver and allows the generations (drivers with

events in different years) to overlap, which aids in the separate identification of the time and

event time effects.

Column 1 of Table 1 shows summary statistics for the event study sample, reported

as of the base period. Cited drivers are, on average, 44 percent female, 38 years old, and

60 percent nonwhite, where Hispanics are considered nonwhite. While average estimated

income is very close to the statewide average of $32,000, the average credit score is 609,

which is just above subprime and about 50 points lower than the statewide average of 662.

The typical driver has 2.8 accounts and a $2,169 balance in collections at baseline. About

two percent of drivers have filed for bankruptcy in the past two years as of the base period.

Prior to a traffic stop, 80 percent of drivers maintain at least one open account, revealing

that borrowing is somewhat tenuous among the sample of cited drivers. The typical driver

maintains 2.82 open revolving accounts and a $6,500 revolving balance. Of drivers in the

event study sample, 34 percent have an auto loan and 25 percent have a mortgage at baseline.

In terms of payroll data measures, 16 percent of drivers in the event study sample are

indicated as having a job, while 11 percent have positive reported earnings. Among those

with earnings, average monthly earnings were $3,399, which corresponds to an annual salary

of $41,000.

17

1.4.2 Matched Difference-in-Differences

I supplement the event study approach with a difference-in-differences analysis. While the

data do not provide an organic control group, I use a coarsened exact matching procedure Ia-

cus et al. (2012) to construct one. The control group aids in the estimations of counterfactual

trends and allows for a fully nonparametric differencing out of age or lifecycle effects.

Citations data linked to credit bureau data span from 2011 through 2015. I use drivers

receiving their first citation in 2011 as the treatment group and drivers receiving their first

citation in 2014–2015 as the control group. The period covering January 2012 through

December 2013 is preserved as a follow-up period where the treatment drivers have all

received treatment (at least one traffic ticket) and control drivers have not. The delineation

of treatment and control groups was meant to balance the desire to maintain a longer follow-

up period with the need to retain sufficient mass in the control group. Matching occurs as

of January 2010, the first month of credit report data. Credit report data from January

2010 through December 2013 is then used in the analysis, guaranteeing that 12 months of

data are available before and 24 months of data are available following the treatment group

citation. Figure 1.2 offers a graphical depiction of the timeline.

Matching Procedure

To be eligible for inclusion, individuals must be present in the credit file as of January

2010. I also require that individuals be between 18 and 64 years of age in January 2010.

There are 818,000 eligible treatment drivers and 613,000 eligible control drivers, about 40%

of the universe of drivers ever matched to the credit bureau data. I use a parsimonious

set of characteristics for the match and intentionally avoid matching on outcome variables.

Treatment and control drivers were matched using age bins (18-24, 25-29, 30-34, 35-39, 40-44,

45-49, and 50+), gender, race (measured as white or nonwhite where Hispanic is considered

nonwhite), county of residence, and quintiles of credit score and estimated income. Gender,

race, and county of residence are measured using the citations data and hence are measured

18

at the the time of citation, while age, credit score, and estimated income are taken from the

credit bureau data and are measured in January 2010. Because credit score and estimated

income are highly correlated with age, the quintiles are computed within age band.

I also use pre-citation growth rates in credit score and estimated income as matching

variables. Specifically, I compute the January 2010–December 2010 change in credit score

and estimated income for each driver, and match on within-age-bin quintiles of these growth

rates. Note that neither estimated income nor credit score are primary outcomes in my

analysis – matching on the first year growth rates in these variables does not ensure parallel

pre-trends in focal outcomes across groups. Ultimately, it does aid slightly with ensuring

pre-trend similarity, which is why I opt for including the growth rates in the list of matching

variables. However, including the first-year growth rates in the set of matching variables is

not at all necessary for obtaining the main results.17

Once all possible matching pairs have been identified, I ensure that control drivers are not

associated with multiple treatment drivers and that each treatment driver is matched to one

and only one control driver using random draws. Control drivers are then assigned the same

traffic stop date as their matched treatment driver, allowing for a comparison of changes

in outcomes around the exact time of a traffic stop for an individual receiving a citation at

that date with her control driver, who is observably similar but does not receive a citation

at that time. Note that, by construction, treated and control drivers are (approximately)

the same age at the time of treatment. Hence, once can think of the identification strategy

as leveraging variation in the age at first citation, with treatment drivers first ticketed when

a few years younger than control drivers.

17In Figure A-11, I plot outcome means for treatment and control drivers using all candidatesand no matching, instead allocating placebo citation dates to control drivers randomly. The vastmajority of main results remain in this no-matching approaching.

19

Characteristics of Matched Sample

Columns 2 and 3 of Table 1 present summary statistics for the matched sample as of January

2010.18 On average, individuals in the matched sample are observably quite similar to those

in the event study sample. By construction, treatment and control drivers are similar in terms

of demographics, credit score and estimated income. But as shown in Panels B-D, individuals

are quite similar on most unmatched dimensions as well. Treatment and control drivers have

similar numbers of collections and collections balances and nearly identical derogatory and

delinquency rates. Treated and control drivers also maintain similar numbers of revolving

accounts, own cars and homes at similar rates, and match very closely in terms of payroll

data outcomes.

Estimation

The first step in the analysis of the matched sample is to plot average outcomes around the

traffic stop date for treatment and control drivers. Recall that control drivers are assigned

their matched treatment driver’s citation date as a placebo date, which allows for the com-

putation of event time (i.e. months since actual or hypothetical citation), for both group of

drivers. The natural regression analogue to comparing changes over time in the raw data is

Yit =24∑

τ=−12

[ θτ × Treati × ατ + ατ ] + φi + εit (1.2)

where ατ is a month relative to citation indicator and φi is an individual fixed effect. The

θτ ’s are the coefficients of interest, measuring treatment-control differences at each month

relative to the citation.

18Table A-2 compares means for matching candidates, all individuals meeting the sample in-clusion criteria described above, and the individuals successfully matched. The primary takeawayfrom a comparison of means for candidates and matches is that control candidates are slightly lessdisadvantaged than treatment candidates. Accordingly, the matching procedure seems to drop theworst-off individuals from the set of treatment candidates and the best-off individuals from the setof control candidates.

20

For the estimation, I sample data between 12 months prior and 24 months following the

treatment date. I further subset the data to include only every third month, centered at

the month of the citation date, which greatly improves estimation speed. Finally, a key

component of the empirical analysis will consider heterogeneous treatment effects across

subsamples. For example, I compare the impact of citations for low versus high income

individuals. While I confirm both in the raw data and with estimates of versions of equation

(1.2) that treatment and control drivers trend similarly prior to the traffic stop on average,

parallel trends may not be perfectly satisfied in every subsample. To ensure that differences

in estimated effects across subsamples are not driven by variation in pre-treatment trends,

my primary specification using the matched sample is a trend-adjusted version of equation

(1.2):

Yit =24∑τ=0

[ θτ × Treati × ατ + ατ ] + φi + κt + Treati × τ + εit (1.3)

Equation (1.3) is identical to equation (1.2) except that event-time and event-time-treatment

interactions for τ < 0 are dropped, while a treatment indicator interacted with a linear trend,

Treati × τ is added. I also add year and month fixed effects, represented by κt, to capture

secular seasonality and time effects. The θτ coefficients are treatment-control differences in

each post-ticket month after adjusting for differences in pre-treatment trends across the two

groups. When presenting the main results, I report the θ’s for 12 and 24 months post-citation.

I cluster standard errors at the matched pair-level.

Identification

Identification in the matched difference-in-differences analysis comes from comparing the

changes around the traffic stop date for treatment drivers, who indeed receive a citation

at that date, and control drivers, who receive citations a few years later. The identifying

assumption is that treatment drivers would have trended similarly to control drivers in the

absence of a traffic stop. As with most applications of difference-in-differences, there are two

primary threats to this assumption – different pre-treatment trends across treatment and

21

control groups and unobserved shocks correlated with both treatment status and treatment

timing. I verify that the two groups follow similar pre-treatment trends by examining the raw

data and estimating non-parametric event study-style specifications in the spirit of equation

(1.2) above. Further, to be conservative, I trend-adjust the regression estimates so that

coefficients are identified off deviations from pre-treatment trends as in equation (1.3).

By construction, treated and control drivers are approximately the same age at the time

of treatment. Hence, one can think of the identification strategy as leveraging differences

in the age at first (observed) citation, with treatment drivers first ticketed when a few

years younger than control drivers. Alternatively, one could think of the matching step as

identifying candidates for a traffic stop at a specific time and the analysis as comparing

candidates with stops that do and do not occur. In this framework, the empirical analysis

parallels studies that compare, for example, accepted and denied applicants around the time

of an application (e.g., Cellini et al. 2010, Mello 2019). Lastly, the empirical design is similar

to studies using individuals who receive treatment but outside the relevant time range as a

control group, such as Currie et al. (2018).

1.4.3 Estimating Impacts of License Suspensions

A potentially important mechanism through which traffic tickets may impact individuals

is through their impacts on driving privileges. Unpaid citations result in suspended driver

licenses, and a lack of a valid driver’s license may jeopardize an individual’s employment

arrangements. Additionally, the effects of license suspensions are of general interest, because

state and local governments use DL suspensions as punishment for an array of infractions.

For example, many states revoke driver licenses for individuals convicted of drug offenses.

While I cannot cleanly identify nonpayment of fines in the citations data, I estimate the

effect of suspensions levied for accruing too many driver license points. The majority of

citations carry three points and twelve points in twelve months results in a 30 day license

suspension. Hence, I estimate the impacts of license suspensions using an event study ap-

22

proach around the time of a fourth citation in one year. I also sample individuals receiving

three, but not four, tickets in a one year period as a quasi-control group. The estimating

equation is

Yit =∑τ

θτ × Treati × ατ +∑w

βw + φi + κt + εit (1.4)

where τ indexes time around a license suspension and w indexes time around an initial ticket.

The βw’s are event time indicators corresponding to the initial citation date and the ατ ’s are

event time indicators corresponding to the 4th citation date, all of which are set to zero for

control drivers.

The final two columns of Table 1 presents summary statistics for the suspensions sample.

There are 79,490 individuals who receive four tickets in the one year following their initial

citation and 135,701 individuals who receive three but not four tickets over the same period.

Treated and control drivers are comparable to each other in terms of demographics but

are distinctly more likely to be male, more likely to be nonwhite, and are slightly younger

on average than drivers in the event study and matched samples. In terms of credit bureau

outcomes, the serial offenders used in the suspensions analysis are clearly more disadvantaged

than the average cited driver.

1.5 Results

1.5.1 Financial Strain

Figure 1.3 plots event study estimates corresponding to equation (1.1) for the financial strain

outcomes. In each case, I show the point estimates and 95 percent confidence bands for full

sample (blue circles) and using only the poorest quartile of drivers in terms of baseline

estimated income (red squares). The figures illustrate a consistent pattern, with all four

strain outcomes increasing following a citation. For collections, collections balances, and

delinquencies, the increase is more pronounced among poor drivers. The response is both

gradual and slightly lagged, which makes sense given that an unpaid bill, for example, will

23

take time to be sent to a collections agency and then appear on a credit report. Dobkin et al.

(2018), who study collections around the time of a hospital admission using an event-study

approach, find a quite similar time pattern.

The first four panels of Figure 1.6 plot the corresponding raw data for treated and control

drivers in the matched sample. In the case of all four strain outcomes, treated drivers follow

nearly identical trends to control drivers prior to the traffic stop date, suggesting a successful

matching procedure. However, trends diverge around the time of treatment, with treated

drivers exhibiting relative increases in collections, collections balances, derogatories, and

delinquencies following a traffic stop.

Table 2 plots the corresponding regression estimates. Each row corresponds to an out-

come and column 1 reports the baseline mean. Columns 2-3 report the 12 and 24 month

estimates from the event study approach, while columns 4-5 report the 12 and 24 month

estimates from the matched difference-in-differences approach. Event study estimates imply

that one year (two years) out from a traffic stop, individuals have about 0.09 (0.14) more

reported collections, 0.04 (0.05) more derogatory accounts, and 0.01 (0.02) more delinquen-

cies. Relative to the baseline means, the one (two) year effects are about three (five) percent

for collections, two (three) percent for derogatories, and two (three) percent for delinquen-

cies. In the fourth row, the outcome is an index that combines collections, derogatories, and

delinquencies, with the point estimate implying that traffic stops increase strain by about

2-3 percent of a standard deviation.19 Balances past due and balances in collections also

increase by about 2-5 percent. Estimates from the difference-in-differences approach are very

similar in most cases.

19The index is computed by standardizing each component, summing, and then standardizingagain. For the event study sample, I standardize relative to the base period. In the matcheddifference-in-differences approach, I standardize relative to the control group in the base period.

24

Table 3 reports estimates separately for the poorest and richest quartile of drivers.20 As

was apparent in Figure 1.3, the impact of traffic stops on collections is significantly larger for

poor than for rich drivers, with the disparity present across both research designs. Estimated

impacts on collections balances, for example, are 3-4 times larger for the poorest quartile of

drivers ($142) than for the richest ($38). The two year impact on collections balances for

poor drivers is over $200, larger than the size of the typical fine, in both specifications.

When considering heterogeneous effects on the account-based measures of financial strain,

we should keep in mind that richer drivers tend to have more accounts and higher balances

(see Table 4), and therefore may have more space for growth in outcomes such as delinquen-

cies and adverse events. Still, I find larger impacts of traffic tickets on delinquencies for poor

than rich drivers. Event study estimates suggest similar effect sizes on derogatory events for

the richest and poorest quartiles, while the difference-in-difference estimates imply a larger

impact for poor drivers.

1.5.2 Payroll Employment

Figure 1.4 plots coefficients from event study estimates where the dependent variable is an

indicator for having positive payroll earnings in a given month. Recall that traffic tickets

may impact employment arrangements either through their impacts on financial distress,

which may reduce labor supply or job-finding rates, or through their impacts on driving

costs. Results for the full sample (blue circles) show a flat pre-event trend and a drop in

the likelihood of employment beginning in the first 2-3 months following a traffic stop and

persisting a full two years later. Poorer drivers appear to be trending slightly upward prior to

a traffic stop and experience a more dramatic drop following the date of a citation. The final

20The quartiles are determined using baseline estimated income in the matched sample. I usethe same thresholds when splitting the event study and license suspensions samples. Worth notingis the fact that the rich quartile of drivers are not particularly well-off due to the apparent negativeselection into receiving a traffic ticket. Nearly 20% of the richest quartile of drivers has a subprimecredit score at baseline. Median estimated income among the richest quartile, about $53, 000, isbelow the 75th percentile of personal income in Florida.

25

panel of Figure 1.6 plots the corresponding raw data from the matched sample, which reveals

a clear disparity between treatment and control drivers emerging only after the treatment

group’s traffic stop date.

Coefficients are reported in the first two rows of Table 4. For the full sample, regression

estimates imply a half a percentage point decline in the likelihood of positive earnings in

the payroll data, about a four percent decline relative to a baseline mean of twelve percent.

Difference-in-differences estimates are nearly identical. Table 5 compares effects for the

richest and poorest quartile of drivers and reveals that the impacts on employment are

significantly more pronounced among poor individuals. For the poorest quartile of drivers,

the one-year impact on employment is nearly a full percentage point (8 percent), while the

effect for rich drivers is about 0.3 percentage points (2.5 percent). The effect size disparities

between rich and poor drivers are even larger when considering the difference-in-differences

specification. Difference-in-differences in estimates of the employment (positive earnings)

effects for the richest quartile of drivers are not statistically different from zero.

Figure A-9 demonstrates that employment effects are driven both by an increase in the

likelihood that a currently employed individual transitions out of the payroll data and a

decrease in the probability that an individual transitions into the payroll data. Specifically,

I split the matched sample into individuals with and without payroll earnings as of 12 months

prior to the citation date and plot employment probability over time. The figure shows that,

relative to the control group, treated drivers in the payroll data at baseline become more

likely to transition out following a traffic stop. In the same vein, treated drivers not in

the payroll data at baseline become relatively less likely to transition into the payroll data

post-treatment.

Table A-4, which presents difference in difference estimates for payroll earnings, suggests

that traffic tickets have little impact on earnings for the average driver who remains in a

covered job. Figure A-7 plots event study coefficients where log monthly earnings is the

dependent variable. Consistent with the difference-in-difference estimates, there appears

26

to be little impact on earnings in the full sample. The event study estimates suggest a

1-2 percent decline in earnings for the poorest quartile of drivers, however. Neither the

difference-in-differences nor the event study estimates are precisely estimated.

1.5.3 Borrowing and Credit Usage

Event study estimates for the borrowing outcomes are plotted in Figure 1.5, while the raw

means for the matched sample are shown in Panels E-H of Figure 1.6. While we would

expect a surprise expense such as a traffic ticket to, if anything, increase financial strain,

the predicted impact of such a shock on borrowing is, ex ante, ambiguous. On one hand,

an unplanned expense may increase demand for credit. However, the impacts on financial

duress discussed above may reduce access to credit through their impacts on credit scores or

borrowing limits. While I estimate relatively small impacts of traffic stops on credit scores

(about minus two points as shown in Table A-3), other studies have found that collections

may result in reduced credit limits. Unfortunately, I do not observe borrowing limits in

the credit report data. Dobkin et al. (2018) estimate that hospital admissions increased

collections balances by $122 and, correspondingly, that credit limits fell by $500, despite

also finding a small effect on credit scores (-1.6).

Both the event study and matched difference-in-differences approaches illustrate a reduc-

tion in number of open revolving accounts following a traffic stop. The event study estimates

for revolving balances are noisy, but the raw means for matched treated and control drivers

suggest a relative decline in balances for treated drivers, although the response appears both

delayed in muted. For auto loans, the pattern of results is a bit strange, but if anything,

both the event study and matched difference-in-differences figures would suggest a decline

the likelihood of car ownership beginning 2-3 months following a citation. Both Panel D

of Figure 1.5 and Panel H of Figure 1.6 suggest a decline in the likelihood of having a

mortgage. The slightly lagged responses of revolving balances and durable consumption are

27

consistent with the view that access to credit is affected by the increases in financial strain

and reductions in employment documented above.

Regression estimates, presented in Table 4, show that traffic tickets induce about a 0.04

(1.5 percent) reduction in the number of open revolving accounts in the first year following

a traffic stop. Using the matched difference in differences approach, I find one and two year

effects on revolving balances of -$91 and -$218, with the two year estimate statistically sig-

nificant and implying about a three percent decline at the mean. Event study estimates are

smaller ($30-$50) and not statistically different from zero. Both strategies suggest statisti-

cally significant declines in car and home ownership. While one should note that pre-event

trends in car ownership do not match perfectly for treated and matched control drivers, the

trend-adjusted matched difference-in-difference estimate is sizable. The two year estimate,

-0.044, represents about a thirteen percent reduction in the likelihood of having an open auto

loan. Both strategies suggest 1-2 percent reductions in the probability of home ownership.

Examination of heterogeneous effects by driver income, shown in Table 5, yields mixed

results. Estimated impacts of traffic tickets on revolving accounts are similar across the

poor and rich subsamples (-0.042 and -0.038 in the difference-in-differences specification),

but the similar point estimates imply quite different percent effects, -5 percent for poor

drivers and -0.6 percent for rich drivers, given the different baseline means. Both event

study and difference-in-differences approaches suggest a larger impact on auto loans for poor

drivers, but the rich-poor disparity is larger when considering the event study estimates.

1.5.4 Interpreting Magnitudes

The estimates for credit report outcomes suggest a consistent pattern of results, with traffic

tickets appearing to increase financial strain and reduce credit usage among cited drivers.

However, it is difficult to interpret the estimated magnitudes given that many of the credit

report measures are not what we would consider real outcomes. I use two approaches to aid

in the interpretation of the results, detailed below.

28

Benchmarking to Other Studies

The most similar study to mine is Dobkin et al. (2018), who examine the impact of hospital

admissions on credit report outcomes using an event study approach. Table 6 allows for a

comparison of effect sizes between my paper and Dobkin et al. (2018) (referred to as DFKN

in the table). Panel A highlights that the hospital admissions sample is older and more

advantaged than the cited driver sample. However, the financial shock accompanying a

hospital admission is also more severe. For the nonelderly insured population, the authors

estimate that an average hospital admission increases out-of-pocket medical expenditures by

about $3,300.

As shown in Panel B, estimated 12 month effects of traffic tickets and hospital admissions

on collections (0.075, 0.11) and collections balances ($94, $122) are quantitatively similar.

Given that the average individual in the hospital sample has fewer collections, however, the

percent effects are larger in Dobkin et al. (2018). As shown in Panel B, hospital admis-

sions are associated with a slightly larger decline in revolving balances, -$293 (-2.5 percent),

than are traffic tickets, -$91 (-1.3 percent). On net, the estimated impacts on financial well-

being appear relatively similar across the two contexts, which perhaps makes sense when

considering the larger shock but more advantaged sample in the Dobkin et al. (2018) study.

For context, I also present estimated effects from two other studies in Table 6. Note

that both Herbst (2018) and Dobbie et al. (2017) study positive shocks, and hence the

effects are opposite-signed. Herbst (2018) finds similar effects to mine of income-driven

student loan repayment plans on the number of revolving accounts but larger effects on

balances. Unsurprisingly, Dobbie et al. (2017) find significantly larger impacts of Chapter

13 bankruptcy protection on financial health outcomes.

Benchmarking to Earnings Changes

An alternative method for benchmarking magnitudes is to ask what change in income would

predict the observed increases in financial strain. To approximate this thought experiment,

29

I take a cross-section of individuals from the matched sample as of three months prior to the

traffic stop date with positive payroll earnings. I then fit annualized payroll earnings to a

quartic in each financial strain measure.21 Using the estimated quartic coefficients combined

with the treatment effect estimate, I compute the income change predicted by the estimated

financial stain effects. Specifically, for strain outcome z, I compute

∆(z) =∂y

∂z

(β, z)× θz.

In words, ∆ is the derivative of income with respect to z, a function of the quartic coefficients

β and evaluated at the sample mean of z, scaled by the estimated treatment effect of citations

on z from Table 2. In additional to the individual account measures, I compute the income

metric for the strain index, which can we interpret as the income change implied by the joint

changes in the strain outcomes.

The results are presented in Table 7. Columns 1 and 2 show income losses implying

the difference-in-differences strain coefficients as of 12 and 24 months post citation for the

full sample, while columns 3-6 repeat the analysis for the poorest and richest quartile of

the sample corresponding to the main result tables. In each case, I evaluate at the relevant

baseline mean shown in Table 2 and Table 3. Below the computed dollar values, I show the

implied percentage change in income, evaluated at the relevant sample mean, in brackets.

Row 1 indicates that the sample-wide, one-year impact on collections, 0.075, is about

what would be predicted by a $360 reduction in annual outcome. For poor drivers, the

income-equivalent effect is much larger. The 12 and 24 month increases in collections are

associated with predicted income changes of $663 and $951, respectively. In other words,

a poor individuals’ long-run post-citation increase in collections is observationally similar

to about a 5.5 percent income loss. The estimated treatment effects on derogatories and

21A flexible functional form is important for fitting the data well. The observed relationshipbetween, for example, number of collections, and earnings is highly nonlinear, with a steep gradientat low values of collections and a much flatter gradient at high values.

30

delinquencies are notably smaller, and therefore the income-equivalent effects are smaller as

well. The income loss predicting the observed increase in the strain index similar to that

predicting the collections effect alone.

It is also useful to benchmark the treatment effects against the estimated impacts sepa-

rations from payroll-covered jobs, which are presented in Appendix .3. The effect of a traffic

ticket on collections (0.075) is about two-thirds as large as the effect of a job separation

(0.114), while the ticketing effect on revolving balances is (-$95) is about one third as large

as the separation effect (-$280). Job separations increase delinquencies by 0.2, or about

twice as much as traffic fines. The estimated impacts of job separations and traffic tickets

on derogatories and collections balances are similar, while the citation effect on number of

credit cards is about 40 percent larger than the separation effect.

1.5.5 Heterogeneity

As discussed above, the impacts of traffic tickets on financial strain and employment differed

meaningfully for high- and low-income drivers. In this section, I consider heterogeneity along

other dimensions. To be parsimonious, I first consider only impacts on the financial strain

index and employment using the matched difference-in-differences framework.

Figure 1.7 plots one year difference-in-differences estimates for the strain index across

subsets of drivers. Impacts are larger for younger (under 35) than for older (over 35) drivers

and appear similar for women and men. Treatment effect estimates are similar for subprime

and prime individuals, but are more pronounced for individuals with low credit usage, mea-

sured either as having a below median revolving balance or having any durable account at

baseline. The most striking cut of the data is along the dimension of baseline collections.

Traffic tickets have no effect on strain for drivers with a collections balance below $150 at

baseline, suggesting that the entire effect is driven by individuals who already have unpaid

bills.

31

Figure 1.8 is identical to Figure 1.7 except that the dependent variable is employment.

The pattern of heterogeneity is similar – subsamples with a large strain effects also tend

to have larger employment effects and vice versa. Treatment effects on employment are

larger for younger individuals and especially pronounced for young women, and are larger

for individuals with higher collections, lower credit scores, and less borrowing at baseline.

Motivated by the striking difference in strain impacts across individuals with high and

low initial collections, I present one year difference-in-differences estimates by baseline credit

score and collections for all outcomes in Table 8. Note that below the standard errors, I

report the relevant baseline control mean in brackets. As mentioned previously, one caveat

with interpreting differences in effects on borrowing-related outcomes across subsamples is

that credit usage may also differ across samples. Subprime individuals maintain about one

quarter as many revolving accounts, for example, and individuals who do not maintain open

accounts cannot experience increases in delinquencies or decreases in balances.

As shown in columns 2-3, impacts on collections and employment are about two times as

large for subprime than for prime individuals. The disparate collections effect makes sense

– credit is more readily available for prime individuals, and such individuals may be able to

cover the unexpected nuisance fine through borrowing.

The effect size gaps are even larger when comparing individuals with high and low base-

line collections in columns 4-5. Point estimates for collections and adverse financial events

are, in fact, negative for individuals with little to no balance under collection at baseline. In-

dividuals with above median baseline collections balances experience a four percent increase

in collections, a six percent increase in collections balances, and a four percent increase in

derogatory accounts in the one year following a traffic stop. Reductions in revolving accounts

and revolving balances are also driven entirely by individuals with unpaid bills at baseline.

The effect of a traffic ticket on payroll employment is about two and a half times larger for

the high collections sample.

32

Overall, there is a clear pattern to the heterogeneity of the results. For individuals

exhibiting financial stability at baseline, e.g. those without unpaid bills and those with high

credit scores, traffic citations have minimal impacts. Drivers showing signs of instability,

such as high collections balance, low credit scores, and low borrowing, experience significant

increases in measures of financial strain and the largest drops in employment. This set of

results suggests the presence of a poverty trap where small shocks have deleterious effects

on already distressed individuals but are negligible for the non-distressed population.

The notion of the poverty or financial distress strap is shown empirically in Figure 1.9.

The figure shows one year (blue circles) and two year (red squares) difference-in-differences

estimates of the impact of a traffic stop on the financial strain index, estimated separately

by quantiles of strain at baseline. The one year treatment effects are clearly increasing in

baseline strain. Through much of the distribution, the gradient in the two year effects is even

stronger. In other words, the effect of a small shock is larger for more distressed individuals

and, further, effect sizes increase more over time for such individuals.

1.5.6 Mechanisms

As detailed in the discussion of the institutional background, a traffic citation represents a

potentially multi-faceted treatment, with the exact treatment faced by any given individual

depending on post-citation decisions such as whether the individual chooses not to pay or

opts to contest the ticket. While it is useful to note that the Florida Clerk’s office’s records

indicate that over 90% of citations are paid on time, the data from the Florida Clerks include

some information on the court disposition associated with each citation that is potentially

useful for disentangling the relative important of the aspects of traffic fines beyond the pure

expense shock in explaining the estimated effects. 22

22There are important caveats to consider regarding the court dispositions data. Traffic citationsare resolved through the ticketing county’s court system. The individual county clerks then sharedisposition information with the Florida Clerk of Courts. However, many of the disposition-relatedfields are not required to be shared with the state clerk. Futher, information on dispositions reflectcurrent status. A disposition indicating payment may not reflect on-time payment, for example.

33

Specifically, I examine treatment effects for individuals whose dispositions indicate pay-

ment and those whose dispositions indicate a traffic school election. Individuals making

on-time payment may opt to participate in traffic school, which consists of four hours of

instruction and costs $25, but suppresses the points associated with the citation from ac-

cruing on the driver’s record. Because she makes an on-time payment and faces no increase

in license points, a driver opting for traffic school almost surely will not suffer a license

suspension or an increase in car insurance premiums.23

Comparing payers and school-attendees to the sample as a whole and to each other

should help isolate the impacts of various components of the treatment. The typical payer

will not incur a license suspension, but those with significant driving histories or making late

payments may. Payers will incur increased license points possibly leading to increased auto

insurance costs. Traffic schools attenders will not bear any burden of license suspensions or

increased license points. However, a traffic school election signals a savviness of institutions,

an ability to come up with an extra $25, and the flexibility to participate in four hours of

instruction. As shown in the footer of Table 9, school participants are older, richer, and have

higher credit scores. While I cannot account for unobservable differences between the two

groups of drivers, I do present estimates using the reweighting scheme from DiNardo et al.

(1996) to account for observable differences across the subsamples at baseline. Specifically,

I group the data into cells according the baseline age, income, and credit score bands used

in the matching step. I then reweight the cells in the payer and school subsamples to match

the distribution in the full sample.

Table 9 shows the one-year difference-in-differences estimates for the financial strain index

and employment by disposition. Columns 2-3 indicate that the impact of a citation on strain

is nearly two times larger for payers than for individuals opting for traffic school. Similarly,

employment effects are about 50 percent larger for payers, with the point estimate not

statistically significant in the traffic school sample. While neither difference is statistically

23Moreover, due to concerns over the quality of the dispositions data raised earlier, traffic schoolattendees are the only subsample who are guaranteed to have made on-time payment.

34

significant, the pattern of results is consistent with the hypothesis that the potential costs of

tickets beyond the pure financial shock, particularly those associated with increased driver

license points, are an important driver of the results.24

However, columns 4-5 reveal that the treatment effect disparities are much smaller after

reweighting the data to account for observable differences between the two samples. While

the point estimates still suggest that those attending traffic school experience slightly smaller

increases in financial strain, the narrowing of the treatment effect disparities suggests that

differences in the type of individuals opting for traffic school are quite important in explaining

the treatment effect disparities. On net, the evidence provides some support for the view

that license suspensions and increased insurance costs are relevant for explaining the impact

of tickets but also highlights that individuals making on-time payment still experience a

worsening in financial standing. The small effects for school attendees using the unweighted

data supports the view that the type of individual choosing traffic school is less susceptible

to the harm caused by a citation.

1.5.7 Effects of License Suspensions

I supplement the comparison of effects across disposition types with a direct analysis of

license suspensions due to the accrual of driver license points using the empirical approach

described in section 4.3. Figure 1.10 plots event study coefficients around the time of an

individual’s fourth citation in twelve months, with proxies for the timing of a 30-day points-

based license suspension. Recall that the regressions also include indicators for months since

initial citation (and use individuals accruing three but not four tickets in twelve months

to help in the estimation of these coefficients), so the estimates should be interpreted as

additive to the effects of an initial traffic stop.

24Another piece of evidence consistent with this view is presented in Figure A-12 in the appendix,which plots estimated impacts of citations by quantiles of the imputed fine amount and showsminimal treatment effect gradients with respect to fine size. If effects are due only to financialshocks, we might expect larger impacts associated with larger fines.

35

Panels A and B document sharp increases in collections following a license suspension.

Quantitatively, the impact appears more pronounced than for the average traffic stop, and

strikingly, the increase in collections is nearly as large for the typical driver as for the poor-

est individuals.25 Panel C documents a fall in borrowing, measured with revolving balances,

coinciding with the timing of a license suspension. Finally, Panel D illustrates an immediate

and sustained drop in the likelihood of having positive payroll earnings following the revo-

cation of driving privileges. The short-run fall in employment appears more pronounced for

the poorest quartile of drivers. Figure A-14 plots event study coefficients for other outcomes.

I present the coefficient estimates in Table 10. One year out from a license suspension,

individuals have about 0.15 (4 percent) more collections and $140 (5 percent) higher col-

lections balances. Both effects are larger than the one-year event study estimates focused

on an initial citation. Incidences of adverse financial events increase by about 4 percent. I

also find evidence of a slight increase in bankruptcy, measured by the presence of any public

records bankruptcy filing in the past 24 months on a credit report, following a suspension.

Revolving balances and employment probability are about 2.5 percent and 3 percent lower

one year out from a suspension. As shown in Panel B, estimated effects are slightly larger

for the poorest subset of drivers. Recall from Table 1 that the license suspension sample is

more disadvantaged, and therefore the poor driver group is more representative of the sample

as a whole than in the analysis of initial citations. On average, one year impacts are 10-25

percent larger for poorer drivers. Poor drivers experience larger drops in employment (about

5 percent), but no increase in bankruptcy filings, likely due to the fact that bankruptcy is

quite rare among individuals without much borrowing.

The analysis of license suspensions is not only independently interesting, but also can

provide insights about the mechanisms underlying the main results. Some of the estimated

effect of citations alone is almost certainly due to suspensions imposed on individuals electing

25Note that I use a baseline estimated income of $21,000 as the threshold for the poorest subsetin the suspensions analysis for comparability between citation effects and suspensions effects amongpoor drivers. $21,000 is the 37th percentile of baseline estimated income in the suspensions sample.

36

non-payment or those with poor driving records at baseline, both of which are difficult to

observe directly in the data. The fact that the effects of suspensions on wellbeing are

substantial lends credence to this view. On the other hand, the suspension effects are not

enormous relative to the main estimates, implying that the treatment effects of citations

cannot be due only to ensuing license suspension effects. The observation that citations

increase distress even among individuals who participate in traffic school, discussed above,

also supports this claim.

1.6 Estimating Welfare Effects

1.6.1 Framework

Thus far, we have considered an array of evidence illustrating declines in wellbeing in the

two years following a traffic stop. To quantify welfare losses, I adapt a common approach

for valuing policies (e.g. Finkelstein et al. 2015, Deshpande 2016) to the dynamic nature of

the treatment effects. The approach approximates the following thought experiment – at

the time of the traffic stop, how much would an individual be willing to pay to avoid the

ensuing utility loss? Specifically, assume individuals have utility over consumption u(c) and

discount the future at rate β. Let D be an indicator for whether an individual receives a

traffic ticket at t = 0. The parameter of interest is V from the following equation:

u(c0 − V ) +T∑t=1

βtu(ct|D = 0) = u(c0) +T∑t=1

βtu(ct|D = 1). (1.5)

The left hand side is the utility value of the consumption path for an unticketed driver

except that the individual pays V at time zero. The right hand side is the consumption

path for a ticketed driver. V is the foregone consumption at t = 0 that makes an individual

indifferent between the ticketed and unticketed consumption streams, which we can interpret

as willingness to pay to avoid the negative downstream consequences of a traffic ticket.

37

Solving equation (1.5) requires a function form assumption on u(·), as well as estimates

of the two consumption streams. A common form for u(·) is a constant relative risk aversion

(CRRA) utility function,

u(c) =c1−γ

1− γ

I take γ = 1, implying a logarithmic utility function, the mean estimate in Chetty (2006b), as

a benchmark. Note that, in this framework, increasing the curvature in the utility function

will typically reduce estimates of V by increasing the pain associated with the one-time

payment at low levels of c.

For simplicity, I consider one- and two-year effects and assume individual’s discount the

future at rate 0.96. To estimate the consumption paths, I take a proxy measure y and use

means over (event) time as the untreated consumption path. I then add the month specific

treatment effects from estimates of (1.3) to the means to obtain the treated consumption

stream:

[ct|D0 = 0] = µyt , [ct|D0 = 1] = µyt + θt.

where µyt is the mean of y for the control group at time t.

1.6.2 Estimating Consumption

Even in credit report data, consumption is not observed. The most straightforward ap-

proach to estimating consumption is to assume no savings and proxy consumption with

income. While income is not observed directly for individuals without payroll earnings, I

can approximate income changes using either the credit bureau’s estimated income measure

or using the employment treatment effects combined with an assumption about the earnings

loss associated with employment transitions. For the average driver, difference-in-differences

estimates imply one- and two-year reductions in estimated income of $189 and $385 (see Ta-

ble A-3). At the mean estimated income of $33,000, and assuming log utility and β = 0.96,

these effects imply V = $534.

38

Alternatively, using the estimated employment impacts does not rely on a measure of

unknown origin, but requires two important assumptions. First, one needs an assumption

about how the employment estimates should be scaled. Difference in differences estimates

suggest declines in employment by between one half and three quarters of a percentage point,

but rely on an employment measure with low coverage. Scaling by the coverage and assuming

a population-wide employment rate of about 90 percent, the estimates imply one and two

year employment declines of 2.7 and 4.5 percentage points. Second, one needs an assumption

on earnings losses occurring from employment transitions. A comparison of payroll earnings

with ACS data in the matched sample implies payroll covered jobs pay about $8,000 more

annually. Hence, a back-of-the envelope calculation suggests one and two year income losses

of $216 ($8, 000× .027) and $360, yielding a very similar estimate of V .

These welfare calculations ought to be considered conservative. I consider two year

impacts because that is the time horizon that can be reliably studied in the data. In nearly all

cases, treatment effects persist for the full two years. To the extent that the effects persist or

grow in the long-run, an estimate of V based on a two-year window is understated. Moreover,

the impacts on outcomes such as collections and adverse financial events may have long-run

impacts on access to credit, diminishing an individual’s ability to smooth consumption in

the future and resulting in additional utility losses. Finally, the computation of V does not

consider welfare effects associated with the reductions in durable consumption.

1.6.3 Discussion

While simplistic, the above welfare calculation is useful for considering the policy implications

of my findings more generally. Before discussing the relevance of the results for policing,

however, it is important to note the argument of Atkinson and Stiglitz (1976) that welfare

losses induced through commodity taxation, in this case the taxation of traffic infractions,

ought to be remedied with redistribution through the income tax system. Moreover, the

finding that many low-income households are not insured against expense shocks suggests

39

that social programs offering insurance against expenditure or income risk may yield large

benefits.

To consider the implications of my findings for criminal justice policy, note that existing

evidence and standard economic theory would suggest that local governments have two

goals when issuing traffic tickets — promoting safety and raising revenue. For example,

DeAngelo and Hansen (2014), Makowsky and Stratmann (2011), and Luca (2015) show that

increases in traffic citations reduce car accidents. Baicker and Jacobson (2007), Makowsky

and Stratmann (2009), and Garrett and Wagner (2009) find evidence of a revenue-raising

motive in policing decisions. Standard models for analyzing criminal justice policy typically

build on Becker (1968), and I present a formal Becker-style model in Appendix .2.

The intuition of the model is that an increase in the traffic ticketing rate deters dangerous

behavior by increasing the probability that an individual is audited and sanctioned, but is

costly in terms of policing effort and reduces the welfare of offenders. Increased ticketing

also raises government revenue. Optimal policing will set marginal benefits equal to marginal

costs:

−h′(p)︸ ︷︷ ︸marginal safety benefit

+ r︸︷︷︸marginal revenue benefit

= c′(p)︸︷︷︸marginal cost of policing

− V ′(p)︸ ︷︷ ︸marginal welfare loss

To the extent that a citation represents a lump-sum transfer from an individual to the

government, there are no efficiency implications. An optimizing government should then

trade off the marginal labor costs and marginal deterrence benefits when deciding the optimal

policing intensity.

However, welfare losses associated with citations exceeding the size of the transfer can

be considered deadweight loss and ought to be weighed against the deterrence benefits when

optimizing ticketing intensity. The welfare metric introduced above, which is an individual’s

willingness to pay to avoid future utility losses, embodies the notion of deadweight loss

40

well.26 I find that the typical ticket, which imposes a fine of about $175, induces welfare

losses slightly larger than $500, implying that the safety benefit associated with a marginal

citation must exceed $300 for its issuance to be optimal. More generally, if governments

set optimal enforcement without taking into account the compounding welfare effects of

fines, they will tend to over-police. Quantifying deterrence benefits is beyond the scope of

this paper, but one could speculate that citations issued for minor offenses such as broken

taillights or marginal citations at already high rates of ticketing are unlikely to provide much

return in terms of safety.

The heterogeneous welfare consequences of fines across driver-income levels also highlight

the potential inefficiency of the flat traffic fine schedule. Appendix .2 considers in detail the

implications of an income-based fine schedule. In particular, I present a stylized environment

with two types of individuals, low-income (yL) and high-income (yH) and consider the effects

of moving from a one-size-fits-all fine f0 to a scheme that charges high-income drivers f0 +

∆ and low-income drivers f0 − ∆, where ∆ is positive, small, and satisfies an additional

simplifying assumption detailed in the appendix. The welfare effects of such a policy change

are proportional to the difference in the marginal utilities for poor and rich drivers:

∆×[∂u

∂c(yL − f0)− ∂u

∂c(yH − f0)

]︸ ︷︷ ︸

difference in marginal utilities

× p[1−G(x∗)]︸ ︷︷ ︸number of tickets

(1.6)

which is positive when u(·) is concave. The empirical estimates suggest that the difference

in marginal utilities is potentially large. Under various assumptions about the compounding

utility consequences of fines for poor drivers and values of γ, and taking into account that

about two million citations are issued in Florida annually, the welfare gains to setting ∆ =

$10 are between $6 and $21 million per year. Using the result in section 6.3, the total utility

26Note that, as shown in Appendix .2, for the class of marginal criminals, the welfare costassociated with writing one more citation is 1

1−p [u(y−f)−u(y)], which for small p is approximatelythe utility cost associated with being sanctioned, i.e. the quantity V estimated above.

41

cost of traffic tickets is about $2 billion, implying that the simple $10 fine perturbation could

erode the welfare costs of enforcement by as much as one percent.

