Estimating the Effect of Incarceration on Recidivismand Employment: An RD Approach

Shawn D. BushwayCatalina FrancoDavid J. HardingJeffrey Morenoff∗

Abstract

This paper analyzes how incarcerating convicted offenders affects their future recidi-vism and employment outcomes. Using data on felony offenders in Michigan sentencedbetween 2003 and 2006 and outcomes collected from various administrative sources,we exploit discontinuities in the structure of the Michigan Sentencing Guidelines asan exogenous source of sentence type assignment. By comparing observations on ei-ther side of the cut-points generated by prior criminal record scores in the SentencingGuidelines, we provide evidence on the causal effect of incarceration on recidivism andemployment for low-level offenders who are on the sanction margin. Preliminary resultsshow that there is a sizable incapacitation effect for offenders sentenced to prison inrecidivism one and three years after sentence and in employment in the fourth quarterafter sentence. This suggests that incarcerated offenders are less likely to recidivate orbe employed as a result of being incarcerated. There is, however, no difference in theoutcomes of prisoners and probationers when the relevant risk period of analysis startsafter release.

∗Bushway: Rockefeller College of Public Affairs & Policy, University at Albany (SUNY) (e-mail: sbushway@albany.edu);Franco: Economics, University of Michigan (e-mail:cfrancob@umich.edu); Harding: Sociology, University of California, Berkeley(e-mail: dharding@berkeley.edu); Morenoff: Sociology, Population Studies Center, and Survey Research Center, University ofMichigan (e-mail: morenoff@umich.edu). This project is funded by NSF, NICHD, PSC, and UM Office of Research. We arethankful to Anh Nguyen, Charley Chilcote, and Paulette Hatchett for all their help with assembling and cleaning the data, andJeff Smith for useful feedback. We would like to acknowledge the support from the Eunice Kennedy Shriver National Instituteof Child Health and Human Development (1R21HD060160 01A1), and the National Science Foundation (SES 1061018).

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1 Introduction

The dramatic increase in the number of people incarcerated in the United States over the

last three decades has generated a discussion among policy makers, criminal justice offi-

cials, researchers, and citizens about the causes and consequences of mass incarceration

and ways of reducing the size of the nation’s prison population without compromising

public safety. One of the central questions in this discussion is whether sentencing a

convicted felon to prison - at considerably higher cost than alternative sentences such

as probation - will reduce the likelihood that the person will reoffend in the future.1 A

related question is whether serving time in prison reduces one’s employability and lowers

wages after prison.

Despite the centrality of these questions to scholarly and policy debates, studies on the

economic and social consequences of incarceration often base their inferences on nebulous

counterfactual comparisons and usually fail to adequately rule out competing explana-

tions for the putative effects of incarceration they estimate, leading some observers to

conclude that existing research is not nearly sufficient for making firm evidence-based

conclusions for either science or public policy (Nagin, Cullen, and Jonson 2009). In re-

cent years, a new wave of studies have used quasi-experimental designs that leverage the

random assignment of judges to felony cases to estimate the effects of incarceration on

measures of subsequent recidivism, employment, and earnings (Abrams 2009; Aizer and

Doyle 2013; Berube and Green 2007; Green and Winik 2007; Kling 2006; Loeffler 2013;

Mueller-Smith 2014).

The current paper contributes to this literature by implementing a novel quasi-

experimental design to estimate the effect of being sentenced to prison compared to

probation on the probability of prospectively being (a) convicted of a new felony offense

1Criminologists use the term specific deterrence to refer to this idea the punishment given for a priorcrime may deter a person from committing a future crime. This is distinguished from general deterrence,which refers to the idea that the threat of punishment may deter people in the general population fromcommitting crime, regardless of their specific experience with prior crime and punishment. Each of thesequestions has spawned its own criminological literature, but in this paper we focus primarily on studies ofspecific deterrence.

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and (b) employed, using data on a sample of convicted felony offenders in the state of

Michigan sentenced between 2003 and 2006. The design emerges from the structure of

the sentencing guidelines and capitalizes on discontinuities in the probability of being

sentenced to prison based on the official system that is used for scoring and classifying

convicted offenders in pre-sentence investigation reports, as dictated by the Michigan

Sentencing Guidelines.

Empirically, the discontinuities in the probabilities of receiving a prison sentence can

be analyzed under a fuzzy regression discontinuity (RD) design framework. Given the

resemblance between the fuzzy RD and the instrumental variables (IV) estimators, we

propose two IV approaches to provide the causal effect of incarceration on recidivism

and employment. The first approach pools together the multiple cutoffs that are present

in the data to construct a single cutoff which is used to instrument the prison sentence

indicator. The second approach uses the individual cutoffs as multiple instruments in

the IV regression. The IV results are complemented by reduced-form regressions that

give insights into the heterogeneity of the treatment effects that are behind the summary

effects estimated by the IV analysis.

The rest of this document is organized as follows: Section 2 provides a brief theo-

retical motivation and discussion of previous studies, section 3 presents the details of

the Michigan sentencing guidelines in which our research design in based, and section

4 discusses the data sources and presents descriptive statistics of our analytical sample.

The last two sections discuss the results and conclude.

2 Theoretical motivation and prior research

Our research questions derive their significance from well-developed bodies of theory and

research linking incarceration to future behavior, and so we review some of the key dis-

tinctions between different perspectives.

Contemporary criminological accounts emphasize three general mechanisms through

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which incarceration can reduce the likelihood that a person will reoffend in the future:

(1) incapacitation, (2) rehabilitation, and (3) specific deterrence. Although being in-

carcerated has a clear mechanical effect on suppressing crime for the duration of one’s

custodial sentence, the effectiveness and efficiency of incapacitation as a crime-control

strategy are open to question. One limitation on its effectiveness is that by removing

offenders from the community, incarceration may create criminal opportunities for new

offenders through so-called replacement effects (Miles and Ludwig 2007). Incapacitation

is also a financially costly way to control crime, with a bed in a state prison or local

jail costing an average of roughly $26,000 per year, compared to average expenditures of

$2,800 per parolee and $1,300 per probationer (Schmitt, Kris Warner, and Gupta 2010).

It is very difficult to disentangle the incapacitative effects of prison from its behavioral

effects, which could operate through rehabilitation, specific deterrence, or other mech-

anisms. Finally, the magnitude of any incapacitation effects depends on the criminal

behavior of the comparison group, those who are not sentenced to prison but rather re-

main in the community.

After the decline in the support for rehabilitation as the guiding philosophy of the

American penitentiary system (Bushway and Paternoster 2010; Cullen 2002), there has

been a resurgence of interest in and support for rehabilitation in recent decades brought

about by new research on corrections programs (Cullen 2005; Cullen 2002). A general

conclusion of this research is that there are successful programs that curb recidivism,

but their effectiveness hinges on the way they are matched to the needs of individual

offenders and the extent to which they maintain program integrity (Bushway and Pa-

ternoster 2010; Cullen 2002). Some scholars also argue that exposure to programs and

interventions that are inappropriately matched to an offender’s needs especially those

that violate the risk principle by exposing low-risk offenders to excessive interventions

can have criminogenic effects (Nagin, Cullen, and Jonson 2009).

Specific deterrence is the primary theoretical framework used to motivate studies of

the effects of incarceration on reoffending. It refers to the possibility that an offender

will be less likely to engage in future criminal activity after being punished for a previous

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crime (Bushway and Paternoster 2010; Nagin, Cullen, and Jonson 2009). Its focus on

deterring people who have already been punished for previous crimes distinguishes it

from the notion of general deterrence, which refers to the broader deterrent effects that

punishments may have on members of society, regardless of their specific experience with

crime and punishment.

Despite the emphasis placed on the three mechanisms outlined above in the litera-

ture, other theoretical perspectives have also been brought to bear on the question of

how incarceration affects subsequent behavior. First, prisons and jails can have labeling

effects that can operate through stigma (and social reaction to the label) or through

transformation of one’s identity (the internalization of the label), and both of these can

be reinforced through interactions inside and outside of prison (Nagin, Cullen, and Jon-

son 2009). Labeling is often evoked as one of the main reasons that former prisoners

have trouble finding jobs (Pager 2009). Also, insufficient opportunities for education and

job training in prisons, along with the atrophy of job skills one brings to prison and

lost job experience can all be viewed from a human capital perspective as reasons why

returning prisoners may have more difficulty (re)connecting with the labor market than

probationers (Kling 2006; Loeffler 2010; Tyler and Kling 2007). Prisons and jails are

viewed by social learning theorists as sites where procriminal attitudes, values, skills,

and roles can be transmitted through informal interactions. To the extent that prisoners

acquire procriminal skills and experience human capital deficits that make it harder for

them to find jobs in the formal labor market, they may face more strain and differential

opportunities that make crime more accessible and profitable than legal forms of work.

Finally, incarceration especially imprisonment can deplete the social capital that one

can access after prison (Loeffler 2010). The combination of time and distance away from

home can make it difficult to stay connected to relatives and friends, especially weak ties

that can be especially useful for finding jobs. In the parlance of control theory, prison

may diminish one’s social bonds, to family, friends, work, and engagement in other forms

of social organization.

In terms of prior research, a small set of studies have utilized quasi-experimental or

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experimental designs to study the effects of incarceration on recidivism and employment.

In a pair of studies using data from the Superior Court of the District of Columbia

(Berube and Green 2007; Green and Winik 2010) use randomly assigned judges as in-

struments and find no statistically significant relationship between incarceration and

reoffending. Abrams (2009) also uses an instrumental variables design in a comparison of

recidivism among prisoners and probationers in Clark County, Nevada, but in his case,

the instruments come from the random assignment of public defenders and his treatment

is sentence length (rather than sentence type). He finds that there is a relationship be-

tween sentence length and recidivism but it is complex and non-monotonic negative for

both the shortest/weakest and longest sentences, and positive for mid-range sentences.

Nagin and Snodgrass (2013) use the random assignment of judges to felony defendants

in Pennsylvania who were sentenced during 1999 to estimate the effects of incarcera-

tion (compared to non-custodial sanctions) on recidivism. Aizer and Doyle (2013) use

the random assignment of judges to defendants in a juvenile court in Chicago, Illinois

between 1991 and 2006 to study the effects of juvenile incarceration on high school com-

pletion and incarceration in adult facilities later in life. Finally, Mueller-Smith (2014)

uses the random assignment of “courtrooms” (combinations of judges and prosecutors)

to misdemeanor and felony defendants sentenced in Harris County, Texas between 1980

and 2009, to estimate the effects of sentence type and length on recidivism, employment,

wages, take-up of food stamps, marriage, and divorce.

In a study of sentences in Washington juvenile courts, Hjalmarsson (2009) used a re-

gression discontinuity design that capitalizes on large discrepancies between neighboring

cells of the sentencing grid in terms of the probability of being incarcerated in a state

detention facility (for 15-36 weeks) vs. a “local sanction (which could include combina-

tions of time served at a local detention center, community supervision, and community

service) and found that incarceration reduced future offending by 35%. Although similar

in spirit to our regression discontinuity design, this study had a very different substan-

tive focus the juvenile justice system where the treatments are qualitatively different.

Manski and Nagin (1998) also studied the effect of a juvenile offender being sentenced

to confinement in a residential treatment facility vs. nonresidential treatment on recidi-

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vism in Utah. Their seminal contribution was to illustrate the importance of studying

(and ideally modeling) the behavioral patterns of human actors (e.g., judges) who make

decisions regarding treatment assignments. They demonstrate how bringing different

behavioral models about judicial decision-making to bear on the identification of causal

effects can be much more informative than the conventional approach of assuming noth-

ing about how judges act. They also show how assumptions about the behavioral model

driving selection can lead to very different conclusions about the causal effect and urge

that researchers focus on better understanding the behaviors of the causal agents who

make the treatment assignments.

Studies of incarceration and employment also find that offenders who have been in-

carcerated or served longer sentences tend to have weaker labor force attachment after

prison (Bushway and Reuter 2002; Bushway and Paternoster 2010; Nagin, Cullen, and

Jonson 2009; Wakefield and Uggen 2010). However, some studies have also shown that

prisoners experience temporary employment increases after their release relative to their

employment status just before going to prison, which may be partially attributable to

the effects of post-prison parole supervision and reentry programs (Bloom et al. 2007;

Kling 2006; Loeffler 2010; Pettit and Lyons 2007; Tyler and Kling 2007). Similar results

were found in two quasi-experimental studies. Kling (2006) used data from the Florida

state and California federal court systems, using judges as instruments to estimate the

effect of sentence length on subsequent employment and earnings. He found that in

the short-term, longer lengths of incarceration are associated with more positive labor

market outcomes, while there is no effect in the medium term. Loeffler (2010) analyzed

employment data on felony cases from the Circuit Court of Cook County, Illinois and

likewise found that incarceration was associated with temporarily higher employment.

He also conducted a non-experimental analysis of data on wages and job tenure and

found that the temporary increase in employment among the incarcerated group was not

accompanied by wage gains or tenure increases, as one might expect if the employment

gains were the result of improvements to human or social capital. Instead, he concludes

that the evidence is more consistent with the benefits that returning prisoners may get

from reentry programs, especially when compared to their employment outcomes just

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before going to prison (as he does in a difference-in-difference analysis).

As a whole, this small group of studies using quasi-experimental designs to analyze

the impacts of incarceration on employment and recidivism yield several general conclu-

sions. First, most of the quasi-experimental studies of the adult criminal justice system

found no significant effects of either sentence type (e.g., incarceration vs. a non-custodial

sanction) or length on recidivism outcomes. The only exception was the Mueller-Smith

(2014) study, one of the few to separate the effects of incapacitation (comparing individ-

uals currently in prison or jail to those who received non-custodial sanctions) from the

longer-run effects of incarceration after the incarcerated group has been released back

to the community. This study found that (a) incarceration was negatively associated

with recidivism when currently incarcerated individuals were compared to those released

to the community on non-custodial sanctions (i.e., an incapacitation effect), but (b) in-

carceration was positively associated with recidivism when both groups were compared

post-release. The two studies of the juvenile justice system produced discrepant results.

Using the identification strategy based on random judge assignment, Aizer and Doyle

(2013) found that juvenile incarceration increased the likelihood of recidivism, defined

as future incarceration as an adult. Hjalmarsson (2008), however, found that juvenile

incarceration was associated with lower probability of future incarceration as a juvenile.

As a recent summary of this literature by the National Research Council (2014)

noted, in the larger literature on the effects of incarceration on labor market outcomes,

there are many observational studies of survey data suggesting that being incarcer-

ated weakens ones future employment opportunities and earnings. The results from

the quasi-experimental literature are more equivocal. Neither Kling (2006) nor Loeffler

(2013) found significant associations between incarceration and employment or wages,

but Mueller-Smith (2014) found that incarceration reduces post-incarceration employ-

ment and wages.

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3 Michigan Sentencing Guidelines

The sentencing guidelines manual contains recommendations in terms of type of sen-

tence and sentence length that judges use in the sentencing process. With the exception

of offenses for which there is no sentencing discretion,2 the sentencing guidelines describe

in detail the recommended sentences and sentence lengths for an offender based on the

current offense, prior criminal history, and type of crime. The current version of the

Michigan sentencing guidelines applies to felonies committed on or after January 1, 1999.

The guidelines are indeterminate in that they (a) provide a range of minimum sen-

tences within each cell for judges to choose from and (b) present recommended rather

than mandatory minimum sentences (Deming, 2000).3 Because the sentencing guidelines

are only recommendations, judges are free to depart from the recommended range,4 but

departures are relatively rare, occurring in less than 2 percent of the cases analyzed in

this sample. The guidelines divide offenses into nine classes based on their severity as

defined by the maximum term of imprisonment allowed by statute for the offense (classes

A-H, with A being the most severe, H the least severe, and class M reserved for second-

degree murder). Each class has its own sentencing grid, with cells divided according

to scores on two measures, the offender prior record (PR) and offense severity (OS),

which are each computed as sums of scores on component measures. There are seven

components to the PR score and 20 components to the OS score.5 The total PR scores

are divided into seven intervals to generate the prior record variable (PRV) level. The

PRV cut points are the same for all grids. The OS scores are also divided in intervals

which determine the offense severity variable (OSV) level. The number of OSV levels

2Examples of felonies excluded from the guidelines are first degree murder, which carries a mandatorylife sentence, or felony firearm, which carries a mandatory two-year flat sentence (sentence to prison for aminimum of 2 years and maximum of 2 years).