1.7 Conclusion

Motivated both by the observation that the incidence of policing falls largely on disadvan-

taged communities and by a growing body of evidence suggesting that many low-income

individuals may be unable to cope with unexpected expenses, this paper studies the effect of

fines for traffic violations on financial wellbeing. To estimate causal effects, I link adminis-

trative traffic citation records to high frequency credit report and payroll data and leverage

variation in the timing of traffic stops for identification.

The empirical analysis reveals that following the receipt of a traffic fine, individuals fare

worse than would otherwise be predicted on a host of credit report outcomes. Citations

increase unpaid bills, delinquencies, and adverse financial events, with the increases most

pronounced for the poorest quartile of drivers. For the average driver, the short-run increases

in measures of financial strain are about what would be predicted by a $285 income loss. For

the poorest drivers, the two-year increases in financial distress are observationally similar

to an $800-900, or about 5 percent, income reduction. I also find evidence of a decline in

borrowing, measured by revolving accounts and balances, as well as the presence of home

and auto loans on credit reports, following a traffic stop

Traffic tickets reduce the likelihood that an individual appears as having any earnings in

payroll data covering large employers by about 0.5 percentage points, or almost 5 percent

relative to the mean. The employment effects are, again, most pronounced among the

poorest drivers. Poor drivers experience an 8 percent drop in the probability of having

payroll earnings in the one year following a traffic stop.

The findings offer several important takeaways. First, consistent with a growing literature

documenting widespread financial fragility among U.S. households, the results imply that

many individuals are not insured against even small financial shocks. When faced with a $175

42

traffic fine, individuals accrue collections and delinquencies on their credit reports, suggesting

an inability to cover the unexpected expense. Second, individuals exhibiting minimal distress

at baseline are largely unaffected by nuisance fines, while those already facing several unpaid

bills experience the most significant declines in financial wellbeing. This pattern of results

is consistent with a poverty trap, whereby already distressed individuals are derailed by

a new expense. Third, both the pure financial shock component of a traffic citation and

the ensuing increases in driving costs, either through increases in insurance premiums or

the revocation of driving privileges, appear to be important mechanisms. And fourth, a

conservative estimate of the welfare loss associated with the average traffic ticket is more

than two times the size of the revenue raised, suggesting that policies to reduce citations

with low public safety benefits could be welfare enhancing.

43

Figure 1.1: Ticketing Frequency and Neighborhood Per Capita Income in Florida

●

●●●

●

●●

●

●

●

●●

●●●

●

●●

●

●

●

●●

●

●

●

●●

●

●

●

10.0 10.5 11.0 11.5 12.0

−0.

4−

0.2

0.0

0.2

0.4

0.6

Log Per Capita Income

Log

Per

Cap

ita C

itatio

ns

Notes: Figure plots binned means of log zip code ticketing frequency (2011-2015) against binnedmeans of log zip code per capita income in 2010 (N=918). Zip code income data taken from theIRS. Number of citations for zip code residents and adjusted gross income are scaled by the numberof tax returns in the IRS data to convert to per capita measures. Coefficient (standard error) fromlinear fit weighted by number of zip code residents is -0.41 (.07).

44

Figure 1.2: Timeline for Matching

●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●

2010 2012 2014 2016

Date

MatchingOccurs

Jan 2010

TreatmentGroup

Ticketed

FollowUp

Period

ControlGroup

Ticketed

Notes: Credit bureau data range from January 2010 through December 2017. Citations datamatched to credit reports range from January 2011 through December 2015. Matching uses creditreport data from January 2010 and growth rates from January 2010 to January 2011. Treateddrivers receive their first citation in 2011. Control individuals receive their first citation betweenJanuary 2014 and December 2016. Subsamples of credit reports from January 2010 through De-cember 2013 are used in the matched difference-in-differences analysis.

45

Figure 1.3: Event Study Estimates for Financial Strain Outcomes

● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ●

−10 −5 0 5 10 15 20 25

−0.

3−

0.1

0.1

0.3

Panel A: Collections

Month Around Traffic Stop

● Full SamplePoorest Quartile

● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ●

−10 −5 0 5 10 15 20 25

−30

0−

100

010

030

0

Panel B: Collections Balance

Month Around Traffic Stop

● ● ● ● ● ● ● ● ● ● ● ● ● ● ●●

●●

●●

●● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ●

−10 −5 0 5 10 15 20 25

−0.

050.

000.

05

Panel C: Derogatories

Month Around Traffic Stop

● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ●

−10 −5 0 5 10 15 20 25

−0.

06−

0.02

0.02

0.06

Panel D: Delinquencies

Month Around Traffic Stop

N otes: Figure plots event study estimates (with 95% confidence bands) for financial strain outcomesusing the event sample (710, 486 individuals). Blue circles correspond to estimates using the fullsample, while red squares correspond to estimates using the poorest quartile of drivers (estimatedincome < $21, 000). Coefficients are normalized to t = −1. All regressions include individual fixedeffects, time fixed effects, individual trends, and control for a quartic in age. Confidence bandsconstructed from standard errors clustered at the individual level.

46

Figure 1.4: Event Study Estimates for (Payroll) Employment

● ● ● ● ● ● ● ● ● ● ● ● ●●

●●

●●

● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ●

−10 −5 0 5 10 15 20 25

−0.

02−

0.01

0.00

0.01

0.02

Month Around Traffic Stop

● Full SamplePoorest Quartile

N otes: Dependent variable is an indicator for positive payroll earnings (µ = 11%). Figure plotsevent study estimates (with 95% confidence bands) using the event sample (710, 486 individuals).Blue circles correspond to estimates using the full sample, while red squares correspond to estimatesusing the poorest quartile of drivers (estimated income < $21, 000). Coefficients are normalized tot = −1. All regressions include individual fixed effects, time fixed effects, individual trends, andcontrol for a quartic in age. Confidence bands constructed from standard errors clustered at theindividual level.

47

Figure 1.5: Event Study Estimates for Borrowing Outcomes

● ● ● ● ● ● ● ● ● ● ● ● ● ● ●●

●●

●●

●● ●

● ● ● ● ● ● ● ● ● ● ● ● ● ●

−10 −5 0 5 10 15 20 25

−0.

050.

000.

05

Panel A: Revolving Accounts

Month Around Traffic Stop

● Full SamplePoorest Quartile

●● ● ●

●● ●

● ● ● ●

●●

● ● ● ● ● ● ●

●● ● ●

● ● ● ● ● ● ● ●● ●

●● ●

−10 −5 0 5 10 15 20 25

−15

0−

500

5010

0

Panel B: Revolving Balance

Month Around Traffic Stop

● ● ● ● ● ● ● ● ●● ●

●●

● ● ●●

●●

●●

●●

●●

●● ● ● ● ● ● ● ● ● ● ●

−10 −5 0 5 10 15 20 25

−0.

020.

000.

02

Panel C: Any Auto Loan

Month Around Traffic Stop

● ● ●●

● ● ●● ● ● ●

●● ● ● ●

● ●● ● ● ● ● ● ● ●

●● ● ● ● ● ● ● ● ● ●

−10 −5 0 5 10 15 20 25

−0.

004

0.00

00.

004

Panel D: Any Mortgage

Month Around Traffic Stop

N otes: Figure plots event study estimates (with 95% confidence bands) for borrowing outcomesusing the event sample (710, 486 individuals). Blue circles correspond to estimates using the fullsample, while red squares correspond to estimates using the poorest quartile of drivers (estimatedincome < $21, 000). Coefficients are normalized to t = −1. All regressions include individual fixedeffects, time fixed effects, individual trends, and control for a quartic in age. Confidence bandsconstructed from standard errors clustered at the individual level.

48

Figure 1.6: Outcomes Around Traffic Stop for Matched DD Sample (Raw Data)

−10 0 5 10 20

2.6

2.8

3.0

Panel A: Collections

Month Around Traffic Stop

●● ●

●●

●

●

●

●

●

●● ●● Treat

Control

−10 0 5 10 20

2000

2200

2400

Panel B: Collections Balance

Month Around Traffic Stop

●●

●●

●

●

●

●

●

●● ●

●

−10 0 5 10 20

1.65

1.75

1.85

Panel C: Derogatories

Month Around Traffic Stop

●

●

●

●●

●●

●●

●● ●

●

−10 0 5 10 20

0.55

0.65

0.75

Panel D: Delinquencies

Month Around Traffic Stop

● ●●

●●

●

●

●●

●

●●

●

−10 0 5 10 20

2.90

3.00

Panel E: Revolving Accounts

Month Around Traffic Stop

●

●

●

●● ● ●

●● ● ● ● ●

−10 0 5 10 20

6500

7000

7500

Panel F: Revolving Balance

Month Around Traffic Stop

●

●

●

●● ● ●

●●

●●

●●

−10 0 5 10 20

0.33

00.

345

0.36

0

Panel G: Auto Loan

Month Around Traffic Stop

●● ● ●

● ●●

● ● ● ●●

●

−10 0 5 10 20

0.26

00.

270

0.28

0

Panel H: Mortgage

Month Around Traffic Stop

●

●

● ● ● ●●

●●

●

●●

●

−10 0 5 10 20

0.11

00.

116

0.12

2

Panel I: Employment

Month Around Traffic Stop

●●

●

●

● ● ● ● ●

●

●

●

●

N otes: Figure plots averages of denoted outcome for the matched treatment (N = 333, 232) andcontrol (N = 333, 232) groups around the traffic stop date. Blue circles correspond to the treatmentgroup and red squares correspond to the control group. Treatment group means are normalized tothe control group at t = −3.

49

Figure 1.7: Impacts on Financial Strain by Baseline Characteristics

●

●

●

●

●

●

●

●

●

●

●

●

12 Month Treatment Effect

No Durable

Any Durable

Low Balance

High Balance

Low Collections

High Collections

Prime

Subprime

Women 35+

Women 35−

Men 35+

Men 35−

−0.03 −0.01 0.00 0.01 0.02 0.03

N otes: Figure plots estimated 12 month impacts (and 95% confidence intervals) of traffic tickets onthe financial strain index for the denoted subsamples. The financial strain index is a standardizedindex summing collections, delinquencies, and derogatory accounts. See text for additional details.Estimates obtained via difference-in-differences regressions (equation 1.3). Each coefficient is froma separate regression. Subprime/Prime refers to credit scores below and above 600. High/LowCollections refers to individuals with above/below median collections balances. High/Low Balancerefers to individuals with above/below median revolving balances. Any Durable refers to individualswith an open auto loan or mortgage.

50

Figure 1.8: Impacts on Employment by Baseline Characteristics

●

●

●

●

●

●

●

●

●

●

●

●

12 Month Treatment Effect

No Durable

Any Durable

Low Balance

High Balance

Low Collections

High Collections

Prime

Subprime

Women 35+

Women 35−

Men 35+

Men 35−

−0.015 −0.005 0.005 0.015

N otes: Figure plots estimated 12 month impacts (and 95% confidence intervals) of traffic tick-ets on the employment for the denoted subsamples. Employment is an indicator for having apayroll-covered job (µ = 0.16). Results using the alternate employment measure (positive payrollearnings) are nearly identical. Estimates obtained via difference-in-differences regressions (equation1.3). Each coefficient is from a separate regression. Subprime/Prime refers to credit scores belowand above 600. High/Low Collections refers to individuals with above/below median collectionsbalances. High/Low Balance refers to individuals with above/below median revolving balances.Any Durable refers to individuals with an open auto loan or mortgage.

51

Figure 1.9: Treatment Effects on Strain by Baseline Financial Distress

●

●

●

●

●●

●

1 2 3 4 5 6 7

−0.

020.

000.

020.

040.

060.

080.

10

Baseline Strain Quantile

Trea

tmen

t Effe

ct

● One YearTwo Years

N otes: Figure plots estimated 12 and 24 month impacts (and 95% confidence intervals) of traf-fic tickets on financial strain (an index capturing collections, derogatories, and delinquencies) byquantiles of baseline strain. Estimates obtained via difference-in-differences regressions (equation1.3). Quantiles are deciles except that there is excess mass at the lower bound. Hence, quantiles2-7 correspond to the 5th-10th deciles, while quantile 1 is the bottom 40% who are approximatelyat the lower bound (i.e. individuals without collections, etc.). Regressions estimated separately byquantile group.

52

Figure 1.10: License Suspension Event Studies

●●●●●●●●●●●●●●●●●●●

●●●●●●●●●●●●●●●●●●

−10 −5 0 5 10 15 20 25

−0.

3−

0.1

0.1

0.3

Panel A: Collections

Month Around Suspension

● Full SamplePoorest Quartile

●●●●●●●●●●●●●●●●

●●

●●●

●●●●●●●●●●●●●●●●

−10 −5 0 5 10 15 20 25

−20

00

100

Panel B: Collections Balance

Month Around Suspension

●●●●●●●●●●●●●●●●

●●●●●●●

●●●●●●●●●●

●●

●●

−10 −5 0 5 10 15 20 25

−20

0−

100

010

020

0

Panel C: Revolving Balance

Month Around Suspension

●●●●●●●●●●●●●

●●●

●●●

●●●●●●●●●●●●●●●●

●●

−10 −5 0 5 10 15 20 25

−0.

010

0.00

00.

010

Panel D: Employment

Month Around Suspension

N otes: Figure plots coefficients and 95% confidence intervals on indicators for month relativeto a point-based license suspension (see text for additional details). Blue squares correspond toestimates for the full sample and red squares correspond to estimates for the poorest quartile ofdrivers (estimated income < $21, 000). All regressions also include month relative to initial citationindicators, a quartic in driver age, and individual and time fixed effects.

53

Table 1: Summary Statistics

Matched Suspensions

(1) (2) (3) (4) (5)Event Study Treat Control Treat Control

Panel A: DemographicsFemale 0.44 0.43 0.43 0.36 0.38Nonwhite 0.61 0.61 0.61 0.72 0.69Age 38.35 37.94 37.97 33.86 35.14Credit File Age 14.12 13.54 13.37 11.77 12.57Credit Score 609 608 609 555 573Estimated Income 31859 32901 32827 23678 25942

Panel B: Financial StrainCollections 2.81 2.75 2.58 4.02 3.64Collections Balance 2169 1998 1898 3182 2874Derogatory Accounts 1.65 1.57 1.58 1.97 1.88Delinquent Accounts 0.62 0.56 0.56 0.85 0.79Past Due Balance 4296 3750 3657 5276 5091Prior Bankruptcy 0.02 0.02 0.02 0.01 0.02

Panel C: Credit UsageAny Account 0.8 0.81 0.81 0.66 0.71Revolving Accounts 2.82 3.15 3.19 1.27 1.71Revolving Balance 6471 8663 8485 1884 2722Any Auto Loan 0.34 0.36 0.35 0.29 0.3Any Mortgage 0.25 0.28 0.28 0.11 0.14

Panel D: Payroll DataEmployed 0.16 0.16 0.16 0.15 0.16Positive Earnings 0.11 0.11 0.11 0.11 0.11Monthly Earnings 3399 3422 3566 2507 2778

Individuals 710486 333232 333232 79490 135701

N otes: Column 1 reports means for the event study sample (a random 25% sample of drivers).Columns 2-3 report means for treated and control drivers in the matched sample. See Table A-2for summary statistics for all matching candidates. Columns 5-6 report means for the driver licensesuspensions sample. See text for further details on sample construction. Summary statistics arereported as of the base period for each sample (January of the year prior to citation for the eventstudy sample, January 2010 for the matched sample, and 12 months prior to the initial citation forthe suspensions sample). As of the 2010 ACS, Florida as a whole was 51% female, 41% nonwhite,and the average age was 40.3. Statewide averages in January 2010 were 662 (credit score) and$32,000 (estimated income).

54

Table 2: Impact of Citations on Financial Strain

Event Study Matched DD

(1) (2) (3) (4) (5)Mean 12 Months 24 Months 12 Months 24 Months

Collections 2.66 0.085∗∗∗ 0.137∗∗∗ 0.075∗∗∗ 0.117∗∗∗

(0.006) (0.012) (0.009) (0.015)

Derogatories 1.74 0.038∗∗∗ 0.052∗∗∗ 0.044∗∗∗ 0.078∗∗∗

(0.004) (0.008) (0.006) (0.01)

Delinquencies 0.59 0.012∗∗∗ 0.017∗∗∗ 0.008 0.011(0.003) (0.006) (0.005) (0.008)

Index 0 0.019∗∗∗ 0.028∗∗∗ 0.018∗∗∗ 0.029∗∗∗

(0.001) (0.003) (0.002) (0.003)

Collections Balance 2111.26 75.941∗∗∗ 123.815∗∗∗ 94.069∗∗∗ 166.995∗∗∗

(8.455) (15.652) (13.842) (22.453)

Past Due Balance 4457.96 61.783∗∗ 111.996∗∗ 138.917∗∗∗ 138.496∗

(28.575) (52.139) (46.125) (75.675)

N otes: Mean in Column 1 is the control mean from the matched sample as of 3 months prior tocitation. Columns 2-3 report 12 and 24 month estimates from event studies (corresponding to Fig-ure 1.3). Number of individuals (observations) for event study regressions is 710,486 (34,103,328).Columns 3-4 report 12 and 24 month estimates from matched difference-in-differences regressions(corresponding to Figure 1.6). Number of individuals (observations) for DD regressions is 666,464(8,664,032). Index refers to the financial strain index, a standardized sum of collections, delinquen-cies, and derogatory accounts. In the event study regressions, standard errors are clustered at theindividual level. In the DD regressions, standard errors are clustered at the matched-pair level.

55

Table 3: Impacts of Citations on Financial Strain by Driver Income

Event Study Matched DD

(1) (2) (3) (4) (5)Mean 12 Months 24 Months 12 Months 24 Months

Panel A: Bottom Income Quartile (<$21,000)Collections 3.91 0.169∗∗∗ 0.257∗∗∗ 0.134∗∗∗ 0.192∗∗∗

(0.016) (0.03) (0.023) (0.038)

Derogatories 1.31 0.045∗∗∗ 0.06∗∗∗ 0.052∗∗∗ 0.098∗∗∗

(0.007) (0.013) (0.009) (0.015)

Delinquencies 0.45 0.026∗∗∗ 0.043∗∗∗ 0.021∗∗ 0.044∗∗∗

(0.007) (0.013) (0.009) (0.015)

Index 0.02 0.033∗∗∗ 0.05∗∗∗ 0.03∗∗∗ 0.052∗∗∗

(0.003) (0.005) (0.004) (0.007)

Collections Balance 2657.4 141.196∗∗∗ 224.426∗∗∗ 125.108∗∗∗ 203.051∗∗∗

(15.816) (29.479) (26.102) (42.108)

Past Due Balance 1478.92 1.58 -9.023 94.495∗∗∗ 215.643∗∗∗

(22.782) (44.076) (34.687) (56.844)

Panel B: Top Income Quartile (>$41,000)Collections 0.45 0.033∗∗∗ 0.063∗∗∗ 0.023∗∗∗ 0.031∗∗

(0.006) (0.011) (0.008) (0.013)

Derogatories 0.68 0.05∗∗∗ 0.071∗∗∗ 0.028∗∗ 0.036∗

(0.007) (0.012) (0.012) (0.019)

Delinquencies 0.36 0 -0.003 0.014∗ 0.014(0.004) (0.008) (0.009) (0.014)

Index -0.49 0.012∗∗∗ 0.018∗∗∗ 0.012∗∗∗ 0.014∗∗∗

(0.002) (0.003) (0.003) (0.005)

Collections Balance 518.85 38.83∗∗∗ 70.924∗∗∗ 45.129∗∗ 78.459∗∗

(13.519) (25.716) (21.434) (34.675)

Past Due Balance 4430.08 347.832∗∗∗ 576.437∗∗∗ 235.609∗∗ 87.908(70.682) (130.903) (113.636) (185.353)

N otes: Number of individuals are as follows – event study, poorest quartile (N = 172, 582), eventstudy, richest quartile (N = 169, 643), matched DD, poorest quartile (N = 163, 100), matched DD,richest quartile (N = 158, 618). See notes to Table 2 for additional details.

56

Table 4: Impact of Citations on Employment and Borrowing

Event Study Matched DD

(1) (2) (3) (4) (5)Mean 12 Months 24 Months 12 Months 24 Months

Employment 0.16 -0.004∗∗∗ -0.004∗∗∗ -0.005∗∗∗ -0.008∗∗∗

(0.001) (0.001) (0.001) (0.002)

Any Earnings 0.12 -0.005∗∗∗ -0.006∗∗∗ -0.005∗∗∗ -0.007∗∗∗

(0.001) (0.001) (0.001) (0.002)

Revolving Accounts 2.93 -0.037∗∗∗ -0.052∗∗∗ -0.049∗∗∗ -0.096∗∗∗

(0.004) (0.007) (0.006) (0.01)

Revolving Balance 7012.45 -33.691 -57.093 -90.98 -217.874∗∗

(25.17) (45.378) (57.02) (91.57)

Any Auto Loan 0.33 -0.007∗∗∗ -0.014∗∗∗ -0.018∗∗∗ -0.044∗∗∗

(0.001) (0.002) (0.002) (0.003)

Any Mortgage 0.27 -0.001∗ -0.002∗ -0.003∗∗∗ -0.006∗∗∗

(0.001) (0.001) (0.001) (0.002)

N otes: Mean in Column 1 is the control mean from the matched sample as of 3 months priorto citation. Columns 2-3 report 12 and 24 month estimates from event studies (corresponding toFigure 1.4 and Figure 1.5). Number of individuals (observations) for event study regressions is710,486 (34,103,328). Columns 3-4 report 12 and 24 month estimates from matched difference-in-differences regressions (corresponding to Figure 1.6). Number of individuals (observations) forDD regressions is 666,464 (8,664,032). In the event study regressions, standard errors are clusteredat the individual level. In the DD regressions, standard errors are clustered at the matched-pairlevel.

57

Table 5: Impacts of Citations on Employment and Borrowing by Driver Income

Event Study Matched DD

(1) (2) (3) (4) (5)Mean 12 Months 24 Months 12 Months 24 Months

Panel A: Bottom Income Quartile (<$21,000)Employment 0.16 -0.009∗∗∗ -0.01∗∗∗ -0.011∗∗∗ -0.015∗∗∗

(0.002) (0.003) (0.003) (0.005)

Any Earnings 0.11 -0.009∗∗∗ -0.012∗∗∗ -0.012∗∗∗ -0.019∗∗∗

(0.002) (0.003) (0.003) (0.005)

Revolving Accounts 0.86 -0.039∗∗∗ -0.058∗∗∗ -0.042∗∗∗ -0.099∗∗∗

(0.006) (0.011) (0.008) (0.013)

Revolving Balance 412.5 7.97 -0.741 -30.313∗∗ -78.118∗∗∗

(9.476) (19.552) (13.203) (20.726)

Any Auto Loan 0.13 -0.011∗∗∗ -0.019∗∗∗ -0.02∗∗∗ -0.054∗∗∗

(0.002) (0.004) (0.003) (0.005)

Any Mortgage 0.02 -0.001 -0.002 0 -0.003∗

(0.001) (0.001) (0.001) (0.002)

Panel B: Top Income Quartile (>$41,000)Employment 0.15 -0.003∗∗ -0.004∗ -0.003∗ -0.004

(0.001) (0.002) (0.002) (0.003)

Any Earnings 0.12 -0.003∗∗∗ -0.006∗∗∗ -0.003 -0.003(0.001) (0.002) (0.002) (0.003)

Revolving Accounts 6.07 -0.029∗∗∗ -0.032∗ -0.039∗∗ -0.059∗∗

(0.009) (0.017) (0.016) (0.026)

Revolving Balance 22918.09 -120.313 -182.541 -117.946 -312.501(96.974) (175.894) (223.667) (358.718)

Any Auto Loan 0.49 -0.002 -0.004 -0.018∗∗∗ -0.035∗∗∗

(0.002) (0.004) (0.004) (0.006)

Any Mortgage 0.7 -0.003 -0.005 -0.008∗∗ -0.017∗∗∗

(0.002) (0.003) (0.003) (0.005)

N otes: Number of individuals are as follows – event study, poorest quartile (N = 172, 582), eventstudy, richest quartile (N = 169, 643), matched DD, poorest quartile (N = 163, 100), matched DD,richest quartile (N = 158, 618). See notes to Table 4 for additional details.

58

Table 6: Treatment Effects Across Studies

Studies

(1) (2) (3) (4)This Paper DFKN Herbst DGY

Panel A: Sample MeansIncome 39,000 47,000 – –Credit Score 607 731 589 581Age 37 49 43 45

Panel B: Financial Strain Effects

Collections .075 .11 – -0.15[2.8%] [12%] [-25%]

Collections Balance 94 122 – -1,315[4.5%] [10%] [-31%]

Panel C: Borrowing Effects

Revolving Accounts -.049 – .07 –[-1.7%] [2.3%]

Revolving Balance -91 -293 2,400 -920[-1.3%] [-2.5%] [17%] [-36%]

Any Auto Loan -.18 – 0 .02[-5%] [0%] [11%]

Any Mortgage -.003 – .02 .132[-1%] [10%] [36%]

Notes: DFKN refers to Dobkin et al. (2018) who study the impact of hospital admissions. Thetypical admission results in $3,275 in out-of-pocket spending. Reported estimates from DFKNcorrespond to the 12 month effects for the non-elderly insured population. Herbst refers to Herbst(2018) who studies the impact of income-driven student loan repayment, which reduces studentdebt minimum monthly payments by $140 per month on average. Reported estimates from Herbst(2018) refer to the first year DD estimates. DGY refers to Dobbie et al. (2017), who study theimpact of Chapter 13 bankruptcy protection. Effects sizes scaled by relevant baseline (i.e. percenteffects) are shown in brackets. This list is to provide context about the range of estimates in otherstudies using credit report data and is not meant to be exhaustive.

59

Table 7: Income Changes Predicting Financial Strain Impacts

Full Sample Bottom Quartile Top Quartile

(1) (2) (3) (4) (5) (6)12 Months 24 Months 12 Months 24 Months 12 Months 24 Months

Collections -361 -564 -663 -951 -144 -195[-1.05%] [-1.64%] [-3.74%] [-5.36%] [-0.25%] [-0.34%

Derogatories -250 -443 -324 -611 -208 -267[-0.73%] [-1.29%] [-1.83%] [-3.45%] [-0.36%] [-0.47%

Delinquencies -38 -52 -106 -222 -73 -73[-0.11%] [-0.15%] [-0.6%] [-1.25%] [-0.13%] [-0.13%

Index -285 -459 -465 -806 -281 -328[-0.83%] [-1.34%] [-2.62%] [-4.55%] [-0.49%] [-0.57%

N otes: Table reports an income-based metric for the matched DD treatment effects on financialstrain. Specifically, for each outcome (e.g. collections), sample (e.g. poorest quartile), and time(e.g. 12 or 24 months), I estimate the income loss that would predict the treatment effect onthe relevant financial strain using the estimates from the matched DD approach. See text forfurther details. In brackets, I report the income change as a percentage of the mean income in eachsubsample.

60

Table 8: Heterogeneous Impacts by Baseline Financial Situation

Baseline Credit Score Baseline Collections

(1) (2) (3) (4) (5)Full Sample Subprime Prime High Low

Collections 0.075∗∗∗ 0.1∗∗∗ 0.047∗∗∗ 0.161∗∗∗ -0.012∗

(0.009) (0.016) (0.007) (0.017) (0.007)[2.66] [4.48] [0.68] [4.29] [1.03]

Collections Balance 94.069∗∗∗ 133.211∗∗∗ 51.357∗∗∗ 200.431∗∗∗ -12.213(13.842) (24.582) (10.878) (23.939) (13.908)[2111.26] [3583.76] [504.43] [3323.54] [899.89]

Derogatories 0.044∗∗∗ 0.046∗∗∗ 0.04∗∗∗ 0.108∗∗∗ -0.021∗∗∗

(0.006) (0.01) (0.007) (0.009) (0.008)[1.74] [2.81] [0.58] [2.53] [0.96]

Delinquencies 0.008 0.001 0.015∗∗∗ -0.004 0.02∗∗∗

(0.005) (0.008) (0.006) (0.007) (0.006)[0.59] [0.86] [0.29] [0.77] [0.4]

Revolving Accounts -0.049∗∗∗ -0.04∗∗∗ -0.06∗∗∗ -0.091∗∗∗ -0.008(0.006) (0.006) (0.01) (0.007) (0.01)[2.93] [1.16] [4.86] [1.53] [4.33]

Revolving Balance -90.98 -72.554 -111.088∗∗∗ -282.195∗∗∗ 100.092(57.02) (54.52) (103.34) (48.507) (103.178)

[7012.45] [2149.66] [12318.82] [2747.69] [11274.03]

Auto Loan -0.018∗∗∗ -0.021∗∗∗ -0.014∗∗∗ -0.018∗∗∗ -0.018∗∗∗

(0.002) (0.002) (0.003) (0.002) (0.003)[0.33] [0.24] [0.44] [0.26] [0.41]

Mortgage -0.003∗∗∗ -0.002 -0.004∗∗∗ -0.002 -0.004∗∗

(0.001) (0.001) (0.002) (0.001) (0.002)[0.27] [0.13] [0.42] [0.15] [0.4]

Employment -0.005∗∗∗ -0.007∗∗∗ -0.003∗∗∗ -0.008∗∗∗ -0.003∗

(0.001) (0.002) (0.002) (0.002) (0.002)[0.16] [0.16] [0.16] [0.16] [0.16]

Individuals 666464 347768 318696 333356 333108

N otes: Table reports 12 month matched difference-in-differences estimates across subsamples. Sub-prime referes to individuals with credit scores below 600 at baseline. High collections refers toindividuals with an above median (∼ $150) collections balance at baseline.

61

Table 9: Treatment Effects of Payers and Traffic School Attendees

Unweighted Reweighted

(1) (2) (3) (4) (5)Full Sample Paid School Paid School

Strain 0.018∗∗∗ 0.0197∗∗∗ 0.0108∗ 0.0195∗∗∗ 0.0159∗∗

(0.002) (0.004) (0.006) (0.004) (0.008)

P-Value - - 0.21 - 0.67Control Mean 0 0.05 -0.16 0.01 0.01

Employment -0.0054∗∗∗ -0.0078∗∗∗ -0.0054 -0.0074∗∗∗ -0.0071(0.001) (0.002) (0.004) (0.002) (0.005)

P-Value - - 0.62 - 0.96Control Mean 0.16 0.16 0.16 0.16 0.16

Individuals 666464 198986 60288 198986 60288N 8664032 2586818 783744 2586818 783744Age 37.95 37.5 39.74 37.96 37.96Income 32.86 31.86 37.94 32.83 32.96Credit Score 609 601 644 608 609

N otes: Table reports 12 month matched difference-in-differences estimates for individuals withdispositions indicating a straight-pay and individuals with dispositions indicating a traffic schoolelection. Columns 2-3 present unweighted estimates. Column 3-4 present estimates DFL reweight-ing the payer and school subsamples to replicate the baseline age × baseline income × baselinecredit score distribution of the full sample. P-values are for tests of equality between coefficientsin columns 2-3 and columns 3-4.

62

Table 10: Event Study Estimates of Impact of License Suspensions

Event Study Estimates

(1) (2) (3) (4) (5)Mean 3 Months 6 Months 12 Months 24 Months

Panel A: Full SampleCollections 3.63 0.034∗∗∗ 0.074∗∗∗ 0.145∗∗∗ 0.184∗∗∗

(0.006) (0.008) (0.012) (0.017)

Collections Balance 2860.01 27.95∗∗∗ 70.848∗∗∗ 138.717∗∗∗ 165.685∗∗∗

(8.136) (10.814) (14.71) (19.26)

Derogatories 1.88 0.023∗∗∗ 0.044∗∗∗ 0.078∗∗∗ 0.078∗∗∗

(0.003) (0.005) (0.007) (0.011)

Bankruptcy 0.02 0 0.001∗∗ 0.001∗ 0.001(0) (0) (0) (0.001)

Revolving Balance 2732.85 2.786 -26.905∗∗ -68.114∗∗∗ -149.406∗∗∗

(9.633) (13.193) (18.046) (24.102)

Employment 0.11 -0.002∗∗∗ -0.003∗∗∗ -0.003∗∗ -0.003∗∗

(0.001) (0.001) (0.001) (0.001)

Panel B: Bottom Income Quartile (<$21,000)Collections 3.79 0.061∗∗∗ 0.108∗∗∗ 0.173∗∗∗ 0.244∗∗∗

(0.01) (0.014) (0.02) (0.029)

Collections Balance 2539.17 37.257∗∗∗ 87.269∗∗∗ 169.645∗∗∗ 204.426∗∗∗

(11.016) (14.954) (20.662) (26.994)

Derogatories 0.85 0.032∗∗∗ 0.05∗∗∗ 0.097∗∗∗ 0.132∗∗∗

(0.004) (0.006) (0.009) (0.014)

Bankruptcy 0 0 0 0 0(0) (0) (0) (0)

Revolving Balance 280.81 -18.692∗∗∗ -36.706∗∗∗ -75.562∗∗∗ -146.456∗∗∗

(4.324) (5.455) (7.794) (11.843)

Employment 0.11 -0.004∗∗∗ -0.006∗∗∗ -0.005∗∗ -0.005∗

(0.001) (0.002) (0.002) (0.002)

N otes: Table reports event study estimates around the time of a license suspension using thesuspensions sample (215,191 individuals, 79,490 treated). Regressions also includes months sinceinitial citation effects, individual fixed effects, and time effects. Standard errors clustered at theindividual level. Employment refers to positive payroll earnings.

63

Appendices

64

.1 Appendix Figures and Tables

Figure A-1: Local Policing Intensity and Per Capita Income in the U.S.

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Notes: Figure plots binned means of log sworn officers per capita against binned means of log localper capita income using a 2010 cross-section from the sample of municipal police departments inMello (2019) (N = 4, 327). Dashed line is a linear fit. Coefficient (standard error) from linear fit is-0.24 (.03).

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Figure A-2: Reliance on Fines and Fees and Per Capita Income in the U.S.

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Figure A-3: Credit File Match Rate by Zip Code Per Capita Income

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N otes: Figure plots local means of the match rate (fraction of citations matched to the credit file)against the log per capita income of the driver’s home zip code computed from the IRS public usefiles. Sample is the universe of citations sent to credit bureau (N = 8, 851, 688). Dashed line is alinear fit. Coefficient (standard error) from the implied regression is 0.035 (0.003).

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Figure A-4: Correlation Between Estimated Income and Payroll Earnings

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N otes: Figure plots local means of estimated income against annual earnings in the payroll dataas of January 2010. Sample is individuals in the matched sample with positive payroll earningsat that date (N = 69, 548). Red dashed line is a linear fit. Coefficient (standard error) from theimplied regression is 0.3515 (0.0023). Purple dashed line is the 45-degree line.

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Figure A-5: Age Profiles for Select Outcomes

20 30 40 50 60

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N otes: Figure plots the cross-sectional age profiles in January 2010 for selected outcomes usingcited drivers present in the credit report data as of that date using ages 18-64 (N = 2, 720, 749).

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Figure A-6: Event Study Estimates without Individual Trends

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Panel B: Collections Balance

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Month Around Traffic Stop

N otes: Figure plots coefficients (with 95% confidence bands) from event study regressions. Coef-ficients are normalized to t = −1. Blue circles correspond to estimates using the full sample andRed squares correspond to estimates using the poorest quartile. Identical to Figure 1.3, Figure 1.4,and Figure 1.5 except that regressions do not include individual trends.

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Figure A-7: Event Study Estimates for Monthly Earnings

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Month Around Traffic Stop

● Full SamplePoorest Quartile

N otes: Dependent variable is a log monthly earnings from the payroll data. Figure plots eventstudy estimates (with 95% confidence bands) using individuals from the event sample ever havingpositive earnings (N = 191, 054). Coefficients are normalized to t = −1. All regressions includeindividual fixed effects and time effects.

71

Figure A-8: Fully Non-Parametric Matched Difference-in-Differences Estimates

● ● ● ● ● ● ● ● ● ● ● ● ●

−10 0 5 10 20

−0.

30.

00.

2

Collections

Month Around Traffic Stop

● Full SampleBottom Income QuartileTop Income Quartile

● ● ● ● ● ● ● ●● ● ● ● ●

−10 0 5 10 20−

300

−10

010

030

0

Collections Balance

Month Around Traffic Stop

● ● ● ● ● ● ●● ● ● ● ● ●

−10 0 5 10 20

−0.

150.

000.

10

Derogatories

Month Around Traffic Stop

● ● ● ● ● ● ● ● ● ● ● ● ●

−10 0 5 10 20

−0.

050.

05

Delinquencies

Month Around Traffic Stop

● ● ● ● ● ● ●●

● ●●

● ●

−10 0 5 10 20

−0.

150.

000.

10

Revolving Accounts

Month Around Traffic Stop

● ● ● ● ● ● ● ● ● ● ● ● ●

−10 0 5 10 20−

1000

050

0

Revolving Balance

Month Around Traffic Stop

● ●●

●● ●

●●

●●

●●

●

−10 0 5 10 20

−0.

030.

000.

02

Any Auto

Month Around Traffic Stop

● ● ● ● ● ● ● ● ● ● ● ● ●

−10 0 5 10 20

−0.

020.

000.

02

Any Mortgage

Month Around Traffic Stop

● ● ● ● ●● ● ● ● ● ● ● ●

−10 0 5 10 20

−0.

015

0.00

00.

015

Employment

Month Around Traffic Stop

N otes: Figure plots coefficients (95% confidence intervals) on interactions between a treatmentindicator and event time indicators, normalized to equal zero at t = 3, corresponding to equation(1.2). All regressions include event time fixed effects, individual fixed effects, and year and monthfixed effects. Standard errors are clustered at the matched pair-level. Blue circles are estimatesusing the full matched sample, red squares are estimates using the poorest quartile of drivers, andpurple diamonds are estimates using the richest quartile of the sample. Each series (outcome ×sample) is from a separate regression.

72

Figure A-9: Employment Effects by Baseline Employment Status

−10 −5 0 5 10 15 20 25

0.6

0.7

0.8

0.9

1.0

Panel A: Employed

Month Around Traffic Stop

●

●

●

●

●

●●

●●

●●

●●

● TreatControl

−10 −5 0 5 10 15 20 25

0.24

0.28

0.32

Panel B: Employed (Poor)

Month Around Traffic Stop

●

●

●

●●

●●

●●

●●

●●

−10 −5 0 5 10 15 20 25

0.00

0.02

0.04

0.06

Panel C: Not Employed

Month Around Traffic Stop

●

●

●

●

●●

●●

● ● ● ● ●

−10 −5 0 5 10 15 20 25

0.03

0.05

0.07

Panel D: Not Employed (Poor)

Month Around Traffic Stop

●

●

●

●

●●

●●

● ● ● ● ●

N otes: Figure plots mean employment rates (covered by payroll data) around the time of a trafficstop for the treatment and control groups (analogous to Figure 1.6), splitting the sample by baselineemployment status. Blue dots denote the treatment group and red dots denote the control group.Treatment group means normalized to control group at t = −3. Panels A and C plot means forthe full sample, while Panels B and D plot means for the poorest quartile of drivers.

73

Figure A-10: Means Around Traffic Stop Date for Other Outomes (Raw Data)

−10 −5 0 5 10 15 20 25

614

616

618

620

Panel A: Credit Score

Month Around Traffic Stop

●

●●

● ●●

● ● ● ●●

●

●

● TreatControl

−10 −5 0 5 10 15 20 25

0.47

0.48

0.49

0.50

Panel B: Subprime

Month Around Traffic Stop

●●

● ● ●● ● ● ●

●●

●

●

−10 −5 0 5 10 15 20 25

33.0

33.4

33.8

34.2

Panel C: Estimated Income

Month Around Traffic Stop

●●

●

●

●●

●●

●●

●●

●

−10 −5 0 5 10 15 20 25

0.02

50.

035

0.04

50.

055

Panel D: Bankruptcy to Date

Month Around Traffic Stop

●

●

●

●

●

●

●●

●

●●

●●

N otes: Figure plots means around the time of a traffic stop for the treatment and control groups(analogous to Figure 1.6). Blue dots denote the treatment group and red dots denote the controlgroup. Treatment group means normalized to control group at t = −3. Dependent variable inPanel B is an indicator for having a subprime (< 600) credit score. Estimated income (Panel C) isannualized and in thousands. Dependent variable in Panel D is an indicator for any bankruptcy todate, computed using an indicator variable for the presence of a public records bankruptcy filingin the past 24 months.

74

Figure A-11: Outcome Means Using All Match Candidates

−10 0 5 10 20

2.6

2.8

3.0

Collections

Month Around Traffic Stop

●● ●

●●

●

●

●

●

●

●● ●

−10 0 5 10 20

1900

2100

2300

2500

Collections Balance

Month Around Traffic Stop

●●

●●

●

●

●

●

●●

● ●●

−10 0 5 10 20

1.60

1.70

1.80

Derogatories

Month Around Traffic Stop

●

●

●

●●

●●

●●

● ● ●●

−10 0 5 10 20

0.55

0.65

0.75

Delinquencies

Month Around Traffic Stop

● ●●

●●

●

●

●

●

●●

●●

−10 0 5 10 20

3.05

3.15

Revolving Accounts

Month Around Traffic Stop

●

●

●

●●

● ●●

● ● ● ● ●

−10 0 5 10 20

6800

7400

8000

Revolving Balance

Month Around Traffic Stop

●

●

●

●● ● ●

●●

●●

●●

−10 0 5 10 20

0.33

50.

350

0.36

5

Any Auto Loan

Month Around Traffic Stop

●● ● ● ●

●●

● ● ● ●●

●

−10 0 5 10 20

0.28

00.

290

Any Mortgage

Month Around Traffic Stop

●

●

●● ● ●

●●

●●

●●

●

−10 0 5 10 20

0.15

40.

158

Employment

Month Around Traffic Stop

●●

●

●●

● ● ● ●●

●

●

●

N otes: Figure plots means of outcomes for treatment and control groups using all match candidates(N=1,430,723). Blue dots denote the treatment group and red squares denote the control group.Treatment groups means normalized to equal control group means at t = −3. Placebo traffic stopdates are assigned to the control group randomly to replicate the distribution of traffic stop datesin the treatment group.

75

Figure A-12: Imputed Fine Gradients

●

●●

●●

0 50 100 200 300

−0.