3Maximum sentences are set by statute in Michigan.4Judges must justify any departure in writing and are precluded from basing departures on any in-

formation already taken into account in the guidelines or on race, gender, ethnicity, nationality, religion,employment, or similar factors.

5Our understanding is that many other states have a more discrete sentencing guidelines system forclassifying offenders based on prior record. Our application of the regression discontinuity method in thisstudy depends on the fairly continuous nature of the prior record variables in Michigan.

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and the cut points defining them are not the same across grids. Each cell defined by the

intersection of PRV and OSV levels contains a range of possible minimum sentences in

months. In the example grid (see appendix) the lowest minimum sentence (in months) is

the large number on the left of the cell while the four numbers on the right of the cell are

the highest minimum sentence lengths in months. These four subdivisions correspond to

the offender’s habitual status for offenders with prior felony records (Michigan Judicial

Institute, 2010), and their function is basically to increase the upper limit of the mini-

mum sentence of the appropriate cell by a fixed percentage.

Judges are responsible for guideline score calculations, but in practice this work is

done as part of the pre-sentence investigation and sentencing information report that is

provided to the judge by the Michigan Department of Corrections and typically prepared

by an MDOC probation officer. 6 The officer relies on police reports, interviews with

victims, and criminal history searches to calculate the continuous prior record (PR) and

offense severity (OS) scores and to determine the offender’s habitual status. The proba-

tion officer is also the person who typically places the offender in a cell on the relevant

grid based on the calculated guidelines scores. Our conversations with probation officers

suggest that judges rarely request that scores be recalculated.

There is the possibility of manipulation in assigning points to the components of the

scores, but we consider this far more likely for offense severity scores than for prior record

scores. Offense severity scores include potentially subjective aspects of the crime, such

as whether there was psychological injury to a victim or a victim’s family member or

whether a firearm was discharged in the direction of a victim, whereas prior record scores

include objective characteristics of the offender’s prior criminal history, such as whether

the offender was on parole or probation at the time of the offense and how many prior

misdemeanors, low severity felonies, or high severity felonies the offender had been con-

victed of in the past (with severity defined by the exact crime of the prior conviction).

6Michigan is somewhat unique compared to other states in that the Department of Corrections handleprobation supervision of all offenders sentenced to felony probation. Offenders sentenced to jail or jailfollowed by probation for a felony also appear in MDOC records because MDOC conducts all pre-sentenceinvestigations for all circuit courts throughout the state.

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For this reason, we focus on variation in sentence type generated by prior record scores,

as described below.

Another potential source of manipulation is the plea bargaining process, as prose-

cutors and defense attorneys are well aware of the details of the sentencing guidelines

system. In our analytic sample, 97% of convictions occurred through a plea bargain (as

opposed to a bench or jury trial). If a prosecutor were to base plea agreements on the

exact grid cell that the individual would be placed in and on her expectations of the

probability of recidivism (or employment) from the likely sentence in that cell, then such

manipulation would be a threat to the validity of our regression discontinuity design.

However, our conversation with the probation officers who prepare pre-sentence investi-

gations and sentencing information reports for judges lead us to doubt that such extreme

and intentional manipulation is occurring. First, the cases in our analytical sample are

typical cases that are processed very quickly, leaving little time and attention for such

careful calculation or concern. Second, we believe that most plea bargaining occurs over

the exact crime the offender will plead guilty to, and therefore which crime severity grid

will govern his or her sentencing. Our analysis only makes comparisons within sentencing

grids.

For our purposes, a key aspect of the sentencing guidelines is that cells on most

grids (classes B-G) are divided into three categories based on the types of sentences

recommended: (1) Intermediate cells, including jail, probation and other (rarely used)

sentences like fines, drug treatment, or house arrest; (2) straddle cells, in which any type

of sentence is possible, and (3) prison only cells. 7 In the example grid in the appendix,

intermediate cells are marked with asterisks, straddle cells are shaded, and prison cells are

unmarked. As we will explain in section 5, our research design exploits the discontinuous

7Grids M and A contain only prison cells. Grid H contains intermediate and straddle cells but no prisoncells. Intermediate cells have ranges in which the upper recommended limit is 18 months or less. Whenoffenders in intermediate cells are sentenced to jail, their jail term can be 0-12 months (or zero to thestatutory maximum if the statutory maximum is less than 12 months). Straddle cells have ranges in whichthe lower limit of the range of the minimum sentence is 12 months or less and the upper limit is at least 18months. When offenders in straddle cells are sentenced to jail, their jail terms can be 0-12 months.

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jump in the probability of going to prison when crossing from an intermediate cell to a

straddle cell.

4 Data

The data used in the analysis comes from different sources. We draw primarily on admin-

istrative data from the Michigan Department of Corrections (MDOC), which provided

information on all individuals convicted of a felony between 2003 and 2006. The pre-

sentence investigation records, called the Basic Information Report (BIR), contain the

individual sentencing guidelines scores and components, identifiers for the sentencing grid

and cell for each case, legal codes for the offense first charged and convicted, habitual

offender status, type of conviction (plea, bench trial, jury trial, etc.), offense date, convic-

tion date, sentence date, days spent in jail (jail credits), sentence(s) imposed, and IDs for

judges, defense attorneys, counties, and circuits. Additionally, the BIR records offender

demographics, prior convictions and arrests, and substance abuse history.8

The two outcomes of interest we analyze in this study are recidivism and employment

in different time frames. Recidivism is measured in three ways: new felony convictions,

arrests, and entry to prison. Arrest records were provided by the Michigan State Police

and are available through 2012. Data on new felony convictions (convictions recorded af-

ter the original sentence and for offenses occurring after the original sentence) are drawn

from BIR from MDOC. Lastly, supervision records from MDOC document subsequent

incarceration in prison, for a technical violation or a new sentence.9 Conviction and incar-

ceration records are available through 2013. We analyze recidivism outcomes 1, 3 and 5

years after sentence and after release. In this draft we analyze only new felony recidivism.

8Demographic and economic characteristics used in the analysis include age, race, gender, marital statusat arrest, and years of schooling. A few characteristics in the PSI are crudely measured (i.e., whether or notthe offender has a history of mental illness, drug abuse, or alcohol abuse) but were nonetheless retained inthe analysis as they serve as important pre-sentence variables.

9Our access to data on multiple forms of recidivism and to MDOC data on the supervision of all paroleesand probationers allows us to capture moves to prison for parole and probation violations that are notrecorded in arrest records, a potentially important form of censoring that is not addressed in many studies.

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Employment data comes from the Michigan Unemployment Insurance Agency (UIA)

which is matched to the MDOC administrative records using social security numbers and

aliases.10 These data provide information on employment histories in the formal labor

market prior to sentencing and employment outcomes post-sentence and post-release.

The employment variables are whether the individual is observed to be employed in the

4th, 12th, and 20th quarters after sentence and after release. An individual is observed

to be employed if he or she was recorded as having any wages during the quarter.

An important distinction that we make concerns the start of the risk period for the

outcome. One approach taken by many previous studies is starting the risk period at

release. This means that for a probationer, the risk period starts at sentence but for the

other three sentence types it starts once the incarceration period ends.11 An alternative

approach is to define the risk period as beginning at the date of sentencing for offenders

in all sentence types. We view both approaches as having strengths and weaknesses.

Starting the risk period at release allows for comparisons with prior research and re-

moves any incapacitation effects during incarceration. However, this method introduces

a number of potential problems. It confounds the effects of incarceration with effects of

10Records for the study population were matched with UI records using the following procedures. First,all social security numbers available in MDOC databases for the population were sent to the MichiganUnemployment Insurance Agency and Workforce Development Agency for matching. In some cases, morethan one social security number was available for each subject. Returned UI records were matched withnames from MDOC databases, including aliases, to eliminate incorrect social security numbers. If more thanone social security number that MDOC had recorded for the same person matched records in the UI data,project staff selected the best match by comparing employer names listed in the UI records with those listedin MDOC records (from parole or probation agent reports). For cases in which no single match could bedetermined, UI data were retained for all social security numbers listed in the MDOC records for a givenindividual, under the assumption that such people worked under multiple social security numbers.