050.

050.

150.

25

Panel A: Collections

Imputed Fine

● Full SampleBottom Income Quartile

●

●

●

●●

0 50 100 200 300

−50

5015

025

0

Panel B: Collections Balance

Imputed Fine

●

●

●

●

●

0 50 100 200 300

−0.

10−

0.06

−0.

020.

02

Panel C: Revolving Accounts

Imputed Fine

●

●

●

●

●

0 50 100 200 300

−40

00

200

Panel D: Revolving Balance

Imputed Fine

N otes: Figure plots 12 month matched difference-in-differences estimates (and 95% confidenceintervals) separately by quintile of imputed fine for the treatment group’s citation. Blue circlescorrespond to estimates using the full sample, while red squares correspond to estimates using onlythe bottom income quartile.

76

Figure A-13: Effects by Common Violation Types

●

●

●

●

●

●

●

Panel A: Strain Index

Treatment Effect

SDL

Equipment

Toll

Tag

RLC

Seatbelt

Speed

−0.08 −0.04 0.00 0.04 0.08

(21,532)

(29,601)

(29,558)

(35,625)

(33,593)

(30,600)

(38,646)

●

●

●

●

●

●

●

Panel B: Employment

Treatment Effect

SDL

Equipment

Toll

Tag

RLC

Seatbelt

Speed

−0.0100 −0.0025 0.0025 0.0075

N otes: Figure plots 12 month matched difference-in-differences estimates by violation type for com-mon violation categories. SDL refers to driving with a suspended license. Numbers in parenthesesare average estimated income (in thousands) and credit score at baseline for the relevant sample.

77

Figure A-14: License Suspension Event Studies for Other Outcomes

●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●

−10 0 5 10 20

−0.

150.

000.

10

Panel A: Derogatories

Month Around Suspension

● Full SamplePoorest Quartile

●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●

−10 0 5 10 20

−0.

060.

000.

04

Panel B: Delinquencies

Month Around Suspension

●●●●●●●●●●●●●●●

●●

●●●●●●●●●●●

●●●●

●●●●●

−10 0 5 10 20

−0.

002

0.00

00.

002

Panel C: Bankruptcy

Month Around Suspension

●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●

−10 0 5 10 20

−0.

150.

000.

10

Panel D: Revolving Accounts

Month Around Suspension

●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●

−10 0 5 10 20

−0.

040.

000.

04

Panel E: Auto Loan

Month Around Suspension

●●●●●●●●●●●●●●●●●●●●●●●●●●●●●

●●●●●●●●

−10 0 5 10 20

−0.

010

0.00

00.

010

Panel F: Mortgage

Month Around Suspension

●●●●●●●●●●●●●

●●●●

●●●●●●●●●●

●●●●●●

●●●

●

−10 0 5 10 20

−0.

010

0.00

00.

010

Panel G: Employment

Month Around Suspension

●●●●●●●●●

●●

●●

●●

●●●●●●●●●●●●●●●●●●●●●●

−10 0 5 10 20

−4

−2

02

4

Panel H: Credit Sore

Month Around Suspension

●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●●

−10 0 5 10 20

−0.

60.

00.

4

Panel I: Estimated Income

Month Around Suspension

N otes: Figure plots coefficients and 95% confidence intervals on indicators for month relative to apoint-based license suspension (same as Figure 1.10). All regressions also include month relativeto initial citation indicators, a quartic in driver age, and individual and time fixed effects.

78

Table A-1: Credit File Match Rate by Driver Characteristics

Any Match Current Match

(1) (2) (3) (4)

Female 0.044∗∗∗ 0.043∗∗∗ 0.060∗∗∗ 0.059∗∗∗

(0.001) (0.001) (0.002) (0.002)

Age <18 −0.154∗∗∗ −0.152∗∗∗ −0.534∗∗∗ −0.533∗∗∗

(0.005) (0.004) (0.007) (0.006)

Age 25-34 0.070∗∗∗ 0.069∗∗∗ 0.200∗∗∗ 0.200∗∗∗

(0.002) (0.002) (0.006) (0.006)

Age 35-44 0.098∗∗∗ 0.097∗∗∗ 0.241∗∗∗ 0.240∗∗∗

(0.004) (0.004) (0.008) (0.008)

Age 45-54 0.107∗∗∗ 0.106∗∗∗ 0.256∗∗∗ 0.255∗∗∗

(0.004) (0.004) (0.008) (0.008)

Age 55+ 0.121∗∗∗ 0.121∗∗∗ 0.276∗∗∗ 0.276∗∗∗

(0.006) (0.007) (0.011) (0.011)

Black −0.017∗∗∗ −0.020∗∗∗ −0.020∗∗∗ −0.024∗∗∗

(0.005) (0.002) (0.004) (0.002)

Hispanic −0.028∗∗∗ −0.035∗∗∗ −0.041∗∗∗ −0.048∗∗∗

(0.006) (0.005) (0.006) (0.006)

Other/Unknown 0.002 −0.006 −0.002 −0.009(0.007) (0.007) (0.008) (0.008)

Log Zip Income 0.025∗∗∗ 0.030∗∗∗ 0.028∗∗∗ 0.034∗∗∗

(0.005) (0.003) (0.005) (0.002)

Mean 0.82 0.82 0.75 0.75County FE No Yes No YesTime FE No Yes No YesR2 0.022 0.026 0.09 0.094N 8,851,688 8,851,688 8,851,688 8,851,688

N otes: Regression is estimated at the citation level. Any Match refers to whether the driver wasmatched to the credit file at any point. Current Match refers to whether the driver was matched tothe credit file at the time of citation. Ages 18-24 and white are the excluded age/race categories.County fixed effects refer to county of the traffic stop. Time fixed effects are for the month (year× month) of the traffic stop.

79

Table A-2: Summary Statistics for Matching Candidates and Matches

Candidates Matches

(1) (2) (3) (4) (5)Treat Control Treat Control Statewide

Panel A: DemographicsFemale 0.4 0.45 0.43 0.43 0.51Nonwhite 0.65 0.53 0.61 0.61 0.41Age 36.96 38.65 37.94 37.97 40.3Credit File Age 13 13.94 13.54 13.37 -Credit Score 597 616 608 609 662Estimated Income 31323 33788 32901 32827 32000

Panel B: Financial StrainCollections 2.95 2.58 2.75 2.58 -Collections Balance 2139 1846 1998 1898 -Derogatory Accounts 1.68 1.53 1.57 1.58 -Delinquent Accounts 0.6 0.54 0.56 0.56 -Past Due Balance 4092 3479 3750 3657 -Prior Bankruptcy 0.02 0.02 0.02 0.02 -

Panel C: Credit UsageAny Account 0.8 0.82 0.81 0.81 -Revolving Accounts 2.85 3.32 3.15 3.19 -Revolving Balance 7802 8929 8663 8485 -Any Auto Loan 0.35 0.36 0.36 0.35 -Any Mortgage 0.26 0.3 0.28 0.28 -

Panel D: Payroll DataEmployed 0.16 0.15 0.16 0.16 -Positive Earnings 0.11 0.11 0.11 0.11 -Monthly Earnings 3203 3612 3422 3566 -

Individuals 817775 612948 333232 333232 -

N otes: Candidates refers to individuals eligible for the matching procedure. Matches refers toindividuals successfully matched. Benchmark values for demographic characteristics computedfrom the 2010 ACS. Benchmark values for credit score and estimated income were provided by thecredit bureau.

80

Table A-3: Difference in Difference Estimates for Other Outcomes

(1) (2) (3) (4)Credit Score Subprime Estimated Income Bankruptcy

Panel A: Full Sample

12 Months Post -1.452∗∗∗ 0.006∗∗∗ -186.988∗∗∗ 0(0.25) (0.002) (34.353) (0)

24 Months Post -0.106 0.001 -385.384∗∗∗ 0.001(0.39) (0.003) (54.384) (0.001)

Control Mean 615.38 0.5 33154.02 0.03Individuals 666464 666464 666464 666464N 8641126 8641126 8664025 8664032

Panel B: Bottom Income Quartile (<$21,000)

12 Months Post -2.33∗∗∗ 0.01∗∗∗ 6.055 0(0.532) (0.003) (38.949) (0)

24 Months Post -2.3∗∗∗ 0.01∗ -203.058∗∗∗ 0(0.825) (0.005) (61.563) (0.001)

Control Mean 556.62 0.73 16517.7 0.01Individuals 163100 163100 163100 163100N 2108433 2108433 2120295 2120300

Panel C: Top Income Quartile (>$41,000)

12 Months Post -0.909∗ 0.002 -507.786∗∗∗ 0.001(0.49) (0.003) (114.526) (0.001)

24 Months Post 0.835 -0.007 -871.389∗∗∗ 0.003(0.767) (0.005) (181.841) (0.002)

Control Mean 711.46 0.15 57946.12 0.02Individuals 158618 158618 158618 158618N 2060092 2060092 2062034 2062034

N otes: Table presents matched differences-in-differences estimates (same as columns 4-5 in Ta-ble 1.3) for other outcomes. Dependent variable in column 2 is an indicator for having a subprime(< 600) credit score. Dependent variable in column 4 is any bankruptcy to date, constructed froma variable indicating the presence of a public records bankruptcy filing in the past 24 months. Notethat credit score and estimated income variables are not imputed and hence missing person-monthsare dropped.

81

Table A-4: Difference-in-Differences Estimates for Employment and Earnings

Full Sample Positive Earnings

(1) (2) (3) (4)Employed Any Earnings Earnings Log Earnings

Panel A: Full Sample

12 Months Post -0.005∗∗∗ -0.005∗∗∗ -126.103 -0.004(0.001) (0.001) (78.933) (0.009)

24 Months Post -0.008∗∗∗ -0.007∗∗∗ -112.557 -0.007(0.002) (0.002) (131.556) (0.014)

Control Mean 0.16 0.12 3697 7.74Individuals 666464 666464 146141 146141N 8664032 8664032 1015962 1015962

Panel B: Bottom Income Quartile (<$21,000)

12 Months Post -0.011∗∗∗ -0.012∗∗∗ -52.391∗ -0.027(0.003) (0.003) (30.16) (0.022)

24 Months Post -0.015∗∗∗ -0.019∗∗∗ -3.251 -0.041(0.005) (0.005) (69.609) (0.035)

Control Mean 0.16 0.11 1611 7.1Individuals 163100 163100 44652 44652N 2120300 2120300 244051 244051

Panel C: Top Income Quartile (>$41,000)

12 Months Post -0.003∗ -0.003 -279.688 0.004(0.002) (0.002) (192.022) (0.015)

24 Months Post -0.004 -0.003 -425.991 -0.002(0.003) (0.003) (309.955) (0.024)

Control Mean 0.15 0.12 6926 8.39Individuals 158618 158618 27284 27284N 2062034 2062034 241762 241762

N otes: Table presents matched differences-in-differences estimates (same as columns 4-5 in Ta-ble 1.3) for employment and earnings.

82

Table A-5: Sensitivity of 12 Month Effects to Imputation

Data Type

(1) (2)Imputed Not Imputed

Panel A: Financial StrainCollections 0.075∗∗∗ 0.079∗∗∗

(0.009) (0.009)Derogatories 0.044∗∗∗ 0.047∗∗∗

(0.006) (0.006)Collections Balance 94∗∗∗ 94∗∗∗

(14) (14)Past Due Balance 139∗∗∗ 148∗∗∗

(46) (48)

Panel B: Credit UsageRevolving Accounts -0.049∗∗∗ -0.051∗∗∗

(0.006) (0.007)Revolving Balance -91 -58

(57) (109)Any Auto Loan -0.018∗∗∗ -0.022∗∗∗

(0.002) (0.002)Any Mortgage -0.003∗∗∗ -0.003

(0.001) (0.002)

N otes: Table presents 12 month matched difference-in-differences estimates (standard errors inparentheses) with and without data imputation. Column 1 reports estimates identical to those inTable 2 and Table 4.

83

.2 Becker-Style Model

B-1 Model Environment

The model is based on the canonical model of the economics of crime in Becker (1968) and

follows closely the formulation in Burlando and Motta (2016). Society is comprised of a

unit mass of individuals indexed by their endowed income y and taste for crime x. I assume

that income is exogenous, and to start, homogenous in the population. Taste for crime x is

distributed according to the cumulative distribution function G(·). Individuals have strictly

concave utility over consumption u(c) and receive utility x from (successfully) committing

crime.

Each criminal act causes harm to society. Hence, the government tries to curb crime

through an enforcement scheme θ = (p, f), where p represents the probability a citizen is

audited and f denotes the fine paid by an individual found to be engaging in crime. Taking

the enforcement scheme as given, individuals choose whether to engage in crime to maximize

expected utility. Hence, individuals choose crime if

pu(y − f) + (1− p) [u(y) + x]︸ ︷︷ ︸expected utility for criminals

> u(y)︸︷︷︸utility for abstainers

(B.1)

Equation B.1 determines a threshold value of x as a function of y and θ:

x∗(y, p, f) =p

1− p[u(y)− u(y − f)] (B.2)

Individuals with x > x∗ engage in crime, while those with x ≤ x∗ abstain. Given y and θ,

the amount of crime is 1−G(x∗(y, θ)). One can think of this expression as a demand curve,

mapping the (expected) price of crime to the quantity of offenses.

84

It is also useful to note that given y and θ, total welfare of citizens can be expressed as

V (y, θ) =

∫ x∗

0

u(y)g(x)dx+

∫ ∞x∗

{pu(y − f) + (1− p) [u(y) + x]

}g(x)dx (B.3)

which is the utility of abstainers and criminals integrated over the distribution of x.

B-2 Enforcement and Welfare

Before turning to policy discussion, it is useful to note that policy analysis in this Becker-

style model will require an understanding of the relationship between welfare V and the

enforcement scheme θ. In particular, one needs to differentiate V with respect to the policy

parameters p and f . Taking y as given and beginning at the enforcement scheme θ0 = (p0, f0),

consider a small change in one of the policy parameters moving to θ1.

With respect to a policy change, there are three distinct types of citizens. First, there is

a group of never-takers. Never-takers are individuals who abstain from crime regardless of

the enforcement scheme, i.e. individuals with x ≤ x1. If the policy change is, for example,

an increase in p, then x1 = x∗(y, p0, f0). Second, there is a group or always-takers. Always-

takers are citizens who choose crime regardless of the enforcement scheme, i.e. individuals

with x > x2, where x2 = x∗(y, p1, f0) for an increase in p. Finally, there is a group of

compliers. Compliers are individuals with x ∈ (x1, x2], and therefore whose behavior is

altered by the policy change. For an increase in p, compliers are individuals who choose

crime under θ0 but abstain under θ1. Hence, the welfare change associated with a small

policy change can be expressed as

∫ x1

0

[∂u

∂θ|x ≤ x1

]g(x)dx+

∫ x2

x1

[∂u

∂θ|x ∈ (x1, x2]

]g(x)dx+

∫ ∞x2

[∂u

∂θ|x > x2

]g(x)dx (B.4)

The first term is the change in utility for the never-takers. Because such individuals abstain

regardless, they receive u(y) under either θ. There is no welfare change for never-takers,

meaning the first term is zero.

85

The second term is the welfare change for the compliers. Such individuals were marginal

to abstaining under θ0 and choose to abstain under θ1. By the envelope theorem, there is no

welfare change for compliers. The second term is zero.

The third term is the welfare change for the always-takers. Policy parameters do impact

the expected payoff associated with crime, thereby affecting the expected utility of the infra-

marginal criminals. Hence, given tht the first two terms are zero, the only welfare impacts

of a small change in enforcement are the effects on inframarginal criminals:

∂V

∂θ=

∫ ∞x2

∂

∂θ

{pu(y − f) + (1− p) [u(y) + x]

}g(x)dx (B.5)

The following discussion below makes use of this result.

B-3 Optimal Enforcement

The government chooses an enforcement scheme to maximize the welfare of citizens, net of

the social costs of crime and the costs of enforcement. For simplicity, assume the government

takes the fine f as given and chooses only p. This assumption captures the fact that, in many

cases, fines are set at the state or county-level but policing intensity is chosen locally.27

To begin with a reduced-form version of the planner’s problem, let h(p) represent the

social cost of crime as a function of p and let c(p) denote the cost of policing. One could

think of this formulation as expressing that only the government cares about crime or that

victimization costs are evenly distributed throughout the population. The government’s

problem is

maxp

V (p)− h(p)− c(p) (B.6)

27Standard Becker-style models typically assume that increasing the number of searches is costlybut increasing the charged fine is not, which leads to the prediction of much higher fines than aregenerally observed in cases such as traffic enforcement. Assuming the government takes the fineas given is isomorphic to assuming there is maximum acceptable fine amount f , reflecting fairnessconcerns for example, because optimization will always dictate f = f .

86

Under standard regularity conditions, the solution is characterized by the first-order condi-

tion

−h′(p)︸ ︷︷ ︸marginal safety benefit

= c′(p)︸︷︷︸marginal cost of policing

− V ′(p)︸ ︷︷ ︸marginal welfare loss

(B.7)

In words, the government tickets until the marginal safety benefit equals the marginal cost

of writing tickets and the marginal lost surplus to citizens. It is worth noting that if the

government also faces a revenue-raising motive when issuing citations, this would enter the

first-order condition as a constant on the left-hand side of B.7. With a revenue benefit, the

government is willing to allow a larger welfare loss to citizens when optimizing.

Using B.5, the marginal welfare loss associated with increasing p, V ′(p) is

∂V

∂p=

∫ ∞x∗

[u(y − f)− u(y)− x

]g(x)dx (B.8)

This expression depends on the utility losses associated with punishment and the benefits to

criminal behavior. To obtain a more tractable expression, one can think of a small increase

in p as writing one more traffic ticket. Moreover, assume that the marginal person ticketed

was close to the margin of criminal behavior. Hence, we can substitute the indifference x∗

condition into the derivative of the expected utility of criminals to get the marginal welfare

loss associated with one more ticket is

1

1− p[u(y − f)− u(y)

](B.9)

Assuming p is small, then, optimal enforcement sets

u(y)− u(y − f) = −h′(p)− c′(p) (B.10)

We can think of the left-hand side of B.10 as a reduced-form expression of the quantity

estimated in the data, the welfare cost of punishing an individual.

87

B-4 Income-Based Fines

Now suppose that society is comprised of types of individuals, those with high incomes yH

and those with low incomes yL, where yH > yL. Assume taste for crime x is distributed

identically across the two types of individuals. I examine the effect of moving from an initial

enforcement scheme θ0 = (p0, f0) to a small perturbation in the fines for the two types.

Specifically, I consider an increase in the fine for rich individuals to fH = f0 + ∆ and a

decrease in the fine for rich individuals to fL = f0 −∆, where ∆ > 0.

To simplify the exposition, let ∆ satisfy the following condition:

x∗(yH , p, f0 + ∆) = x∗(yL, p, f0) (B.11)

The relevance of this assumption is as follows.28 Recall from section B-2 that, for small ∆,

we need only consider the utility implications for the always-takers when evaluating welfare

effects. When moving from f0 to f0 + ∆, the always-takers among the rich are those with

x > x∗(yH , p, f0 + ∆), or those who engage in crime when f is either f0 or f + ∆. When

moving from f0 to f0−∆, the always-takers among the poor are those with x > x∗(yL, p, f0).

Hence, B.11 ensures that the distribution of x’s among the rich and poor always-takers are

identical, allowing for a simpler expression of welfare effect that abstracts from compositional

changes.

Equation B.5 shows that the derivative of the expected utility of criminals with respect

to the relevant enforcement parameter is a key object in evaluating welfare effects. With

respect to fine changes, this quantity is

∂

∂f{pu(y − f) + (1− p) [u(y) + x]} = −p∂u

∂c(y − f) < 0 (B.12)

28To see that such a ∆ exists, note that by the definition x∗, ∆ solves u(yL) − u(yL − f0) =u(yH)−u(yH−f0−∆). The properties of u(·) dictate that u(yL)−u(yL−f0) > u(yH)−u(yH−f0)and that u(yH)− u(yH − f0 −∆) is increasing in ∆.

88

Substituting B.12 into B.5 gives the following expression for the net welfare change associated

with the change in the fine scheme:

∫ ∞x∗(yL,f0,p)

∆p∂u

∂c(yL − f0)g(x)dx+

∫ ∞x∗(yH ,f0+∆,p)

−∆p∂u

∂c(yH − f0)g(x)dx (B.13)

where the first term is the welfare change among poor always-takers and the second term

is the welfare change among rich always-takers. Using assumption B.11, which ensures that

the limits of integration are equal, this expression can be rewritten as

∆×[∂u

∂c(yL − f0)− ∂u

∂c(yH − f0)

]︸ ︷︷ ︸

difference in marginal utilities

× p[1−G(x∗)]︸ ︷︷ ︸number of tickets

(B.14)

The first and last components are positive by assumption and definition. Strict concavity

of u(·) ensures that the difference in marginal utilities is positive, and therefore, that the

welfare change is positive.

To obtain a money metric for the welfare changes, I rescale by marginal utility at the

low income level (Chetty, 2006a).29 For a CRRA utility function with risk aversion γ, the

money-metric welfare change is

(yL − f0)−γ − (yH − f0)−γ

y−γL×∆× p[1−G(x∗)] (B.15)

To relate this expression to the paper’s empirical exercise, let yL =$20,000, yH =$40,000,

and f0 =$200. One of the main insights offered by the empirical analysis is the fact that

fines have outsized effects on the utility of poor drivers. To incorporate this finding into

the welfare analysis in a reduced-form way, let e capture the excess burden of fines on poor

drivers. We can think of this quantity as the “effective” fine size, corresponding to the welfare

cost estimates in Section 6. Taking this heterogeneity into account, the change-in-welfare

29The unit of the welfare change is change in utils. Multiplying by one over the marginal utilityscales by the price of a util, i.e. converts the change in utility into dollar units.

89

expression becomes

(yL − f0 − e)−γ − (yH − f0)−γ

y−γL×∆× p[1−G(x∗)] (B.16)

Figure B-1 plots the first term of B.16, which is the per-dollar (of fine change), per-citation

change in utility, as a function of the excess burden e and for different values of risk aversion.

Unsurprisingly, welfare effects depend heavily on γ, which governs the curvature of the utility

function. For low-levels of risk aversion and without excess burden on poor drivers, the

welfare benefit of a $10 fine perturbation is about $3 per citation. For γ = 1, benefits are

between $5 and $5.60 depending on the excess burden. At higher levels of risk aversion, both

baseline benefits and the dependence of benefits on the excess burden increase considerably.

When γ = 3 and e = $1000, per ticket welfare effects of a $10 fine perturbation are about

$10.10. At current ticketing rates, the total utility benefit associated with such a policy is

between $6 and $21 million.

Impacts on Crime

Of course, the net social welfare implications of the policy change also depends on the policy’s

effects on crime and/or revenue from fines. Note that for a given y and enforcement regime

θ, the amount of crime is C = 1−G(x∗(y, θ)). Hence, crime changes with f according to

∂C

∂f= −g(x∗)× p

1− p× ∂u

∂c(y − f) (B.17)

where the expression beginning with p1−p follows from differentiating x∗ with respect to f .

The income-based fine regime increases (decreases) the price of crime for the rich (poor),

thus decreasing crime among rich individuals but increasing crime among poor individuals.

The net effect of the policy on crime can be expressed as

∆p

1− p

[g(x∗(yL, p, f0))

∂u

∂c(yL − f0)− g(x∗(yH , p, f0))

∂u

∂c(yH − f0)

](B.18)

90

Figure B-1: Welfare Effects by Risk Aversion and Excess Burden

0 200 400 600 800 1000

0.0

0.2

0.4

0.6

0.8

1.0

1.2

Excess Burden on Poor Drivers

Wel

fare

Cha

nge

per

Tic

ket p

er D

elta

gamma = 0.5gamma = 1

gamma = 2gamma = 3

N otes: The figure plots the money metric per-dollar per-ticket welfare change (first term of B.16),i.e. the per-ticket welfare increase from a $1 fine perturbation, as a function of the excess welfareburden of fines on poor drivers, e, for different values of risk aversion γ.

The first term inside the brackets represents in the increase in crime for the poor and the

second term represents the decline for the rich. While concavity of u(·) ensures that u′(yL−

f0) > u′(yH − f0) and x∗0(yL) > x∗0(yH), the sign of B.18 depends on the functional form of

g(·), or more specifically the shape of the distribution of crime tastes in the range of the

cutoff values. If x has a strictly decreasing probability distribution function (an exponential

distribution, for example), the policy increases crime. If g(·) is increasing in the range of the

initial x∗ values, the policy could reduce crime.

An important point to note is that the above analysis of welfare changes relies on a

specific magnitude of ∆ to simplify the exposition. However, one could also have chosen an

alternate fine scheme specifically to hold crime constant. The redistributive welfare benefits

91

would still be present under such an alternative policy, but one would also need to consider

changes in the composition of criminals and the associated welfare implications.

92

.3 Effects of Payroll-Job Separations

In this section, I estimate the impact of a separation from a payroll-covered job on credit

report outcomes. This exercise serves two distinct purposes. First, it provides a test of the

hypothesis that payroll employment is a meaningful and positive outcome. Second, to the

extent that a separation impacts credit report outcomes, the estimates can be used as a

benchmark to help interpret the magnitudes of the estimated traffic ticket effects.

C-1 Sample Construction

To isolate the impacts of separations unrelated to traffic citations, I sample from the set of

individuals who receive their first traffic ticket after January 2014 and analyze data from Jan-

uary 2010 through 2013. I drop individuals included in the matched difference-in-differences

sample, require that individuals are present in the credit file in January 2010, and require

that individuals are between 18 and 60 years of age as of that date.

I then identify individuals with a separation from the payroll data during in 2011 or 2012,

measured as a transition from having at least one covered job to having zero covered jobs

in adjacent months. Requiring that the separation occurs in the 2011-2012 period allows

a balanced 12-month period before and after the separation for analysis and allows for the

computation of a crude tenure measure. That is, using the one-year pre-period, I can at least

distinguish between spells of, e.g., three months and spells of longer than twelve months.

There are 26,718 individuals meeting all the above requirements. To help estimate time and

age effects, I include individuals meeting the same criteria but whose payroll employment

spells begin after 2013 as a quasi-control group. There are 38,345 such individuals.

Table C-1 presents summary statistics for the separations sample. The treatment (sepa-

rations) and control groups are quite similar on most dimensions. Compared with the event

study and matched difference-in-differences samples, this group of drivers is a higher fraction

female and slightly younger, but otherwise similar on most dimensions.

93

C-2 Estimation

To estimate the impacts of separations, I use an event-study approach. Specifically, I estimate

regressions of the following form:

Yitτ =∑τ

θτ + φi + κt + γi(t) + εit (C.1)

Here, the θτ ’s are month around separation indicators and φi and κt are individual and

time fixed effects. I group event-time values larger than +/-13 into +/-13. I also include

individual-specific linear trends γi(t) in the regressions. Finally, I control for a quartic in

driver age and include a set of job tenure indicators, which are indicators for number of

months since the payroll employment spell began, topcoded at twelve because this is the

longest look-back period allowed for the universe of separations. Event-time and tenure

indicators are set to zero for the control group. I cluster standard errors at the individual-

level.

C-3 Results

94

Table C-1: Summary Statistics for Job Separations Sample

(1) (2)Separations Control

Panel A: DemographicsFemale 0.51 0.52Nonwhite 0.47 0.49Age 34.7 35.15Credit File Age 11.85 12.13Credit Score 600 599Estimated Income 28746 28972

Panel B: Financial StrainCollections 3.01 3.03Collections Balance 1991 2010Derogatory Accounts 1.59 1.56Delinquent Accounts 0.53 0.55Past Due Balance 2793 2881Prior Bankruptcy 0.02 0.02

Panel C: Credit UsageAny Account 0.78 0.77Revolving Accounts 2.63 2.63Revolving Balance 5302 5376Any Auto Loan 0.32 0.32Any Mortgage 0.23 0.24

Individuals 26718 38345

N otes: The table reports summary statistics for the event-study analysis of payroll job separations.Columnn 1 reports means as of January 2010 for individuals with a separation in 2011-2012 andcolumn 2 reports means as of January 2010 for control individuals (those with a spell in the payrolldata after January 2014). See notes to Table 1 for further details.

95

Figure C-1: Effect of Payroll Separations on Financial Strain

(a) Collections

●● ● ● ●

● ● ● ● ● ● ●●

● ● ●

●

●

●

●

●

● ●●

●

−10 −5 0 5 10

−0.

15−

0.10

−0.

050.

000.

050.

100.

15

Month Around Separation

● b(12)=0.114

(b) Collections Balance

●

● ●●

● ●

●● ● ●

● ●●

● ●●

●

●

●

● ●

● ●● ●

−10 −5 0 5 10

−10

0−

500

5010

0

Month Around Separation

● b(12)=70

(c) Derogatories

●● ● ● ● ● ●

●● ●

●●

●●

● ●

●● ●

●●

● ●

● ●

−10 −5 0 5 10

−0.

06−

0.04

−0.

020.

000.

020.

040.

06

Month Around Separation

● b(12)=0.038

(d) Delinquencies

● ● ●

●● ●

●● ●

● ● ●● ●

●

●

●

●

●●

●●

●●

●

−10 −5 0 5 10

−0.

04−

0.02

0.00

0.02

0.04

Month Around Separation

● b(12)=0.02

N otes: Each figure plots coefficients and 95% confidence intervals on month around payroll sep-aration indicators. Regressions also include individual and time fixed effects, payroll tenure fixedeffects, a quartic in age, and individual-specific linear trends. Standard errors are clustered atthe individual level. The average separation corresponds to a $1,600 decline in monthly payrollearnings. Legend reports the 12-month estimate.

96

Figure C-2: Effect of Payroll Separations on Credit Cards

(a) Revolving Accounts

●

● ●● ● ● ●

● ● ●●

● ●● ●

●● ●

●

●

●

●●

● ●

−10 −5 0 5 10

−0.

04−

0.02

0.00

0.02

0.04

Month Around Separation

● b(12)=−0.027

(b) Revolving Balance

●●

●● ● ●

●● ●

● ●● ● ●

●●

●● ● ●

●

● ●●

●

−10 −5 0 5 10

−40

0−

200

020

040

0

Month Around Separation

● b(12)=−280

N otes: Each figure plots coefficients and 95% confidence intervals on month around payroll sep-aration indicators. Regressions also include individual and time fixed effects, payroll tenure fixedeffects, a quartic in age, and individual-specific linear trends. Standard errors are clustered atthe individual level. The average separation corresponds to a $1,600 decline in monthly payrollearnings. Legend reports the 12-month estimate.

97

Chapter 2

A Few Bad Apples? Racial Bias in

Policing 1

2.1 Introduction

The disparate treatment of whites and minorities in the criminal justice system is a central

policy concern in the United States. Blacks and Hispanics are more likely to be stopped by

the police (Coviello and Persico, 2013), convicted of a crime (Anwar et al., 2012), denied

bail (Arnold et al., 2018), and issued a lengthy prison sentence (Rehavi and Starr, 2014)

relative to observably similar whites. In light of these disparities, a literature has developed

to test whether these outcomes can be explained by discrimination on the part of police

1This chapter is co-authored with Felipe Goncalves. We are grateful to Will Dobbie, IlyanaKuziemko, and Alex Mas for guidance and support throughout this project. We benefited fromhelpful comments by Peter Bergman, Leah Boustan, Jessica Brown, Nicholas Buchholz, Janet Cur-rie, Rebecca Diamond, Nik Engbom, Kirill Evdokimov, Hank Farber, Jeremy Fox, Sara Heller,Nathaniel Hendren, Daniel Herbst, Bo Honore, Sierra Kuzava, Andrew Langan, Michael Luca,Neale Mahoney, Michael Makowsky, Michael Mueller-Smith, Christopher Neilson, Emily Owens,Aurelie Ouss, Jakob Schlockermann, Petra Todd, and participants of the Hamilton-Colgate Eco-nomics Seminar, the NBER Summer Institute Crime Session, the Transatlantic Conference on theEconomics of Crime, and various Princeton seminars. We thank Beth Allman, Jeffrey Bissainthe,Kiara Guzzo, Wilton Johnson, Timothy Kutta, Stacy Lehmann, and Brenda Paige for assistancewith data from various agencies. The Princeton University Industrial Relations Section providedgenerous financial support. Any errors are our own.

98

officers, judges, and other criminal justice agents (Knowles et al., 2001; Anwar and Fang,

2006; Grogger and Ridgeway, 2006; Antonovics and Knight, 2009; Persico, 2009; Abrams

et al., 2012; Horrace and Rohlin, 2016; Fryer, 2018; Arnold et al., 2018). The view that

discrimination is responsible for these disparate outcomes has gained traction in recent years,

particularly within minority communities, following several highly publicized police killings of

minorities. A 2013 Gallup poll found that half of black adults agreed that racial differences in

incarceration rates are “mostly due to discrimination,” while only 19% of white respondents

agreed.2

While current methods focus on detecting the presence of racial discrimination on aver-

age, an unresolved challenge is how to identify discrimination at the level of the individual

criminal justice agent. Existing approaches largely do not differentiate between discrimina-

tion that is widespread versus that which is concentrated among a few agents. However,

the optimal policy for mitigating the presence of discrimination depends crucially on how it

varies across individuals. Without knowing which agents are discriminatory, it is not possible

for institutions to target individuals for discipline or training. More generally, the optimal

remedy will depend on the concentration of discrimination across agents. If misbehavior is

widespread, a targeted policy of disciplining specific individuals will be ineffectual, and the

appropriate response may require a department-wide solution.3

In this paper, we study traffic policing by the Florida Highway Patrol and examine

whether officers discriminate when enforcing punishments for speeding. We exploit a common

institutional feature in traffic policing and use a bunching estimation design to identify

discrimination. In many states, the punishment for speeding increases discontinuously with

2See www.gallup.com/poll/175088/gallup-review-black-white-attitudes-toward-police.aspx.

3The question of whether misbehavior is systemic or the product of a few bad individualshas also garnered policy interest with regard to federal oversight of local police departments. InJanuary 2017, Attorney General nominee Jeff Sessions stated, ”I think there’s concern that goodpolice officers and good departments can be sued by the Department of Justice when you just haveindividuals within a department who have done wrong. These lawsuits undermine the respect forpolice officers and create an impression that the entire department is not doing their work consistentwith fidelity to law and fairness.”

99

the speed of the driver, exhibiting “jumps” in harshness. A jump may involve not only a

higher fine, but also a mandated court appearance or permanent mark on the driver’s record.

Although officers typically observe a driver’s speed via radar before stopping them, they are

free to choose what speed to charge. It is thus a common practice for officers to reduce the

written speed on a driver’s ticket to right below a jump in the fine schedule.4 Our objective

is to identify discrimination in discounting at the level of the individual officer, where we

define discrimination as the differential treatment of drivers on the basis of their race when

stopped for the same speed.

Several features of our setting are ideal for studying discrimination. When testing for

discrimination in many criminal justice outcomes, a central concern is accounting for unob-

served differences in criminality across individuals. In the context of speeding tickets, guilt

is summarized by the driving speed, which is both one-dimensional and typically observed

by the ticketing officer. Further, in many criminal justice contexts, the lenience of an agent

is calculated relative to his peers’ behavior. In our setting, officers make an explicit deci-

sion to reduce a driver’s speed, allowing us to see each officer’s absolute degree of lenience

and observe officers who practice no lenience. Perhaps most importantly, we observe agents

making many decisions in very similar contexts, which allows us to construct an accurate

measure of discrimination for each officer by comparing his treatment of white and nonwhite

drivers.

As shown in Figure 2.1, the distribution of speeds ticketed by the Florida Highway

Patrol between 2005 and 2015 shows substantial excess mass at speeds just below the first

fine increase, where speeds are reported relative to the speed limit. Meanwhile, a remarkably

small portion of tickets are issued for speeds just above. We take this bunching as evidence

that officers systematically manipulate the charged speed, commonly charging speeds just

below fine increases after observing a higher speed, perhaps to avoid an onerous punishment

4This practice is similar to teachers’ bunching up of grades on high-stakes exams (Dee et al.,2016; Diamond and Persson, 2016).

100

for the driver. However, when disaggregated by driver race in Figure 2.2, we see that

minorities are significantly less likely to be found at the bunch point.

The first task of this paper is to confirm that this disparity is evidence of officer discrim-

ination. Our central challenge is in ruling out that racial differences in treatment are due

to differences in criminality. Minorities may be driving faster than whites when stopped,

leading officers to treat them less leniently. While our data record the speed that is charged

on a ticket, we do not observe the true stopped speed of the drivers in our data. To deal

with this challenge, we use the fact that one-third of officers practice no lenience. Namely,

they exhibit no bunching in their distribution of ticketed speeds.5 For these officers, we

argue that their distribution of ticketed speeds reflects the true distribution of driven speeds

among stopped and ticketed drivers. We show that, conditional on location and time, driver

characteristics are not predictive of whether the officer he encounters is lenient. Non-lenient

officers do not write fewer tickets than lenient officers, and a similar share of their tickets are

for speeding offenses. These facts suggest that lenient and non-lenient officers are pulling

over similar types of drivers, and thus non-lenient officers can be used to identify the “true”

distribution of speeds.

Using a difference-in-differences framework, we then find that white drivers differentially

benefit from being stopped by a lenient officer. White drivers stopped by lenient officers are

six percentage points more likely to be discounted than minority drivers, off a base of 45%.

This gain stems from the fact that minorities are treated less leniently when stopped for

speeds ranging from 12 to 25 MPH over the limit.

The central contribution of our paper is to further provide an estimate of the discrimina-

tion of each individual officer. Specifically, we compute an officer’s lenience toward minorities

relative to his own treatment of white drivers, differencing out the treatment of each race

by non-lenient officers and adjusting for other features of the stop, and treat that difference

as the officer’s discrimination. Disaggregating to the officer level reveals significant hetero-

5The existence of non-lenient officers also leads us to conclude that the bunching of ticketedspeeds is not due to drivers strategically driving below the jump in fine.

101

geneity in the degree of discrimination. An officer at the 90th percentile of discrimination

is nearly twice as likely to discount a white driver as a minority driver. The modal officer

practices no discrimination, and forty percent of officers explain the entirety of the aggregate

disparity. Correlating officer-level discrimination to demographics, we find that minority and

female officers tend to practice less discrimination than other officers.

We then show that a police department could feasibly use our approach to identify

discriminatory officers early in their careers. We construct our measure of each officer’s

discrimination using only his first 100 tickets and show that this early measure is closely

correlated with the full-sample estimate of her discrimination. An officer in the top 2% of

discrimination in the early measure is on average at the 8th percentile of discrimination

in our full-sample estimate, suggesting that a department can quickly identify the worst

offending officers.

The remainder of the paper exploits our officer-level measures of lenience and discrimina-

tion to understand the mechanisms that lead to the disparity in treatment. To what extent

are minorities being discounted less often because they are driving faster? Conversely, how

much of the gap in discounting is caused by discrimination? And what policies can be used

to reduce any disparity that is due to discrimination?

To answer these questions, we estimate a simple model that identifies both differences in

driving speeds, by each race and county, and preferences for discounting, by each officer and

race of driver. Model estimates indicate that, within location, forcing all officers to treat

minority drivers the same as they treat white drivers removes 83% of the gap in discounting.

Only 17% of the gap is due to minorities driving faster. Across locations, a large share of

the disparity in treatment is due to the fact that minorities drive in areas where officers are

less lenient to all motorists.

Performing the counterfactuals discussed above, we find that policies that target discrim-

ination directly are only mildly effective for reducing the treatment gap. Firing the most

discriminatory officers (both for and against minorities) reduces the gap, as does increasing

102

the presence of minority or female officers, but the gains are limited. Perhaps most effective

and easily implemented, reassigning officers across counties within their troops so that mi-

norities are exposed to more lenient officers can remove essentially the entire white-minority

discounting gap.

While the central focus of the paper is not to differentiate between taste-based discrim-

ination (Becker, 1957) and statistical discrimination (Arrow, 1973; Phelps, 1972), several

pieces of evidence suggest that the discrimination we observe is taste-based. First, our set-

ting is not as conducive to statistical discrimination as other criminal justice interactions.

In a speeding stop, the officer is aware of the crime committed (i.e., the speed driven) and

does not need to use race as a signal of criminality. This knowledge contrasts with cases

such as vehicle searches or stop and frisk, where the officer may use demographics to infer

whether an individual is carrying contraband. Further, the fact that minority and female

officers are less discriminatory on average suggests that the discrimination we observe is a

function of preferences rather than statistical inference. We also provide evidence that of-

ficers are not statistically discriminating on the basis of whether drivers are deterred from

future speeding by getting the full ticket. While we do find evidence that officers discount

partly on the basis of whether the individual will contest the ticket in court, this selection

cannot explain the racial disparity in discounting. Therefore, for the remainder of the paper,

we use discrimination and bias interchangeably.

This paper contributes to a growing literature on methods of testing for the presence

of discrimination in criminal justice and beyond. Popular approaches include audit studies

that vary individual race (Bertrand and Mullainathan, 2004; Edelman et al., 2017; Agan and

Starr, 2016), studies that vary the observability of race or gender (Goldin and Rouse, 2000;

Grogger and Ridgeway, 2006; Donohue, 2014), and studies of settings with rich controls for

underlying behavior and context (Fryer, 2018). Another popular approach to testing for

bias is the “hit rate test,” pioneered by Becker (1957), where discrimination is identified

103

by comparing the success in treatment across two groups where the treator ostensibly cares

about a single objective (Knowles et al., 2001; Arnold et al., 2018).

Another popular set of methods for detecting racial bias are benchmarking procedures,

whereby the behavior of one agent is compared to a proposed control group.6 Ridgeway and

MacDonald (2009) compare the racial makeup of NYPD officers’ stop and frisks to those

of nearby officers and are able to identify a set of officers with a disproportionately high

share of minority stops. To date, Ridgeway and MacDonald (2009) is the only study that

aims to identify discrimination of individual criminal justice agents. As they concede, the

central limitation of their approach is that they are unable to identify an overall level of

discrimination since they use the average officer within a beat as the comparison group for

officers who disproportionately stop minorities.