11For those sentenced to jail or jail followed by probation, we must estimate the date of release from jailbased on the jail credits at sentencing and the sentence length because MDOC does not run the jails or trackjail inmates who are not also under MDOC supervision or custody (e.g. parolees or probationers servingjail time, prisoners temporarily housed in local jails for court appearances). In an unknown number of casesthese release dates are overestimates due to early release from jails, which is at the discretion of the localjail and often due to overcrowding. Given the short length of most jail sentences anyway and because we arenot concerned with estimating the effects of jail or jail followed by probation sentences, we do not see thisas a problem for the present analysis.

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elapsed time, both period and aging effects. Measuring outcomes from time since release

also risks allowing some endogeneity to creep back into our estimates, as release dates

are potentially a function of behavior during prison. In addition, those sentenced to

particularly long minimum sentences will not have post-release outcomes, especially for

time periods furthest from release. Measuring outcomes starting at sentence avoids these

problems, but produces estimates that may be dominated by incapacitation effects.12 In

what follows, we report results from both approaches.

The analytic sample excludes resentences, flat or mandatory sentences (including life

sentences), community service and fines sentences, as well as records from specialty courts

(e.g., drug and family courts). We retained only the carrying or most severe offense and

associated sentencing outcome when the offender was convicted of multiple offenses. We

perform all analyses using records for non-habitual offenders only as this category con-

tains the vast majority of observations. The analytic sample for the RD analysis consists

of around 21,500 individual records from 83 counties in Michigan which correspond to

individuals whose PRV score (running variable) is within 16 points of the relevant cutoff.13

Table 1 shows basic descriptive statistics by sentence type. About 90% of offenders

in the sample are sentenced to intermediate sentences while only 10% are sentenced to

prison. Minimum sentence lengths are largest for probation and jail with probation with

27 and 31 months on average, respectively. The table also shows means of the baseline

covariates. The sample of offenders is primarily male, white, and non-married. Across all

sentence types, around a third of individuals have very low education, about 20% have

a mental illness, and between 30 and 50% have an addiction to alcohol. On average, at

the time of sentence the offenders were 30 years old, and were first arrested when they

were 20 years old. Finally, employment was very low with the average offender working

12Starting the risk period at sentence may also has more policy relevance because legislators and judgessurely consider incapacitation effects in making decisions or policies related to sentencing or release fromprison.

13The OSV score could potentially be used as an alternative or secondary running variable; nevertheless,it is more likely to be subject to manipulation than the PRV scores. The explanation of why the bandwidthof 16 point from the cutoff is chosen is given in the results section.

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only about a third of the time before sentence.

Table 1: Descriptive statistics

Sentence type

Prison Probation JailJail withprobation

% of observations in sample 10.69 28.82 7.69 52.80

Average sentence length (months) 17.75 27.00 7.14 30.64

Median sentence length (months) 18.00 24.00 7.00 24.00

% of women 0.08 0.18 0.11 0.14

% white 0.59 0.49 0.57 0.69

% married 0.14 0.14 0.12 0.14

% with less than high school 0.44 0.45 0.47 0.42

Average age at sentence 32.90 30.80 32.75 31.98

Average age at first arrest 19.46 20.43 19.57 20.46

% with mental illness 0.19 0.18 0.19 0.21

% with drug addiction 0.54 0.50 0.52 0.51

% with alcohol addiction 0.50 0.32 0.42 0.52

Proportion of quarters employed within 3years before sentence

0.30 0.35 0.27 0.38

Proportion of quarters employed within 6years before sentence

0.33 0.36 0.29 0.39

Notes: All figures correspond to observations within 16 points from the cutoff. Sample sizes are

between 18,300 and 21,700 depending on the variable. Sentence length for jail with probation is

for the probation part of the sentence. Less than high school does not include GED.

Descriptive statistics of the outcomes are presented in Table 2. As mentioned above,

we analyze both after sentence and after release risk periods. Panel A shows average

recidivism for the four sentence types. Within 6 months after sentence the incidence of

new felonies is close to zero for all offenders (this reflects in part the fact that we measure

new felonies at the conviction date, not the offense date, because offense dates were more

frequently missing and in some cases unreliable). It increases monotonically with time

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for all sentence types, although the rates of increase are highest for probationers. This

group exhibits the highest recidivism rates after sentence with around 20% of offenders

committing a new felony within 5 years of sentence. This is in contrast to prisoners,

for whom the recidivism rate is around 8% in the same time frame, reflecting in part

incapacitation in prison, as the median prison minimum sentence length is 18 months.

Individuals sentenced to jail and jail with probation exhibit recidivism rates similar to

those of probationers.

The incidence of recidivism is also low within 1 year after release for all groups. How-

ever, in contrast to the after sentence statistics, the increase in the rate is similar in all

cases, reaching 12% and 20% on average within 3 and 5 years after release, respectively.

The fact that after sentence but not after release the Lower recidivism rates for recidi-

vism measured after sentence than after release for individuals in prison, jail, and jail

with probation reflects the incapacitation effect of incarceration in prison and jail. The

differences are smaller for sentences involving jail because jail stays are relatively short.

The employment statistics are shown in Panel B of Table 2. Four calendar quarters

after sentence offenders sentenced to prison seem to be at a large disadvantage in terms

of the probability of being employed than individuals in other sentence types. Presum-

ably, this is also a consequence of the incapacitation effect. It does not show up in other

incarceration sentences such as jail and jail with probation because incarceration in jail

is typically fairly short. Further out in time, at 12 and 20 quarters after sentence, the

employment rate oscillates around 20% for individuals in all sentence types, although

those in jail with probation seem to have slightly better employment outcomes.

After release, it is interesting that employment rates start out higher in the fourth

quarter after release but then decline substantially in the 12th and 20th quarters. In the

case of prisoners whose decline from the 4th quarter to the 12th and 20th quarters is the

largest, almost 30% are employed soon after release but only around 17% have a job in

the 20th quarter after release. A post-prison peak in employment has been observed in

other studies using UI records (see Bushway et al., 2007).

16

Table 2: Descriptive statistics of outcomes of interest

Panel A. Any new felony within:

After sentence After release

1 year 3 years 5 years 1 year 3 years 5 years

Prison 0.003 0.116 0.247 0.063 0.237 0.350

Probation 0.075 0.233 0.324 0.075 0.233 0.324

Jail 0.031 0.207 0.301 0.073 0.234 0.317

Jail with probation 0.036 0.189 0.282 0.065 0.210 0.296

Panel B. Any employment in:

After sentence After release

4th quarter 12th quarter 20th quarter 4th quarter 12th quarter 20th quarter

Prison 0.103 0.200 0.166 0.281 0.190 0.169

Probation 0.324 0.256 0.208 0.324 0.256 0.208

Jail 0.203 0.175 0.153 0.185 0.173 0.140

Jail with probation 0.357 0.290 0.237 0.342 0.277 0.227

Panel C. Fraction released

After sentence

1 year 3 years 5 years

Prison 0.304 0.806 0.930

Probation 1 1 1

Jail 1 1 1

Jail with probation 1 1 1

Notes: All figures correspond to observations within 16 points from the cutoff. Sample sizes are between 21,300 and 21,700

depending on the variable.

17

5 Empirical Strategy

Our analysis exploits the exogenous change in the probability of being sentenced to prison

arising from the marginal increase in PRV scores that moves an offender from an interme-

diate cell (where the presumptive sentence is something other than prison) to a straddle

cell (where recommended sentence types include prison). In other words, offenders with

similar PRV scores face different probabilities of going to prison depending on whether

their PRV score lies to the left or right of a cut point that determines the boundary

between an intermediate and a straddle cell. This setting naturally leads to a fuzzy

regression discontinuity (RD) design because the increase in the probability of going to

prison from crossing the boundary between an intermediate and a straddle cell is less

than 1.

One complexity in our application of fuzzy RD is that the Michigan sentencing guide-

lines contain many potential discontinuities. Depending on the grid and OV level where

an offender is placed, the offender will be affected by a different cutoff. For example,

in the grid shown in the appendix, an offender in OV level I would be affected by the

PRV score cutoff of 50 points while the relevant cutoff for an offender in OV level II is 25

points. Therefore, only one cutoff is relevant for each individual. This differs from the

setup in other RD designs with multiple discontinuities in which the same individual is

affected by all the cutoffs (see for example van der Klaauw, 2002).