In the paper most closely related to ours, Anbarci and Lee (2014) study the discounting

behavior of traffic officers and, using a benchmarking design, find that the racial makeup

of discounted tickets is whiter for white officers than for minority officers, suggesting that

at least one group is biased in favor of their own race. Our approach broadly falls into the

benchmarking literature, as we use the set of non-lenient officers as a benchmark for the

behavior of other officers. Relative to this existing literature, a strength of our approach

is that the non-lenient officers are by construction non-discriminatory. This fact allows

us to avoid the common benchmarking challenge that the comparison group may itself be

discriminatory, leading to an underestimate of overall discrimination.

This paper also falls into a broad category of recent research using “bunching” estima-

tors to recover behavioral parameters (Kleven, 2016). Predominantly used in the literature

on taxation, these studies traditionally attempt to estimate the hypothetical distribution of

interest in the absence of bunching by looking at the distribution outside a region around

the manipulated area and inferring out-of-sample how the distribution should look at the

discontinuity (Chetty et al., 2011; Saez, 2010). Bunching is then estimated to be the differ-

6See Ridgeway and MacDonald (2010) for a review of the benchmarking literature.

104

ence between the true and hypothetical distribution around the bunch point. In contrast,

our approach is similar to Best et al. (2015) in that we use panel data and differences across

individuals in propensity to bunch to identify the true underlying distribution.

The rest of the paper is organized as follows. Section 2.2 provides institutional back-

ground on the Florida Highway Patrol and describes the data. Section 2.3 presents a con-

ceptual framework, and Section 2.4 describes our empirical strategy. Section 2.5 presents

the central findings, and Section 2.6 considers specification checks and alternative inter-

pretations of our results. Section 2.7 discusses applications of our officer-level measures of

discrimination. In Section 2.8, we present and estimate a model of officer behavior and

perform counterfactuals, and Section 2.9 concludes.

2.2 Institutional Background and Data

2.2.1 Institutions of the Florida Highway Patrol

State-level patrols are the primary enforcers of traffic laws on interstates and many highways.

When on patrol, officers are given an assigned zone, within which they combine roving patrol

and parked observation patrol. During the course of a traffic stop for speeding, officers have

two primary ways to exercise discretion. They can give a written or verbal warning, which

leads to no fine or points on the driver’s license, or they can reduce the speed charged

on the ticket. Florida Highway Patrol (FHP) officers are told explicitly in their training

manuals that no enforcement actions during a traffic stop can be based on any demographic

characteristics, including race and gender.

In Florida, driving 10 MPH over the limit leads to about a $75 higher fine than 9 MPH

over.7 While drivers receive points on their license for speeding, tickets received for 9 and

10 MPH over the limit carry the same number of license points. While it is also common

7The actual fine schedule depends on the county in Florida, though the jump point is the sameacross all counties and always includes at least a $50 jump in fine.

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to find a jump in fine between 19 and 20 MPH over, the data strongly suggest that officers

prefer to reduce the ticket to 9 MPH over.

Officers in the FHP are divided into one of 12 troops, almost all of which patrol six to

eight counties each. Officer assignments operate on eight-hour shifts and cover an assignment

region that roughly corresponds to a county, though the size of a “beat” can vary based on

the population density of the region. In practice, because we do not observe the exact beat

policed by an officer, we will use the county of the stop as a proxy for the officer’s assignment

region.

Officers face no revenue incentive to collect tickets, as all fines paid by drivers are collected

by the government of the county in which the fine was issued. There is also, to the best

of our knowledge, no quota system for a minimum number of tickets officers must write.8

Officers do, however, potentially have a promotion incentive to write a certain number of

tickets, as the number of tickets they write appears on their performance evaluations. We

believe these set of institutional factors contribute to an environment in which officers are

encouraged to write tickets but also have the freedom to write reduced charges, which is

ideal for our research design.

While all speeding beyond 5 MPH over the limit commands a statutory fine, the evidence

suggests that drivers are not regularly pulled over for less than 10 MPH over, and the data

show very few tickets for 8 MPH over and 10 MPH over. As we will reiterate in Section 2.4,

many officers have almost no tickets issued at 9 MPH over the limit, suggesting that the

majority of the bunching of tickets is for higher speeds that have been reduced.

2.2.2 Data

From the Florida Court Clerks & Comptrollers, we obtained data on traffic citations issued

by the Florida Highway Patrol (FHP) for the years 2005-2015. These data include all in-

8We checked for a spike in the number of issued tickets at certain days of the month or days ofthe week, and found no evidence of an ”end of the period” effect.

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formation provided on the stopped motorist’s driver’s license – name, address, race, gender,

height, and date of birth, as well as driver’s license state and number. The make, model, and

year of the stopped automobile is provided, but this information is recorded inconsistently.

In the final sample of citations, 69% of tickets list the vehicle make and year. The citing

officer is identified by name, rank, troop number, and badge number.9 While we see the

speed charged by the officer, we do not see the original speed recorded by the officer. We

also do not see stops and interactions that do not result in a traffic citation.10

To supplement the citations data, we obtained officer demographic information from the

Florida Department of Law Enforcement (FDLE). These data include officer race, sex, age,

education level, and the Florida law enforcement employment history of all law enforcement

officers employed in the State of Florida. It further includes every misconduct investigation

made by the state against an officer, the type of alleged violation, and the ultimate verdict

of the state. From the FHP, we also collected information on all use of force incidents and

civilian complaints against officers for the period 2010-2015, which list the name of the officer,

the date of the incident, and a description of the incident.

While the citations record the driver race, there appear to be inconsistencies in the

recording of Hispanic. For example, Miami-Dade County issues fewer than 1% of their

tickets to Hispanic drivers. To address this issue, we match the drivers’ names to Census

records, which record all names that appear more than 1,000 times and the share of white,

black, Hispanic, and other that carry that name. If an individual in our data has a name

that is more than 80% Hispanic, we record them as such.

We restrict the sample to citations in which the main offense is speeding; no accident is

reported; the cited speed is between zero and 40 above the posted speed; race of the driver

9The full data from the FCC contain all traffic citations for 2005-2015, including tickets notgiven by the highway patrol. We use these tickets to measure an individual’s previous drivingrecord. We do not use non-FHP tickets in our measures of bias, because officers are harder toidentify in these data. Further, much of the personnel information we collected is unique to theFHP.

10The problem of only seeing interactions that lead to enforcement is general in the discriminationliterature. For a recent paper that addresses this issue, see West (2018).

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is reported as white, black, or Hispanic (or is imputed as such); and the gender, age, and

driver’s license number are not missing. To link citations and officer information, we first

narrowed the list of FDLE personnel to include only officers with an employment spell as a

sworn officer with the FHP covering some portion of the 2005-2015 period. We then match

the list of candidate officers with the citations data using the officer name. We exclude stops

that cannot be matched to an officer. Lastly, we restrict the sample to officers issuing at

least 100 citations, with at least 20 given to minorities and 20 to whites.

The final sample includes 1,142,628 citations issued by 1,591 officers, from an initial

sample of 2,124,692 speeding citations. The two most binding restrictions are requiring that

race be specified (84% of tickets) and requiring that the officer be linkable to the FDLE

(77%). In the appendix Section .1 we include a table that documents the sample reduction

from each restriction we make. In all of our analyses, we consider speed relative to the speed

limit (or posted speed) rather than absolute speed. We often refer to this quantity as MPH

Over or simply as “the speed.”

Beginning in 2013, about 40% of tickets are geocoded with the latitude and longitude

of a stop (135,586 observations). We link the geocoded tickets to a Florida Department

of Transportation roadmap shapefile using ArcGIS.11 The shapefile is at the level of road

“segments,” which are on average 6.7 miles long and roughly correspond to entire streets

within cities and uninterrupted stretches of road on interstates and highways. Tickets are

linked to the nearest segment, and we remove tickets that are more than 100 meters from the

nearest road (dropping 1.5% of observations). Officers in more rural areas and on interstates

are given priority for vehicles with GPS, as they cannot clearly describe the location of their

ticket using street intersections. 40% of officers have fewer than 5% of their stops geocoded,

and there is some variation across counties in the share of tickets geocoded. Throughout the

analysis, we provide results for the restricted sample of tickets with GPS with corresponding

fixed effects at the road-segment level. Because we do not have perfect information on officer

11http://www.fdot.gov/planning/statistics/gis/road.shtm; We use the ”Basemap Routes withMeasures” shapefile.

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assignment (and use the county of the stop as a proxy), the road-segment analysis allows us

to consider a more granular comparison of drivers.

2.2.3 Summary Statistics

Table 1 presents summary statistics for the sample, broken out by driver race. 58% of

drivers are white, 18% are black, and about 23% are Hispanic. Drivers are 35% female

and about 36 years old on average, with Hispanics less likely to be female and minority

drivers typically younger. In-state drivers account for 84% of tickets. The average driver

has been cited about 0.34 times in the past year, though minorities have 0.13 more prior

tickets. On average, minority drivers are charged with higher speeds than whites: just over

1 MPH higher for blacks and almost 3 MPH higher for Hispanics. Consistent with Figures

2.1 and 2.2, drivers of all races have a high probability of being ticketed at 9 MPH over

the limit, which is just below the first jump in the fine schedule. However, minority drivers

are also less likely to be charged this speed. As we show in Appendix Tables A.1 and A.2,

these disparities in speed and ticketing below the jump persist after controlling for all stop

characteristics and time and location fixed effects.

A notable feature of the distribution of tickets is the heaping of charged speeds at multi-

ples of five above the bunch point. This heaping occurs because, in many instances, officers

do not use a radar gun, and their recording of the speed may be approximate. For 51% of

the tickets, the officers do record the ”method of arrest,” and 17% of these tickets report

that the officer used a radar gun. We report in Appendix Figure A.1 the distribution of

ticketed speeds for this subsample, and there is no heaping at multiples of five.12

In Table 2, we compare the racial distribution of speeding tickets with the racial distri-

bution of residents and drivers in Florida using the 2006-2010 American Community Survey

12In Appendix Table 5, we also show that our main result is not changed when restrictingattention to this subsample.

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(ACS) 1% samples.13 These data demonstrate that whites account for about 65% of Florida’s

population, and 63% of its drivers (an ACS respondent is considered a driver if they indi-

cate that they drive to work), and about 59% of tickets.14 Blacks represent around 14%

of the population and driving population, but 18% of tickets. Similarly, Hispanics are 20%

of the population, almost 19% of the driving population, and 24% of tickets. In Columns

(4) and (5), we present the racial distribution of black, white, and Hispanic drivers involved

in crashes and crashes with injuries over the 2006-2010 period. These shares are computed

from records provided by the Florida Division of Motorist Services that contain information

on all auto accidents known to police. These data likely correspond more closely to the de-

mographic composition of speeders than the general population of drivers. The racial shares

in the crash data correspond very closely to the citations data, with black drivers slightly

overrepresented and Hispanic drivers slightly underrepresented among crashes with an in-

jury. Overall, we do not have the impression that minorities are severely overrepresented or

underrepresented in the tickets data relative to the population or the distribution of speeding

drivers.

2.3 Conceptual Framework

In the previous section we documented the disparity in ticketing at 9 MPH over between

whites and minorities. Here we introduce a simple framework of officer decision-making that

can explain the disparity in discounting through two mechanisms – differences in speeding

and discrimination – and motivates our empirical strategy in Section 2.4 and our modeling

exercise in Section 2.8.

13We obtained these data from Integrated Public Use Microdata Series (IPUMS). So that thesamples are parallel, we use only citations from 2006-2010 and keep only white, black, or Hispanicindividuals aged 16 or over in the ACS. We use sampling weights when computing the shares fromthe ACS data.

14To match to the shares in our data, we restrict attention to ACS respondents who report theirrace as white, black, or Hispanic.

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Officer j stops motorist i for speeding. His observed speed x is drawn from some discrete

distribution Fr(·), which can be a function of the driver’s race r. For simplicity, we suppress

here the possible dependence of the distribution on other driver characteristics. If the driver’s

speed is above xd, the officer has the choice to reduce the charged speed to xd to reduce the

fine the driver will face. Otherwise, the speed is set to x. When deciding whether to reduce

the ticket, we suppose the officer weighs a mix of personal concerns such as the inconvenience

of attending traffic court; policing objectives such as the blameworthiness of the individual

and the potential deterrence effect of ticketing the individual; and bias against certain groups

r. Balancing these objectives, the officer has some probability Pj(x, r(i)) of discounting the

individual, which may be a function of the driver’s race r and the driver’s speed x.

In this framework, it is natural to define discrimination in the following way: We say that

officer j is discriminatory if Pj(x, r(i) = w) > Pj(x, r(i) = m) for a given speed x. While

we describe the officers’ preferences as potentially reflecting bias, we are not yet taking a

stand on whether any disparity in treatment is taste-based versus statistical. For example,

it is possible that some officers prefer whites because they believe the likelihood of having

to go to court later is lower. We discuss statistical discrimination in Section 2.6 and why we

believe the observed discrimination in discounting is taste-based.

The first empirical step we take is to model the likelihood of an individual appearing at

the discount point and above, given his observables. In our model, the probability of being

charged the discount speed is the summed likelihood of appearing at or above that speed

times the likelihood of being discounted:

Pr(Xi = xd| i, j ) = Fr(i)(xd) +∑k>xd

Fr(i)(k) · Pj(x, r(i)) (2.1)

and the probability of appearing at a point above the discount point,

Pr(Xi = x > xd| i, j ) = Fr(x) ·(1− Pj(x, r(i))

)(2.2)

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is the likelihood of having driven that speed and then not being discounted.

2.4 Empirical Strategy

From Equations (2.1) and (2.2), we see that racial differences in the likelihood of appearing

at the bunch point and above can arise from either differences in speeds Fr(x) or differences

in speed-specific discounting, Pj(x, r(i)). Primarily in the latter case will the disparity be

of policy interest, as it would be due to discrimination rather than differences in behavior.

To determine whether the observed disparity is due to differences in driving speed, we use

the fact that one-third of officers in our sample practice no lenience. In other words, these

officers have no bunching in their distribution of speeds.

In Figure 2.3, we motivate this approach by documenting the significant heterogeneity in

discounting across officers. Panel A plots the officer-level distribution of lenience, defined as

the share of tickets written for 9 MPH or above that are for exactly 9 MPH. A large share of

officers appear to exhibit very little lenience, with 30% writing less than 1% of tickets for this

bunching speed. Panel B plots the distribution of officer lenience after residualizing county

and month-of-stop fixed effects and driver characteristics. The observed disparity suggests

that the heterogeneity across officers is not due to differences in location or characteristics

of the stopped drivers.

The lower two panels confirm that officers are persistent in their level of lenience across

time and location. In Panel C, we plot each officer’s residualized lenience in his year with the

second-most stops (y-axis) against his residualized lenience in his year with the most stops

(x-axis). A strong correlation is evident: an officer who charges 9 MPH relatively more often

in one year also does so in other years. In Panel D, we plot lenience in the county where the

officer has made the second most stops against lenience in the county where he has made

the most stops, confirming that officer lenience is highly correlated over space.

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We treat the 33% of officers with fewer than 2% of their tickets issued at 9 MPH over as

non-lenient officers, and we use these officers for two purposes.15 First, we suppose that these

officers’ ticketing distribution reflects the true distribution of speeds within their location

and shift and use them to uncover the true racial difference in speeding. Secondly, we use

these officers as a control group in a difference-in-differences style framework to estimate the

effect of encountering a lenient officer on the likelihood of being discounted for each racial

group.

To do so, we run a linear probability model, where the outcome is an indicator Skij of

whether a driver is stopped at a given speed k, and the race of the driver is interacted with

the lenience of the officer:

Skij = β0 + β1 ·Whitei + β2 · Lenientj (2.3)

+β3 ·Whitei · Lenientj +Xijγ + εij

For all regressions, the primary coefficient of interest is β3, the interaction between white

driver and lenient officer. For the bunch point of 9 MPH over the limit, β3 reflects how much

more a white driver benefits from encountering a lenient officer than a minority driver. For

all speeds above 9 MPH, the interaction reflects how much less likely minorities are to be

discounted by a lenient officer. Xij contains the set of all observable characteristics of the

drivers, including gender, age, age squared, number of previous tickets, whether the driver is

in-state, the log average income of the driver’s home zip code, vehicle age and age squared,

and indicators for vehicle make.

We also include fixed effects interacted at the level of the stop’s year, month, day of the

week, shift, county, and whether it was on a highway, which we henceforth refer to as the

time and location of the stop. The purpose of the fixed effects is to make the difference-

15An alternative approach is to explicitly test for the presence of bunching officer-by-officer.When we do so using the Frandsen (2017) test, the set of officers identified as non-lenient remainvery similar and the regression results do not change. These results are reported in Appendix Table5.

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in-differences comparison among drivers stopped in the same beat and shift. As mentioned

earlier, county is our best available approximation to an officer’s beat. To provide an even

more granular comparison, we will also report results for our GPS sample, where we include

fixed effects interacted at the year, month, day of the week, shift, and road segment level.

To calculate each officer’s individual discrimination coefficient, we take a similar approach

and use non-lenient officers as a control for the baseline frequency of tickets at 9 MPH over,

but we allow the coefficients for Lenientj and Whitei·Lenientj to vary by individual officer:

S9ij = β0 + β1 ·Whitei + βj2 · Lenientj (2.4)

+βj3 ·Whitei · Lenientj +Xijγ + εij

The coefficients of interest, βj3, are identified from each officer’s difference in discounting

between whites and minorities, differencing out the disparity in ticketing for non-lenient

officers. We denote βj3 as officer j’s degree of discrimination. For the purpose of reporting the

distribution of discrimination across officers, we treat non-lenient officers as having βj3 = 0,

since by definition they cannot be discriminatory.

The intuition for our difference-in-differences procedure is shown in the top two images in

Figure 2.4. Here we plot the histogram for non-lenient officers over the histogram for lenient

officers, separately by driver race. The gap in histograms between lenient and non-lenient

officers above 9 MPH over indicates the speeds at which drivers are reduced to 9 MPH over.

The difference in these gaps between white and minority drivers indicate the difference in

discounting between races for each speed.

For lenient officers to be a valid control group, it must be the case that, conditional on

location and time of the stop, the lenience of the officer is uncorrelated with the error term,

Cov(Lenientj, εij) = 0. This assumption entails two presumptions about the stop. First, we

require that officers in the same shift and beat are not systematically different in who they

stop; second, officers do not systematically differ in the characteristics of drivers to whom

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they give a warning, which would lead to differential selection into our data. As mentioned

above, we see no information about stops that do not result in a ticket, so one concern is

that officers who differ in their lenience toward discounting may also differ in their lenience

in the initial margin of whether to even write a ticket.

In Figure 2.5, we evaluate how the characteristics of an officer’s stops vary with whether

the officer is lenient or not, where both variables have been residualized with location-time

fixed effects. The top left panel of the figure shows that officer lenience is not predictive of

his share of tickets written to minorities. The top right panel shows that officer lenience is

uncorrelated with whether a driver’s race is missing, and the bottom left panel shows that

officer lenience has only a small, though significant, correlation with the likelihood that a

ticket is for speeding. The bottom right panel shows the relationship between officer lenience

and the average daily number of tickets. For this figure we calculate both measures at the

annual level, during which officers write most of their tickets in one county, allowing us to

control for county-by-year fixed effects. We find that whether or not an officer is lenient is

not predictive of the number of tickets written per day.

To further test for selection on observables, Table 3 estimates how officer lenience varies

with driver characteristics. The outcome for all regressions is the indicator for whether the

stopping officer is identified as lenient. The F-tests report a joint test of the hypothesis

that all driver characteristics have zero correlation with officer lenience. Column (1) reports

results with no controls for location or time. Here officer lenience varies significantly with

driver characteristics. Hispanic drivers and in-state-license drivers are ticketed in areas where

officers are less lenient to everyone. Columns (2) and (3) restrict attention to variation within

location and location plus time, respectively. With these controls, officer type varies much

less significantly with driver characteristics. A joint F-test fails to reject at 10% significance

that all driver characteristics are equal to zero. Columns (4) and (5) report results for our

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GPS’ed sample. Both with and without fixed effects for the road-segment of the stop, we

find that our indicator for officer lenience is uncorrelated with driver characteristics.16

2.5 Results

Our first use of non-lenient officers is to test whether minorities truly drive faster than white

drivers. The bottom two panels of Figure 2.4 report the distribution of ticketed speeds

for non-lenient officers. Unconditional on any covariates, minorities drive 1.5 MPH faster

than whites. However, when controlling for county and individual covariates, this disparity

shrinks to 0.39 MPH, and the disparity is barely perceptible visually. The majority of the

reduction comes from accounting for county fixed effects, since minorities tend to drive in

counties in which all drivers are stopped at faster speeds. The fact that the county-specific

disparity is so small suggests that the racial disparity in discounting cannot be explained

by differences in driving speed. In Appendix Table (A.3), we show that this small gap is

consistent across various specifications for time and location controls.

Figure 2.6 and Table 4 report the results of the difference-in-differences test of discrimi-

nation. The figure reports regression coefficients from both a specification with no controls

and our preferred specification with individual covariates and fixed effects for county by year

by month by shift by highway. As indicated by the interaction variable for white drivers

and lenient officers encountered at 9 MPH over, white drivers are significantly more likely

to receive a discount than minority drivers. Off a mean probability of 45%, white drivers

stopped by lenient officers are encountered at the bunch point 6-8.4pp more often than mi-

norities, and this disparity persists regardless of the specification. In Columns (4) and (5) of

Table 4, we perform the same regression for the restricted sample with GPS ticket location.

16In Appendix Table A.4, we consider a similar set of randomization checks, where the outcomeis the officer’s share of tickets at 9 MPH over rather than the indicator for lenience. The resultsare similar to Table 3. However, in Column (3) we reject the null of no relationship between theoutcome and observables at the 5% level. We believe this correlation is due to our inability toperfectly control for officer assignment. When we restrict attention to our GPS sample in Columns(4) and (5), we continue to have no relationship between observables and officer lenience.

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The results continue when allowing for stretch-of-road fixed effects, though the coefficient is

a slightly smaller 5.5pp.

The interpretation of these coefficients tell us how much more likely a lenient officer is

to discount a white driver. To calculate a differential probability of discount by an average

officer, we use the fact that two-thirds of tickets are written by lenient officers and scale

accordingly, finding that an average encounter leads to a 4pp higher discount probability for

white drivers, off a base of 30%.

The interaction coefficients for speeds above 9 MPH shown in Figure 2.6 indicate where

minority drivers are disproportionately being ticketed, and thus the speeds at which white

drivers are being differentially discounted. The interaction coefficient is negative and signif-

icant for all speeds between 12 and 20 MPH, suggesting that at these speeds minorities are

less likely to receive a break.

A natural question to ask is how this estimate aggregates to a total cost of discrimination.

Every year, about 590,000 speeding tickets are given to drivers in Florida for 9 MPH over or

greater, 240,000 of which are given to black and Hispanic drivers. The jump from 9 MPH

over to 10 MPH over leads to a $75 fine increase. Using our estimate that minority drivers

are 4 percentage points less likely to be discounted, we calculate the cost of discrimination

toward minority drivers to be $720,000 per year. Scaled up to the entire US population, that

figure increases to $11.3 million.17

Officer-level results are reported in Figure 2.7. The figure displays the across-officer

distribution of the interaction coefficient βj3, where non-lenient officers are assigned βj3 = 0.

The line represents a kernel density plot of our measure of discrimination against minority

drivers, so that the farther right an officer is in the distribution of discrimination, the greater

his level of discrimination. The unit of our measure is probability difference in percentage

points. An officer whose discrimination against minorities is 0.1, for example, is 10 percentage

17Florida’s 2016 population is 20.6 million, and the US population is 323.1 million, so we multiplyour figure by 323.1/20.6

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points more likely to offer a fine reduction to a white than a minority driver. The percentiles

of officer discrimination are also reported in Appendix Table A.5.

The first fact to note is the substantial heterogeneity in discrimination across officers.

While the modal officer practices no discrimination, we find a large mass of officers with

positive discrimination. Officers at the 10th and 90th percentiles of discrimination have a 14

percentage point difference in their racial disparity. When calculating their lenience toward

minorities as a share of their lenience toward whites, officers at the 90th percentile are more

than 40% less likely to discount minorities.

The second notable fact is that the median level of discrimination is quite small, three

percentage points off a base of 30%. While this disparity is comparable to the black-white

wage gap (Neal and Johnson, 1996), it is possible that the officer in question is not aware

of such a disparity. A large literature has explored the role of implicit bias as a source of

discrimination (Greenwald and Krieger, 2006; Banks et al., 2006), and in many cases the

individual in question is not aware of his bias. We believe that for the median officer our

results are consistent with such a theory. However, for higher percentiles of the distribution,

it is hard to explain large gaps in treatment as a practice that is imperceptible to the officer.

An officer at the 75th percentile has a 6.8pp difference in treatment, and this gap nearly

doubles to 12.8pp at the 90th percentile.

Even under a data-generating process in which officers all have the same true discrimina-

tion, our estimates would have a distribution due to sampling error. This scenario, however,

cannot explain the heterogeneity we find. The average standard error for an officer’s βj3

is 0.014 – less than one-fourth the standard deviation of βj3 across officers, 0.068. In the

scenario in which true discrimination is uniform, these numbers would be similar in magni-

tude. We thus conclude that the majority of the variation is due to true officer differences

in discrimination rather than estimation error. 18

18One way to calculate officer heterogeneity’s accounting for noise is to do a Bayes shrinkageprocedure. When we replicate the approach of Aaronson et al. (2007), our distribution of discrim-ination looks nearly identical to the unshrunk version.

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2.5.1 Share of Officers Who Are Discriminatory

Another approach to understanding the variance in discrimination across officers is to esti-

mate what share of officers are discriminatory. We know that each officer’s discrimination

measure is an additive function of his true discrimination plus estimation error, θj = θj + εj,

where εj is asymptotically normally distributed and σ2j is estimated in the officer-level re-

gression. We can assume an officer’s discrimination can take on a finite set of values on a

fine grid, θj ∈ {θk},19 and calculate the likelihood of observing each officer’s discrimination

measure θj given the noise in the measure and the true distribution f(θk):

Prob(Θj = θj) =∑{θk}

f(θk) · Prob(εj = θk − θj)

We then estimate {f(θk)} by maximum likelihood. Using this approach, and calculating

1− F (0) as the share, we find that 41% (CI 38.5-43.7%) of officers are discriminatory.20 In

contrast, we find that only 7% (CI 5.6-8.7%) of officers have θj < 0, i.e., practice reverse

discrimination.21

2.6 Robustness Checks and Alternative Explanations

In this section we report various specification and robustness checks to evaluate the strength

of our findings. In particular, we consider various explanations of our findings that are not

officer racial bias.

In Section 2.4, we reported various specification checks for the randomization of officer

lenience. An additional test for the random assignment of officer to driver is that officer

discrimination is not correlated with driver characteristics. We report such regressions in

19The grid is 99 points spanning the 1st to 99th percentiles of the empirical distribution of θj .20Confidence intervals are calculated through bootstrapping by performing 100 draws of the set

{θj} and performing MLE on each draw.21This approach is a discretized version of a deconvolution procedure (Delaigle et al., 2008).

Doing the continuous deconvolution leads to an identical estimate for the share of officers who arediscriminatory.

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Appendix Table A.6. As before, Column (1) reports the regression with no controls, and the

F-test indicates that some driver characteristics are correlated with officer discrimination,

statewide. All other regressions, which include controls for county, report no relationship

between officer discrimination and driver demographics.

In Table 5 we report the primary difference-in-differences results with various changes in

the regression specification, with Column (1) re-reporting the baseline specification. In Col-

umn (2), we conduct a split-sample analysis where we calculate whether an officer is lenient

using a randomly-selected 20% of officers’ tickets, which we exclude from the regression. In

Column (3), lenience is calculated separately for each officer’s year of ticketing, allowing for

changes in officer behavior over a career. In Column (4), we calculate an officer’s measure

of lenience using the Frandsen (2017) test for manipulation of a discrete running variable

(designed for testing the validity of the regression discontinuity research design). In Col-

umn (5), we re-weight the set of observations so that the “share” minority in each county

is the same. This approach is borrowed from Anwar and Fang (2006) and accounts for the

possibility that officers differ across counties in their lenience, which could be correlated

with minority status. In Column (6), we interact officer lenience with all driver characteris-

tics, testing that lenience towards whites is not confounded by lenience towards observable

non-race characteristics.

One feature of the data discussed earlier is that the histogram of ticketed speeds exhibits

jumps at multiples of five, and we argue that this heaping is due to officers not using a radar

gun and writing an approximate speed for the driver. In Column (7) of Appendix Table 5,

we find that our baseline regression is essentially unchanged when restricting to the sample

of tickets from a radar gun.

In all these specifications, the interaction coefficient between officer lenient and driver race

is significant and quantitatively similar to the baseline specification. The largest disparity is

evident in the re-weighted specification, where the coefficient reduces from 6.8pp to 5.5pp.

This difference suggests that some of the gap in treatment between whites and minorities is

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due to minorities disproportionately driving in counties where officers are less lenient overall.

These differences across counties could be due to differences in how much drivers exceed the

speed limit. In our model in Section 2.8, we explicitly account for the possibility that counties

and races differ in speeds and continue to find a disparity in discounting between races.

2.6.1 Selection into the Data

As we state in Section 2.2, our data are constrained by the fact that we do not observe

interactions that do not result in a ticket. One concern is that differences on the margin of

whether to give a ticket vary across officers and that this difference may make our estimates

of officer-level discrimination inconsistent.

We do not believe that this issue is a serious concern in our setting. In Section 2.4 we

show that officer lenience is only very weakly correlated with the frequency of tickets written

and, in Section 2.6, that discrimination does not correlate with the share of tickets written

for minorities.

We further believe that any discrimination on the stopping margin would likely bias our

results toward finding less discrimination in discounting. To see this argument, imagine a

minority driver who is on the margin of being ticketed, such that if he were white he would

have been let off with a warning. This driver appears in our data only because he is a

minority. Because he is at this margin, it is very likely the officer will give him a discount.

Therefore, discrimination on the ticketing margin places too many minority drivers in our

sample who are disproportionately at the discount point. Thus, the disparity in discounting

would be even greater without a hypothetical disparity in ticketing.22

In Appendix Section .2, we formalize this logic with a simple selection model that allows

for officer differences in propensity to let drivers off with a warning. Using this model, we

22As pointed out in Brock et al. (2012), it is not necessarily the case that an individual at themargin of appearing in the data is guaranteed a certain treatment once in the data. In light oftheir argument, our selection correction procedure allows for an arbitrary relationship between anindividual’s propensity to be ticketed and propensity to be discounted.

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implement a sample selection correction, as in Heckman (1979), that accounts for officer-by-

race differences in propensity to appear in the data. We reports the results of this regression

in Table 6. Column (1) reports our baseline regression, and Column (2) implements the

sample-selection correction. The results look identical after making this correction.

2.6.2 Racial Difference in Requesting a Break

One key insight of our analysis is that while whites and minorities do not seem to be dif-

ferentially exposed to police through traffic enforcement, the quality of the interaction can

vary significantly. This insight has also been made by research that documents racial differ-

ences in the quality of police-civilian interactions (Najdowski, 2011; Najdowski et al., 2015;

Trinkner and Goff, 2016; Voigt et al., 2017).

However, differences in the quality of the interaction leave open the possibility that white

drivers are actually more likely to request a break than minorities. If officers are open to

requests for a discount, this difference in solicitations could generate a disparity in lenience.

As in most discrimination studies, we do not have direct information on the quality and

content of the interaction between officer and driver, so we cannot directly test for whether

drivers differ in their propensity to request a break.

We do not believe, however, that differences in requests for a break can explain the

disparity in discounting we observe. For a given level of lenience toward whites, we still see

differences in discrimination across officers. If officers are simply receiving solicitations for

a discount from the drivers (and whites ask more often), we should expect that for a given

level of lenience toward whites, lenience toward minorities is a fixed fraction of that lenience.

This pattern is not borne out in the data. We find that 50% of the variance in discrimination

across officers remains after conditioning for lenience against whites.

Relative to existing studies in the discrimination literature, one strength of our data

is that individuals can be linked across tickets, allowing us to evaluate whether there are

individual-level differences in propensity to receive a discount. We probe this question further

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in Columns (3)-(5) of Table 6. To do so, we restrict attention to individuals with at least two

tickets. Column (3) presents a regression of discounting on individual characteristics, and

Column (4) adds officer fixed effects. This addition increases the R2 from 0.318 to 0.527. In

contrast, the further addition of individual-fixed effects in Column (5) only increases theR2 to

0.542. This small increase shows that, beyond individual covariates and the stopping officer,

the specific individual has little explanatory power for whether a discount is given, indicating

that individual differences in propensity to request a break is likely not a substantial factor

in the disparity in discounting.

2.6.3 Statistical Discrimination v. Taste-Based Discrimination

Throughout the paper, we have defined racial bias as the differential treatment of drivers

by race who are stopped for the same speed. This definition is not innocuous, as there may

be some reasons for differential treatment unrelated to observed driving speed that, while

contentious in their use, are not specifically racial animus. For example, officers may choose

who to discount on the basis of how individuals respond after the stop: some drivers may

be more deterrable and speed less after a harsh ticket; others may respond by contesting the

ticket in court. Our baseline regressions show that officers differentiate between white and

minority drivers after controlling for previous tickets, suggesting that the observed disparity

does not reflect statistical discrimination on the level of criminality. However, these estimates

do not rule out racial differences in the responsiveness to the ticket.

In Appendix Section .3, we present a simple test for whether officers are attempting to

minimize court contesting or maximize deterrence, which we report in Table 7. To evaluate

the impact of a discounted ticket, we instrument for receiving a discount using the stopping

officer’s persistent (leave-out) level of lenience.23. Our test then follows the logic of Heckman

23This procedure is very commonly used in the criminal justice literature when judges differ intheir punitiveness (Kling, 2006; Dobbie and Song, 2015) We use this approach to evaluate howindividuals respond to their ticket in a follow-up paper, Goncalves and Mello (2017).

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et al. (2010) and claims that non-linearities in the relationship between the outcome and the

propensity score reflect sorting of individuals on the basis of their responsiveness.

We find no evidence that officers choose who to discount on the basis of deterrability:

the impact of a discount on future speeding is positive but constant across levels of officer

lenience. However, we do find that officers choose who to discount based on whether they will

contest their ticket in court: among officers who are not very lenient, the marginal impact

of giving a driver a discount is a large reduction in likelihood of contesting the ticket. In

contrast, more lenient officers have a marginal impact of a discount on court contestation

that is significantly smaller, suggesting that more responsive drivers are discounted first. We

then perform in Column (5) a hit-rate test similar to Arnold et al. (2018) and find that

officers’ statistical discrimination on court contestation cannot explain the racial disparity

in discounting.

2.7 Applications of Officer Heterogeneity

Relative to the literature, our central contribution is the ability to generate officer-level

estimates of discrimination, as presented in Section 2.5. The first insight we gain from this

distribution is that discrimination varies greatly from officer to officer. However, estimating

the degree of discrimination of individual officers allows us to address various previously

unanswerable questions. How does discrimination vary by officer demographics? Are early

measures of discrimination predictive of long-term discrimination? And which personnel

policies can mitigate the effect of discrimination? We answer the first two questions in this

section and the third in Section 2.8.

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2.7.1 Do Officer Characteristics Predict Discrimination?

Given an officer-level measure of racial discrimination, a natural question is how it corre-

lates with other officer characteristics and behaviors. We can tackle this question using the

personnel records collected from the FDLE and the FHP.

The left panel of Figure 2.8 shows how our measure of discrimination varies by officer race.

Perhaps consistent with intuition, white officers are much more likely to be discriminatory

against minority drivers, with a greater rightward skewness in their distribution. However,

minority officers are still, on average, discriminatory against minority drivers. Among black

officers, a very small percentage are discriminatory in favor of minority drivers. Some of

the disparity in discrimination across officer race is driven by minority officers being less

likely to be lenient overall. This fact is due in part to minority officers working in troops in

which all officers are less lenient. In the right panel of Figure 2.8, we show the distribution

of discrimination only for lenient officers. The white officers’ distribution continues to be

shifted farther to the right.

The ability to identify discrimination separately by officer race is another advance beyond

the previous literature. Several benchmarking papers detect bias using comparisons across

officer race (Anwar and Fang, 2006; Antonovics and Knight, 2009; Price and Wolfers, 2010;

Anbarci and Lee, 2014). With such an approach, we can know that some race of officers is

acting in a discriminatory manner, but not which group. With our method, we can see the

magnitude of discrimination separately for each officer race.

In Table 8, we present regressions of officer-level discrimination on officer characteristics.

Here we have disaggregated officer discrimination to be calculated separately against black

drivers and Hispanic drivers24. All observations are weighted by the variance of the noise in

our estimate of the officer’s bias.

24Specifically, we run S9ij = β0 +β1 ·Blacki+β2 ·Hispanici+βj3 ·Lenientj +βjB ·Blacki ·Lenientj +

βjH · Hispanici · Lenientj + Xijγ + εij . We take -βjB and -βjH to be our measures of discriminationagainst black and hispanic drivers, respectively.

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As with the density plots, the clear takeaway from the regressions is that minority officers

are more lenient toward minority drivers, as we might expect. Female officers appear less

biased against black drivers and marginally less biased against Hispanic drivers. Officers

with more years experience are more discriminatory against Hispanic drivers, though the

standard errors are large. There appears to be no relationship between officer discrimination

and level of education, number of civilian complaints, or number of use-of-force incidents.

While some officer demographics are predictive of discrimination, we are also interested

in the usability of our measures of discrimination to predict other officer behavior. A growing

literature is interested in identifying the factors that can predict officer misconduct (Chalfin

et al., 2016a). Here we ask whether our measures of lenience and discrimination can be used

to predict an officer’s propensity to receive a civilian complaint or use force on the job. To

make the analysis at the officer-level – but still account for differences in years and locations

worked – we run regressions of the following form:

Yi = α0 + α1 · Leniencei + α2 · Biasi +Xi · β +∑k

Districtki +∑k

Yearki + εi

where Yi is an outcome of either receiving a civilian complaint or using force. Districtki

is an indicator for an officer ever working in District k in the years 2011-2016, and Yearki

indicates whether an officer appears in our traffic data in year k. Xi are other officer-level

characteristics.

The results, reported in Table A.7, indicate that lenience is statistically predictive of

both civilian complaints and use of force. An increase of one standard deviation in lenience

(25% change in discounting) correlates to 0.19 fewer civilian complaints and a 5.5% decreased

likelihood of receiving any complaints. Similarly, a one SD increase in lenience is associated

with 0.06 fewer incidents of force and 3% lower likelihood of any force. Black officers are

less likely to engage in force, as are older officers. Female officers are less likely to receive

complaints but just as likely as male officers to use force. Discrimination against minorities

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seems to be positively related to force and complaints, though the standard errors are too

large to say conclusively.25

2.7.2 Are Our Estimates Usable by a Police Department?

We argued above that the central value of estimating the distribution of discrimination is

its use for conducting policy. Knowing who is discriminatory is crucial for identifying who

to train or discipline. Given this motivation, a natural question is whether the measure we

have constructed for each officer is actually usable by a department to identify discriminatory

officers. Specifically, we ask whether an individual’s discrimination– as calculated from his

first 100 tickets, which the median officer writes in 400 calendar days– is close to his measure

from the full sample.

To calculate the early measure of discrimination, we first predict whether a ticket is going

to be at the discount point using only our sample of non-lenient officers, fitting E(S9ij|Xij) =

Xijβ. We then calculate εij = S9ij −Xijβ for each ticket, including those by lenient officers.

Then, we take each officer’s first 100 tickets and calculate discrimination as the difference in

residuals across his white and minority drivers.

Dearlyj = εwhite

ij − εminij

We report in Table 9 the relationship between this early measure and our full-sample esti-

mates of discrimination. We find that Dearlyj has significant value for policy. Its correlation

with our full measure βj3 is 0.45. The top panel reports how the percentiles of the two dis-

tributions correspond. Among the 2% of officers with the most discrimination in our early

25Our estimates of lenience and discrimination are both measured with error, leading to attenu-ation in the relationship between these measures and misconduct. To attempt to account for thiserror, we also do a split-sample instrumental variables procedure. We divide each officer’s datarandomly in half and estimate their bias and lenience for each sample. We then use one estimateas an instrument for the other. Doing so, we find the coefficients on discrimination increase overallin magnitude, though the standard errors remain too large to definitively say whether there is atrue relationship.

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measure, the median percentile in the full sample is 3.2. The 5% and 10% most discrimina-

tory also mostly consist of officers who are discriminatory in the full sample. However, the

95th percentile of “early discrimination” officers are quite nondiscriminatory when calculated

in the full sample. This fact implies that some officers who are discriminatory in their early

ticketing grow out of this practice in later years.

This “mistake” in the early measure is confirmed in the bottom panel of Table 9, which

reports Type-I and Type-II error in identifying career-wide discriminators. Among the 398

(25%) officers whose early measure indicates discrimination with 95% confidence, 32.2% are

found not to be discriminatory at 5% significance in the full sample. Restricting attention

to officers whose z-statistic in the early measure exceeds 3 (99.8% confidence) barely reduces

Type-I error, to 28%. The stubbornness of this error suggests that the early measures

are somewhat incorrect – not because of imprecision, but because officers change in their

ticketing practice past their first year in policing. The Type-II error column indicates the

share of officers who are found in the full sample to be discriminatory at the 5% level but

were not detected in the early measure. This number is greater than 50% in all columns,

suggesting that early detection can catch no more than half of discriminatory officers.

Taken together, these calculations suggest that our early measure can be useful for identi-

fying officers for training as part of an early-warning system (Walker et al., 2000). However,

we caution against disciplining or removing officers on the basis of our early measures, as

they often identify officers who are non-discriminatory in the totality of their careers. An

early warning system is also not a panacea, as it fails to identify more than 50% of officers

who will practice discrimination in their later careers.