A second complexity is that our treatment, sentence type, is not dichotomous but

rather has four categories. The sentence types contemplated in the Michigan sentencing

guidelines can be many as discussed in section 3. In particular, the vast majority of of-

fenders in our sample are sentenced to prison, jail, jail with probation, or probation. We

do not consider other possible sentences such as fines or community service because we

believe individuals who receive such sentences have zero probability of receiving a prison

sentence and are therefore not appropriate comparisons for those sentenced to prison.

Our main theoretical question relates to the prison vs. probation comparison but since

other sentence types are possible in intermediate and straddle cells, we must incorporate

18

them in the analysis.

A common strategy to analyze the data from multiple cutoffs in a regression disconti-

nuity setup is to normalize all cutoffs to zero to run a pooled regression on all observations

to obtain the treatment effect based on a single-cutoff estimator. Cattaneo et al. (2015)

show that normalization of the cutoffs estimates an average of local average treatment

effects that is weighted by the relative density of observations around each cutoff. Under

this framework and given the fuzzy nature of our RD design, we are only able to identify

one treatment effect using the single cutoff as an instrumental variable. Since we have

four sentence types, we construct indicator variables for which the reference category is

probation. The sentence type variables are defined as prison vs. everything else, jail vs.

everything else, and jail with probation vs. everything else. When including all three

sentence type indicators in the regression, the indicator variables give the difference in

the outcome between prison and probation, jail and probation, and jail with probation

and probation, respectively. However, our treatment of interest is sentence to prison as

compared to sentence to probation, so we include the indicators for jail and jail with

probation as controls in the regression and do not give a causal interpretation to their

coefficients. As we will show below, the discontinuities at the borders between interme-

diate and straddle cells only produce meaningful variation in treatment assignment for

the prison vs. probation comparison.

The fuzzy RD can be described by the following two-equation system:

yi = β0 + τDi + β1PRVi + β2PRVi ·Di +Xγ + εi (1)

Di = α0 + ηTi + α1PRVi + α2PRVi · Ti +Xθ + νi (2)

Where (2) is the first stage equation relating the treatment dummy (Di) with an

indicator for crossing the cutoff (Ti), and (1) is the outcome equation relating the out-

come yi with the treatment dummy. The matrix X includes the treatment dummies

that are not being instrumented as well as controls for age. The outcomes we consider

19

are recidivism and employment over different time frames as described in the data section.

As shown by Angrist and Pishke (2009), the fuzzy RD estimation is mathematically

equivalent to instrumental variables (IV) estimation. In this sense, the indicator for

crossing the cutoff can be used as an instrument for the treatment dummy, and the two

equations above can be estimated by 2SLS. This method provides the causal effect of

the treatment on the outcomes of interest for those who are affected by the instrument

(crossing the cutoff) provided that the instrument only affects the outcome through its

effect on the probability of going to prison (the exclusion restriction), and that crossing

the cutoff makes offenders more likely to go to prison (monotonicity). One possible threat

to the exclusion restriction is that crossing the cutoff could affect the outcome through

changes in sentence lengths as well as sentence types. However, in this setting crossing

the cutoff does not produce variation in either prison length for those sentenced to prison

on both sides of the cutoff or probation sentence length for those sentenced to probation

on both sides of the cutoff.

In the results shown later, we estimate the models with a linear functional form of the

running variable allowing for a different slope on either side of the cutoff. The running

variable (PRV scores) is centered to zero so that equation (1) estimates the treatment

effect at the cutoff. Consistent with current best practice in RD designs, we use local

linear regressions (LLR) around each cutoff are only using observations that are within

a narrow bandwidth from the cutoff.

We also conduct a reduced-form analysis that estimates the effects of crossing the

cutoffs on the oucomes. From the equations above, the reduced-form equation is obtained

by substituting equation (2) on equation (1) as follows:

yi = β0 + τRTi + β1PRVi + β2PRVi ·Di +Xγ + ϵi (3)

In this case, the coefficient τR is the intent-to-treat effect, that is, the effect of being

eligible for a prison sentence (by crossing the boundary between an intermediate and a

20

straddle cell). We perform reduced-form analyses for the 11 cutoffs separately.

To account for potential heterogeneity in the first stage across multiple cutoffs in

our data, we reformulate the IV setup so that we can use the 11 cutoffs as 11 separate

instrumental variables. This relaxes an assumption implicit in an analysis that pools all

cutoffs together, that the effect of crossing each cutoff on treatment assignment is the

same. Such an assumption may be unreasonable here because the various cutoffs are for

different crime classes (severities), for offenders with different criminal histories, and for

offenses with different characteristics. The two-equation system for a setup that treats

each cutoff as a separate instrument is:

yic = β0 + τDi + β1PRVi + β2PRVi ·Di + δcCi + πcPRVi · Ci +Xγ + εi (4)

Di = α0 + λcTic + α1PRVi + α2PRVi · Tic + ιcCi + θcPRVi · Ci +Xµ+ νi (5)

Where yic is the outcome for individual i in cutoff c, Di is the treatment of interest,

Tic indicates whether the PRV score is to the right of cutoff c, and Ci is an indicator

for whether the individual’s relevant cutoff is cutoff c. We control for a full set of cutoff

dummies as well as their interactions with the running variable . Again, we center

the running variable at zero for each cutoff, and include controls for the non-relevant

treatments and age. Similar to the pooled single-cutoff model, we estimate the model by

2SLS.

6 Results

This section presents graphic and econometric evidence of the magnitude of the rela-

tionship between the probability of receiving a prison sentence and crossing the cutoff,

the so-called first stage. We also show reduced-form results for the recidivism and em-

ployment outcomes. We conclude by showing instrumental-variable regressions based on

pooling all cutoffs together and using the 11 cutoffs as multiple IVs.

21

All estimates in this section are obtained from local linear regressions (LLR) within

a bandwidth of 16 points from the cutoff. The procedure to arrive at this bandwidth

is based on the application of randomization inference to RD proposed by Cattaneo et

al. (2015a). This procedure emerges from the assumption that within a narrow win-

dow around the cutoff, the RD design is analogous to a randomized experiment. Even

though the estimation can be performed relying on parametric extrapolation from flexible

polynomials that use all the observations, we avoid this approach because it produces

biased point-estimates and standard errors if done incorrectly.14 What the randomization

inference procedure proposes is to find the smallest window in which local randomiza-

tion is an appropriate assumption. It consists of running a series of balance tests of

the baseline covariates for each candidate window, and choosing the smallest window in

which covariate balance is not rejected. We implement this test for each of the 11 cut-

offs by running seemingly unrelated regressions (SUR) in which we test the hypothesis

that the covariates in Table 1 are jointly balanced in a given window. We found that a

window of 16 is the smallest window in which the covariates are balanced for all cutoffs.15

Another substantive reason to implement the test derived from randomization infer-

ence is that the nature of the PRV scores (running variable) does not allow to perform

McCrary type tests (McCrary, 2008). As discussed in the sentencing guidelines section,

the PRV scores are constructed from 7 different prior record variables. These variables

are coded in multiples of 5 and 2, so it is impossible to get certain values of the score.

14As we explored the possibility of a strategy involving polynomial functional forms for the running variableand all observations, we conducted AIC tests to obtain the optimal polynomial order for each outcome /cutoff combination when using the whole range of observations in Grids D, E and F. The optimal ordersvaried considerably across cutoffs, so to avoid imposing the same functional form for all cutoffs, we opted forthe randomization inference approach in which the linear approximation is valid for all outcomes / cutoffsonce we restrict the observations to a narrow window around each cutoff.

15For two of the cutoffs (Grid E, OV II and Grid F, OV II) we found that there is no balance of thecovariates in any of the candidate windows. However, once we control for a quadratic on age at sentencein the SUR tests, the covariates are balanced within the bandwidth of 16 points. Hence, we control for aquadratic on age in all estimations. This is appropriate because age is mechanically correlated with therunning variable, a composite of the offender’s prior record. Older offenders will on average have higherprior record scores since they have had more time to commit and be apprehended for crimes. As a result,we understand the RD design to be valid in this setting only once we have conditioned on age.