2.8 Model and Counterfactuals

One of the central motivations of our paper is the need to understand how various personnel

policies affect the aggregate disparity in treatment between whites and minorities. We have

argued that the key input into the outcome of these policies is the distribution of discrimi-

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nation across officers. To perform counterfactual analyses, however, we need to know both

how driver speeds are generated and how officers then choose to discount these speeds. To

do so, we present a simple model that allows us to simultaneously estimate officers’ taste

parameters for each racial group and speed parameters for each race-by-county. Doing so

allows us to perform counterfactuals that change the distribution of discrimination across

officers.

Individual i drives at a speed s that is drawn from a Poisson distribution Pλi(s), where

λi is a function of the county-by-race of the driver and other demographics Z(1):

λi = λrc + γZ(1)

where we include in Z(1) the driver’s gender, age, and number of tickets in the previous three

years. Within a county, officers and drivers match randomly with each other. If the driver

is stopped for a speed s at or below the discount point xd, the officer charges s. If s > xd,

the officer has the choice to discount the driver to xd. He makes this decision by weighing

a cost to discounting, which we impose to have the form c(s) = b · s, against the ”value”

of discounting, tij = trj + αZ(2)i + εij, where trj depends on the officer identity and driver

race, Z(2) are driver demographics, and εij is a standard normal random variable reflecting

differences in preference not captured by driver demographics. Thus, the driver has her

speed reduced to xd if

trj + αZ(2)i + εij > a+ b · si

In addition to the Z(1) demographics, Z(2) includes the share of drivers in a county who are

minorities. We include this share to account for the possibility that officers change their

behavior depending on the racial mix of the county’s drivers.

Two simplifications of the model should be discussed here. First, we do not allow the

driver’s distribution of speeds to respond to the lenience of the officers in their county. We

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are comfortable in making this restriction because we find that there is no cross-sectional

relationship between the county lenience rate and the speeds charged.26

Second, we provide no micro-foundation for an officers’ decision to discount a driver. In

Appendix Section .3, we provide a series of tests for identifying what the officer is maximizing.

However, for the purposes of conducting the counterfactuals, it suffices to identify differences

across officers in their propensity to discount.

2.8.1 Identification

In principle, our model can be identified using only aggregate information, as if all data

came from one officer and one county. Intuitively, the tickets provide 40 moments (for each

potential speed) to estimate three parameters (discount slope, preference for discounting, and

true speed). Such an estimation approach relies heavily on the functional form assumptions

of a Poisson speed distribution.

In practice, our estimation is similar to our difference-in-differences regressions, in that it

relies heavily on the heterogeneity across officers in discount lenience. While all officers’ data

enter the maximum likelihood equations, the speed parameters are primarily identified using

officers who exhibit no lenience, from which we get an estimate of the true distribution of

speeds. To do so, we strongly rely on the assumption that officers and drivers are randomly

sorting within a county, allowing us to suppose that the underlying distribution of speeds

are the same for non-lenient and lenient officers.

Our estimation also depends heavily on the smoothness and parameterization of the

underlying speed distribution. Any excess mass at the bunch point is taken to be lenience

26In Goncalves and Mello (2017), we find that drivers do respond ex-post to receiving a harshticket by speeding less. This should lead to a steady-state relationship between lenience and thefrequency of traffic tickets. However, the magnitude of the deterrence effect is small enough thatthe racial gaps in the counterfactuals would not be meaningfully impacted. For example, in the 11years of our sample, if all minority drivers were treated as white drivers, there would only be about70 more car accidents and fewer than one more death.

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on the part of the officer. As argued earlier, we believe this assumption is valid, and drivers

are not systematically choosing to bunch below the fine increase.

We estimate the model via maximum likelihood. The model parameters to be identified

are the 67×2 county-race speeds λrc; 3 demographic speed parameters γ; 1592×2 officer

average racial preferences, trj; 4 demographic preference parameters α; and the slope of the

cost function b, totaling 3,326 parameters. Details of how the estimation is carried out in

practice are provided in Appendix Section .4.

2.8.2 Model Estimates

The results of the model estimation are reported in Appendix Table A.8. Because the

estimates are closely aligned to the findings from our difference-in-differences approach, we

leave our full discussion of these estimates to Appendix Section .4.1. In short, we find that

the average officer practices substantial lenience, with a significant variance across officers.

Off a baseline of 35.7% likelihood of discounting a driver from 10 MPH to 9 MPH, the

average officer is 2pp less likely to discount minority drivers. We find that minorities drive

significantly faster than white drivers, as do males, younger drivers, and drivers with previous

tickets. The average officer is also more generous to female drivers, old drivers, and drivers

with fewer previous tickets. They are also less lenient to all drivers when ticketing in a

county with more minorities.

Decomposing the Gap in Discounting

A first-order question in the study of discrimination is the extent to which an aggregate

racial disparity can be explained by the measured amount of bias. Table 10 seeks to answer

this question by decomposing the measured racial discounting disparity into discrimination

by officers, sorting of officers across counties, and differential speeding by racial groups. We

do so by simulating the model with different restrictions on the behavior and location of the

officers. In each simulation, drivers are randomly re-assigned a new officer from their county

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and drawn a new speed s from their individual specific distribution Pλi(s). If the driver’s

speed is above the discount point, the officer draws a preference shock ε and gives the driver

a discount to 9 MPH over if tij + ε > b · x. Standard errors are calculated by iterating the

simulation 100 times, as explained in Appendix Section .4.2.

The “Baseline” row of Table 10 shows how the charged speeds of drivers appear in a

simulation of the model that does not change any of the parameters of the model. All of

the decompositions are benchmarked to this baseline. In the ”No Discrimination” row, we

remove discrimination by making each officer treat minority drivers like they treat white

drivers. This restriction reduces the gap in discounting by 25%. In the ”No Sorting” row,

drivers and officers match randomly from throughout the entire state rather than the initial

county. Here we find that 28% of the gap in speeding is removed, consistent with the earlier

finding that officers tend to be more lenient overall in neighborhoods with fewer minorities.

Removing both sorting and discrimination, the gap in speeding is reduced by 45%. The

remaining gap is due exclusively to the fact that minorities are driving faster speeds. In the

second panel of Table 10 we report the same decompositions, where the gap is conditional on

the county of the stop. Removing the sorting of officers no longer has any effect, since that

only leads to differences across counties. Further, notice that over 80% of the within-county

disparity can be explained by discrimination, leaving only about 17% of the disparity to

be explained by differences in speeding across races. In Appendix Table A.9, we perform

these same calculations, where the outcome of interest is the average speed rather than share

discounted.

2.8.3 Policy Counterfactuals

Reported in Table 11, we now use the estimates to conduct a series of policy counterfactuals

to explore how best to curb discrimination in speeding tickets. The results of these counter-

factuals are compared relative to a baseline simulation, reported in the first row, that retains

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the empirical pool of officers and their distribution across counties. As with Table 10, the

calculation of standard errors is discussed in Appendix Section .4.

Firing and Hiring

We first consider the most direct policy for mitigating the disparity in treatment: removing

the most discriminatory officers. We take officers in the 95th percentile and above of dis-

crimination and remove them from the pool of officers. This cutoff removes officers with a

difference in discounting of 16 percentage points or greater between whites and minorities.

For symmetry, we also remove officers who reverse discriminate by that amount (comprising

only 0.4% of officers).

The statewide disparity in treatment barely changes in response to removing these offi-

cers, falling by less than 4%. The lack of effectiveness from this policy partly stems from

the fact that discriminatory officers are on average very lenient. When they are removed,

drivers are left to be stopped by officers who, while less discriminatory, are also less lenient

overall. This fact can be seen by noting that the average discount rate goes down for both

white and minority drivers.

The next counterfactuals we consider are increased hiring of minority and female officers.

Given our earlier finding that minority and female officers exhibit lower levels of discrimina-

tion, we should expect that increasing their presence might lead to lower levels of aggregate

bias. We calculate this counterfactual by re-simulating which officer each driver draws, taken

from within his county, where the probability of drawing a minority or female officer is exoge-

nously changed. Consistent with our intuition, the gap in probability of discount declines,

though very modestly. Increasing the share of female officers from 8% to 18% of the force

leads to a 7.5% reduction in the discount gap. An increase in minority officers from the

empirical share of 35% to 45% reduces the gap by 13.5%.

Demographic policies have been suggested in the past as a possibility for systemically

changing police behavior, particularly toward poor and minority communities. Donohue III

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and Levitt (2001) find that an increase in minority officers leads to an increase in arrests

of white offenders, no effect on non-white offenders, and vice versa for an increase in white

officers. Our results, though only counterfactuals, are consistent with their findings.

Resorting Officers

The final counterfactuals we consider are to reassign officers to specific areas based on their

behavior and the share of minorities in each county. Officers are assigned to troops, which

patrol 6-10 counties. Within the troops, officers regularly vary in which locations they patrol.

It may be potentially feasible for a senior officer to, for example, change the assignment of

officers such that minorities face less biased officers. The bottom two rows of Table 11

present the results of such a policy. Column (1) sorts officers within a troop such that the

least biased officers are in counties with the most minorities. Column (2) sorts officers within

a troop such that the most lenient officers are in counties with the most minorities.

Surprisingly, sorting officers to expose minorities to the least discriminatory has a very

small effect on the treatment gap. The least biased officers are also not very lenient on

average, dampening the impact of their equal discounting across races and reducing the

gap in discounting by only 11%. Much more effective in reducing the gap in treatment is

assigning the most lenient officers to minority counties. This policy reduces the treatment

gap by 86%.

In short, the counterfactual analyses highlight the importance of absolute lenience as

a consideration separate from discrimination. The policy aimed at exposing minorities to

lenience is much more effective than removing overall bias through firing biased officers or

hiring minority and female officers.

2.8.4 Caveats

Our simplified modeling framework and counterfactuals are meant to be suggestive of how

the racial treatment gap might change when various personnel policies are considered. That

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being said, many caveats must be recognized. We are not taking a strong normative stance

on the social welfare function, and the only outcome we consider is the statewide disparity

in discounting. Other outcomes could be relevant to the policy makers’s problem that we do

not consider here.

For example, increasing lenience uniformly may lead to increased speeding, which we

show to be the case in a separate study (Goncalves and Mello, 2017). Changing leniency

standards may also lead officers to give drivers verbal warnings rather than a reduced charge.

A full consideration of the welfare impact of the ensuing policies would likely consider addi-

tional outcomes, such as the speeding response to changes in enforcement (Gehrsitz, 2017;

Goncalves and Mello, 2017; Chalfin and McCrary, 2017) and the tradeoff between the level

and inequality in lenience.

One additional concern is that officers will change their lenience behavior in response to

being reassigned counties. We address this concern in part by allowing officer behavior to

vary by the share of drivers who are minorities, though it is important to note that officers

may respond in other ways.

2.9 Conclusion

The large racial disparities in the criminal justice system have led many to claim discrim-

ination as the root cause. We argue in this paper that identifying discrimination at the

level of the individual criminal justice agent is crucial for understanding the best policy for

mitigating the disparities in outcomes. We study speeding tickets and the choice of officers

to discount drivers to a speed just below an onerous punishment.

By using a bunching estimator approach that allows for officer-by-race measures of le-

nience in tickets, we can explore the entire distribution of both lenience and discrimination

on the part of officers. We find that 83% of the gap in discounting can be attributed to

discrimination. The rest of the gap is due to underlying differences in driving speeds across

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races. Officers are very heterogeneous in their degree of discrimination, with 40% of members

explaining the entirety of the aggregate discrimination.

We explore whether discrimination is predictable by regressing individual officers’ bias on

demographic and personnel characteristics. We find that officers tend to favor their own race,

and female officers are less biased on average. Personnel information, such as failing an entry

exam, receiving civilian complaints, and seeking a promotion, are not strongly informative

about bias.

Using a model of driver speeding and officer decision-making, we confirm that while

minorities drive faster on average, our officer-level estimates of bias are not confounded by

differences in speeding across groups. We find that setting discrimination to zero across

officers fails to remove the majority of the treatment gap, due to the fact that minorities

tend to live in regions where officers are less lenient toward all drivers. Because of this

fact, policies directed at reducing discrimination directly have only a modest effect on the

treatment gap. Policies that instead target officers’ lenience, by reassigning lenient officers

to minority neighborhoods, are much more effective at reducing the aggregate treatment

disparity. These counterfactuals highlight our central argument, that the impacts of various

policy reforms will depend crucially on the distribution across officers in their degrees of

discrimination.

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Table 1: Summary Statistics

(1) (2) (3) (4)White Black Hispanic Total

Driver Female 0.362 0.402 0.305 0.356( 0.481) ( 0.490) ( 0.461) ( 0.479)

Age 37.256 34.228 34.267 36.006(14.850) (12.139) (11.992) (13.838)

Florida License 0.825 0.851 0.896 0.846( 0.380) ( 0.356) ( 0.306) ( 0.361)

Zip Code Income 52.819 37.772 44.375 48.096(51.675) (29.912) (41.444) (46.464)

Citations in Past Year 0.288 0.427 0.408 0.341( 0.721) ( 0.909) ( 0.877) ( 0.799)

MPH Over 15.560 16.658 18.334 16.404( 6.524) ( 7.033) ( 6.988) ( 6.825)

Discount 0.343 0.314 0.204 0.306( 0.475) ( 0.464) ( 0.403) ( 0.461)

Fine Amount 182.060 187.999 197.436 186.636(76.130) (80.366) (80.401) (78.154)

Share 0.584 0.184 0.231 1N 667086 210272 264270 1141628

Notes: Standard deviations in parentheses. Zip code income is miss-ing for 42% of White stops, 40% of Black stops, 37% of Hispanicstops. To account for the fact that a large share of fine amountsare missing or zero in our data, we impute the fine amount with themodal non-zero fine for each county × speed over the limit cell.

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Table 2: Characteristics of Cited Drivers Relative to Other Data Sources

(1) (2) (3) (4) (5)Citations ACS - Any ACS - Drivers Crash - Any Crash - Injury

Female 0.359 0.514 0.474 0.424 0.441

Age 34.979 47.667 41.755 39.692 39.812

White 0.588 0.649 0.632 0.569 0.588

Black 0.177 0.143 0.142 0.193 0.197

Hispanic 0.234 0.208 0.226 0.238 0.216

Notes: ACS data are from 2006-2010 include individuals aged 16 or older and samplingweights are used. To keep the data from the same years, we restrict attention to citationsand crashes for the years 2006-2010.

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Table 3: Officer Lenience Randomization Check

Full Sample GPS Sample

(1) (2) (3) (4) (5)Lenient Lenient Lenient Lenient Lenient

Driver Black -0.000928 0.00211 -0.00215 -0.00464 0.00112(0.0257) (0.00435) (0.00423) (0.00637) (0.00465)

Driver Hispanic -0.120 0.0000806 -0.00116 -0.0181 -0.00291(0.0469) (0.00503) (0.00487) (0.0141) (0.00470)

Driver Female 0.0302 0.00456 0.00317 0.00343 0.00137(0.00736) (0.00268) (0.00228) (0.00249) (0.00309)

Florida License -0.131 0.00143 0.000531 0.00826 -0.00587(0.0402) (0.00349) (0.00386) (0.00824) (0.00438)

Driver Age -0.446 0.0483 -0.0682 0.0584 -0.133(0.273) (0.153) (0.146) (0.105) (0.0988)

1 Prior Ticket -0.0129 0.000478 -0.000193 0.00122 0.00396(0.0101) (0.00125) (0.000975) (0.00311) (0.00341)

2+ Prior Tickets -0.0343 0.000607 0.00181 0.000902 -0.00183(0.0214) (0.00193) (0.00171) (0.00237) (0.00402)

Log Zip Code Income -0.0113 0.00630 -0.00279 -0.000713 0.00184(0.0140) (0.00344) (0.00238) (0.00273) (0.00365)

F-test 0 .359 .144 .564 .324Mean .305 .305 .304 .323 .326Location FE XLocation + Time FE X XGPS FE XObservations 1141628 1141628 1079250 125040 135553

Notes: All regressions includes vehicle type fixed effects and county fixed effects. TheF-test reports the joint hypothesis test that variables Driver Black through Log ZipCode Income are zero. Standard errors are clustered at the county level. ”LocationFE” includes county by highway fixed effects. ”Location + Time FE” includes countyby highway by year by month by day of the week by shift fixed effects. ”GPS FE”includes road segment by year by month by day of the week by shift fixed effects.

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Table 4: Difference-in-Difference Results

Full Sample GPS Sample

(1) (2) (3) (4) (5)Discount Discount Discount Discount Discount

Driver White 0.00126 -0.0205 -0.0119 -0.00766 -0.00650(0.000326) (0.00626) (0.00610) (0.00436) (0.00370)

Officer Lenient 0.396 0.304 0.297 0.243 0.199(0.0355) (0.0377) (0.0453) (0.0192) (0.0321)

Driver White 0.0840 0.0671 0.0620 0.0683 0.0549× Officer Lenient (0.0167) (0.0111) (0.0105) (0.00841) (0.00672)

Mean .305 .305 .305 .32 .32Covariates X X X XLocation FE XLocation + Time FE X XGPS FE XObservations 1141628 1141628 1079250 125040 125040

Notes: Table reports linear probability estimates where the outcome variable iswhether an individual is ticketed for 9 MPH over the limit, as in Equation (2.3).Standard errors are clustered at the county level. ”GPS FE” includes road segmentby year by month by day of the week by shift fixed effects.

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Table 5: Alternative Difference-in-Differences Specifications

(1) (2) (3) (4) (5) (6) (7)Discount Discount Discount Discount Discount Discount Discount

Driver White -0.0114 -0.0123 -0.00872 -0.0212 -0.00286 -0.00411 0.0116(0.00551) (0.00615) (0.00496) (0.00863) (0.00125) (0.00620) (0.00656)

Officer Lenient 0.300 0.279 0.357 0.216 0.318 0.185 0.147(0.0371) (0.0387) (0.0340) (0.0427) (0.0359) (0.0341) (0.0289)

Driver White 0.0694 0.0699 0.0696 0.0763 0.0552 0.0589 0.0563× Officer Lenient (0.0102) (0.0105) (0.0104) (0.0109) (0.00622) (0.0108) (0.0108)

Specification Baseline Split-Sample Lenience Frandsen Re-weighted Lenience-Cov. Radar Gunby Year (2017) Test Interaction Sample

Difference 0 0 .006 -.015 -.011 -.014(.014) (.014) (.014) (.011) (.014) (.014)

Mean .31 .31 .31 .31 .311 .31 .381R2 .344 .337 .379 .317 .339 .346 .328N 1124513 898956 1124513 1124513 1116461 1124513 100705

Notes: All regressions include vehicle type fixed effects and fixed effects for county-year-month. Standard errors areclustered at the county level. The baseline specification is the same regression as Column (3) from Table 4. Column(2) reports a regression where a random sample of 20% of the data is used to estimate whether an officer is lenient, andthe remaining 80% is used in the regression. Column (3) allows officer lenient/non-lenient to vary by year. Column (4)identifies officer lenient/non-lenient using the test from Frandsen (2017) for manipulation of a discrete running vari-able. Column (5) reweights the observations so that the relative weight given to minority drivers is equalized acrosscounty-year-month. Column (6) interacts officer lenient/non-lenient with all observable demographics of drivers. Col-umn (7) restricts attention to a sample of tickets where the officer reports that he/she used a radar gun to identify thedriver’s speed.

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Table 6: Alternative Interpretations

Section 2.6.1 Section 2.6.2

(1) (2) (3) (4) (5)Discount Discount Discount Discount Discount

White -0.0137 -0.0135 0.0203 0.0189(0.00501) (0.00522) (0.00469) (0.00343)

Lenient 0.291 0.289(0.0388) (0.0398)

Driver White 0.0651 0.0657× Officer Lenient (0.00884) (0.00874)

Heckman Correction 0.0172(0.0196)

Individual Demographics X X X X XLocation + Time FE X X X X XOfficer FE X XIndividual FE XMean .31 .31 .288 .284 .278R2 .377 .377 .318 .527 .542N 1124513 1124513 189629 181769 172810

Notes: Column (1) reports the same regression as the baseline regression in Table 4.Column (2) reports the same regression with the addition of the Heckman Correctionterm, as explained in Section 2.6.1 and Appendix Section .2. Columns (3)-(5) corre-spond to Section 2.6.2. Column (3) restricts attention to drivers with two or moretickets and regresses discounting on individual demographics and county-year-monthfixed effects. Column (4) reports the same regression with the addition of officer fixedeffects. Column (5) additionally includes driver-level fixed effects.

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Table 7: Alternative Interpretations, Section 2.6.3

(1) (2) (3) (4) (5)Recidivism Recidivism Court Court Court

P(Discount) 0.00683 0.00887 -0.120 -0.153 -0.110(0.00364) (0.00582) (0.0221) (0.0232) (0.0219)

Driver Minority 0.00465 0.00465 0.0451 0.0451 0.0519(0.00218) (0.00218) (0.00393) (0.00392) (0.00690)

P(Discount)2 -0.00245 0.0403(0.00764) (0.0171)

P(discount) × -0.0235Driver Minority (0.0113)

Location + Time FE X X X X XMean .104 .104 .379 .379 .379R2 .024 .024 .376 .376 .376N 844422 844422 844422 844422 844422

Notes: Columns (1)-(2) use as outcome whether an individual receives another speed-ing ticket in Florida in the following year. Column (1) regresses recidivism on driverdemographics and the propensity score for receiving a discount. The propensity scoreuses driver demographics and an instrument for officer lenience interacted with driverrace, as explained in Appendix Section .3. Column (2) additionally includes a quadraticterm for the propensity score. Columns (3) and (4) are analogous to Columns (1) and(2), where the outcome is whether the driver contests the ticket in court. Column(5) regresses court contestation on propensity score, where propensity score is also in-teracted with driver race. For all regressions, we restrict attention to in-state driverswith a ticket at 9 MPH or over for whom we have a court record of whether the drivercontested.

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Table 8: Predicting Officer Bias

(1) (2) (3)White Lenience Black Bias Hispanic Bias

Black Officer -0.034 -0.017 -0.023(0.020) (0.003) (0.004)

Hispanic Officer -0.042 -0.007 -0.016(0.018) (0.004) (0.004)

Other Race 0.004 0.014 0.001(0.047) (0.013) (0.011)

Female Officer -0.050 -0.009 -0.006(0.025) (0.003) (0.004)

Age (/10) 0.010 0.001 0.002(0.011) (0.002) (0.002)

Experience (/10) 0.154 0.010 0.015(0.047) (0.008) (0.009)

Failed Entrance Exam 0.029 -0.003 0.001(0.024) (0.003) (0.004)

Any College -0.014 -0.001 -0.001(0.016) (0.003) (0.003)

Number of Complaints -0.010 -0.001 -0.000(0.004) (0.000) (0.000)

Use of Force Incidents -0.006 -0.000 0.000(0.006) (0.001) (0.001)

Mean .289 .03 .043Observations 1,402 1,402 1,402R2 .316 .127 .129

Notes: Robust standard errors in parentheses. Outcomes are derived fromthe regression S9

ij = β0 + β1 ·Blacki + β2 ·Hispanici + βj3 · Lenientj + βjB ·Blacki · Lenientj + βjH ·Hispanici · Lenientj +Xijγ + εij . White Lenience

is calculated as β0 + βj3Lenientj . Black Bias and Hispanic Bias are cal-

culated as βjB · Lenientj and βjH · Lenientj , respectively. The sample ofofficers is reduced from 1591 to 1402 because of the restriction that eachofficer stop both black and Hispanic drivers.

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Table 9: Early Discrimination

Early Measure Cutoff Full Sample Percentiles

(1) (2) (3)N Median 95th percentile

2% most discriminatory 28 3.2 23.6

5% most discriminatory 76 6.5 60.2

10% most discriminatory 153 9.2 82.6

Early Sample Full Sample

(1) (2) (3)N Type I Error Type II Error

θj > 1.96 · SE(θj) 398 32.2% 54.6%

θj > 2.33 · SE(θj) 329 31.0% 61.8%

θj > 3 · SE(θj) 236 28.0% 71.4%

Notes: This table presents the relationship between early measuresof discrimination (using first 100 tickets) and discrimination usingall an officer’s data. The first panel reports how different cutoffsin the percentile of early discrimination translate to percentiles inthe full sample. For example, the median percentile of full-samplediscrimination for an officer who is in the top 2% of early discrim-ination is 3.2. The 95th percentile among those from the early 2%cutoff is 23.6. The bottom panel reports how often the early mea-sures mislabels an officer as discriminatory and how often it missesa discriminatory officer. Type-I Error reports the percentage of of-ficers identified as discriminatory in the early sample who are notdiscriminatory at the 5% level in the full sample. Type-II Error re-ports the percentage of officers who are discriminatory in the fullsample at the 5% level who are not identified as discriminatory inthe early sample.

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Table 10: Discounting Gap Decomposition

State-Wide Disparity

(1) (2) (3) (4)White Mean (MPH) Minority Mean Difference Percent

Baseline 0.347 0.266 -0.081 100(0.001) (0.001) (0.001)

No Discrimination 0.347 0.286 -0.061 75.553(0.001) (0.001) (0.001) (0.010)

No Sorting 0.327 0.269 -0.059 72.045(0.001) (0.001) (0.001) (0.014)

Neither 0.327 0.291 -0.037 45.016(0.001) (0.001) (0.001) (0.012)

County-Level Disparity

(1) (2) (3) (4)White Mean (MPH) Minority Mean Difference Percent

Baseline 0.347 0.321 -0.027 100(0.001) (0.001) (0.001)

No Discrimination 0.347 0.343 -0.005 17.903(0.001) (0.001) (0.001) (0.033)

No Sorting 0.327 0.300 -0.027 100.888(0.001) (0.001) (0.001) (0.043)

Neither 0.327 0.322 -0.005 17.656(0.001) (0.001) (0.001) (0.035)

Notes: Table presents how the racial gap in discounting and changes without biasand sorting of officers across counties. The probability gap is the probability of beingdiscounted if you are at the speed right above the jump in fine. Both gaps are theminority drivers’ outcome minus white drivers’ outcome. No bias is calculated by as-signing each officer’s preferences toward minorities to be the same as his preference towhites. No sorting is calculated by simulating a new draw of officers for each driver,where the draw is done at the state level. The county-level disparities reweight theminority observations so that the “share” minority is identical across counties.

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Table 11: Model Counterfactuals

Hiring & Firing

(1) (2) (3) (4)White Mean Minority Mean Difference Percent

Baseline 0.3473 0.2661 -0.0813 100(0.0007) (0.0007) (0.0010)

Fire 5% Most Biased Officers 0.3440 0.2655 -0.0785 96.5733(0.0013) (0.0012) (0.0012) (0.0154)

Increase Female Share 10pp 0.3423 0.2671 -0.0752 92.4890(Base of 8%) (0.0007) (0.0008) (0.0011) (0.0131)

Increase Minority Share 10pp 0.3057 0.2354 -0.0703 86.5128(Base of 35%) (0.0016) (0.0018) (0.0024) (0.0293)

Resorting Officers

(1) (2) (3) (4)White Mean Minority Mean Difference Percent

Exposing Minorities 0.3327 0.2602 -0.0725 89.1587To Least Biased (0.0022) (0.0018) (0.0017) (0.0212)

Exposing Minorities 0.2989 0.2879 -0.0110 13.5403To Most Lenient (0.0008) (0.0010) (0.0011) (0.0129)

Notes: Results are reporting the probability of being ticketed 9MPH over, where the av-erages are statewide. In the bottom panel of counterfactuals, officers are resorted withintroops.

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Figure 2.1: Distribution of Charged Speeds and Fine Schedule

0

50

100

150

200

250

Fine

Am

ount

0

.1

.2

.3

Frac

tion

of T

icket

s

0 10 20 30 40MPH Over

Notes: Connected line shows histogram of tickets. Dashed line plots fine schedule for BrowardCounty. 30 MPH over is felony speeding and carries a fine to be determined following a courtappearance.

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Figure 2.2: Charged Speed Distributions by Driver Race

0

.1

.2

.3

.4

Den

sity

0 10 20 30 40 MPH Over

White Drivers

Minority Drivers

Notes: Connected line shows histogram of ticketed speeds, separately by driver race. 34.3% oftickets to white drivers are given at 9 MPH over compared to 25.2% of tickets for minority drivers.

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Figure 2.3: Evidence of Officer Lenience

0

.1

.2

.3

.4

Frac

tion

of O

ffice

rs

0 .2 .4 .6 .8 1Share of Tickets at 9 MPH

Panel A: Lenience Distribution

0

.05

.1

.15

Frac

tion

of O

ffice

rs

-1 -.5 0 .5 1Share of Tickets at 9 MPH

Panel B: Residualized Lenience Distribution

-1

-.5

0

.5

1

Leni

ence

in S

econ

d Ye

ar

-1 -.5 0 .5 1Lenience in First Year

Panel C: Correlation Across Time

-1

-.5

0

.5

1

Leni

ence

in S

econ

d Co

unty

-1 -.5 0 .5 1Lenience in First County

Panel D: Correlation Across Space

Notes: Panel A plots the across-officer distribution of lenience, calculated as the share of ticketsgiven for 9 MPH over the limit. Panel B plots the across-officer distribution of residualized lenience.Panel C plots officers’ residualized lenience in the years with the most and second most citations.Panel D plots the residualized lenience in the county with the most and second most citations.Estimates residualized by conditioning on county fixed effects, speed zone fixed effects, year andmonth fixed effects, and day of week fixed effects.

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Figure 2.4: Difference-in-Difference Raw Data Plot

0

.1

.2

.3

.4

.5

Shar

e

0 10 20 30 40MPH Over

White Drivers

0

.1

.2

.3

.4

.5

Shar

e

0 10 20 30 40MPH Over

Non-Lenient Officers

Lenient Officers

Minority DriversLenient v. Non-Lenient Officers

Mean Diff: 1.48

0

.05

.1

.15

Den

sity

0 10 20 30 40 MPH Over

No Controls

Mean Diff: .39

0

.05

.1

.15 D

ensi

ty

0 10 20 30 40 MPH Over

White Histogram

Minority Histogram

Loc.-Time FE + Ind. Cov.Non-Lenient Officers

Notes: The top left figure plots the histograms of speeds for white drivers, separately for stopsmade by lenient and non-lenient officers. The top right figure plots the same histograms of speedsfor minority drivers, separately by officer lenience. The bottom left figure plots the histograms forspeeds ticketed by non-lenient officers, separately for white and minority drivers. The bottom rightfigure plots the histograms of speeds ticketed by non-lenient officers separately by race, where wehave controlled for other demographics and county-year-month fixed effects. Specifically, for eachspeed, we regress whether an individual is ticketed at that speed, controlling for minority driverand all other demographics and county-year-month fixed effects. The white histogram is the sameas the bottom left figure, and the minority histogram is the white histogram with the addition ofminority regression coefficient for each speed.

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Figure 2.5: Officer Lenience and Stop Characteristics

Notes: Figure plots the relationship between officer lenience and various characteristics of theofficers’ stops, where both officer’s lenience and the stop characteristic have been residualized toremove location-time fixed effects. By officer lenience here we mean the indicator for whether anofficer has more than 2% of tickets charge at 9mph over. The top left panel plots officer lenienceagainst his share of tickets given to minority drivers, the top right the share of tickets with racemissing, and the bottom left the share of tickets that are for speeding. For the bottom right figure,we calculate the number of daily tickets for each officer-by-year, and similarly calculate whether anofficer is lenient in each year. We residualize both with county-by-year fixed effects.

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Figure 2.6: Difference-in-Difference Results

-.05

0

.05

.1

.15

Whi

teXL

enie

nt C

oeffi

cien

t

5 10 15 20 25 30 MPH Over

No Controls

Ind. Covariates, Location + Time FE

Notes: Figure plots the difference-in-difference regression results for each speed. The y-axis plotsthe interaction between driver being white and the officer being lenient. Standard errors are at the5% level.

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Figure 2.7: Difference-in-Differences Officer-Level Results

SD = .068

Avg. SE = .014

0

5

10

15

Den

sity

-.3 -.2 -.1 0 .1 .2 .3 Minority Disparate Treatment

Notes: Figure plots each officer’s βj3 from the regression

S9ij = β0 + β1 ·Whitei + βj2 · Lenientj + βj3 ·Whitei · Lenientj +Xijγ + εij .

Officers who are non-lenient are assigned βj3 = 0. SD reports the standard deviation across βj3, and

Avg SE. reports the average standard error for each individual βj3.

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Figure 2.8: Officer-Level Results

0

10

20

30

Dens

ity

-.4 -.2 0 .2 .4Disparate Bunching

Black Officers

Hispanic Officers

White Officers

All Officers

0

2

4

6

8

-.4 -.2 0 .2 .4Disparate Bunching

Lenient Officers

Notes: Left figure plots the discrimination coefficient βj3 for all officers. Right figure plots thediscrimination coefficient for all lenient officers.

155

Appendix

156

.1 Data Appendix

.1.1 Citations Data

Our data cover the universe of citations written by the Florida Highway Patrol for the years

2005-2015, comprising 2,614,119 observations. We make several restrictions that reduce the

number of observations:

1. speeding is the primary citation (2,124,692 observations)

2. no crash is involved (2,123,311 observations, 99.9% of previous sample)

3. speed is between 0 and 40 over the limit (2,109,258, 99.3%)

4. posted speed limit is between 25MPH and 75MPH (2,107,933, 99.9%)

5. citations not from an airplane (2,103,923, 99.8%)

6. race/ethnicity is not missing (1,759,257, 83.6%)

7. race/ethnicity is white, black or Hispanic (1,671,089, 95.0%)

8. not missing driver’s license state, gender, or age (1,667,558, 99.8%)

9. officer is identifiable (1,215,588, 72.9%)

10. officer has at least 100 tickets, and at least 20 for minorities and 20 for whites (1,174,284,

96.6%)

11. driver has no more than 20 citations in Florida for period 2005-2015 (1,141,628, 97.2%)

.1.2 Linking Offenses to Personnel Information

Officers enter their information by hand onto each speeding ticket, leading to inconsistencies

in how their names are recorded. Some names are misspelled, and sometimes officers place

157

only their last name and first initial. The Florida Department of Law Enforcement (FDLE)

maintains a record of each certified officer in the state, along with demographic information.

We link these using each officer’s last name and first three letters of first name (if available

on ticket) using a fuzzy match algorithm in Stata (reclink). We restrict attention to officers

who are unique up to last name and first three letters of first name in the FDLE data.

Among tickets where only the first initial is listed, we keep matches where the last name and

first initial of an officer are unique in the FDLE data. Of the 2,124,692 speeding tickets in

our data, 504,644 match successfully to the FDLE data.

.1.3 Hours and Shifts of Tickets

Officers manually enter time of day, and there are several inconsistencies in how these are

recorded. Most officers use either a 12-hour time and clarify AM versus PM, and others use

24-hour military time. Some officers regularly use 12 hour time and do not record AM versus

PM. We set these times to be missing.

The FHP has three shifts, 6am to 2pm, 2pm to 10pm, and 10pm to 6am. We record these

directly from the hour of the ticket if it is properly recorded above. If there is no correct

hour of day, we take a two-week moving average of the officer’s modal shift for his citations

and impute the shift. For the remaining tickets we leave shift as missing. Of the 1.6 million

initial speeding citations, 692,416 have shift missing, and 413,560 remain missing after the

imputation procedure.

.2 Accounting for Stopping Margin Selection

As discussed in Section 2.6, one concern we face is that we do not observe interactions

that do not result in a ticket. Therefore, officer differences in lenience and discrimination

on whether to give a ticket may bias our estimates of discrimination on whether to give a

discount. Here we write down a simple selection model to discuss the potential bias from

158

selection into the data and present a procedure to correct our estimates for officer-by-race

differences in ticketing.

Consider a model of ticketing where there is a first margin of whether or not a driver is

ticketed at all:

D∗ij = θWj + θMj ·Mi + εij

Zij = αWj + αMj ·Mi + ηij

D∗ij is a latent variable for whether the driver receives a discount, and Zij is a latent variable

for whether the officer tickets the driver at all, where we assume ηit ∼ N(0, 1). We observe

Dij if Zij crosses zero and the officer chooses to ticket the driver:

Dij =

1I(D∗ij ≥ 0) if Zij ≥ 0

missing otherwise

Therefore, the comparison we make to determine the degree of discrimination is based on

the difference in discounting among observed drivers27:

θMj = E[D∗ij|Mi = 1, Zij > 0]− E[D∗ij|Mi = 0, Zij > 0]

= θMj + E[εij|ηij > −αWj − αMj ]− E[εij|ηij > −αMj ]

If there’s a difference in treatment in the first margin (αMj 6= 0) and corr(εij, ηij) 6= 0, then

our estimate of θMj will be inconsistent. In particular, if αMj > 0 (discrimination in ticketing)

and corr(εij, ηij) < 0 (drivers more likely to be ticketed are less likely to be discounted), then

27We abstract here from the lenient v. non-lenient approach from the main text as well asincluding observable characteristics. However, when implementing the correction procedure wereturn to both.

159

the error term above will be positive, suggesting that our measure of discrimination will be

biased toward zero.

To deal with the issue of potential correlation between ticketing on the first margin and

discounting, we will use an approach similar to the Heckman (1979) correction. Imagine

that all officers working in the same county and year face the same number of drivers of a

certain race on a given day of work, Nr. Officers choose whether or not to write a ticket for

the driver, Zij, and thus the daily rate of tickets for that officer for that race-county-year is

Nrj = Nr · P (Zij = 1).

Under the presumption that all officers in the same county-year face the same quantity of

drivers who could potentially be ticketed for speeding, we can compare officers to calculate

their propensity to give a ticket. Within each county-year-race, we calculate the average

daily number of tickets given by each officer. To account for large right-tail values, we allow

the 95th percentile across officers of Nrj for each county-year-race to be our value for Nr.

Then for each officer-race-county-year, P (Zij = 1) =Nrj

Nr, which we call Pij. Using this

value, we can identify the expectation for the error term ηij in the ticketing equation for

each driver:

Pij = Pr(αWj + αMj ·Mi + ηij ≥ 0)

= Φ(αWj + αMj ·Mi)

=⇒ E(ηij|Zij = 1) =φ(αWj + αMj ·Mi)

Φ(αWj + αMj ·Mi)

=φ(Φ−1(Pij))

Pij

Note that in the uncorrected approach, the conditional expectation of the error term is

potentially nonzero because of a correlation with the ticketing error term:

E(εij|ηij > −αWj − αMj ·Mi) = ρ · E(η|ηij > −αWj − αMj ·Mi)

= ρE(ηij|Zij = 1)

160

Therefore, we can address the potential selection into the data using our officer-county-

year-race-specific expected value for the ticketing error term, which we call the Heckman

Correction term, and re-run the main regression with this addition. The results of this

procedure are presented in Table 6. Column (1) presents again the baseline regression, and

Column (2) presents the same regression with the additional Heckman Correction term. The

addition of the correction does not change the value of the interaction term on Driver White

and Officer Lenient or any other coefficients, suggesting that our result is not due to any

issues with sample selection. This finding should not be surprising, as we found in the bottom

right panel of Figure 2.5 that officer lenience is uncorrelated with ticketing frequency.

.3 Testing for Statistical Discrimination

Our paper argues that racial disparities in officer lenience reflect bias. However, a compelling

alternative explanation is that officers are using race as a signal for an unobserved driver

type. Our baseline regressions show that officers differentiate between white and minority

drivers after controlling for previous tickets, suggesting that the observed disparity does not

reflect statistical discrimination on the level of criminality. However, officers may be sorting

individuals on how they respond to a discount. For example, officers may be trying to

identify drivers who will react to a harsh ticket by speeding less in the future. Alternatively,

they may choose to discount a particular driver because they are likely to respond by not

contesting the ticket. To formalize these stories, imagine that drivers who are stopped for

speeding have some outcome after the ticket, Yi, that depends on whether a discount Di is

given:

Yi = Xiβ + αiDi + εi

Whether or not they speed, or contest the ticket, is potentially a function of the treatment

given to them by the current stopping officer. As throughout the paper, the officer chooses

whether to give a discount, and he does so on the basis of demographics, but also potentially

161

other unobservables:

Di = 1I(Zijθ − vi ≥ 0

)where Zij is written to encapsulate both the individual covariates Xi and an instrument

for discounting based on the officer identity, which we discuss below. The story we are inter-

ested in testing is whether officers choose who to discount on the basis of how Yi responds.

In other words, do we have αi |= Di|Xi or not? Heckman et al. (2010) provide a number

of tests for whether there is such a correlation, from which we borrow directly below. In

particular, they show that a lack of correlation between discounting and treatment effect

implies a linear relationship between the outcome and propensity score for treatment. To

see this, we first reformulate the discount equation:

1I(D = 1) = 1I(v ≤ Zijθ) = 1I(Fv(v) ≤ Fv(Zijθ)) = 1I(Ud ≤ P (Zij))

where Ud is a uniform random variable and P (zij) = Pr(D = 1|Zij = zij) is the propensity

score. The marginal treatment effect is defined as the treatment effect for an individual at

a given propensity to be treated (Bjorklund and Moffitt, 1987):

MTE(x, ud) = E(αi|X = x, Ud = ud)

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The conditional expectation of Yi as a function of Xi and Zi can then be written as a

function of the marginal treatment effects:

E(Y |Z = z) = Xiβ + E(αiDi|z)

= Xiβ + E(αiDi|P (z))

= Xiβ + E(αi|D = 1, P (z)) · p

= Xiβ +

∫ p

0

E(αi|Ud = ud)dud

Under no correlation between αi and Di, then E(αi|Ud = ud) = E(αi). Therefore, the

conditional expectation of Yi should be linear in P (z):

∂E(Y |Z = z)

∂P (z)= E(αi|Ud = P (z))

= E(αi) under αi |= Di|Xi

Therefore, a test for the linearity of Yi in P (Z) tells us whether officers are sorting individuals

on the basis of their treatment effect of Di on Yi. Under linearity, the marginal treatment ef-

fects of individuals with different propensities to be treated (in our case, stopped by different

officers) will be the same.