22

In this sense, the running variable is not only not continuous but very rugged, which

makes the McCrary test non-informative, as the test will appear to detect evidence of

manipulation where there are merely mathematically impossible values of the running

variable. Hence, we rely on balance tests of the covariates to establish the validity of our

RD design.

6.1 First stages

Figure 1 shows the basic relationship between the probability of going to prison and the

dummy for crossing the cutoff when all cutoffs are pooled into a single one and centered

at zero. The y axis shows the probability of going to prison relative to the other three

types of sentences, and the x axis shows the PRV scores. Scores greater or equal to zero

indicate that the individual’s PRV score is at or to the right of the cutoff relevant for that

individual. In the graph, each dot represents the average probability of going to prison

for each value of the PRV scores, and the lines are the fitted values from a regression

of the prison indicator on a dummy for crossing the cutoff, the running variable and an

interaction between the two.16 There is a clear discontinuity in the probability of being

sentenced to prison for individuals with PRV scores at and to the right of the cutoff,

i.e. offenders whose PRV score places them in a straddle cell. Visually, the jump in the

probability of prison at the cutoff is around 10 percentage points.

The first stage graph in Figure 1 illustrates the raw discontinuity, that is, without

controlling for age and cutoff fixed effects. Table 3 presents the first stage regressions

for the pooled sample and each cutoff individually. In the pooled case, the regression

controls for a quadratic on age, cutoff fixed effects and their interactions with the running

variable. Crossing the cutoff increases the probability of receiving a prison sentence by

9.3 percentage points, very similar to what we observe in Figure 1.

We estimate the first stage for each of the cutoffs in Grids D, E and F. The magnitude

16Note that although all dots are drawn the same size, they may represent vary different numbers ofobservations. This is the case with all graphs we present in this paper.

23

0.1

.2.3

.4P

r (P

rison

)

−20 −10 0 10 20PRV scores centered at zero

First stagePrison vs. all other sentences

Figure 1: First stage - pooled cutoffs

of the first stage oscillates between 4.85 percentage points in Grid E, OV I to 39.9

percentage points in Grid F, OV IV. Notice the variation in the size of the jump across

cutoffs, as well as the variation in the sample sizes. The small sample sizes in each cutoff

suggest that estimating separate models for each cutoff would lead to underpowered

estimates. The cutoffs that seem to provide stronger first stages in terms of the size of

the jump and the statistical significance are those in Grid D. This makes sense based

on the classification of the crime classes provided by the Michigan sentencing guidelines;

high severity crimes are in grids letters closer to A. Offenders in Grid D have committed

more serious crimes, and are therefore more likely to be sentenced to prison if their scores

place them in a straddle cell. Although not smaller in magnitude than other first stages,

two of the cutoffs (Grid E, OV IV and Grid F, OV I) are not statistically significant.

This is probably due to lack of power because other cutoffs with similar sample sizes have

a significant first stage when the point estimate is much higher than those in these two

cutoffs, and because other cutoffs with similar first stage coefficients have a significant

first stage when the sample size is larger. The first stage graphs for each of the 11 cutoffs

24

Table 3: First stages

1{PRVi ≥ cutoff} S.E. Observations R-squared

All cutoffs pooled 0.0931*** 0.0091 21,737 0.13

Grid DOV I 0.1894*** 0.0545 1,034 0.13

OV II 0.1186*** 0.0354 1,597 0.14

OV III 0.2313*** 0.0517 586 0.10

Grid EOV I 0.0485*** 0.0130 6,000 0.10

OV II 0.1166*** 0.0151 6,631 0.139

OV III 0.1386*** 0.0415 1,192 0.16

OV IV 0.0640 0.0423 1,017 0.12

Grid FOV I 0.0680 0.0541 730 0.05

OV II 0.0811*** 0.0225 2,132 0.08

OV III 0.1418** 0.0566 607 0.11

OV IV 0.3985*** 0.0921 211 0.10

Notes: Robust standard errors. All models regress the prison dummy on a dummy for

crossing the cutoff, the PRV scores, the interaction between the two, cutoff fixed effects,

their interaction with the PRV scores and a quadratic on age at sentence.

*** p

than the cutoff, a linear term on the running variable, an interaction between the cutoff

dummy and the PRV scores that allows for a different slope on either side of the cutoff,

and a quadratic on age at sentence. In the case of the pooled regressions, cutoff fixed

effects and their interactions with the running variable are also included. All regressions

include observations within a 16-point window from the respective cutoff.

Table 4 presents the results from the recidivism reduced form regressions for all cut-

offs pooled together and for each individual cutoff. Six outcome variables are examined:

binary indicators for whether the offender recidivates within 1 year, 3 years, and 5 years

after sentence and after release. The after-sentence estimates capture in part any incapac-

itation effect that emerges from the fact that a significant portion of offenders sentenced

to prison are still incarcerated in the time frames at which the outcome variables are

measured. Recall from Table 2 that, in this sample, only 30% of prisoners have been

released to the community 1 year after sentence. The first row of the table shows that

compared to being in an intermediate cell, being to the right of the cutoff translates into a

probability of committing a new felony that is 1.24 percentage points lower. Three years

after sentence the probability is lower by 3.27 percentage points, and 5 years later, it is

lower by 2.52 percentage points. All these figures are statistically significant, although

the last one is only significant at the 10% level. After release, the picture is substantially

different. None of the effects are significant at the 5% level, meaning that after being

released to the community, the likelihood of committing a new crime is basically the

same for an individual who was sentenced to prison than for somebody with a different

sentence type. This is consistent with what was shown in Table 2, i.e., all sentence types

had very similar recidivism rates after release.

Table 4 also shows a great deal of heterogeneity across cutoffs. While most of the

signs of the point estimates are negative, some are positive, suggesting that crossing the

cutoff increases the probability of committing a new crime. The majority of positive

signs are found in Grids E and F in which the severity of the crime for which individu-

als were originally sentenced is lower than in grid D. It is worth noticing that at times

the coefficients are sizeable in magnitude but the small number of observations increases

26

Table 4: Reduced forms by cutoff (recidivism)

Any new felony within:

After sentence After release1 year 3 years 5 years 1 year 3 years 5 years

All cutoffs -0.0124** -0.0327*** -0.0252* -0.0063 -0.0196* -0.0172pooled (0.0059) (0.0113) (0.0129) (0.0073) (0.0118) (0.0132)

Grid D

OV I -0.0137 -0.0939* -0.0319 0.0225 -0.0667 -0.0295(0.0297) (0.0549) (0.0635) (0.0393) (0.0600) (0.0649)

OV II -0.0329 -0.0458 -0.0045 -0.0208 -0.0320 -0.0031(0.0221) (0.0434) (0.0485) (0.0283) (0.0450) (0.0495)

OV III -0.0106 -0.1432* -0.1628* -0.0137 -0.1818** -0.1452(0.0355) (0.0777) (0.0939) (0.0477) (0.0844) (0.0981)

Grid E

OV I -0.0284** -0.0538** -0.0679** -0.0162 -0.0488** -0.0704***(0.0142) (0.0243) (0.0265) (0.0161) (0.0248) (0.0267)

OV II -0.0090 -0.0417** -0.0202 -0.0109 -0.0209 -0.0063(0.0092) (0.0191) (0.0224) (0.0119) (0.0202) (0.0230)

OV III 0.0263 0.0492 0.0409 0.0658** 0.0709 0.0892*(0.0225) (0.0455) (0.0518) (0.0308) (0.0481) (0.0537)

OV IV 0.0134 -0.0338 -0.0644 -0.0178 -0.0338 -0.0643(0.0191) (0.0546) (0.0656) (0.0313) (0.0585) (0.0692)

Grid F

OV I 0.0107 0.0547 0.0138 -0.0381 0.0533 0.0124(0.0312) (0.0646) (0.0744) (0.0430) (0.0695) (0.0775)

OV II -0.0074 0.0189 0.0386 -0.0021 0.0292 0.0403(0.0166) (0.0332) (0.0388) (0.0199) (0.0348) (0.0399)

OV III 0.0220 -0.0658 -0.0592 0.0140 -0.0629 -0.0620(0.0274) (0.0590) (0.0691) (0.0385) (0.0642) (0.0738)

OV IV -0.0529 0.0621 -0.1820 -0.0081 0.1073 -0.1162(0.0520) (0.1305) (0.1479) (0.0796) (0.1388) (0.1575)

Notes: Robust standard errors in parentheses. Results are from regressions of each outcome on a

dummy for crossing the cutoff, a linear term on the PRV scores and the interaction between

the two. A quadratic on age at sentence is also included.