The instrument Zij we use for whether an individual receives a discount is based on the

identify of the officer and is a leave-out measure of the officer’s propensity to give a discount:

Zij =1

Nj − 1

∑k∈J\i

Dk

where Nj is the number of individuals stopped by officer j. This average-lenience-of-treater

instrumenting design has been used in various settings to study the effect of criminal sentence

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length (Kling, 2006; Mueller-Smith, 2014), bankruptcy protection (Dobbie and Song, 2015),

foster care (Doyle, 2007; Doyle Jr, 2008), and juvenile incarceration (Aizer and Doyle Jr,

2015).

We then calculate an individual’s propensity to receive a discount based on their stopping

officer and demographic characteristics. Because an officer’s lenience can vary with the race

of the driver, we interact the instrument with driver race:

P (Z,X) = Xiγ + θ0Zij + θMDriverMinorityiZij

We then run regressions of Yi on specifications that are linear and quadratic in P (z, x), where

the outcomes we consider are whether a driver receives another ticket in the year following

the FHP stop28 and whether the driver contests the ticket.

The results of this analysis are presented in Table 7. We restrict attention to in-state

drivers with a ticket at 9 MPH or over for whom we have a court record of whether the driver

contested. These restrictions leave us with 844,422 tickets. The first two columns treat an

individual’s recidivism as the outcome. In Column (1) we see that an increase in the proba-

bility of receiving a discount increases an individual’s likelihood of recidivating.29 However,

the quadratic in the second column is insignificant. Though not shown, a specification that

includes a cubic in the propensity score also has insignificant higher terms.

Columns (3) through (5) use as an outcome whether the driver contests the ticket in

court. As with recidivism, we find an effect of receiving a discount: drivers stopped by

officers who are more likely to give discounts are less likely to contest their ticket. However,

when we add a quadratic term in Column (4), we find a non-linear relationship, with the

28The recidivism of the driver is calculated as an indicator for whether they receive any trafficticket in the state of Florida in the following year. We link drivers by driver’s license number. Moreinformation is available in Goncalves and Mello (2017).

29Though we do not report it here, the first-stage coefficient on the instrument is close to 1 andslightly smaller for minority drivers. The first-stage relationship is essentially linear, indicatingthat any non-linearity in the reduced form regressions presented here are not due to differences inthe strength of the instrument at different levels.

164

quadratic having a significant positive coefficient. Drivers stopped by very harsh officers

have a larger marginal response to discounting than drivers stopped by less harsh officers.

The intuition for this result is the following: imagine an officer who is very lenient toward

his drivers. If he is going to be harsh to one driver, he will pick someone who is not very

responsive to a harsh ticket and will not contest. We will thus see that officer have a small

effect of discounting on contesting. In contrast, imagine an officer who is harsh toward

nearly all drivers. If he is going to give a break to someone, that discount should give him a

large return in reduced court time. We should thus expect a large contest response among

that officer’s drivers. Our findings are thus consistent with the story that officers do try to

identify driver’s propensity to not contest their ticket.

While we therefore do find evidence of statistical discrimination on court contest response,

our primary objective is to determine whether any form of statistical discrimination can

explain the disparity we observe between whites and minorities. To do so, we implement a

test based on Arnold et al. (2018). They implement the logic of the Becker (1957) hit-rate

test in the random-judge design and show that, under no discrimination, the impact of a

treatment should be the same at the margin across racial groups. To conduct this test, we

interact the propensity score with the race of driver in Column (5). Doing so, we find that

the marginal effect of a discount on contesting is statistically larger for minorities than for

white drivers, indicating that the discrimination we observe cannot be explained by sorting

on contest response.

.4 Notes on Model Estimation

While the setup of the model is simple, the non-parametric identification of the distribution

of officer bias and the distribution county-by-race speeds leads to a significant number of pa-

rameters to be identified. We estimate the model through maximum likelihood, programmed

in Matlab. We provide the program with the gradient vector and utilize ”fminunc” with a

quasi-newton search algorithm option. The variance matrix of the parameters is calculated

165

as the inverse of the information matrix, which we calculate as the variance of the score

functions.

One issue to note is that the log likelihood function is essentially flat for certain regions

of the parameter space for some officer preference parameter values. This flatness occurs

because some officers have no (all) drivers at the bunch point, consistent with an infinitely

negative (positive) ”t.” The optimization algorithm reaches values that are large in mag-

nitude. However, because the score function is essentially flat at these large values, the

parameters’s standard errors are extremely large.

To deal with this issue, we treat these parameters (specifically, the t estimates for officers

with P (Discount | X = 10) < .02 or P (Discount | X = 10) > .98) as known and set their

variances to be zero.

.4.1 Model Estimates Discussion

Table A.8 presents estimates of the model parameters. Columns in the top panel present

the mean and variance of each class of parameters, broken down by race, and the final

column compares differences across racial groups in the mean parameter estimates. The

slope parameter is positive and significant at 0.0395. Consistent with our intuition, officers

face an upward-sloping cost with respect to speed, meaning that tickets are less likely to

be discounted the higher the observed speed. The parameter t represents an officer’s mean

valuation of a racial group. We find both significant heterogeneity and a significant disparity

across whites and minorities in how officers value discounting drivers, with officers’ mean

valuation for whites being 0.0275 higher than for minorities.

While the values of t are by themselves hard to interpret, the racial differences in treat-

ment are more easily understood in terms of the probability of discount (i.e., fine reduction).

Pr(Discount|E(Z), j,X = 10) represents the likelihood of receiving a reduced ticket if the

driver is at the speed right above the bunching speed, where, besides race, the driver has the

average demographics Z. Consistent with the reduced-form evidence, the average officer is

166

substantially lenient, with a large variance across officers. Officers are 3.3 percentage points

less likely to discount minorities than whites, off a baseline of 35.7% likelihood of discount.

Figure A.2 further shows this disparity, highlighting how racial bias results in a decreased

mass of officers with very high lenience and an increase in mass of officers with very low

lenience. Figure A.3 shows how the disparity only arises among officers with some degree of

lenience.

The λ estimates tell us how races-by-counties differ in their underlying speeds prior to

officers’ choice of lenience. As we found in Section 2.5 when restricting our attention to non-

lenient officers, model estimates suggest that minorities on average drive significantly faster

than whites, on the order of 0.5 to 0.7 MPH. Figure A.4 presents this gap by county, showing

that minority speeds stochastically dominate white speeds. These results are in line with

previous studies of highway patrol ticketing, which argue that much of the gap in ticketing

between whites and minorities can be explained by higher speeds by minorities (Smith et

al., 2004; Lange et al., 2005). However, these previous studies and the news coverage that

followed implicitly argued that the racial difference in speeds rules out the presence of bias

by officers. Our study highlights how this thinking is incorrect by showing that disparities

in driving and racial bias coexist in our setting. As shown in Figure A.5, the distribution of

bias across officers looks very similar to the distribution found in our reduced form estimates

from Section 2.5.

The bottom panel of Table A.8 presents the demographic-specific speed and preference

parameters. Female drivers, older drivers, and those with fewer tickets all drive slower

speeds on average and are more likely to be discounted. The effect of county minority share

indicates that officers are less likely to discount everybody in a more minority neighborhood,

regardless of the race of the stopped individual.

We report in Figure A.6 various estimates of model fit to the data. For each panel, we

construct the model statistics by simulating 100 times and averaging across iterations. The

top left panel compares the aggregate histograms of speeds. The top right panel compares

167

the average ticketed speeds by race-county. The bottom left panel compares the share of

tickets at 9 MPH over by officer-race. The bottom right panel compares the racial disparity

in bunching at 9 MPH over by officer. In all cases, the model estimates match very closely

with the true data.

.4.2 Counterfactuals

Here we provide information on how the counterfactuals and their standard errors are cal-

culated. There are several sources of uncertainty in the estimation that lead to standard

errors on our calculations: 1) uncertainty of our parameter estimates, 2) randomness of the

matching between officers and drivers, 3) randomness in the speed draws for the drivers, and

4) randomness in the officers’ decisions to discount. We therefore calculate standard errors

through a sampling procedure as follows:

• Draw a sample of parameters θ(1) ∼ N(θ, Σ), where θ and Σ are our parameter point

estimates and variance matrix, respectively.

• Within each county, randomly match officers and drivers. In the baseline estimation,

the probability of encountering an officer is the share of tickets in the data which that

officer gave. All the counterfactuals consist of changing the distribution of officers

being matched.

• Drivers draw a speed from their Poisson distribution, s ∼ Pλi .

• We draw a set of εij ∼ N(0, 1) for all stops, and an officer discounts her driver if

trj + αZ(2) + εij > b · s.

• Iterate 500 times.

Then, our estimates and standard errors for the racial gaps in each counterfactual are

the average and standard deviation across all iterations.

Here we describe explicitly how each counterfactual is performed:

168

• Decomposition with no sorting: Rather than matching drivers and officers randomly

within a county, they are matched randomly across the entire state.

• Decomposition with no bias: Identical to the baseline, officers and drivers are matched

randomly within a county. Officers preferences for minority drivers is set to be their

white preference, twj.

• Firing 5% most discriminatory officers: Calculate P biasj ≡ Prj(Discount | X =

10, E(Z), r = w) − Prj(Discount | X = 10, E(Z), r = m), and find the 5th per-

centile for the entire state and ”remove” all officers below this threshold. We also

remove officers that cross the same threshold of discrimination against white drivers.

The probability of an individual encountering a specific officer is that officer’s share of

tickets among the remaining officers.

• Hiring more minority officers: We increase the share from 35% to 45%. We do so

by proportionately increasing the number of minority officers in each county. e.g. a

county that previously was 10% minority officers is now 16% minority. The distribution

of officer tastes trj is the same as the existing distribution within officer race. The

procedure is identical for increasing the share of female officers.

• Re-assigning officers based on discrimination: Within a troop, officers are ranked based

on their discrimination. In the county of that troop with the most minorities, the

lowest-ranked officers are assigned. The second-most minority county receives the next-

least discriminatory officers, and so on. Officers write as many tickets as in the true

data, so some officers may write tickets in two counties that are adjacent in their share

minority. The procedure is identical when assigning officers based on their lenience,

where the most lenient officers are assigned to the most minority neighborhoods.

169

Table A.1: Racial Disparity in Speeding

Full Sample GPS Sample

(1) (2) (3) (4) (5) (6) (7)MPH Over MPH Over MPH Over MPH Over MPH Over MPH Over MPH Over

Driver Black 1.073 0.809 0.728 0.637 0.622 0.890 0.782(0.268) (0.0877) (0.0844) (0.0832) (0.0759) (0.0703) (0.0751)

Driver Hispanic 2.765 0.875 0.793 0.648 0.652 1.027 0.764(0.526) (0.128) (0.134) (0.137) (0.135) (0.214) (0.134)

Driver Female -0.619 -0.563 -0.436 -0.379(0.0453) (0.0403) (0.0600) (0.0572)

FL License -0.183 -0.353 -0.685 -0.534(0.0810) (0.0808) (0.152) (0.127)

Driver Age -0.0443 -0.0421 -0.0378 -0.0338(0.00135) (0.00130) (0.00164) (0.00199)

1 Prior Ticket 0.281 0.268 0.285(0.0243) (0.0507) (0.0682)

2+ Prior Tickets 0.799 0.682 0.740(0.0379) (0.0760) (0.0637)

Log Zip Code Income 0.123 0.0843 0.0313(0.0501) (0.0443) (0.0478)

Mean 16.554 16.554 16.587 16.587 16.587 16.027 16.027Vehicle FE X X XLocation FE X XLocation + Time FE X X X XGPS FE XObservations 1124513 1124513 1063227 1063227 1063227 123516 123516

Notes: Table reports regressions where the outcome is the speed for which the individual is ticketed. ”Location FE”are fixed effects at the county by posted speed limit. ”Location + Time FE” are fixed effects at the county by postedspeed limit by year by month by day of week by hour fixed effects. ”GPS FE” are fixed effects at the road segmentby posted speed limit by year by month by day of week by hour fixed effects. GPS sample are tickets with the GPSlocation available. Standard errors are clustered at the county level.

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Table A.2: Racial Disparity in Discounting

Full Sample GPS Sample

(1) (2) (3) (4) (5) (6) (7)Discount Discount Discount Discount Discount Discount Discount

Driver Black -0.0316 -0.0270 -0.0241 -0.0218 -0.0229 -0.0378 -0.0310(0.0179) (0.00454) (0.00480) (0.00488) (0.00456) (0.00665) (0.00616)

Driver Hispanic -0.143 -0.0401 -0.0392 -0.0345 -0.0357 -0.0559 -0.0378(0.0331) (0.00883) (0.00939) (0.00892) (0.00883) (0.0120) (0.00859)

Driver Female 0.0288 0.0269 0.0198 0.0179(0.00434) (0.00407) (0.00402) (0.00395)

FL License 0.00806 0.0143 0.0308 0.0191(0.00404) (0.00438) (0.00805) (0.00883)

Driver Age 0.00136 0.00128 0.00122 0.000999(0.000244) (0.000234) (0.000203) (0.000206)

1 Prior Ticket -0.0121 -0.0102 -0.0129(0.00257) (0.00376) (0.00450)

2+ Prior Tickets -0.0294 -0.0219 -0.0274(0.00581) (0.00638) (0.00719)

Log Zip Code Income -0.00950 -0.00381 -0.00112(0.00217) (0.00336) (0.00445)

Mean .31 .31 .309 .309 .309 .324 .324Vehicle FE X X XLocation FE X XLocation + Time FE X X X XGPS FE XObservations 1124513 1124513 1063227 1063227 1063227 123516 123516

Notes: Table reports regressions where the outcome is an indicator for the individual being ticketed at 9MPHover the limit. ”Location FE” are fixed effects at the county by posted speed limit. ”Location + Time FE” arefixed effects at the county by posted speed limit by year by month by day of week by hour fixed effects. ”GPSFE” are fixed effects at the road segment by year by month by day of week by hour fixed effects. GPS sampleare tickets with the GPS location available. Standard errors are clustered at the county level.

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Table A.3: Racial Disparity in Speeding, Non-lenient Officers

Full Sample GPS Sample

(1) (2) (3) (4) (5) (6) (7)MPH Over MPH Over MPH Over MPH Over MPH Over MPH Over MPH Over

Driver Black 1.230 0.702 0.637 0.516 0.487 0.730 0.584(0.184) (0.160) (0.148) (0.135) (0.129) (0.148) (0.203)

Driver Hispanic 1.578 0.485 0.418 0.264 0.259 0.423 0.378(0.277) (0.0677) (0.0614) (0.0668) (0.0741) (0.150) (0.171)

Driver Female -0.523 -0.466 -0.423 -0.323(0.0770) (0.0705) (0.112) (0.0999)

FL License -0.211 -0.378 -0.575 -0.530(0.0839) (0.0855) (0.165) (0.199)

Driver Age -0.0454 -0.0429 -0.0330 -0.0329(0.00264) (0.00244) (0.00254) (0.00257)

1 Prior Ticket 0.267 0.256 0.195(0.0309) (0.0790) (0.106)

2+ Prior Tickets 0.708 0.669 0.626(0.0444) (0.116) (0.138)

Log Zip Code Income 0.0240 0.0576 0.0440(0.0497) (0.0759) (0.0725)

Mean 20.378 20.378 20.403 20.403 20.403 20.024 20.024Vehicle FE X X XLocation FE X XLocation + Time FE X X X XGPS FE XObservations 366146 366146 348275 348275 348275 30285 30285

Notes: Table reports regressions where the outcome is the speed for which the individual is ticketed, restricting atten-tion only to non-lenient officers. ”Location FE” are fixed effects at the county by posted speed limit. ”Location + TimeFE” are fixed effects at the county by posted speed limit by year by month by day of week by hour fixed effects. ”GPSFE” are fixed effects at the road segment by year by month by day of week by hour fixed effects. Standard errors areclustered at the county level.

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Table A.4: Officer Lenience Randomization Check

Full Sample GPS Sample

(1) (2) (3) (4) (5)Lenience Lenience Lenience Lenience Lenience

Driver Black 0.000635 0.00166 -0.000493 -0.00704 0.000622(0.0166) (0.00292) (0.00337) (0.00549) (0.00550)

Driver Hispanic -0.0900 -0.00594 -0.00666 -0.0224 -0.00255(0.0287) (0.00497) (0.00462) (0.0130) (0.00338)

Driver Female 0.0188 0.00423 0.00251 0.00148 0.00163(0.00428) (0.00217) (0.00181) (0.00132) (0.00201)

Florida License -0.0774 0.000511 0.000401 0.00769 -0.00196(0.0252) (0.00346) (0.00317) (0.00806) (0.00422)

Driver Age -0.214 0.216 0.0744 0.134 0.0371(0.162) (0.129) (0.119) (0.103) (0.0741)

1 Prior Ticket -0.0113 -0.000750 -0.000483 0.00244 0.0000311(0.00645) (0.000896) (0.000948) (0.00144) (0.00223)

2+ Prior Tickets -0.0235 -0.00132 -0.0000563 0.00443 0.00212(0.0125) (0.00145) (0.00149) (0.00225) (0.00371)

Log Zip Code Income -0.00361 0.00276 -0.00415 -0.000165 -0.000452(0.00855) (0.00295) (0.00195) (0.00312) (0.00211)

F-test 0 .616 .039 .419 .946Mean .31 .31 .309 .326 .33Location FE XLocation + Time FE X XGPS FE XObservations 1139734 1139734 1077412 124916 135427

Notes: All regressions includes vehicle type fixed effects and county fixed effects. TheF-test reports the joint hypothesis test that variables Driver Black through Log ZipCode Income are zero. Standard errors are clustered at the county level. ”LocationFE” includes county by highway fixed effects. ”Location + Time FE” includes countyby highway by year by month by day of the week by shift fixed effects. ”GPS FE”includes road segment by year by month by day of the week by shift fixed effects.

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Table A.5: Difference-in-Differences Officer-Level Results

Discrimination Percentile

(1) (2) (3) (4) (5) (6)10 % 25% 50% 75% 90% N

All Officers -0.0113 0.0000 0.0053 0.0681 0.1275 1591

White Officers -0.0076 0.0000 0.0231 0.0835 0.1386 1591

Black Officers -0.0339 0.0000 0.0000 0.0228 0.0637 1591

Hispanic Officers -0.0112 0.0000 0.0000 0.0404 0.1199 1591

Notes: Table reports percentiles of the distribution of officer-level discrimi-nation, as calculated from Equation (2.4).

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Table A.6: Officer Discrimination Randomization Check

Full Sample GPS Sample

(1) (2) (3) (4) (5)Discrimination Disc Disc Disc Disc

Driver Black 0.000888 0.00152 0.000661 0.00233 0.00000407(0.00190) (0.000604) (0.000553) (0.00182) (0.000880)

Driver Hispanic -0.00617 0.000164 -0.000751 -0.000986 -0.000444(0.00319) (0.000849) (0.000668) (0.00258) (0.000699)

Driver Female 0.00124 -0.000176 -0.000154 0.000703 0.000367(0.000615) (0.000181) (0.000202) (0.000523) (0.000431)

Florida License -0.0111 -0.000238 -0.000563 -0.0000257 0.0000737(0.00304) (0.000715) (0.000657) (0.00227) (0.000606)

Driver Age -0.0139 -0.00259 -0.000300 -0.0122 -0.00549(0.0274) (0.0169) (0.0156) (0.0253) (0.0153)

1 Prior Ticket -0.000769 0.0000154 0.0000520 0.000813 0.000519(0.000693) (0.000174) (0.000178) (0.000773) (0.000515)

2+ Prior -0.00198 0.0000737 0.000178 0.00114 0.000326Tickets (0.00144) (0.000223) (0.000215) (0.000886) (0.000511)

Log Zip Code 0.00115 0.00150 0.0000372 0.000848 0.0000294Income (0.00128) (0.000721) (0.000377) (0.00110) (0.000641)

F-test 0 .175 .148 .221 .687Mean .305 .305 .304 .323 .323Location FE XLocation + Time FE X XGPS FE XObservations 1141628 1141628 1079250 125040 125040

Notes: All regressions includes vehicle type fixed effects and county fixed effects. The F-testreports the joint hypothesis test that variables Driver Black through Log Zip Code Incomeare zero. Standard errors are clustered at the county level. ”Location FE” includes county byhighway fixed effects. ”Location + Time FE” includes county by highway by year by monthby day of the week by shift fixed effects. ”GPS FE” includes road segment by county by high-way by year by month by day of the week by shift fixed effects.

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Table A.7: Predicting Officer Complaints/Force

(1) (2) (3) (4)# Complaints Any Complaints # Use of Force Any Use of Force

Lenience -0.622 -0.184 -0.184 -0.108(0.206) (0.0546) (0.152) (0.0494)

Discrimination -0.247 0.134 0.0642 -0.0698(0.574) (0.192) (0.433) (0.166)

Black 0.111 0.00131 -0.196 -0.0863(0.176) (0.0401) (0.0908) (0.0335)

Hispanic -0.00981 0.0165 0.0309 0.00569(0.144) (0.0372) (0.0993) (0.0373)

Other 0.178 0.0242 -0.234 -0.0727(0.380) (0.0996) (0.181) (0.0938)

Female -0.295 -0.109 -0.0149 0.0125(0.158) (0.0496) (0.104) (0.0443)

Age -0.120 0.163 -0.736 -0.194(0.332) (0.0900) (0.212) (0.0793)

Age Squared 0.0167 -0.0249 0.0611 0.0138(0.0478) (0.0131) (0.0266) (0.0108)

Experience -0.0633 -0.0800 -0.554 -0.00694(0.414) (0.130) (0.331) (0.117)

Exp Squared -0.0209 0.0350 -0.00580 -0.00173(0.0766) (0.0249) (0.0457) (0.0195)

Failed Entrance Exam 0.259 0.0432 -0.106 -0.00330(0.205) (0.0483) (0.110) (0.0458)

Any College -0.183 -0.0250 0.103 0.0134(0.104) (0.0293) (0.0946) (0.0264)

Sought Promotion -0.194 -0.0664 -0.0405 0.0239(0.113) (0.0294) (0.0884) (0.0277)

Mean 1.26 .551 .559 .294Observations 1402 1402 1402 1402Regression OLS OLS OLS OLS

Notes: Heteroskedasticity-robust standard errors in parentheses. Column title indicates the de-pendent variable. Data is at the officer level. Regressions have indicator variables for years whenand districts where the officer worked.

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Table A.8: Model Parameter Estimates

White Minority

(1) (2) (3) (4) (5) (6) (7)µ σ2 # Param µ σ2 # Param Mean Diff

b, slope 0.0395 — 1 — — — —(0.0006)

t, officer valuations -0.2824 4.5876 1591 -0.3099 4.2300 1591 0.0275(0.0031) (0.1627) (0.0035) (0.1500) (0.0046)

λ, speeds 20.5058 2.7202 67 20.9833 2.1300 67 -0.4775(0.0517) (0.4735) (0.0407) (0.3708) (0.0658)

Pr(Discount | E(Z), j) 0.3745 0.1283 1591 0.3547 0.1204 1591 0.0198(0.0007) (0.0000) (0.0008) 0.0000 (0.0011)

Speed Parameters γ Preference Parameters α

(1) (2) (3) (4)Female -0.4813 (0.0087) 0.1353 (0.0036)

Age -0.0453 (0.0003) 0.0057 (0.0001)

Previous Tickets 0.1868 (0.0027) -0.0388 (0.0013)

County Minority Share -1.8714 (0.0270)

Notes: This table presents estimates of the model introduced in section 2.8. b is the slope parameterfor how officers weight the speed of drivers in choosing to discount, t is each officer’s mean valuation ofa racial group in choosing to discount, and λ is the poisson speed parameter for each race by county.Pr(Discount | E(Z), j) = Φ(trj + E(Z)α − 10b), i.e. the probability of being discounted when drivingright above the bunch point for an average driver. The variances are empirical variances of the estimates,not adjusted for sampling error.

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Table A.9: Speed Gap Decomposition

State-Wide Disparity

(1) (2) (3) (4)White Mean (MPH) Minority Mean Difference Percent

Baseline 15.531 17.296 1.764 100(0.009) (0.011) (0.014)

No Discrimination 15.530 17.087 1.557 88.244(0.008) (0.012) (0.013) (0.014)

No Sorting 15.645 17.166 1.521 86.193(0.009) (0.012) (0.015) (0.015)

Neither 15.644 16.927 1.283 15.644(0.009) (0.012) (0.014) 0.013

County-Level Disparity

(1) (2) (3) (4)White Mean (MPH) Minority Mean Difference Percent

Baseline 15.531 16.194 0.662 100(0.009) (0.011) (0.014) (NaN)

No Discrimination 15.530 15.967 0.436 65.868(0.008) (0.012) (0.013) (0.022)

No Sorting 15.645 16.341 0.695 104.980(0.009) (0.012) (0.015) (0.027)

Neither 15.644 16.106 0.462 69.714(0.009) (0.012) (0.014) (0.024)

Notes: Table presents how the racial gap in speeds changes without bias and sort-ing of officers across counties. The gap is the minority drivers’ outcome minus whitedrivers’ outcome. No bias is calculated by assigning each officer’s preferences towardminorities to be the same as his preference to whites. No sorting is calculated bysimulating a new draw of officers for each driver, where the draw is done at the statelevel.

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Figure A.1: Distribution of Charged Speeds for Radar Gun Sample

0

.1

.2

.3

.4

Shar

e

0 10 20 30 40MPH Over

Notes: Line shows histogram of ticketed speeds for observations where the officer records that thespeed is detected from a radar gun (N = 101,716).

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Figure A.2: Model Estimates: Officer Lenience by Race

0

.5

1

1.5

2

Dens

ity A

cros

s O

ffice

rs

0 .2 .4 .6 .8 1Probability of Discount

White Driver

Minority Driver

Notes: Prj ≡ Pj(Discount|X = 10, Driver Race = r, Z = E(Z))

Figure A.3: Model Estimates: Percentiles of Officer Lenience

0

.2

.4

.6

.8

Prob

abilit

y of

Disc

ount

10 20 30 40Speed Over Bunch Point

White Driver

Minority Driver

25th Pctile

0

.2

.4

.6

.8

Prob

abilit

y of

Disc

ount

10 20 30 40Speed Over Bunch Point

Median Lenient Officer

0

.2

.4

.6

.8

Prob

abilit

y of

Disc

ount

10 20 30 40Speed Over Bunch Point

75th Pctile

Notes: Prj ≡ Pj(Discount|X = 10, Driver Race = r, Z = E(Z))

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Figure A.4: Model Estimates: Speed Distribution

0

.1

.2

.3

Den

sity

15 20 25Average Speed

White

Minority

Notes: Figure plots the distribution of speed parameters λ across counties, separately by raceof the driver, where individual covariates are set to the average value. In other words, we plotλ = λcr + γE(Z)

Figure A.5: Model Estimates: Racial Discrimination by Officer

0

5

10

15

Den

sity

-.2 -.1 0 .1 .2Bias in Probability of Discount

Notes: Pj(Discount|X = 10, Driver Race = White, Z = E(Z)) − Pj(Discount|X =10, Driver Race = Minority, Z = E(Z)) 181

Figure A.6: Model Diagnostic Figures

0

.1

.2

.3

Shar

e

0 10 20 30 40MPH Over

Data

Model

10

15

20

25

Coun

ty-R

ace

Spee

ds: M

odel

10 15 20 25County-Race Speeds: Data

45° line

0

.2

.4

.6

.8

1

Offi

cer-R

ace

Bunc

hing

: Mod

el

0 .2 .4 .6 .8 1Officer-Race Bunching: Data

45° line-.4

-.2

0

.2

.4

.6

Offi

cer B

unch

ing

Disp

arity

: Mod

el

-.4 -.2 0 .2 .4 .6Officer Bunching Disparity: Data

45° line

Notes: Figures compare various model estimates with their counterparts in the true data. Modelestimates are found by simulating 100 iterations of the model and calculating averages acrossiterations. The top left panel compares the aggregate histograms of speeds. The top right panelcompares the average ticketed speeds by race-county. The bottom left panel compares the shareof tickets at 9 MPH over by officer-race. The bottom right panel compares the racial disparity inbunching at 9 MPH over by officer.

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Chapter 3

More COPS, Less Crime 1

3.1 Introduction

Provision of public safety is a central responsibility of local governments. Crime victimization

is estimated to cost Americans over $200 billion per year and public spending on police

protection exceeds $100 billion annually (Chalfin et al., 2016b). Consistent with canonical

models of the economics of crime such as Becker (1968), which predict that police presence

reduces crime by deterring potential offenders, hiring police is the main policy instrument

used by local governments for crime prevention. The causal effect of expanding police forces

on crime rates is, therefore, a parameter of substantial interest for policymakers. In practice,

estimating this effect is made difficult by the fact that police hiring decisions are endogenous

1This chapter is published in the Journal of Public Economics 172: 174-200, April 2019. I amgrateful to Ilyana Kuziemko and Alex Mas, who provided considerable advice and encouragementon this project. I benefitted from the guidance of Camille Landais (co-editor) and four anonymousreferees. I thank Jessica Brown, John Donohue, and Felipe Goncalves, who read earlier drafts andoffered valuable insights and criticisms. Amanda Agan, Leah Boustan, Mingyu Chen, David Cho,Janet Currie, Will Dobbie, Hank Farber, Paul Heaton, Andrew Langan, David Lee, Chris Neilson,David Price, Mica Sviatschi, Danny Yagan, Owen Zidar, and seminar participants at PrincetonUniversity and the 2018 ASSA/Econometric Society Annual Meetings provided helpful comments.I also benefitted from discussions with John Kim and Matthew Scheider at the COPS Office. Iacknowledge financial support from a Princeton University Graduate Fellowship and the Fellowshipof Woodrow Wilson Scholars. Any errors are my own.

183

to local crime conditions, which introduces simultaneity bias in OLS estimates (Klick and

Tabarrok, 2010).

In this paper, I exploit a unique natural experiment generated by the distribution of

grants to hire over 7,000 police officers to estimate the causal effect of police on crime. In

February 2009, President Obama signed into law the American Recovery and Reinvestment

Act (ARRA), which provided for over $490 billion in stimulus spending between 2009 and

2011. ARRA allocated about $2 billion to the Department of Justice (DOJ), a large share

of which was used to finance a reinvigoration of the DOJ’s police hiring grant program.

The Community Oriented Policing Services (COPS) hiring program, which covers the salary

cost of new police hires for local law enforcement agencies, was a cornerstone of President

Clinton’s Violent Crime Control and Law Enforcement Act of 1994. Between 1995 and 2005,

the COPS hiring program spent almost $5 billion to help local police departments hire about

64,000 officers (Evans and Owens, 2007). Allocations for the program fell from over $1 billion

per year in the late 1990’s to almost zero in the years 2005–2008. The injection of Recovery

Act funding restored the COPS hiring program budget to $1 billion in fiscal year (FY) 2009.

Grants issued in 2009 were allocated according to an application process. Law enforce-

ment agencies applied for funds and the COPS office scored the applications and determined

grant amounts. The funding rules generated application score thresholds, above which cities

received hiring grants and below which cities did not. I compare the change over time

in police and crime for municipalities whose application scores were above and below the

threshold. Specifically, I estimate difference in differences models with city and year fixed

effects and city-specific linear trends. Using a 2004-2014 panel of 4,327 cities and towns, I

show that treatment and control cities follow similar trends in police and crime prior to the

program. Beginning in 2009, however, police levels increase while crime declines in cities

with application scores above the threshold. My baseline difference in differences estimates

indicate that police rates increase by 3.2% while victimization cost-weighted crime rates de-

crease by 3.5% following the distribution of the 2009 hiring grants. The corresponding IV

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estimate, obtained by instrumenting the police rate with an interaction between a treatment

indicator and a post-program indicator, suggests that each additional sworn officer reduces

victimization costs by about $352,000. The implied elasticity of cost-weighted crime with

respect to police is -1.17, which is large relative to most existing estimates in the literature.

Though noisier, the results are nearly identical when using only cities with application

scores very close to the cutoff, for whom the assumption that grants are randomly assigned

is most plausible. Further, the first stage and reduced form estimates are largest when

using the true score thresholds, rather than placebo thresholds, to identify the treatment

and control groups. This results suggests that crossing the threshold, and thereby receiving

hiring grant funding, rather than differences in application scores per se, explains the post-

program divergence for the treatment and control groups. I also demonstrate that neither

differential exposure to the Great Recession nor different levels of other ARRA funding can

account for the results.

Consistent with the existing literature, I find that violent crime is more responsive than

property crime to increases in police force size (Chalfin and McCrary, 2018). IV estimates

imply crime-police elasticities of about -1.3 for violent crime -0.8 for property crime. Declines

in robbery and auto theft are particularly pronounced, with the point estimates suggesting

that an additional police officer prevents 1.9 robberies and 5.1 auto thefts. I also find evidence

that police reduce murders. The coefficient is imprecisely estimated but significant at the

10% level, with the point estimate suggesting that each officer prevents 0.11 murders and

thereby that one life can be saved by hiring about 9.5 additional police officers.

Using a subsample of cities that report arrests to the FBI, I find little evidence that

arrests increased with the program-induced police force expansions. The lack of arrest rate

increases suggests that a deterrence, rather than incapacitation, mechanism underlies the

crime reductions. Additionally, by comparing changes in crime for non-applicant jurisdictions

near treatment and control cities, I find no evidence for geographic spillovers or displacement

associated with the local police increases.

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An analysis of treatment effect heterogeneity reveals that the impact of police on crime

is largest among cities more exposed to poor macroeconomic conditions during the Great

Recession. The elasticity of victimization costs with respect to police is about -0.7 for cities

with the smallest 2007-2009 unemployment increases but about -1.4 for cities with the largest

2007-2009 unemployment increases. This pattern of results is consistent with the hypothesis

that fiscal distress caused cities to employ fewer than the optimal number of officers, which

may explain the large estimated treatment effects.

A back of the envelope calculation suggests that the ARRA hiring program added about

9,450 officer-years at a total cost of about $1.75B, suggesting that the hiring grants are cost-

effective if the annual social benefit attributable to a marginal police officer exceeds $185,000.

My baseline estimate is about $350,000, suggesting a favorable benefit-cost ratio for program

spending. The program fails a cost-benefit test under more conservative assumptions about

the crime reduction benefit, however.

The rest of the paper proceeds as follows. Section 2 provides a brief literature review and

institutional background on the COPS hiring program. I describe the data in Section 3 and

explain the empirical strategy in Section 4. Results are presented in Section 5. In Section

6, I conduct a brief cost-benefit analysis of the hiring program. Section 7 concludes.

3.2 Background

3.2.1 Research on Police and Crime

Beginning with Levitt (1997), researchers have tried to overcome endogeneity issues in esti-

mating the police-crime relationship by relying on quasi-experimental research designs. Two

strands of research comprise the bulk of the quasi-experimental literature. The first uses

city level panel data and instrumental variables that predict variation in police levels at

the city-year level. Some examples include Levitt (1997), who relies on the timing of may-

oral election years, and Evans and Owens (2007), who rely on COPS hiring grants during

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the 1990’s as instrumental variables. The second exploits sharp micro-time series variation

within cities, such as increased police deployments following terror attacks, notably Di Tella

and Schargrodsky (2004), Klick and Tabarrok (2005), and Draca et al. (2011).2

Quasi-experimental studies typically document that police reduce crime, although esti-

mated magnitudes vary widely. Further, the literature is not without potential flaws. Binary

instruments, such as election years, discard much of the variation in police rates and are often

weak by modern standards. Studies instrumenting police levels with federal grants (Zhao,

Scheider and Thurman 2002, Evans and Owens 2007, Worrall and Kovandzic 2010) typically

lack a clear control group and suffer from the possibility that such grants are targeted where

they are most needed or most likely to succeed, either of which would violate the exclusion

restriction. My paper contributes to this strand of literature by employing a cleaner iden-

tification strategy as well as studying a larger fraction of U.S. cities and a different time

period.

Papers using within-city variation in police deployments provide convincing evidence

that police deter property crimes. However, these studies typically estimate effects specific

to single jurisdictions, raising questions of external validity (Klick and Tabarrok, 2010).

Further, the deployment increases under study typically do not approximate increases in

force size or policing intensity that are realistic for long run policy decisions (Blanes and

Mastrubuoni, 2017). Finally, scholars have documented that neighborhood crime declines

caused by temporary increased policing may be offset by crime displacement (Blattman,

Green, Ortega, and Tobon 2017; Ho, Donohue, and Leahy 2014).

3.2.2 History of COPS Hiring Program

In September 1994, President Bill Clinton signed into law the Violent Crime Control and

Law Enforcement Act, the largest federal crime bill to date. The bill authorized $8.8B in

2Another noteworthy study is the recent paper by Chalfin and McCrary (2018). The authorsposit that OLS estimates are biased by measurement error in police levels rather than simultaneitybias and estimate crime-police elasticities corrected for measurement error.

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spending on grants for state and local law enforcement agencies between 1994 and 2000 and

established the office of Community Oriented Policing Services (COPS) to administer the

new grant programs. A key tenet of the crime bill was the creation of the COPS Universal

Hiring Program (CHP), which covered 75% of the cost of new police hires for grant recipients.

The stated goal of the hiring grant program was to put 100,000 new police officers on the

street.3

CHP funding exceeded $1B in fiscal years 1995–1999, but appropriations fell considerably

in the early 2000’s. Less than $200M was allocated for the hiring program in 2003–2004,

and less $20M was appropriated in each year 2005–2008 (James, 2013). The program was

defunded due both to the retreat of crime as a central policy issue and to questions over

the program’s effectiveness (Evans and Owens, 2007). Reports authored by the Heritage

Foundation in 2001 and 2006, for example, argued that hiring grants did not reduce crime

because grants were used to supplant other expenditures rather than to expand police forces.

Funding for the hiring program saw a dramatic resurgence in 2009 with President

Obama’s signing of the American Recovery and Reinvestment Act (ARRA), which provided

$2B in new funds to the Department of Justice, with $1B earmarked specifically for the

COPS hiring program. The funding was seen both as a precautionary measure for keeping

crime rates low in the face of a worsening economy and as a means to create or preserve

as many as 5,000 police officer jobs across the country. Following the injection of ARRA

funds in FY2009, congressional appropriations exceeded $140M annually between 2010 and

2013, a large increase from 2004–2008 funding levels (James, 2013). Hiring grants awarded

in FY’s 2009–2011 were also more generous than in previous years, covering 100%, rather

than 75%, of entry-level salary and fringe benefits for hires or rehires for three years.4

3See http://www.justice.gov/archive/opa/pr/Pre_96/October94/590.txt.html.4The program reverted to covering 75% of salary and benefits beginning in 2012.

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3.2.3 Details of COPS 2.0

ARRA hiring grants were distributed based on an open solicitation application process. Any

state, local, or tribal agency with primary law enforcement responsibility was eligible to

apply for funding. Applicant agencies provided an array of statistical information, such as

indicators of fiscal health, local unemployment and poverty rates, and local crime rates.

Applicants also provided answers to several open-ended essay style questions detailing their

usage of community policing strategies and requested a specific number of officers for which

they required funding.5

The COPS office assigned each applicant a fiscal need score and a crime score. Program

documentation indicates that these scores were generated by ranking applicants on each ap-

plication question then weighting each question to obtain an overall ranking. I was unable

to replicate the score generation process due to my inability to observe a large share of the

application materials.6 The two component scores were added to create an aggregate appli-

cation score. Table A-2 shows the relationship between city characteristics and application

scores in 2009. Unsurprisingly, higher-scoring cities are larger, poorer, and have significantly

higher crime rates.

Applications were funded in descending order of the application score until funding was

exhausted and two distributional rules were met. The COPS office was required to allocate

at least 1.5% of total CHP funding to each state and was required to distribute at least

50% of all funding to jurisdictions with populations exceeding 150,000. These distributional

considerations generated different score cutoffs depending on state and size category. For

applicants in states that initially received more than $5 million in total funding, the cutoff was

65.75 for small agencies (population under 150,000) and 68.75 for large agencies (population

over 150,000). For applicants in states that would not meet the required 1.5% using these

5See http://www.cops.usdoj.gov/pdf/CHP/e05105273-CHP.pdf.6Municipal level employment and financial data, for example, are publicly available on an annual

basis for only a small fraction of cities.

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cutoffs, the relevant threshold is the application score of the last agency funded in that state

(Cook et al., 2017).

A similar application process has been repeated each year since 2009. In this paper, I focus

on the 2009 application round because of its magnitude. Total program spending was more

than three times higher in 2009 than in any year 2010–2014. 46% of all funded applications

and 49% of all officers granted over the 2009–2014 period occurred in 2009. Further, focusing

on the ARRA grant round allows for a very simple and transparent difference in differences

approach with clearly defined treatment and control groups. Studying additional grant

rounds, and in particular dealing rigorously with repeat applicants, complicates the empirical

analysis significantly but yields minimal payoff.7

Funding for the 2009 hiring grants was made available in the summer of that year and

distributed via a reimbursement system. Specifically, police departments were required to

submit paperwork indicating that a grant-covered officer was hired, then submit quarterly

financial reports for the duration of the grant period. Each period, the COPS office reim-

bursed the department for the quarterly pay of the officer.8

3.2.4 Research on the COPS Program

Several existing papers have studied the first iteration of the COPS hiring program during

the 1990’s. The most noteworthy paper on the topic is the careful and well-regarded study

by Evans and Owens (2007). Papers by the Zhao et al. (2002) and Worrall and Kovandzic

(2010) also study the original COPS program and employ similar research designs.

In the first part of the paper, Evans and Owens (2007) examine whether COPS grants

increased police forces. Using a twelve-year (1990-2001) panel of 2074 cities, they regress

7In an earlier version of this paper, available at https://mello.github.io/files/cops_jan_2017.pdf, I estimated effects for all grant rounds jointly using stacked panels, following the ap-proach in Cellini et al. (2010). I found crime-police elasticities of -1.36 for violent crime and -0.84for property crime, which are nearly identical to those obtained here.

8For more detail, see https://cops.usdoj.gov/pdf/2017AwardDocs/chp/AOM.pdf (accordingto COPS office officials, the award owner’s manual has remained unchanged since the early 2000’s).