*** p

0.0

5.1

.15

−20 −10 0 10 20PRV scores centered at zero

Reduced formNew offense within 1 year after sentence

(a)

.06

.08

.1.1

2.1

4.1

6

−20 −10 0 10 20PRV scores centered at zero

Reduced formNew offense within 1 year after release

(b)

.15

.2.2

5.3

.35

−20 −10 0 10 20PRV scores centered at zero

Reduced formNew offense within 3 years after sentence

(c)

.1.2

.3.4

.5

−20 −10 0 10 20PRV scores centered at zero

Reduced formNew offense within 3 years after release

(d)

.2.3

.4.5

.6

−20 −10 0 10 20PRV scores centered at zero

Reduced formNew offense within 5 years after sentence

(e)

.2.3

.4.5

.6

−20 −10 0 10 20PRV scores centered at zero

Reduced formNew offense within 5 years after release

(f)

Figure 2: Recidivism reduced forms (all cutoffs pooled)

the uncertainty with which they are estimated. Grid E is perhaps an exception to the

small sample problem. In fact, in this grid we find most of the significant estimates. In

28

particular, for OV level I we find that being in a straddle cell reduces the probability of

committing a new crime 1, 3, and 5 years after sentence, and 3 and 5 years after release.

The magnitudes of these reductions are important: 3 and 5 years after sentence, the

probability of recidivating is about 5 and 7 percentage points lower, respectively, after

sentence and after release. In this case, it seems that more than having an effect through

the incapacitation effect, being in a straddle cell is effectively reducing the probability

of committing new crimes once the offenders are released to the community. This is of

course not generally the case. For example, in OV II in the same grid we find the op-

posite effect (that individuals in a straddle cell are more likely to recidivate) both after

sentence and after release, and these estimates are statistically significant 1 and 5 years

after release.

Regarding employment, Table 5 shows the reduced form coefficients in the same

format discussed above. The employment outcomes are measured by binary variables

indicating whether the individual is observed receiving formal sector wages in a given

period (4th, 12th, and 20th quarters) after sentence and after release. Pooling all cut-

offs together, the coefficients across all outcomes are very close to zero and insignificant.

This suggests that employment outcomes are similar for individuals sentenced to any of

the sentence types. Recall also that the employment rates for this sample are very low,

almost never surpassing 35% in any of the sentence groups or time frames (see Table 2).

Examining individual cutoffs separately supports our conclusions from the pooled

case. Most of the regressions give very small coefficients that are statistically insignifi-

cant. As with recidivism, there seems to be heterogeneity, as the signs of the coefficients

are not the same across the table. The few coefficients that are significant are very large

in magnitude. For example, in the 20th quarter after release in Grid D, OV III, crossing

the cutoff is associated with a probability of having a job that is 21.3 percentage points

larger than being to the left of the cutoff. Similarly, for the same quarter after release,

this probability is 15 percentage points larger in Grid F, OV I.

Graphical presentations of the reduced forms are provided in Figures 2 and 3. As

29

Table 5: Reduced forms by cutoff (employment)

Any employment in:

After sentence After release4th quarter 12th quarter 20th quarter 4th quarter 12th quarter 20th quarter

All cutoffs -0.0175 0.0078 0.0039 -0.0071 -0.0023 0.0039pooled (0.0133) (0.0127) (0.0119) (0.0135) (0.0127) (0.0121)

Grid D

OV I -0.0149 0.0081 -0.0527 -0.0707 -0.0528 0.0260(0.0506) (0.0518) (0.0460) (0.0549) (0.0507) (0.0466)

OV II 0.0319 0.0404 0.0123 0.0650 0.0790* -0.0068(0.0471) (0.0452) (0.0422) (0.0481) (0.0451) (0.0437)

OV III 0.0554 0.1265 0.0711 0.0895 0.0726 0.2128**(0.1142) (0.1135) (0.1084) (0.1165) (0.1108) (0.1080)

Grid E

OV I 0.0229 -0.0053 -0.0237 -0.0035 -0.0103 -0.0087(0.0251) (0.0235) (0.0220) (0.0252) (0.0235) (0.0222)

OV II -0.0329 0.0053 0.0245 -0.0037 0.0014 0.0209(0.0246) (0.0238) (0.0225) (0.0250) (0.0237) (0.0227)

OV III -0.0880 -0.0352 0.0225 -0.0868 -0.0581 -0.0092(0.0556) (0.0535) (0.0502) (0.0563) (0.0527) (0.0511)

OV IV -0.1036 -0.0329 -0.0756 -0.0730 0.0303 0.0073(0.0856) (0.0836) (0.0790) (0.0868) (0.0830) (0.0820)

Grid F

OV I 0.0114 0.0833 0.0840 0.1048 0.0886 0.1499**(0.0663) (0.0637) (0.0587) (0.0696) (0.0633) (0.0581)

OV II -0.0571 0.0465 0.0297 -0.0332 -0.0049 0.0267(0.0428) (0.0395) (0.0366) (0.0429) (0.0398) (0.0371)

OV III -0.0717 0.0010 -0.0382 0.0131 -0.0924 -0.0730(0.0780) (0.0727) (0.0674) (0.0798) (0.0710) (0.0727)

OV IV -0.3509 -0.1211 0.3496* -0.2665 -0.1171 0.3133(0.2140) (0.2019) (0.1931) (0.2205) (0.2149) (0.1897)

Notes: Robust standard errors in parentheses. Results are from regressions of each outcome on a dummy for

crossing the cutoff, a linear term on the PRV scores and the interaction between the two. A quadratic on age

at sentence is also included.

*** p

.15

.2.2

5.3

.35

.4

−20 −10 0 10 20PRV scores centered at zero

Reduced formAny employment in 4th quarter after sentence

(a)

.2.2

5.3

.35

.4

−20 −10 0 10 20PRV scores centered at zero

Reduced formAny employment in 4th quarter after release

(b)

.05

.1.1

5.2

.25

.3

−20 −10 0 10 20PRV scores centered at zero

Reduced formAny employment in 12th quarter after sentence

(c)

.05

.1.1

5.2

.25

.3

−20 −10 0 10 20PRV scores centered at zero

Reduced formAny employment in 12th quarter after release

(d)

.05

.1.1

5.2

.25

−20 −10 0 10 20PRV scores centered at zero

Reduced formAny employment in 20th quarter after sentence

(e)

.05

.1.1

5.2

.25

−20 −10 0 10 20PRV scores centered at zero

Reduced formAny employment in 20th quarter after release

(f)

Figure 3: Employment reduced forms (all cutoffs pooled)

before, the graphs show the average of the outcome variable for each value of the running

variable, and the lines show the predicted values from regressions as described above.

31

Due to space constraints, we only present graphs based on the pooled sample. These

graphs are consistent with the reduced form estimates for the pooled models presented

in Table 4 and Table 5.

6.3 OLS and 2SLS estimates

Our last set of results exploits the fact that our RD is a fuzzy design because the prob-

ability of going to prison does not increase from zero to one when crossing the cutoff.

As discussed in section 5, a fuzzy RD design is basically an instrumental-variable design

in which the first stage is given by the change in the probability of receiving the treat-

ment when crossing the cutoff. In this sense, 2SLS is an appropriate estimation method

to obtain a consistent estimate of the treatment effect for observations near the cutoff

and for whom crossing the cutoff changes the treatment assigned. As explained in the

beginning of this section, we implement local linear regressions within a bandwidth of

16 points around the cutoff. This is the widest bandwidth for which we found that the

covariates were balanced across all 11 cutoffs. As we have done throughout this paper, in

the results that follow we differentiate between the effects after sentence and after release.