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sworn officers per 10,000 residents on the lagged number of officers granted by the COPS

office per 10,000 residents in panel data models, finding that local police forces increased

by 0.7 sworn officers for each granted officer. In the second part of the paper, the authors

instrument the police rate with the lagged grant rate in 2SLS regressions where the crime rate

is the outcome of interest, finding that increases in police are associated with statistically

significant declines in robberies, assaults, burglaries, and auto thefts.

Relative to Evans and Owens (2007), my contribution is as follows. First, I improve on

their identification strategy. The application-based grant allocations allow for the use of

rejected applicants as a control group. I argue that the set of applicants denied funding is

a better control group than the broader set of cities who report crimes to the FBI. I also

use graphical analysis to check parallel trends assumptions and show results using only a

subsample for whom grant offers are plausibly randomly assigned. Second, I study a wider

range of cities. Much of the existing research on police effectiveness has focused on large

cities, while Evans and Owens (2007) study about 2,100 cities with populations greater than

10,000. I study all applicant cities and towns with populations exceeding 1,000, which results

in greater coverage of U.S. municipalities. And third, I study a different era of the program.

Evans and Owens (2007) examine the introduction of the COPS program in the mid 1990’s,

when crime rates were high and crime in general was a central policy issue. The stated

goal of the program was to induce large increases in police forces across the country. My

focus is the reinvigoration of the program following the injection of ARRA funding. The

goal of COPS 2.0 was to preserve law enforcement jobs and prevent a rise in crime due to

worsening economic conditions. The poor fiscal health of many cities during this period,

combined with a lower program budget than during the original COPS period, generated a

highly competitive application process. The different context, various program changes, and

the availability of a cleaner identification strategy warrant a new evaluation. Further, this

paper contributes to a broader literature on the effectiveness of ARRA spending and offers

insights on the relative benefits of including law enforcement funding in stimulus packages.

191

Two additional studies authored concurrently with mine bear mentioning here. Weisburst

(2017) uses COPS funding over the period 1994–2014 as an instrument to estimate the

effect of police on crime using a panel of cities. Results presented in Weisburst (2017)

are very similar to mine. The author finds that hiring grants increase police forces by

about 0.65 and estimates crime-police elasticities of -1.28 for violent crime and -0.73 for

property crime. My study differs from Weisburst (2017) mainly in terms of identification.

She uses a panel of cities (applicants and non-applicants) and controls for the presence of

grant applications at the city-year level, allowing for a larger sample size and for the use of

more grant rounds in identifying the estimates. I focus on a sample of applicants and study

a single program year, explicitly relying on denied applicants as a control group and allowing

for a more transparent presentation of the results. As mentioned above when comparing my

study to Evans and Owens (2007), another advantage of my approach is that I am able to

incorporate the program application scores in the analysis, showing that my estimates hold

when only considering cities very near the funding threshold, among whom the assumption

of randomized grant offers is most likely to hold.

The COPS office also funded a study of the 2009 hiring grant program, authored by

Cook et al. (2017). This paper implements a regression discontinuity design to estimate the

effect of grant receipt in 2009 on police forces and crime rates in 2009–2012. The authors

find that at the cutoff, cities experience increases in police per capita of 2.1% and declines

in violent (property) crimes per capita of 9.2% (3.6%) in 2010 relative to 2008, with implied

crime-police elasticities of -4.4 and -1.7. The estimates are relatively imprecise, however.

Again, my study differs from Cook et al. (2017) mostly in terms of identification. I also

focus on the 2009 grant round but use a difference in differences approach. An advantage

of the difference in differences approach in this context is that it is that it allows for the

192

inclusion of city and time fixed effects to absorb residual variance, resulting in more precisely

estimated coefficients.9

Another contribution of my study relative to Weisburst (2017) and Cook et al. (2017)

is my analysis of heterogeneous treatment effects motivated by a simple economic model. I

show that impact of additional police is largest in areas most exposed to poor macroeconomic

conditions during the Great Recession. This result helps both to rationalize the relatively

large effects in my study (and the two concurrent papers) compared with past work and to

draw an important policy lesson that grants for crime prevention are likely to offer large

returns during bad macroeconomic times.

3.3 Data

3.3.1 Grants Data

The COPS office provided information on the universe of applications and grants awarded for

2009-2014 in response to a Freedom of Information Act (FOIA) request. For each program

year and applicant law enforcement agency, the data include the corresponding application

score and information on the grant received in terms of both the number of officers funded

and dollar value. Agencies are identified in the applications data by an agency name and

a 7-character ORI (originating agency) code, which is also used to identify agencies in the

FBI datasets discussed below.10

Raw application scores in 2009 ranged from 15-100 with a mean of about 50. I compute

the score thresholds following Cook et al. (2017) as described above in Section 2.2. I then

standardize both the application scores and cutoffs so that the score relative to the threshold

9In Appendix B, I argue that in the context of evaluating COPS hiring grants, a regressiondiscontinuity design suffers from insufficient statistical power due to small N and relatively variableoutcome measures.

10A number of ORI codes were present in the applications data but not in the FBI data. Wherepossible, I corrected the codes by matching on name with the FBI datasets. 184 of the 4,327agencies in the main sample (4.25%) are assigned a different ORI code from that reported in theapplications data. See the Appendix for more detail.

193

is measured in standard deviations. Figure 3.2 displays the distribution of application scores

relative to the cutoff as well as the fraction of applicants that received hiring grants in each

score bin of width 0.25. No agency with a score below the threshold was funded, while

99% of agencies with scores above received hiring grants. The RD estimate of the effect of

crossing the threshold on funding probability using the Imbens and Kalyanaraman (2012)

[IK] optimal bandwidth and a triangular kernel yields a coefficient (standard error) of 0.948

(0.019).

3.3.2 FBI Data

Data on police employees and reported crimes are from the FBI’s Uniform Crime Reporting

Data System (UCR). I obtained the agency-level Law Enforcement Officers Killed in Action

(LEOKA) files for 2002–2014 from the National Archive of Criminal Justice Data (NACJD)

website. The data files report each agency’s number of sworn officers and civilian employees

as of October for each year. Criminal offenses known to police are reported in the UCR

Return A file, which provides monthly counts of index I crimes for all reporting agencies.

Index I crimes include the core violent (murder, rape, robbery, aggravated assault) and

property (burglary, larceny, motor vehicle theft) crimes. Michael Maltz, a criminologist at

the Criminal Justice Research Center at the Ohio State University, maintains an updated

version of the Return A file, and the COPS office provided his version of the data for this

study.11 Because police officers counts are reported annually, and many agencies report their

full-year crime counts once rather than report each month individually, I aggregate the crime

counts to the agency-year level. For city population, I use a smoothed version of the measure

reported in the UCR files.12

11Maltz’s data is identical to the publicly available version on the NACJD website except thathe (1) has identified reasons for missing values and (2) has identified certain zeroes or extremevalues as outliers. My own examination of the data revealed that many record errors remained inhis version and I further cleaned the data as described in the Appendix.

12Chalfin and McCrary (2018) note that the UCR population measure tends to jump discontin-uously around census years. For this reason, I follow their procedure and smooth the populationmeasure using local linear regression. For more detail, see the Online Data Appendix.

194

Prior research has noted the existence of record errors in the FBI datasets (Evans and

Owens 2007, Chalfin and McCrary 2018, Maltz and Weiss 2006).13 As such, the data require

thorough cleaning before use. I implement a regression-based approach similar to that used

in Evans and Owens (2007) to identify record errors and extreme outliers. The procedure

is described in more detail in the Appendix. Values identified as errors are recoded to

missing, then all missing values due either to outlier status or non-reporting are imputed

using backwards/forwards filling and linear interpolation.14 I cleaned the crime data for

2002–2014, but only use years 2004–2014 in the analysis because a large fraction (over 17%)

of the crime data was imputed for 2002-2003 via backfilling. In the main analysis sample,

1.5% of police observations and 8.8% of crime observations are imputed.15

Empirical studies of public safety typically focus on crimes per 10,000 residents as the

outcome of interest, showing results separately for each type of crime. To simplify the

presentation of results, I focus primarily on a single index outcome which I term the cost-

weighted crime rate or crime costs per capita. One could focus on the total crime rate,

but this measure heavily weights property crimes relative to violent crimes. While property

crimes are nearly six times more common than violent crimes, the average violent crime is

about seventeen times more severe based on existing victimization cost estimates (Cohen

and Piquero, 2009). I follow Autor et al. (2017) and compute the cost-weighted crime for

city i in year t as

yit = $67, 794× Violent Crimesit + $4, 064× Property Crimesit

13For example, reported violent crimes in Boulder, CO for the period 2007–2011 are 219, 202,952, 210, 246. Police in Lansford, PA for 2006–2010 are 4, 3, 40, 9, 9.

14For example, if a city’s first year of nonmissing violent crime is 2005, the 2005 value is imputedfor the years 2002–2004.

15Figure A-2 illustrates the relationship between treatment status and imputation. Treatmentgroup cities are slightly less likely to have imputed police values prior to 2006 and after 2012.There is no discernible relationship between crime imputation and treatment status. Table A-6shows that results are nearly identical when replacing imputed values to missing.

195

where $67,794 and $4,064 are the direct costs of the average violent and property crimes

based on the estimates in Cohen and Piquero (2009). Note that one could instead compute

this measure as the cost-weighted sum of each individual crime type. However, such a

measure would weight murder 35 times more heavily than all other crime types, despite the

fact that murder is the crime type with the greatest year-to-year variability (McCrary, 2002).

Weighting the violent and property crime counts by the category average costs compromises

by weighting up violent crimes but not excessively weighting the highest variance crime

types.

3.3.3 Other Data Sources

Standard demographic and economic information are not available at the city-level on an

annual basis. I obtained demographic information from two sources. To examine city-

level characteristics at the time of the program, I use demographic information, as well as

employment rates and median family income, from the 2009 American Community Survey

collected at the FIPS (Federal Information Processing Standard) place code level. To use

as controls in the regressions, I obtained data at the county-year level from several sources.

I computed percent black, percent Hispanic, and percent young male (age 15-29) from the

intercensal county population estimates maintained by the Surveillance, Epidemiology, and

End Results (SEER) program at the National Institutes of Health. County-level income per

capita was obtained from the Bureau of Economic Analysis and county-level unemployment

rates were obtained from the Bureau of Labor Statistics Local Area Unemployment Statistics

data files. I use county-level percent black, percent Hispanic, percent young male, log per

capita income, and unemployment rates as controls in the crime regressions.

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3.3.4 Sample Construction

The main analysis focuses on municipal police agencies applying for COPS hiring program

funding in 2009. There are 5,314 such police departments.16 I drop 237 agencies that never

report crimes to the FBI and drop an additional 229 agencies with populations below 1,000

because per-capita measures are much noisier, and often orders of magnitude higher, below

this threshold. Among the remaining 4,848 departments, I require that an agency report

police and crimes at least once prior to 2008 and after 2010, report positive police at least once

and positive crimes at least once, and report police and crimes each for at least four years.

The analysis sample is comprised of 4,327 agencies, which is 81% of all applicant municipal

police departments and 89% of applicant municipal police departments that ever report to

the UCR and have populations above 1,000. The most binding sample restriction was crime

reporting pre and post 2009. Figure A-1 shows the relationship between the application

score and inclusion in the sample. Comfortingly, sample inclusion is not discontinuous at

the funding cutoff.

3.3.5 Characteristics of Analysis Sample

The sample includes 4,327 police departments, 18% (791) of which scored above the threshold

in 2009. The total population served by such departments is 142.6 million as of 2008, about

47% of total U.S. population in that year. The sample includes at least one department

from all 50 states and the District of Columbia. 1,588 counties (53% of all U.S. counties)

are represented. Table A-1 provides examples of cities in the sample at quantiles of the size

distribution.

Characteristics of the sample, measured at the time of the program, are presented in

Table 1. The average city has about 30,000 residents (median ≈ 10,000), an unemployment

rate of nearly 7.5%, and median family income of $50,000. Cities typically employ about

16Municipal police comprise 74% of all applicants. The remainder were sheriff’s and regionalpolice departments (18%), school police departments (5%), tribal agencies (1.4%), and specialagencies(1.3%).

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23 sworn officers per 10,000 residents and face cost-weighted crimes per capita of about

$556. Cities above and below the application score threshold differ on most observable

characteristics. High-scoring cities have larger populations, higher unemployment rates,

lower family incomes, and larger nonwhite populations. High scoring cities employ three

additional officers per 10,000. Violent and property crime rates are about 60% larger in the

average high-scoring city.

Over 98% of cities above the threshold were offered hiring grants. The average grant

funded 1.7 officers per 10,000 residents, about 6% of current force size in a typical winning

department, and carried a dollar value of $29 per city resident, or about $67,000 per funded

officer per year.

Figure 3.3 illustrates the relationship between the application score and select city char-

acteristics at the time of the program. Consistent with the summary statistics, city size,

police rates, crime rates, and unemployment rates all increase with the application score.

Further, all four measures appear to increase discretely at the threshold, with RD estimates

statistically significant for population and the unemployment rate. I return to this point in

Section 4.2.

Figure 3.4 illustrates trends in police and crime for cities above and below the threshold.

Specifically, I plot average police per 10,000 residents and crime costs per capita for the two

groups in each year. The above-cutoff (treatment group) means are normalized to be equal

to the below-cutoff (control group) means in 2008 to adjust for level differences. The figure

foreshadows the main results. Police rates (Panel A) in treatment and control cities follow

similar trends prior to the program but diverge sharply beginning in 2009, with police rates

increasing slightly in high-scoring cities but declining sharply in low-scoring ones. A similar,

but inverse, divergence occurs in crime costs per capita (Panel B), with treatment cities

experiencing reductions in crime relative to the control group beginning in 2009.

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3.4 Empirical Strategy

3.4.1 Difference in Differences

I leverage the natural experiment created by the 2009 hiring grant application process using

a difference in differences design. The spirit of the analysis is to compare the change over

time in police and crime for cities with application scores above the funding cutoff (treat-

ment group) and cities below the funding cutoff (control group). Under a set of identifying

assumptions discussed below, differential changes in crime in treatment and control cities

can be attributed to differential changes in police, and the ratio of ∆crime and ∆police is

an estimate of the causal effect of police on crime.

Specifically, I estimate the following first stage equation:

Policeit = βFSHighi × Postt + φi + κt + λ(t)i + εit (3.1)

Policeit is sworn officers per 10,000 residents in city i in year t. Highi indicates that city i’s

2009 application score exceeded the threshold and Postt is an indicator for t ≥ 2009.17 φi is

a city fixed effect, which absorbs level differences across cities. κt is a year fixed effect and

λ(t)i is a city-specific linear trend. I include city-specific trends to account for heterogeneity

in pre-program trends, which vary widely given the distribution of city sizes in the sample. In

the estimation, I also allow κt to vary across city size groups, so that κt adjusts for common

deviations from trend among cities of similar size.18 Standard errors are clustered at the

city-level. β is a difference in differences estimate capturing the extent to which changes in

police from pre to post 2009 differ for treatment and control cities. We can also think of β is

also an intent-to-treat estimate of the effect of a 2009 hiring grant offer on police force size.

I then estimate the corresponding reduced form equation,

17I consider 2009 a post-program year because hiring grant funding was distributed in the summerof 2009 and police is measured in October.

18The size groups are 1,000-2,500; 2,500-5,000; 5,000-10,000; 10,000-15,000; 15,000-25,000;25,000-50,000; 50,000-100,000; 100,000-250,000; >250,000. Cities appearing in multiple groupsare placed in the group they appear most often.

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Crimeit = βRFHighi × Postt + φi + κt + λ(t)i + εit (3.2)

where Crimeit is crime cost per capita in city i in year t. β captures the extent to which

treatment and control cities differ in their crime rates in the post period relative to the pre

period. The Wald IV estimate of the effect of police on crime is the ratio βRF

βFS . In practice,

I obtain IV estimates via 2SLS, estimating the equation

Crimeit = βPoliceit + φi + κt + λ(t)i + εit (3.3)

using High× Post as an instrumental variable for Police.

To be clear, the identifying assumption is not random assignment of grant offers. Rather,

the assumption is that police and crime would have trended similarly in grant-winning and

grant-losing cities in the absence of the program (Yagan, 2015). This assumption could be

violated in one of two important ways. First, treatment and control cities could be trending

differently prior to the program. I test for this possibility directly by estimating a fully

dynamic specification of (1)-(2),

Yit = θtHighi × κt + φi + κt + λ(t)i + εit (3.4)

Here, θt measures the treatment-control difference in each year. If trends in high-scoring and

low-scoring cities diverge prior to the program, the θt’s for t < 2009 will differ from zero.

The second threat to identification is that treatment status could be correlated with

other shocks occurring exactly at the time of the program. One cause for concern is the fact

that the program’s timing coincided with the ramp up of the Great Recession. The nation-

wide unemployment rate increased from 5% in January 2008 to a peak of 10% in October

2009 and remained above 9% through most of 2010. Standard models of the economics of

crime (e.g. Becker 1968) predict that crime rates increase as economic conditions worsen,

a relationship verified empirically by Raphael and Winter-Ember (2001). The identifying

assumption may be violated if high-scoring cities experience different macroeconomic shocks

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than low-scoring ones.19 In the main specification, I control for county-level unemployment

rates to partially address this concern. As a robustness check, I also present results identified

only by comparing cities with similar unemployment rate shocks. Specifically, I bin cities

into ten deciles of the change in the unemployment rate from 2005–2007 to 2008–2011 and

estimate regressions with recession decile × year fixed effects, which has almost no impact

on the results.

A second concern is that the program scale-up occurred as part of the larger American

Recovery and Reinvestment Act, a broad-based stimulus package which allocated over $490

billion between 2009 and 2011 for an array of programs to support the struggling economy.20

Correlation between treatment status and ARRA funding could violate the identifying as-

sumption. I address this potential issue in two ways. I collect data on grants and contracts

issued as part of ARRA from the Federal Procurement Data System (FPDS) and aggregate

local ARRA spending to the ZIP code-year level. I match these data to the subset of cities

in my data that I could match to ZIP codes and control for local ARRA spending in the

regressions. I also show that although there is no difference in local ARRA funding among

cities within a narrow bandwidth of the threshold, the main results hold when considering

only such cities.

Finally, for the IV estimates to recover the causal effect of police on crime, an exclusion

restriction is required. Specifically, grant receipt can only impact crime through its effect

on police manpower. Statutorily, hiring grants could only be used for police hiring, as dis-

cussed above in Section 2.3, which reduces concern that grant funding worked to reduce

crime through other channels. However, as noted in an existing public finance literature

on the so-called flypaper effect (e.g. Hines and Thaler 1995, Gordon 2004), even tagged

grants such as COPS grants could be fungible. To further limit concerns over the exclusion

19One should note that local fiscal conditions played a role in determining grant allocations,as discussed in Section 2, so we might expect high-scoring cities to be more severely affected bythe recession. Given the findings in the literature, this should bias the reduced form relationshipbetween grant receipt and crime rates towards zero.

20See https://www.cbo.gov/publication/42682.

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restriction, I show in Figure A-5 that neither civilian police employees nor total police expen-

ditures increased among grantees using a subset of cities with available budget data. While

I cannot definitively rule out that grant money was spent outside the police department

through careful budgetary manipulation, it is difficult to believe any such spending would

have immediate impacts on crime.

3.4.2 Why Not Regression Discontinuity?

A regression discontinuity (RD) design would seem appropriate given the application score-

based funding allocations. One could look for a discontinuity in the pre-post change in police

(first stage) and crimes (reduced form) at the score threshold and obtain a causal estimate

of the effect of police on crime by dividing the reduced form by the first stage.

In practice, the RD design is not well suited to this context for several reasons. First,

a key identifying assumption of the RD design is violated. As discussed in Section 3.5 and

illustrated in Figure 3.3, cities just above the threshold differ from those just below on several

dimensions at the time of application. In particular, city size, police per capita, cost-weighted

crime per capita, and the local unemployment rate all appear to increase discontinuously at

the application score threshold, with the RD estimates statistically significant for population

and unemployment. The difference in differences approach, which includes city fixed effects,

relies only on a parallel trends assumption.

Second, an RD design introduces concerns over statistical power. Power depends largely

on sample size and the variability of the outcome of interest – one can reliably detect smaller

effect sizes as N grows and as the variance of y shrinks. Relative to most applications of

the RD design, the available sample for studying the COPS program is quite small. My

sample includes 4,327 applicant cities, with only about 2,100 within one standard deviation

of the cutoff and only about 1,100 within 0.5 standard deviations. Further, the most natural

specification would use changes in police and crime rates as the outcomes of interest, both

of which exhibit significant variability relative to effect sizes one would expect. For example,

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my difference in differences estimate of the effect of grant receipt on cost-weighted crimes

per capita is -25, while the standard deviation of changes in cost-weighted crimes per capita

is 211.

In Appendix B and Table A-3, I formalize this concern with explicit power calcula-

tions. The calculations indicate that even under very generous assumptions, an RD is not

sufficiently powered for an analysis of violent crimes or cost-weighted crimes based on the

variability in the outcome and small sample sizes. The RD is barely powered to examine

police and property crime outcomes, but the closeness suggests that under more realistic

estimation approaches (for example, allowing functional forms to vary on either side of the

cutoff), the design lacks sufficient statistical power for even these less noisy outcomes.

I do, however, use insights from the RD literature to probe the robustness of my difference

in differences estimates. I show that results hold when considering only cities in a narrow

bandwidth around the score threshold, for whom the assumption of random assignment of

grant offers is most credible. I also illustrate that results in the primary specification are not

attainable when replacing the true cutoffs with placebo thresholds. Finally, I present simple

regression discontinuity estimates in Figure A-3. Consistent with the arguments above, the

RD estimates are quantitatively similarly to the difference in differences estimates but much

less precisely estimated.

3.5 Results

Figure 3.5 plots the coefficients on interactions between a high score indicator and year fixed

effects. Coefficients are normalized to 2008. I present the corresponding regression coeffi-

cients in Table A-4. Circles plot the results where the dependent variable is sworn officers

per 10,000 residents. Coefficients hover near zero prior to 2008, indicating that treatment

and control cities follow similar trends prior to the program. However, coefficients become

positive and statistically significant beginning in 2009. Relative to low-scoring applicants,

cities above the threshold employ nearly one additional sworn officer per 10,000 in 2010.

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As a placebo check, I repeat the dynamic first stage specification where civilian employees

per 10,000 and log police expenditures per capita are the dependent variables of interest.

Civilian employees are reported in the LEOKA dataset, while I obtained data on police

spending from the Annual Survey of Governments.21 Treatment and control cities exhibit

no measurable difference in civilian employment or expenditures both before and after 2009.

Squares in Figure 3.5 plot the results where the dependent variable is victimization cost-

weighted crime per capita. The coefficients follow an inverse pattern to those for police.

Pre-period coefficients are near zero and statistically insignificant, again indicating parallel

trends prior to application. Relative to low-scoring cities, high-scoring cities experience a

decline in cost-weighted crimes beginning in 2009. One year out from the program, crime

cost per capita is about $31 lower in treatment cities. As of 2010, the implied Wald estimate

is that one additional sworn officer reduces victimization costs by $310,000 ($31 × 10,000

to account for the different denominators). Scaling by the pre-program means for marginal

cities, this estimate corresponds to an elasticity of about -1.1.

Figure A-6 illustrates the sensitivity of the results to the inclusion or exclusion of city-

specific trends. The figure suggests that parallel pre-trends hold in either case, although the

pre-period coefficients are larger when trends are excluded. I opt for using city-trends in the

main estimates both to be conservative and because their inclusion improves the statistical

precision of the first-stage relationship between grant receipt and police per 10,000.

Table 2 presents the main difference in differences estimates. The first stage estimate,

presented in Column 1, suggests that police rates increase in treatment cities by 0.723 sworn

officers per 10,000 over the period 2009–2014. The estimate is highly significant, with an

F-statistic of 20.96, indicating that the interaction High × Post satisfies the instrument

relevance condition by conventional standards. The reduced form estimate, shown in Column

2, indicates that relative to the control group, treatment cities experience reductions in cost-

weighted crime per capita of $25.43 in the post-program period. The estimated coefficient is

21Note that these results use a subset of the data because only a subset appear in the ASG. Seethe Table notes.

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statistically significant at the 1% level. Columns 3-4 show OLS and IV estimates of the effect

of police on crime. The OLS estimate illustrates the standard simultaneity bias result. The

coefficient is positive and statistically significant, implying that more police are associated

with a slight increase in crime costs. On the other hand, the IV estimate indicates that an

additional officer per 10,000 reduces cost-weighted crime per capita by $35.17. The implied

elasticity of victimization costs with respect to police force size is -1.17.22

3.5.1 Robustness

Relevance of Application Score Thresholds

While the identification strategy does not require random assignment of grant offers, one

could make the case that grant offers are approximately randomly assigned for cities close

to the cutoff due to the inherent randomness of the exact threshold locations (Lee and

Lemieux, 2010). Motivated by this observation, I repeat the first stage and reduced form

estimates using only cities within varying bandwidths of the threshold. The results are

presented in Panel A of Figure 3.6. In both cases, the point estimates are quite similar

regardless of the bandwidth. When using only cities within 0.25 standard deviations of the

threshold (N = 558), the first stage and reduced form coefficients are 0.65 and -26.87, while

the coefficients using the full sample are 0.723 and -25.43. Estimates using the narrower

bandwidths are less precise, however, due to shrinking sample sizes. Still, the similarity of

the main estimates to those obtained using a sample for whom the assumption of random

assignment is plausible lends further credibility to the results.

I also test whether exceeding the score threshold, whose location is plausibly random,

rather than simply having a high application score, drives the police increases and crime

declines. Specifically, I estimate the first stage and reduced form equations coding cities as

treated if their score was above the cutoff + p, where p is a perturbation. If crossing the

22Table A-5 examines the sensitivity of the IV estimate to including controls in the regressions.Results are similar when including and excluding the basic controls and when adding a control forpopulation.

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threshold, rather than the score itself, is the relevant distinction, the estimates should be

largest (in absolute value) when using the true cutoff. As shown in Panel B of Figure 3.6,

this is indeed the case. Both the first stage and reduced form coefficients are larger when

using the true threshold than using narrowly perturbed thresholds in either direction. The

reduced form estimate is largest when using the cutoff + one standard deviation, but the

estimate is very noisy given that only 102 cities are considered treated under this placebo

cutoff.

Accounting for Differential Recession Exposure

In Section 4, I highlighted that the acceleration of the Great Recession coincided with the

timing of the program and, given the application score inputs, treatment cities may be dif-

ferentially affected by the recession. Although the main results condition on county-year

level unemployment rates and per capita income, I present a further robustness check here.

Specifically, for each city, I compute the change in the county unemployment rate from 2005–

2007 to 2008–2010. I then bin cities into deciles of this change and estimate regressions with

recession decile × year fixed effects. Results from this exercise are presented in Table 3.

In Column 1, I estimate the main difference in differences specification with the unemploy-

ment rate on the left hand side. The estimate indicates that treatment cities are indeed

more exposed to the poor macroeconomic conditions, with unemployment rates increasing

by 0.8 percentage points in 2009-2014 relative to the control group. Once one conditions

on recession decile × year effects, however, the relationship between treatment status and

recession exposure disappears, as indicated in Column 2. Columns 3-4 demonstrate that

the IV estimate of police-crime relationship is unaffected by the inclusion of the recession

× year effects. In other words, the results are unchanged when identifying effects only off

cities who experience similar recession exposure, suggesting that the differential exposure of

the treatment group does not drive the results.

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Accounting for Differential Stimulus Spending

The second, and related, identification concern was that treated cities may receive differential

amounts of non-COPS ARRA funding. If high-scoring cities received more aid, the stimulus

funding, rather than increased police, could explain the crime declines in treatment cities. I

collected data on all ARRA grants and contracts from the Federal Procurement Data System

and aggregated by ZIP code, year, and originating federal agency (DOJ versus non-DOJ).23

I then aggregated to the FIPS place code level and matched the ARRA funding data to the

3,277 cities in the sample that could be matched from their place codes to a set of ZIP codes.

Using these data, I repeat the main specification but control for log per capita non-DOJ

ARRA spending at the city-year level. Table 4 presents the results. Column 1 repeats the

main specification from Table 2. Column 2 presents the corresponding estimate using only

the 3,277 cities matched to ZIP codes, with the point estimate changing very little relative

to the main specification. Column 3 adds a control for log local ARRA spending per capita.

Again, the coefficient on police is very similar, suggesting that differential stimulus spending

cannot explain the crime declines in treated cities.

Figure A-7 plots log per capita ARRA funding over the period 2009–2013 as a function

of the application score. DOJ-originating funding increases discontinuously at the threshold,

lending credibility to the FPDS data and the matching process. On the other hand, non-

DOJ funding is smooth through the cutoff. As shown in Figure A-8, there is no disparity

in local ARRA spending among treatment and control cities close to the threshold. The IV

estimate is of similar magnitude using only such cities, however, suggesting that differential

stimulus spending cannot explain the results.

3.5.2 Results by Crime Type

In the main analysis, I focus on cost-weighted crime per capita both to simplify presentation

and because this variable captures the relevant outcome for policymaking. Also of interest,

23See https://www.fpds.gov/fpdsng_cms/index.php/en/.

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however, are results broken down by crime type. Figure 3.7 shows the effect of exceeding

the cutoff over time on the index crime categories. Violent crime is the sum of murder, rape,

robbery, and aggravated assault. Property crime is the sum of burglary, larceny, and auto

theft.24 In both cases, the pattern is quite similar to that for cost-weighted crime. Treatment

and control cities follow similar trends in the pre-period, but a difference emerges beginning

in 2009. Corresponding regression results, shown in Table A-4, indicate that relative to cities

below the cutoff, those above experience declines in violent (property) crimes of 3.72 (14.25)

per 10,000 in 2010.

IV estimates for the index crime categories, as well as for individual crime types, are

presented in Table 5.25 Each regression is identical to that in Table 2, Column 4, except that

crimes per 10,000 is the outcome of interest. The estimates indicate that each additional

sworn officer is associated with 4.27 fewer violent crimes and 15.39 fewer property crimes.

Implied elasticities are -1.3 and -0.81, which conforms to a consistent finding in the literature

that crime-police elasticities are larger for violent than for property crimes (Chalfin and

McCrary, 2018). My estimated magnitudes are larger than most in the literature, however.

For example, Evans and Owens (2007), find elasticities of -0.99 and -0.26.

Among violent crimes, the results are negative and statistically significant for murder,

rape, and robbery, while the estimate is not significant for assault. I find that an additional

officer prevents .11 murders, .53 rapes, and 1.98 robberies. While robbery accounts for just

15% of all violent crimes, it accounts for nearly half of the estimated impact of police on

violent crime. This result is in line with Evans and Owens (2007), who find that robbery

responds most to police increases in terms of elasticities, and with Abrams (2012), who

finds that robbery is a particularly deterrable crime type. The estimated impact of police

on murder is also noteworthy. Due to the high variability in murder rates, statistically

significant estimates of the effect of police on crime, even at the 10% level, are rare in the

24For crime type definitions, see https://www2.fbi.gov/ucr/cius_04/appendices/appendix_02.html.

25Reduced form, rather than IV, estimates are reported in Table A-7

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literature. Although not precisely estimated, the point estimate implies that one life can be

saved by hiring about 9.5 new police officers.

Among property crimes, the estimates indicate that police are associated with statisti-

cally significant declines in larceny (-15) and auto theft (-5.15). I find that police increase

burglaries, although the coefficient is not statistically different from zero. Consistent with

existing studies, the effect on auto thefts is particularly strong, implying an elasticity of

-3.35. The estimate similar to that in Lin (2009), who finds an elasticity of about -4, but

larger than most existing work.

3.5.3 Geographic Spillovers

Analyses of place-based policies often examine whether treatment effects spillover to neigh-

boring regions. For example, increased police in one jurisdiction may reduce crime in neigh-

boring jurisdictions by increasing the probability of apprehension near town borders. Alter-

natively, increased police in one jurisdiction may displace criminal activity to neighboring

areas (Blattman et al., 2017). If local police increases carry positive or negative (i.e. dis-

placement) spillover effects, one needs to take such spillovers into account when considering

the aggregate welfare consequences associated with a program such as COPS.

Although a rigorous examination of spillovers is beyond the scope of this paper, I present

a simple test here. Starting with the full sample of municipal police departments with valid

crime data (N = 12, 245), I divide cities into four groups: losing applicants (N = 3, 536),

winning applicants (N = 791), non-applicants in the same county as a losing applicant

(N = 2, 837), and non-applicants in the same county as a winning applicant (N = 3, 673).

Non-applicants in counties with no applicants are dropped, leaving a sample of 9,369 mu-

nicipalities. I then estimate a dynamic difference in differences specification (equation 4),

interacting indicators for each group with the year effects. As in the main analysis, I nor-

malize coefficients to the losing applicants.

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The estimates allow a simple comparison of changes in crime for jurisdictions near treated

cities and jurisdictions near control cities. Figure 3.8 shows the results. Relative to the

large reduction in crime in treated cities (circles), there is little change in crime in non-

applicants near treated cities (squares) and non-applicants near control cities (diamonds).

The similarity in the trends for jurisdictions near treated and control cities suggests that

geographic spillovers associated with local police increases were negligible.

3.5.4 Mechanisms

As with other crime control policies, police hiring may reduce crime through two channels

– deterrence or incapacitation. Standard economic models of crime, such as Becker (1968),

predict that police deter crime by raising the expected cost associated with criminal behavior,

causing fewer potential offenders to engage in crime. However, police may also increase the

number of individuals detained or incarcerated, which would reduce crime by incapacitating

potential offenders. By which mechanism police reduce crime is of considerable interest

because incapacitation is associated with increased incarceration costs in addition to the

police wage bill.

In practice, my estimates almost surely identify a combination of deterrence and incapac-

itation effects (Chalfin and McCrary, 2017). To get a sense of the relative importance of the

two mechanisms, I examine whether COPS-induced police force increases were associated

with increases in arrest rates. As highlighted in Owens (2012), the intuition behind this test

is that for police to have an incapacitation effect, hiring police must increase the number of

arrested potential offenders. Hence, one can rule out that incapacitation plays a large role in

the estimated crime declines if arrests do not increase along with the manpower increases.26

26To the extent that police reduce crime by means other than incapacitation or deterrence, thearrest rate test cannot distinguish between deterrence and other non-incapacitation explanations.For example, police may substitute from arresting offenders to activities that raise money for themunicipal government. However, existing work such as Goldstein et al. (2018) highlights thatsuch activities typically do not enhance public safety. Additionally, much of the existing workon the police-crime relationship, such as Owens (2012) and Weisburd (2016) has highlighted theimportance of deterrence as a mechanism by which police reduce crime.

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For this exercise, I rely on data from the UCR Arrests file, which reports yearly arrest

counts by offense category at the agency level. Not all agencies that report crimes also

submit arrest data and I use a sample of 3,914 (of 4,327) cities with valid arrest data.

Table 6 reports IV estimates of the effect of police increases on arrests per 10,000. I show

results separately for violent and property crime arrests. For reference, because the sample

is slightly different, I also show the corresponding estimates for violent and property crimes

when using the arrests sample.

Columns 1-2 indicate that an additional officer is associated with 4.4 fewer violent crimes

and .17 additional violent crime arrests. The estimated impact on violent arrests is not

statistically significant and implies a small arrest-police elasticity of .17. Similarly, columns

3-4 demonstrate that an additional officer reduces property crimes by 18 and reduces property

arrests by .5. The arrest impact is again not statistically different from zero. On net, the

evidence suggests that arrests did not increase with the police force expansions, which is

consistent with a deterrence mechanism underlying the estimated crime reductions.

3.5.5 Treatment on the Treated Program Effects

The first stage regression of police per 10,000 residents on High×Post recovers an intent-to-

treat estimate of the effect of a hiring grant offer on police force size. The estimate is an ITT,

rather than a treatment on treated (TOT) estimate, because control cities can receive hiring

grants during later funding rounds, eroding the disparity in treatment status between high

and low scoring cities. Note that such an erosion has no bearing on the estimated police-

crime relationship. Control cities becoming treated impacts both the first stage and reduced

forms, and the IV estimate is a TOT estimate of the effect of police on crime. However, one

may also be interested in the TOT effect of hiring grants on police force size. For example,

to estimate the total number of officers added by program, one should use the TOT rather

than the ITT.

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A very simple estimate of the TOT can be obtained by scaling the pre-post (ITT) dif-

ference in police by (one minus) the fraction of control cities who are ever treated in the

post-period.27 11% percent of control cities are treated at some point over 2010–2014. Hence,

a TOT estimate is 0.723/0.89 = 0.81 sworn officers per 10,000 added by each grant offer.

Alternatively, one can deal more rigorously with the dynamic relationship between police

and grants and estimate TOT effects at years 1,2,..,5 since a grant offer. I estimate dynamic

TOT effects using a recursive method outlined in Cellini et al. (2010). The intuition of the

strategy is as follows. The treat-control difference in police in 2009 is both an ITT and TOT

estimate of the effect of grants on police in the year of grant receipt. In 2010, the treat-

control difference is an ITT estimate because some control cities become treated. One can

estimate directly the extent to which the disparity in treatment status erodes. Further, the

2009 ITT offers an estimate of the increase in police in 2010 for control cities that become

treated in 2010. Hence, an estimate of the TOT in 2010 is the 2010 ITT estimate minus the

fraction of control cities who become treated multiplied by the 2009 ITT estimate.

To operationalize this intuition, I estimate the following two equations:

Fundedit = πt ×Highi × κt + κt + φi + εit

Policeit = θITTt ×Highi × κt + κt + φi + εit

The πt’s measure the relationship between crossing the threshold in 200 and grant receipt

in each year. The θITTt ’s are ITT estimates of the effect of crossing the threshold in 2009 on

police, identical to those presented in Figure 3.5. The TOT estimates are then

θTOT2009 = θITT2009

θTOT2010 = θITT2010 − π2010θTOT2009

θTOT2011 = θITT2011 − π2010θTOT2010 − π2011θ

TOT2009

27Figure A-4 shows the fraction of cities in the treatment and control group applying for (PanelA) and receiving (Panel B) hiring grant funding in each program year.

212

and so on. To obtain standard errors, I bootstrap the TOT estimation procedure using 500

iterations of city-level resampling.

Results are presented in Table 7, with the corresponding estimates shown graphically in

Figure A-9. Cities below the cutoff in 2009 are about 7% more likely to receive treatment

in 2010 than those above, indicating that the 2010 ITT is an underestimate of the one-

year TOT effect. Correspondingly, the 2010 TOT estimate is 0.972, compared with an ITT

estimate of 0.935. On the other hand, cities above the threshold in 2009 are slightly more

likely to receive additional funding in each year 2011–2014. As a result, the TOT estimates

become slightly smaller then the ITT estimates beginning in 2012. On net, this exercise

suggests that the ITT estimates are a reasonably good approximation to TOT effects, which

is unsurprising given the relatively small treatment-control differences in grant receipt during

2010–2014 as compared to 2009.

3.5.6 Heterogeneity

An analysis of treatment effect heterogeneity may offer insights as to why the estimated

impacts of police on crime are so large relative to the literature.28 To get a sense of the

estimates we might expect, consider a model of optimal police force size. Cities hire police x

to minimize total costs, which is the sum of victimization costs, v× c(x), where v is the cost

associated with each crime and c(x) is the number of crimes as a function of police, and the

cost of employing police, w × x, where w is the wage. In other words, the city’s problem is

minx

vc(x) + wx

The first order condition for an interior solution is −vc′(x) = w. My IV estimate of −vc′(x)

is about $350,000 with a lower 90% confidence bound of $96,508 (Table 2). The average

28One possibility is that I use smaller cities than most existing studies, and treatment effectsare larger in these cities. Figure A-10 demonstrates that this is not the case. While police forcesincrease most for small cities, crime rates also decrease most. There is no clear relationship betweencity size and the treatment effect or crime-police elasticity.

213

police officer wage for cities in my sample is about $67,000, while the true marginal cost of

adding an additional officer is thought be around $130,000. The large estimated marginal

benefit relative the marginal cost appears inconsistent with optimization at the city level.

Municipalities ought to have hired police until the marginal benefit equals the wage.

One potential explanation could be that cities were forced away from their optimal police

levels due to fiscal stress and tightening budgets during the Great Recession. To test for

this, I compute each city’s change in the unemployment rate from 2007-2009, δi, to proxy for

recession exposure. I then examine heterogeneous effects by δ using both a nonparametric

and parametric strategy. For the nonparametric approach, I split the sample into quintiles of

δi and interact the quintiles with the instrument, High×Post, in the first stage and reduced

form. For the parametric approach, I simply interact the instrument linearly with δi.

Panel A of Figure 3.9 shows the first stage and reduced form effects. On average, police

increases and crime reductions associated with the crossing the threshold are larger for cities

with more severe recession exposure. Such a pattern is apparent from both the parametric

and nonparametric approaches. The estimated effect of grant receipt on police per 10,000

is about 0.5 for cities in the bottom quintile but over 1 for cities in the top quintile. Corre-

sponding effects on crime cost per capita are -$12 for cities in the bottom quintile and -$50

for cities in the top quintile.

Panel B converts the first stage and reduced form estimates into IV estimates of the

effect of police on crime that vary by recession exposure. The figure highlights that while

both the first stage and reduced form effects are largest for cities enduring worse economic

conditions, the reduced form increases (in absolute value) more dramatically than does the

first stage with δ. Hence, the treatment effect of additional police is largest for the cities

most exposed to the recession. The parametric approximation implies that the return to

an additional officer is close to zero for cities with increases in unemployment of around

2 percentage points, while the return is around $60 per capita in cities with 8 percentage

point increases in the unemployment rate. Overall, the evidence suggests that the returns to

214

additional police were highest for cities under more fiscal distress, which is consistent with

the hypotheses that the recession forced cities below their optimal police levels.

Additional evidence in favor of such a hypothesis can be seen by comparing the treatment

effects of police hiring versus not-firing (or less firing). As is apparent in the raw data

(Figure 3.4), losing applicants tended to experience significant reductions in police forces

beginning in 2009, implying that in many cases, hiring grants prevented firings that would

have otherwise taken place. I examine whether the treatment effects of hiring and not-firing

differ by splitting the sample into predicted firer and predicted hirer groups and estimating

the main IV specification in each subsample.

First, using only control cities, I regress the 2008-2010 log change in police per 10,000

residents on 2008 controls and size group indicators. The estimated coefficients are used to

construct a predicted change in police for all cities, and I split cities at the median predicted

change to form predicted firer (below median) and predicted hirer (above median) groups.

Figure 3.10 shows the trends in police per 10,000 for treatment and control cities by predicted

firer and hirer status. Panel A illustrates that among predicted firers, police levels fall in

both treated and control cities, with hiring grants appearing to reduce or postpone firings.

On the other hand, Panel B shows that among the predicted hirers, control cities experience

slight reductions in police beginning in 2009 while treated cities increase their police levels

on average.

Table 8 shows IV estimates separately for the two city groups. Note that the predicted

change in police, and therefore predicted firer/hirer status, is highly correlated with my

measure of recession exposure – cities in more recession-exposed areas tend to be predicted

firers and vice versa.29 Hence, we should expect a similar pattern in the results as in the

analysis of heterogeneity above, which is indeed the case. The estimated impact of an

additional officer is larger for predicted firers than predicted hirers, with implied crime-

police elasticities of -1.5 and -0.92, respectively. While caution is needed in interpreting the

29Figure A-11 documents the relationship between predicted change in police and recessionexposure.

215

coefficients – I cannot reject that the two coefficients are equal (p-value=0.55) – the pattern

of results is consistent with diminishing returns to police and with the view that poor fiscal

health forcing cities to cut back on police may explain the relatively large estimated treatment

effects.

3.6 Cost-Benefit Analysis

Given that police added by the program reduced crime, a natural question is whether the

COPS hiring program passes a cost-benefit test. The average grant carried a dollar value of

$295,974 per 10,000 residents (recall that grants covered three years of salary). If one uses

the simple TOT estimate above, a reasonable estimate of the number of officer-years per

10,000 residents added by the program is 0.8 officers × 4 years = 3.2 (four years because

grants covered three years salary with the expectation that the officer would be retained for a

fourth year). Hence, police forces increased by one for each $92,492 in grant funding. About

$874.4M was allocated to cities in my sample in 2009, implying that 9,454 officer-years were

added by the ARRA funding round. After accounting for deadweight loss associated with

raising government revenue, the federal cost is in the range of $1.14B. Most estimates in the

literature suggest that the annual cost of a fully-equipped police officer is around $130,000,

which implies that local governments spent an additional $600M on the estimated police

increases. Hence, a reasonable estimate of the program’s total cost is about $1.75B.

Given estimates of total cost and officer-years added, the program is cost-effective if the

social value added by one officer-year exceeds $1.75B / 9,454 = $185,107. The IV point

estimate in Table 2 indicates that each officer-year contributes $352,000 in social benefit

from crime reduction. Under this assumption, the program easily passes a cost-benefit test.

If one instead uses the lower 95% confidence bound, the social benefit associated with each

officer is around $54,000 and the program appears cost-ineffective.

Alternatively, one could estimate the social value per officer by summing the estimated

coefficients for each individual crime type in Table 5, weighting by the associated social cost

216

for each crime type. Such a computation is sensitive both to the coefficients and crime cost

estimates used. Further, given the incredibly high social costs associated with murder, such

a computation is especially sensitive to the estimated murder effect. At a VSL estimate of

$5 million, the point estimate in Table 5 implies that an officer provides $535,000 in social

benefit due to homicide reduction alone. On the other hand, using the cost estimates in

Chalfin et al. (2016b), the social benefit per officer attributable to the robbery, larceny, and

auto theft reductions is $160,548, which is close to but does not exceed the required $185,000.

On net, the evidence suggests that the program is cost-effective, but it is difficult to say for

sure. Similarly, the evidence suggests that police hiring more generally is cost effective for

the average city in my sample, consistent with Chalfin and McCrary (2018). However, local

governments may want to weigh the costs and benefits across an array of crime prevention

tools when choosing optimal policy. For example, Lochner and Moretti (2004) argue that a

crime reduction equivalent to that provided by an additional police officer can be obtained

by increasing the high school graduation rate and that public spending on education carries

a higher overall benefit-cost ratio than police spending.

As a component of the American Recovery and Reinvestment Act, COPS program fund-

ing was intended, at least in part, to create or save police officer jobs. The degree to which

ARRA spending increased employment has been the subject of much debate. The academic

literature has focused on estimating the cost per job created by the Recovery Act, relying

on cross-state variation in the generosity of transfers received from the federal government.

Despite apparently similar methodologies, existing estimates vary widely. Chodorow-Reich

et al. (2012) estimate a cost per job-year of $26,000, with most job-creation in the private

sector. Conley and Dupor (2013) find that most jobs created were in government and es-

timate cost per job-year of $200,000. My analysis implies a cost per job-year of $92,500,

which is on the larger end but certainly within the range of existing estimates. Given the

reasonable cost per job-year and the large ensuing crime reductions, the benefit-cost ratio

associated with police hiring grants may compare favorably with other stimulus spending.

217

Such programs may be more politically feasible, as well, since spending under the heading

of crime reduction is more likely to gain bipartisan support than many federal programs.30

3.7 Conclusion

In this paper, I exploit a natural experiment to circumvent the endogeneity of police hiring

and estimate the causal effect of police on crime. My identification strategy relies on the

fact that COPS hiring grant funding in 2009 was distributed through an application process.

I compare the change over time in police and crime in cities with application scores above

and below the funding threshold, with the underlying premise that rejected applicants are

a valid control group for accepted ones. Studying dynamics non-parametrically, I show that

police and crime follow similar trends in high and low scoring cities prior to 2009, but trends

diverge as high scoring cities receive hiring grant funding. The corresponding instrumental

variables estimates imply that an additional officer per 10,000 residents reduces victimization

costs by about $35 per capita, with an implied crime-police elasticity of -1.17. The estimated

magnitude suggests that expanding the police force is easily cost-effective for the average

city in my sample.

The main results are robust to a series of specification checks, including relying on only

cities with scores close to the threshold and therefore for whom the assumption of randomly

assigned treatment is plausible. An examination of individual crime types reveals that the

treatment effects are larger for violent than for property crimes and most pronounced for

robbery and auto theft. I also find evidence that treatment effects are largest for cities

most exposed to poor macroeconomic conditions during the Great Recession. Such a result

is consistent with the theory that fiscal distress caused cities to reduce their police forces

below optimal levels, which could explain the large magnitudes of my estimates relative to

the literature.

30See, e.g. Bipartisan House group seeks to bolster nation’s police forces with COPS bill, MileLillis for thehill.com, 5/14/2011.

218

Whether the COPS hiring program passes a cost-benefit test depends on the social ben-

efit attributable to an additional officer year. The point estimate in my main specification

implies that the program is easily cost-effective. I estimate that one officer-year was added

for every $95,000 spent by the federal government and that the social benefit associated with

the ensuing crime reduction on the order of $350,000. Under more conservative assumptions,

the program fails a cost-benefit test. The results highlight that fiscal support to local gov-

ernments for crime prevention may offer large returns, especially during bad macroeconomic

times.

219

Figure 3.1: COPS Hiring Program Funding Over Time

0

500

1000

1500

Millions

1995 2000 2005 2010 2015Year

Notes: Historical appropriations data from James (2013).

220

Figure 3.2: Distribution of Application Scores and Funding Probability

0

.2

.4

.6

.8

1

Frac

tion

Fund

ed

0

50

100

150

200

250

Num

ber o

f App

lican

ts

-4 -3 -2 -1 0 1 2 3 4Score Around Cutoff

Number of Applicants (Left Axis)Fraction Funded (Right Axis)

Notes: An observation is a city. Figure plots of histogram of the 2009 application score relative tothe cutoff (left axis). The application score is standardized, so the units are standard deviations.Figure also plots the fraction of applicants in each bin (width=0.25 score points) that received ahiring grant (right axis).

221

Figure 3.3: Baseline Characteristics by Application Score

0

2

4

6

8

0

50

100

150

200

250

-4 -2 0 2 4Score Around Cutoff

RD Estimate: 1.2 (.64)

Population

20

22

24

26

28

0

50

100

150

200

250

-4 -2 0 2 4Score Around Cutoff

RD Estimate: .32 (.96)

Police Per 10,000

50

100

150

200

250

300

0

50

100

150

200

250

-4 -2 0 2 4Score Around Cutoff

RD Estimate: 8.48 (7.71)

Crime Cost Per Capita

6

8

10

12

0

50

100

150

200

250

-4 -2 0 2 4Score Around Cutoff

RD Estimate: 1.14 (.36)

Unemployment Rate

Notes: Each panel plots local linear regression fits of the denoted outcome (right axis) estimatedseparately for cities above and below the threshold over a histogram of the application score (leftaxis). Legend denotes the RD estimate using a triangular kernel and the IK optimal bandwidth.Population in ten thousands. Population, police, and crimes are from the UCR and measured in2008. Unemployment rate is from the ACS and measured in 2009.

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Figure 3.4: Trends in Police and Crime by Treatment Status (Raw Data)

19.5

20

20.5

21

21.5

2004 2006 2008 2010 2012 2014

Above CutoffBelow Cutoff

Panel A: Police Per 10,000

300

350

400

450

500

550

2004 2006 2008 2010 2012 2014

Above CutoffBelow Cutoff

Panel B: Crime Cost Per Capita

Notes: Figure plots annual averages of police per 10,000 (Panel A) and crime costs per capita(Panel B) by treatment status (above or below the cutoff). Treatment group means are normalizedto be equal to the control group in 2008.

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Figure 3.5: Effect of Exceeding the Threshold on Police and Crime

-100

-50

0

50

100

-1.5

-1

-.5

0

.5

1

1.5

2004 2006 2008 2010 2012Year

Police per 10,000 (Left Axis)Crime Cost per Capita (Right Axis)

Notes: Figure plots coefficients on interactions between year indicators and an indicator for whetherthe 2009 application score exceeded the threshold. Regressions also include city fixed effects, year× size group fixed effects, and city-specific linear trends. 95% confidence intervals are constructedfrom standard errors clustered at the city level.

224

Figure 3.6: Sensitivity of First Stage and Reduced Form Estimates

-75

-50

-25

0

25

50

75

-1.5

-1

-.5

0

.5

1

1.5C

oeffi

cien

t on

Hig

h x

Post

0 1 2 3 4Bandwidth

Police per 10,000 (Left Axis)Crime Cost per Capita (Right Axis)

Panel A: Changing Bandwidth

-100

-75

-50

-25

0

25

50

75

100

Coe

ffici

ent o

n H

igh

x Po

st

-1.5

-1

-.5

0

.5

1

1.5

-1 -.5 0 .5 1Change to Cutoff

Police per 10,000 (Left Axis)Crime Cost per Capita (Right Axis)

Panel B: Placebo Cutoffs

Notes: Figures plot coefficients and 95% confidence intervals on High × Post from regressionswhere police per 10,000 (crime cost per capita) is the outcome of interest. Regressions includecontrols, city fixed effects, year × size group fixed effects, and city-specific linear trends. Panel Aplots coefficients when only departments within the denoted bandwidth are used. Panel B plotscoefficients when using perturbed score cutoffs (i.e., the coefficient at -0.5 is the coefficient obtainedwhen treating the cutoff as if it were 0.5 points below the true cutoff).

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Figure 3.7: Effect of Exceeding the Threshold on Violent and Property Crimes

-30

-20

-10

0

10

20

30

-12

-8

-4

0

4

8

12

2004 2006 2008 2010 2012Year

Violent (Left Axis)Property (Right Axis)

Notes: Dependent variable is crimes per 10,000. Figure plots coefficients on interactions betweenyear indicators and an indicator for whether the 2009 application score exceeded the threshold.Regressions also include city fixed effects, year × size group fixed effects, and city-specific lineartrends. 95% confidence intervals are constructed from standard errors clustered at the city level.

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Figure 3.8: Testing for Geographic Spillovers

-100

-50

0

50

Crim

e C

ost P

er C

apita

2004 2006 2008 2010 2012Year

TreatedNon-Applicant with Treated in CountyNon-Applicant with Control in County

Notes: Dependent variable is crime costs per capita. Figure plots coefficients on interactionsbetween treatment status indicators and year effects. Cities are grouped into four categories:winning applicants (treated) (N=791), losing applicants (control) (N=3,536), non-applicants inthe same county as a treated city (N=3.673), and non-applicants in the same county as a controlcity (N=2,837). Coefficients are normalized to the losing applicants. Each regression includescontrols, size × year effects, city trends, and city fixed effects.

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Figure 3.9: Heterogeneous Effects by Recession Exposure

-80

-60

-40

-20

0

20

40

60

80

Crim

e C

ost p

er C

apita

-1.5

-1

-.5

0

.5

1

1.5Po

lice

per 1

0,00

0

0 2 4 6 8 10Change in Unemployment Rate

Police (Bins) Police (Linear)Crime (Bins) Crime (Linear)

Panel A: First Stage and Reduced Form

-80

-60

-40

-20

0

20

40

60

80

Crim

e C

ost p

er C

apita

-80

-60

-40

-20

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60

80

Crim

e C

ost p

er C

apita

0 2 4 6 8 10Change in Unemployment Rate

BinsParametric

Panel B: IV Estimates

Notes: Change in Unemployment Rate is the 2007-2009 change in the local unemployment rate.See text for additional details on computation.

228

Figure 3.10: Trends in Police for Predicted Firers and Hirers (Raw Data)

19

20

21

22

23

2004 2006 2008 2010 2012 2014

Above CutoffBelow Cutoff

Panel A: Predicted Firers

19

20

21

22

23

2004 2006 2008 2010 2012 2014

Above CutoffBelow Cutoff

Panel B: Predicted Hirers

Notes: Figure plots average police per 10,000 residents for cities above and below the fundingthreshold by predicted firer/hirer status. Treatment group means are normalized to be equal tothe control group in 2008. See text for details on sample construction.

229

Table 1: Summary Statistics for Applicant Cities

Above Cutoff Below Cutoff Total

Population (Ten Thousands) 6.996 2.467 3.295(21.74) (15.29) (16.74)

Unemployment Rate 9.552 6.976 7.447(4.020) (3.127) (3.454)

Family Income (Ten Thousands) 3.960 5.334 5.083(1.112) (2.164) (2.082)

Percent Black 20.76 7.753 10.13(22.51) (12.38) (15.59)

Percent Hispanic 15.19 10.05 10.99(20.67) (14.92) (16.25)

Percent Young Male 23.54 21.60 21.95(5.874) (6.909) (6.773)

Police Per 10,000 26.10 22.69 23.32(10.94) (11.26) (11.28)

Violent Crimes Per 10,000 93.20 56.83 63.47(51.00) (42.35) (46.24)

Property Crimes Per 10,000 497.4 267.6 309.7(228.2) (162.0) (197.1)

Crime Cost Per Capita 834.0 494.0 556.2(395.3) (322.0) (361.3)

Officers Funded Per 10,000 1.679 0 0.307(1.601) (0) (0.943)

Funding Per Capita 29.60 0 5.411(23.83) (0) (15.32)

Notes: Number of observations: 791 (above); 3,536 (below); 4,327 (total). Standard deviations inparentheses. Population, police, and crime are from the 2008 Uniform Crime Reports. Demographicand economic information are from the 2009 American Community Service (FIPS place code level).

230

Table 2: Difference in Differences Estimates

(1) (2) (3) (4)Police Crime OLS: Crime IV: Crime

High x Post 0.723*** -25.43***(0.158) (9.083)

Police 2.198*** -35.17**(0.710) (15.19)

Mean 22.85 689.23 689.23 689.23Elasticity - - .07 -1.17F-Stat 20.96 - - -Controls Yes Yes Yes YesSize x Year Effects Yes Yes Yes YesCity Trends Yes Yes Yes YesClusters (Cities) 4327 4327 4327 4327Observations (City-Years) 47597 47597 47597 47597

Notes: Standard errors clustered at the city-level in parentheses. Police is sworn officers per 10,000residents. Crime is cost-weighted crime per capita. Elasticity computed using pre-program meansfor marginal cities. Regressions include city fixed effects.

231

Table 3: Accounting for Differential Recession Exposure

(1) (2) (3) (4)UER x 100 UER x 100 IV: Crime IV: Crime

High x Post 0.797*** 0.0405(0.0845) (0.0380)

Police -39.32** -42.67**(15.86) (17.18)

F-Stat - - 19.89 19.34Controls No No No NoSize x Year Effects Yes No Yes NoRecession Decile x Year Effects No Yes No YesCity Trends Yes Yes Yes YesClusters (Cities) 4327 4327 4327 4327Observations (City-Years) 47597 47597 47597 47597

Notes: Standard errors clustered at the city-level in parentheses. UER × 100 is the unemploymentrate (on a scale from 0-100). Mean unemployment rate in 2008 is 5.9. Mean unemployment rate in2010 is 9.6. Police is sworn officers per 10,000 residents. Crime is cost-weighted crime per capita.Regressions include city fixed effects.

232

Table 4: Accounting for Other ARRA Spending

(1) (2) (3)Crime Crime Crime

Police -35.17** -36.79** -37.52**(15.19) (16.98) (17.18)

F-Stat 20.96 16.88 16.66Controls Yes Yes YesSize x Year Effects Yes Yes YesCity Trends Yes Yes YesARRA Spending No No YesClusters (Cities) 4327 3277 3277Observations (City-Years) 47597 36047 36046

Notes: Standard errors clustered at the city-level in parentheses. Table presents IV estimates.Dependent variable is cost-weighted crime per capita. Column (1) is the same as Column (4) inTable 2. Column (2) repeats the specification from Column (1) using only cities matched to ZIPcodes. Column (3) adds a control for log non-DOJ ARRA spending per capita at the city-yearlevel. Regressions include city fixed effects.

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Table 5: IV Estimates by Crime Type

(1) (2) (3) (4) (5) (6) (7) (8) (9)All Violent Murder Rape Robbery Assault All Property Burglary Larceny Auto Theft

Police -4.265** -0.107* -0.532** -1.984*** -1.309 -15.39** 2.747 -14.96*** -5.149***(2.022) (0.0601) (0.227) (0.554) (1.683) (6.674) (2.048) (5.494) (1.341)

Mean 75.16 .42 3.85 10.79 59.69 436.05 86.83 311.27 35.15Elasticity -1.3 -5.84 -3.16 -4.2 -.5 -.810 .72 -1.1 -3.35Controls Yes Yes Yes Yes Yes Yes Yes Yes YesSize x Year Effects Yes Yes Yes Yes Yes Yes Yes Yes YesCity Trends Yes Yes Yes Yes Yes Yes Yes Yes YesClusters (Cities) 4327 4327 4327 4327 4327 4327 4327 4327 4327Observations (City-Years) 47597 47597 47597 47597 47597 47597 47597 47597 47597

Notes: Standard errors clustered at the city-level in parentheses. Table presents IV estimates. Dependent variable is crimes per 10,000residents. First stage F-statistic is 20.96. Regressions include city fixed effects. Reduced form estimates are reported in Table A-7.

234

Table 6: IV Estimates, Crimes and Arrests

(1) (2) (3) (4)Violent Crimes Violent Arrests Property Crimes Property Arrests

Police -4.377** 0.173 -18.28** -0.498(2.093) (0.690) (7.256) (2.002)

Mean 75.52 23.02 439.74 76.77Elasticity -1.31 .17 -.940 -.15Controls Yes Yes Yes YesSize x Year Effects Yes Yes Yes YesCity Trends Yes Yes Yes YesClusters (Cities) 3914 3914 3914 3914Observations (City-Years) 43054 43054 43054 43054

Notes: Standard errors clustered at the city-level in parentheses. Dependent variable is crimes(arrests) per 10,000 residents. Each column presents a 2SLS regression where High× Post instru-ments for police per 10,000. Sample is the subset of the main sample with valid arrest reportingdata. Regression include city fixed effects.

235

Table 7: Dynamic TOT Effects of Grant Offers on Police

Police per 10,000

Year Funded ITT TOT

2009 .99*** .484*** .484***(.004) (.154) (.146)

2010 -.076*** .935*** .972***(.007) (.204) (.204)

2011 .05*** .801*** .851***(.009) (.251) (.252)

2012 .049*** .75** .742**(.009) (.303) (.292)

2013 .079*** .936*** .864***(.012) (.34) (.327)

2014 .06*** .578 .43(.01) (.366) (.328)

Notes: Dependent variable is police per 10,000 residents. Standard errors for ITT estimates areclustered at the city level. Standard errors for recursive TOT estimates are bootstrapped using 500iterations of city-level resampling. All regressions include city fixed effects, size group × year fixedeffects, and city trends. See text for details on computation of the TOT estimator.

236

Table 8: Testing for Asymmetric Treatment Effects

(1) (2)Predicted Firers Predicted Hirers

Police -45.42** -27.38(22.72) (19.76)

P-Val of Difference - .55Mean 653.21 718.73Elasticity -1.5 -.92First Stage Beta .61 .84F-Stat 14.56 9.02Controls Yes YesSize x Year Effects Yes YesCity Trends Yes YesClusters (Cities) 2164 2163Observations (City-Years) 23804 23793

Notes: Dependent variable is crime cost per capita. Columns report coefficients from IV regressionsusing the predicted firers (1) and predicted hirers (2) samples. See text for sample constructiondetails. Standard errors clustered at the city-level in parentheses. Police is sworn officers per 10,000residents. Elasticity computed using pre-program means for marginal cities. Regressions includecity fixed effects. The t-test for treatment effect equality is performed by estimating both modelssimultaneity.

237

Appendix

238

.1 Data

A-1 Grants Data

The grants data provided by the COPS office included applicant names and ORI codes as

well as application scores and grant amounts. A number of ORI codes, however, could not

be linked to the FBI data. 619 of 7,167 applicants in 2009 had ORI codes ending in ”ZZ”,

which are not valid FBI codes. It appears that the COPS office assigned these fake ”ZZ” ORI

codes to applicants who either did not know their ORI code or did not have an ORI code.

For each applicant with an ORI not appearing in the crimes reported dataset, I searched

the crimes dataset and updated the code wherever possible. I updated 521 codes, 461 “ZZ”

codes and 60 non-“ZZ” codes. 4% of agencies in the analysis sample (184 of 4,327) have

updated codes.

A-2 FBI Sample Creation

Sample construction begins with the 2005 Law Enforcement Agency Identifiers Crosswalk

(ICPSR 4634), which maps FBI ORI codes to information on government and agency type

as well as county and place FIPS codes. I updated the directory to include 178 agencies

that appear in both the grants data and the FBI crimes reported data but not the original

LEAIC file. After dropping state and special police departments (such as tribal and school

departments), the directory includes 15,153 agencies. I then clean the data for the subset of

these agencies that meet the following conditions:

1. Report positive population at least once prior to (inclusive) 2008 and at least once

after (inclusive) 2010.

2. Report police and crime at least once prior to (inclusive) 2008 and at least once after

(inclusive) 2010.

3. Report population, police, and crimes at least four times over 2002–2014.

239

There are 12,740 such agencies that meet these conditions prior to cleaning and 12,351

such agencies after cleaning. The main analysis focuses on municipal police departments in

cities with at least 1,000 residents. There are 8,752 such departments in the list of 12,351

agencies. The 4,327 of the 8,752 agencies that applied for a 2009 hiring grant comprise the

main sample.

A-3 Cleaning the FBI Data

As noted in Chalfin and McCrary (2018), the annual city population reported in the FBI

files tends to jump discretely around census years. I replace the reported population with

a smoothed version. Specifically, I fit the population time series for each city using local

linear regression with a bandwidth of two, and replace the reported population with the

fitted values.

To identify extreme outliers and record errors in the FBI data, I follow a procedure similar

to Evans and Owens (2007) and Weisburst (2017). For each city, using the years 2002–2014,

I fit the time series of police, violent crimes, property crimes, violent crime arrests, and

property crime arrests using a local linear regression with bandwidth two. I then compute

the absolute value of the percent difference between the actual and predicted values, δ(yit).

I then recode the observation as missing if δ exceeds a specific threshold.31

The thresholds are the 99th (police) and 97.5th (crimes or arrests) percentiles of the

within-size group distributions δ, where the size categories are 1,000-2,500; 2,500-5,000;

5,000-10,000; 10,000-15,000; 15,000-25,000; 25,000-50,000; 50,000-100,000; 100,000-250,000;

>250,000. Cities appearing in multiple groups are placed in the group they appear most

often. I chose the thresholds by manually checking the data for a random subset of 250

cities. About 1% of police observations and about 2.5% of crime observations appeared

to be mistakes. I use the within-group distributions of δ because the δ’s tend to be more

31In practice, I add one to each value to avoid dealing with zeroes. The percent differencebetween two values is always exactly 2 when one of the values is zero. The original values are usedonce outliers have been determined.

240

dispersed for smaller than larger cities, but my manual inspection suggested the error rate

is uncorrelated with city size.

Observations missing either due to nonreporting or outlier status are then imputed using

a combination of backwards/forwards filling and linear interpolation. For example, if a city’s

first year of nonmissing police is 2007, then that city’s police value in 2007 is imputed in

2004–2006. If a city has nonmissing police in 2009 and 2011 but not 2010, the 2010 value

is linearly interpolated. I opt for imputation, rather than leaving values as missing, so that

estimated year effects do not reflect compositional changes.

Finally, as an empirical caution against results being driven by outliers not detected using

the strategy above, I winsorize the police and crimes per 10,000 prior to the analysis. Specif-

ically, I winsorize the bottom and top 1% of values within each size group (i.e. observations

in group g with police per 10,000 below the 1st percentile in that group have their police per

10,000 replaced to equal the 1st percentile). This procedure is, again, an empirical caution

and has little impact on the results. See Table A-6 for more details.

.2 Power Calculations

Suppose we want to estimate the effect of a hiring grant offer on ∆(y) (for example, the

change in police and crime rates). If grants are randomly assigned, the minimum detectable

effect size (MDE) for significance level α and power κ is

MDE = (tα/2 + t1−κ)×

√1

D(1−D)

σ2∆(y)

N

where D is the fraction of cities assigned to treatment.

Now suppose grants are allocated according the score discontinuity. Schochet (2009)

shows that under the assumption that ∆(y) is a linear function of the application score

241

absent the discontinuity, the MDE in a regression discontinuity design is

MDE = (tα/2 + t1−κ)×

√1

D(1−D)

σ2∆(y)

N

1

(1− ρ2)

where ρ is the correlation between the score and treatment status. The fraction 1/(1 − ρ2)

is referred to as the RD design effect. Note that the linearity assumption is very restrictive.

Under less restrictive assumptions about the relationship between the score and the outcome,

the MDE will be strictly larger. The main intuition of the above formula is that MDE is

decreasing in N but increasing the outcome variability.

Following convention, set α = 0.5 and κ = 0.8 so that tα/2 + t1−κ = 2.8. When computing

the MDE for an RD design, we must take note of the fact that typically only observations

within a certain bandwidth of the score threshold are used in estimation. For a given score

bandwidth, D, N , ρ, and σ2∆y are observable. Assuming a bandwidth of 1 (so cities within

one standard deviation of the threshold are used), the MDE’s are:

1. Police: 0.6 (DD Estimate = 0.723).

2. Crime Cost : 29.11 (DD Estimate = -25.43).

3. Violent Crime: 4.09 (DD Estimate = -3.09).

4. Property Crime: 11.7 (DD Estimate = -11.13).

For reference, I note the difference in differences estimate from the main specification in

parentheses. At a bandwidth of 1 and a correctly specified linear score–outcome relation-

ship, an RD is sufficiently statistically powered to detect the DD estimates for police and

property crime (albeit narrowly), but not for crime costs or violent crimes. The RD de-

sign is underpowered for all outcomes when bandwidth less than one are used. Further, as

mentioned above, these MDE’s are lower bounds of the true MDE because of the (almost

242

certainly) incorrect linearity assumption. I show the MDE calculations for each outcome

and bandwidth in Table A-3.

243

.3 Appendix Figures and Tables

Figure A-1: Probability of Sample Inclusion by Application Score

0

.2

.4

.6

.8

1

Frac

tion

in S

ampl

e

0

100

200

300

Num

ber o

f App

lican

ts

-4 -2 0 2 4Score Around Cutoff

RD Estimate: .01 (.02)

Notes: Sample is 5,314 municipal police departments applying for a hiring grant in 2009. Figureplots local linear regression fits of an indicator for being in the sample against the application scorerelative to the cutoff (right axis), laid over a histogram of the application scores (left axis). Legendshows corresponding RD estimate using the IK optimal bandwidth and a triangular kernel.

244

Figure A-2: Data Imputation by Treatment Status

-.02

0

.02

.04

.06

2004 2006 2008 2010 2012 2014Year

PoliceCrime

Notes: Figure plots coefficients and 95% intervals on interactions between a high score indicatorand year effects. Standard errors clustered at the city-level. Regressions include city fixed effectsand size × year fixed effects. Dependent variable is an indicator for police (crime) being imputed.City as coded as having crime imputed if either violent or property crime is imputed.

245

Figure A-3: Changes in Police and Crime by Application Score (2008–2009)

-.5

0

.5

1

-1 -.5 0 .5 1Score Around Cutoff

RD Estimate: .69 (.28)

Panel A: Police Per 10,000

-60

-40

-20

0

20

-1 -.5 0 .5 1Score Around Cutoff

RD Estimate: -19 (16.99)

Panel B: Crime Cost Per Capita

Notes: Figure plots local means (bin width equals .1 score points) of the 2008-2009 change inpolice (crime). Dashed lines denote linear fits, estimated separately for cities above and below thethreshold. Legend indicates the RD estimate (standard error) when using the IK bandwidth and atriangular kernel.

246

Figure A-4: Application and Funding Rates by 2009 Treatment Status

0

.2

.4

.6

.8

1

2009 2010 2011 2012 2013 2014

Above CutoffBelow Cutoff

Panel A: Fraction Applying

0

.2

.4

.6

.8

1

2009 2010 2011 2012 2013 2014

Above CutoffBelow Cutoff

Panel B: Fraction Funded

Notes: Figure plots the fraction of cities applying (Panel A) and receiving funding (Panel B) byyear and by whether the 2009 application score exceeded the cutoff.

247

Figure A-5: First Stage Placebo Tests

-.1

-.05

0

.05

.1

-1

-.5

0

.5

1

2006 2008 2010 2012...

Police Per 10,000Civilians Per 10,000Log Expenditures Per Capita

Notes: Sample is 2,075 agencies in main sample that could be matched to the Annual Survey ofGovernments (ASG). Civilians refers to civilian police employees reported in the UCR LEOKAfiles. Expenditures is direct expenditures reported in the ASG.

248

Figure A-6: Dynamic Estimates with and without City Trends

-100

-50

0

50

100

-1.5

-1

-.5

0

.5

1

1.5

2004 2006 2008 2010 2012 2014Year

Police (Without Trends) Police (With TrendsCrime (Without Trends) Crime (With Trends)

Notes: Same as Figure 3.5 except that results are presented when city-specific trends are excluded(hollow circle/squares) and included (solid circles/squares). Estimates with city trends are thesame as Figure 3.5.

249

Figure A-7: Total ARRA Funding By Source, 2009–2013.

-5

0

5

10

Log

ARRA

Fun

ding

Per

Cap

ita

0

50

100

150

200

Num

ber o

f App

lican

ts

-4 -3 -2 -1 0 1 2 3 4Score Around Cutoff

DOJ RD Estimate: 3.11 (.37)Non-DOJ RD Estimate: -.02 (.2)

Notes: Sample is 3,227 agencies in main sample that could be matched to ZIP codes. Dependentvariable is log ARRA funding per capita by source (DOJ versus Non-DOJ) at the FIPS place codelevel for the period 2009-2013, computed from FPDS data. Legend displays RD estimates usingusing the IK optimal bandwidth and a triangular kernel.

250

Figure A-8: IV Estimates and ARRA Funding Differences by Bandwidth

-.6

-.4

-.2

0

.2

.4

.6

-200

-150

-100

-50

0

50

100

150

200

0 1 2 3 4Bandwidth

IV Estimate (Left Axis)Treat-Control Difference in Non-DOJ ARRA Funding (Right Axis)

Notes: Sample is 3,227 agencies in main sample that could be matched to ZIP codes. Blue dotsshow IV estimates from main specification when only cities within the indicated bandwidth areused. Red squares show the coefficient on a regression of log total non-DOJ ARRA funding percapita on a high score indicator (estimated at the city, not the city-year level).

251

Figure A-9: Dynamic TOT Estimates of Effect of Grants on Police

-.1

-.05

0

.05

.1

2008 2010 2012 2014Year

ITT

Panel A: Funding Probability

-.5

0

.5

1

1.5

2008 2010 2012 2014Year

ITT TOT

Panel B: Police Per 10,000

Notes: Panel A plots estimates of the effect of exceeding the cutoff in 2009 on future funding.The coefficient for 2009 is 0.99 (0.0035) and is not shown for scaling purposes. Panel B plots ITTestimates (same as Figure 3.5) and TOT estimates. See text for details.

252

Figure A-10: Heterogeneous Effects by City Size

-2

-1

0

1

2

Elas

ticity

-.1

-.05

0

.05

.1

Coe

ffici

ent o

n H

igh

x Po

st

<5,000 5,000-10,000 10,000-25,000 25,000-50,000 >50,000Size Group

Log Police Per CapitaLog Crime Cost Per CapitaElasticity (Right Axis)

Notes: Figure plots reduced form and first stage estimates when using only cities in the denotedsize group. I use a log specification here to account for differing means across groups. Note thatmain results using logs are very similar to those using rates as shown in Table A-8. Elasticity (rightaxis) is the ratio of the reduced form and first stage coefficients.

253

Figure A-11: Relationship Between Predicted Hiring and Recession Exposure

-.8

-.7

-.6

-.5

-.4

Pred

icte

d H

ires

2 4 6 8 10Recession Exposure

Beta = -.033 (.002)

Notes: Figure plots a binscatter of predicted hires against recession exposure for 4,327 cities inthe main sample. Predicted hires is the predicted value from a regression of log change in policeper 10,000 between 2008 and 2010 using only control cities. Recession exposure is the 2007-2009change in the local unemployment rate.

254

Table A-1: Sample Police Departments

ORI Code City Size Percentile Population Police Crime Costs

NC05202 Maysville, NC 0 992 35 682NY05139 Quogue Village, NY 1 1,086 133 337AL02904 Coosada, AL 5 1,491 27 412MD00807 Rising Sun, MD 10 2,063 31 962OH02701 Gallipolis, OH 25 4,056 34 3,688IL05008 Peru, IL 50 9,953 25 206IL06003 Collinsville, IL 75 25,746 17 262KS04609 Shawnee, KS 90 60,674 15 211MO01002 Columbia, MO 95 99,941 15 488TX22001 Arlington, TX 99 372,418 16 635NY03030 New York, NY 100 8,244,256 43 486

Notes: Cities are eligible for inclusion in the sample if their population was above 1,000 more oftenthan not over 2002-2014. Hence, there are some city-year observations with populations below1,000.

255

Table A-2: Relationship Between Application Scores and Baseline Characteristics

(1) (2)All Municipal In Sample

Log Population 0.156*** 0.213***(0.0135) (0.0118)

Unemployment Rate 0.0267*** 0.0309***(0.00388) (0.00380)

Log Family Income -0.650*** -0.502***(0.0449) (0.0404)

Percent Nonwhite 0.0126*** 0.00840***(0.000722) (0.000743)

Percent Young Male -0.00819*** -0.00639***(0.00161) (0.00146)

Log Police Per -93.85*** 14.77Capita (12.94) (11.80)

Log Violent Crime 20.91*** 23.60***Per Capita (4.102) (3.996)

Log Property Crime 11.14*** 18.39***Per Capita (1.531) (1.064)

Mean .19 .21R-Squared .47 .57Observations (Cities) 4598 4327

Notes: Robust standard errors in parentheses. Dependent variable is the standardized 2009 appli-cation score. Note that the mean is not zero because standardization is to the universe of applicants(i.e. including non municipal agencies).

256

Table A-3: Regression Discontinuity Power Calculations

MDE when Bandwidth Equals

Outcome DD Estimate 0.25 0.5 1 2 3 4

Police 0.723 1.11 0.79 0.6 0.5 0.483 0.482

Crime Cost -25.43 70.54 48.97 37.69 31.77 30.12 30.03

Violent Crime -3.08 9.86 6.91 5.3 4.47 4.23 4.22

Property Crime -11.13 29.46 20.79 15.19 12.41 11.76 11.73

Notes: See Appendix B for detail. Table shows the minimum detectable effect (MDE) for a re-gression discontinuity design under a linearity assumption where the outcome is change in police(crimes) per 10,000 and the denoted bandwidth is used to construct the sample. Column 2 showsthe corresponding difference in difference estimate from the main specification.

257

Table A-4: Dynamic Difference in Differences Estimates

(1) (2) (3) (4)Police Crime Cost Violent Property

High x 2005 0.114 5.241 0.874 -1.684(0.109) (6.520) (0.920) (2.756)

High x 2006 -0.0252 1.547 0.425 -3.281(0.145) (7.866) (1.111) (3.337)

High x 2007 -0.0206 4.324 0.825 -3.115(0.116) (6.901) (0.974) (2.734)

High x 2009 0.491*** -24.20*** -2.875** -11.60***(0.154) (8.461) (1.195) (3.924)

High x 2010 0.948*** -31.03*** -3.717** -14.35***(0.202) (11.60) (1.612) (5.343)

High x 2011 0.823*** -31.59** -4.180** -8.008(0.250) (15.25) (2.127) (6.473)

High x 2012 0.779** -36.44** -4.794** -9.694(0.302) (17.65) (2.432) (8.118)

High x 2013 0.964*** -41.12** -5.463* -10.04(0.339) (20.75) (2.837) (9.524)

High x 2014 0.607* -37.91 -5.080 -8.531(0.366) (23.37) (3.190) (10.69)

Mean 22.85 686.74 75.16 436.05Controls Yes Yes Yes YesSize x Year Effects Yes Yes Yes YesCity Trends Yes Yes Yes YesClusters (Cities) 4327 4327 4327 4327Observations (City-Years) 47597 47597 47597 47597

Notes: Standard errors clustered at the city-level in parentheses. Dependent variable is po-lice/crimes per 10,000 residents (columns 1,3-4) and cost-weighted crimes per capita (column 2).Regressions include city fixed effects. Regressions are identical to those graphed in Figure 3.5 andFigure 3.7 except that they include controls.

258

Table A-5: Sensitivity of IV Estimates to Controls

(1) (2) (3)Crime Crime Crime

Police -39.32** -35.17** -35.96**(15.86) (15.19) (15.52)

Mean 686.74 686.74 686.74Elasticity -1.31 -1.17 -1.2F-Stat 19.89 20.96 20.36Controls No Yes YesPopulation as Control No No YesSize x Year Effects Yes Yes YesCity Trends Yes Yes YesClusters (Cities) 4327 4327 4327Observations (City-Years) 47597 47597 47597

Notes: Standard errors clustered at the city-level in parentheses. Dependent variable is crime costper capita. All regressions include city fixed effects. Column 1 is the same as Table 2 exceptwithout controls. Column 2 is identical to Table 2. Column 3 adds population as a control.

259

Table A-6: Sensitivity of IV Estimates to Data Cleaning

(1) (2) (3) (4)Main No Winsorizing No Imputation No Cleaning

Police -35.17** -36.84** -35.41** 50.62(15.19) (16.55) (17.06) (76.25)

Mean 686.74 694.02 690.88 689.15Elasticity -1.17 -1.22 -1.18 1.7First Stage Beta .72 .73 .74 -.5F-Stat 20.96 19.24 17.83 .46Controls Yes Yes Yes YesSize x Year Effects Yes Yes Yes YesCity Trends Yes Yes Yes YesClusters (Cities) 4327 4327 4327 4327Observations (City-Years) 47597 47597 43026 44603

Notes: Standard errors clustered at the city-level in parentheses. Dependent variable is crime costper capita. All regressions include city fixed effects. Column 1 is the same as Table 2. Column 2uses non-winsorized crimes and police. Column 3 replaces imputed values to missing. Column 4uses the raw data (no outliers deleted).

260

Table A-7: Reduced Form Estimates by Crime Type

(1) (2) (3) (4) (5) (6) (7) (8) (9)All Violent Murder Rape Robbery Assault All Property Burglary Larceny Auto Theft

High x Post -3.084** -0.0777** -0.384*** -1.435*** -0.947 -11.13*** 1.987 -10.82*** -3.724***(1.252) (0.0390) (0.141) (0.259) (1.184) (4.064) (1.438) (3.109) (0.530)

Mean 75.16 .42 3.85 10.79 59.69 436.05 86.83 311.27 35.15Controls Yes Yes Yes Yes Yes Yes Yes Yes YesSize x Year Effects Yes Yes Yes Yes Yes Yes Yes Yes YesCity Trends Yes Yes Yes Yes Yes Yes Yes Yes YesClusters (Cities) 4327 4327 4327 4327 4327 4327 4327 4327 4327Observations (City-Years) 47597 47597 47597 47597 47597 47597 47597 47597 47597

Notes: Standard errors clustered at the city-level in parentheses. Table presents reduced form estimates. Regressions include city fixedeffects.

261

Table A-8: IV Estimates by Crime Type (Logs)

(1) (2) (3) (4) (5) (6) (7) (8) (9)All Violent Murder Rape Robbery Assault All Property Burglary Larceny Auto Theft

Log Police -1.352** -2.768*** -2.970** -2.294*** -0.732 -1.024** -0.565 -1.334** -1.552*(0.588) (0.961) (1.203) (0.821) (0.629) (0.498) (0.657) (0.561) (0.819)

Controls Yes Yes Yes Yes Yes Yes Yes Yes YesSize x Year Effects Yes Yes Yes Yes Yes Yes Yes Yes YesCity Trends Yes Yes Yes Yes Yes Yes Yes Yes YesClusters (Cities) 4327 4327 4327 4327 4327 4327 4327 4327 4327Observations (City-Years) 47597 47597 47597 47597 47597 47597 47597 47597 47597

Notes: Same as Table 5 except using a log-log specification. That is, the dependent variable is log crimes per capita and police is logsworn officers per capita. The first stage F-statistic is 25.4.

262

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