Tables 6 and 7 present results for the recidivism and employment outcomes, respec-

tively, for the pooled sample only.17 We show only the coefficient for the treatment of

interest, i.e. the indicator for whether the individual was sentenced to prison as compared

to probation. Each table contains three panels indicating the estimator that was used to

obtain the coefficient. In Panel A, the nave OLS regression coefficient is reported. This is

a regression of the outcome on three indicators for sentence type (excluding probation),

a linear term on the PRV scores, interactions of the sentence type indicators and the

PRV scores, interaction of the cutoff dummy with the PRV scores, a quadratic on age

at sentence, and cutoff fixed effects and their interactions with the PRV scores. Since

the omitted treatment dummy is probation, the coefficient on the dummy for prison is

measuring the difference, at the cutoff, in the outcome of interest between an individual

17As we saw previously, most coefficients in the reduced form regressions by cutoff were not significant.Hence, presenting 2SLS regressions by cutoff would not be reasonable since the standard errors in the 2SLSregressions will be higher than those in the reduced form regressions.

32

sentenced to prison relative to one sentenced to probation.

The OLS coefficient is naive in the sense that it does not instrument for the treat-

ment using the change in probability of treatment attributable to crossing the cutoff.

In other words, it does not take into account the fact that the probability of going to

prison does not automatically jump to one to the right of the cutoff. For this reason, we

implement two IV approaches. The first approach is based on pooling all cutoffs together

to create a single cutoff that will serve as a single instrumental variable for the prison

treatment indicator. The IV is simply a dummy equal to one if the PRV score is to the

right of the cutoff. Under this approach, we have one endogenous variable that we want

to instrument and one IV, so the model is exactly identified. In the second approach

we make use of the multiple instruments that the 11 cutoffs provide. As before, we can

construct the same type of instrumental variables by generating 11 dummy variables for

whether the PRV is greater than or equal to each individual cutoff value. In this case,

we will use 11 IVs to instrument the prison dummy, so the model is overidentified. We

expect that sampling variability will be lower under this approach because the first stages

more accurately capture the change in treatment probability that comes from crossing

each cutoff (rather than assuming that change is the same for all cutoffs as the pooling

approach does), leading to a (slightly) stronger first stage. In 2SLS, a stronger first stage

leads to smaller SEs for the treatment effect coefficient(s) (Wooldridge, 2002). In each

of the two approaches we include an interaction between the treatment dummy and the

running variable, which is instrumented by interactions between the IV and the PRV

scores in the first case, and by interactions between each of the IVs and the PRV scores

in the second.

The results for the recidivism outcomes are presented in Table 6. The OLS estimates

show that the probability of committing a new crime is reduced by 7.2, 12.6, and 9.8

percentage points 1, 3, and 5 years after sentence, respectively, when the individual is

sentenced to prison as compared to probation. Similarly, the probability of recidivating

is 1.68 points lower 1 year after release. For longer periods after release, there does not

seem to be any difference between individuals sentenced to prison rather than probation.

33

Table 6: LLR results (recidivism)

Any new felony within:

After sentence After release1 year 3 years 5 years 1 year 3 years 5 years

Panel A. OLS

1{Sentence = prison} -0.0723*** -0.1256*** -0.0979*** -0.0168** -0.0138 -0.0096(0.0046) (0.0101) (0.0123) (0.0071) (0.0120) (0.0137)

Observations 21,737 21,737 21,737 21,641 21,594 21,399

Panel B. 2SLS - All cutoffs pooled

1{Sentence = prison} -0.1549** -0.3639*** -0.2908** -0.0742 -0.2252 -0.2213(0.0670) (0.1309) (0.1481) (0.0853) (0.1434) (0.1673)

Observations 21,737 21,737 21,737 21,641 21,594 21,399

Panel C. 2SLS - Multiple cutoffs

1{Sentence = prison} -0.1391*** -0.2461** -0.1782 -0.0473 -0.0765 -0.0554(0.0539) (0.1056) (0.1206) (0.0702) (0.1173) (0.1390)

Observations 21,737 21,737 21,737 21,641 21,594 21,399

Notes: Robust standard errors in parentheses. OLS results are from regressions of each outcome on three treatment dummies

which indicate the sentence type: prison, jail, and jail with probation. The reference category is probation. Regressions include

a linear term on the PRV scores and the interaction between the treatment dummies and the PRV scores. In Panel B, 2SLS

regressions run the same OLS regression instrumenting the dummy for prison with a dummy indicating whether the PRV score

is to the right of the pooled cutoff. In Panel C, the dummy for prison is instrumented with 11 dummies indicating whether the

PRV score is to the right of each of 11 cutoffs. All models include cutoff fixed effects and their interactions with the PRV scores,

as well as a quadratic on age at sentence.

*** p

this is primarily capturing an incapacitation effect. After release, none of the coefficients

are statistically significant, although the coefficients are large in magnitude. With more

than 21,000 observations, the large standard errors are attributable to the fact that the

standard errors in IV estimation tend to be large (Wooldridge, 2002).

The last panel of Table 6 shows the coefficients obtained from the IV approach with

multiple instruments. The magnitudes are fairly consistent with those found in the IV

approach with only one instrument. For example, being sentenced to prison reduces the

probability of committing a new crime by 13.9, 24.6, and 17.8 percentage points when

measured 1, 3, and 5 years after sentence. Even though the standard errors are smaller

under this approach, we find that the effect 5 years after sentence is not statistically

significant. Moreover, the reduction in standard errors is not sufficient to make the after-

release coefficients statistically significant, although the magnitude of these estimates is

more consistent with a no post-release effects than those from the pooled cutoffs single

IV approach, for which the coefficients were very large in magnitude but not significant.

In summary, we see a large incapacitation effect arising from the fact that a signif-

icant fraction of offenders sentenced to prison are still in prison when measuring these

outcomes while individuals in other sentences have already been released or have been

released for longer periods of time. The effects shrink considerably once we compare pris-

oners and probationers after release, and the estimated effects are no longer statistically

significant. We note, however, that the point estimates are still potentially substantively

large in their potential implications, as they represent changes in recidivism rates of

approximately 5-8 percentage points. Even in the models with multiple cutoffs treated

as multiple instruments, our models are underpowered to detect effects of such magnitude.

The employment results presented in Table 7 are consistent with the findings from the

reduced-form regressions. First, the OLS estimates are statistically significant for 5 out

of 6 outcome variables. In the fourth quarter after sentence, prisoners are 19.5 percentage

points less likely to have a job than a probationer. In the 12th and 20th quarters, the

35

negative coefficients are smaller (3.2 and 2.1 percentage points, respectively).18 After

release, there is no difference between a prisoner and a probationer in the fourth quarter,

but the coefficients in the 12th and 20th quarters are almost identical to those in the

corresponding after-sentence quarters.

Table 7: LLR results (employment)

Any employment in:

After sentence After release4th quarter 12th quarter 20th quarter 4th quarter 12th quarter 20th quarter

Panel A. OLS

1{Sentence = prison} -0.1947*** -0.0324*** -0.0213** -0.0172 -0.0394*** -0.0252**(0.0103) (0.0115) (0.0108) (0.0130) (0.0118) (0.0119)

Observations 21,504 21,504 21,504 21,387 21,278 20,612

Panel B. 2SLS - All cutoffs pooled

1{Sentence = prison} -0.1821 0.0921 0.0527 -0.1171 -0.0343 0.1842(0.1501) (0.1443) (0.1351) (0.1594) (0.1515) (0.1912)

Observations 21,504 21,504 21,504 21,387 21,278 20,612

Panel C. 2SLS - Multiple cutoffs

1{Sentence = prison} -0.2326* -0.0123 0.0259 -0.2231* -0.0436 0.0968(0.1210) (0.1160) (0.1088) (0.1310) (0.1249) (0.1452)

Observations 21,504 21,504 21,504 21,387 21,278 20,612

Notes: Robust standard errors in parentheses. OLS results are from regressions of each outcome on three treatment dummies which indicate

the sentence type: prison, jail, and jail with probation. The reference category is probation. Regressions include a linear term on the PRV

scores and the interaction between the treatment dummies and the PRV scores. In Panel B, 2SLS regressions run the same OLS regression

instrumenting the dummy for prison with a dummy indicating whether the PRV score is to the right of the pooled cutoff. In Panel C, the

dummy for prison is instrumented with 11 dummies indicating whether the PRV score is to the right of each of 11 cutoffs. All models

include cutoff fixed effects and their interactions with the PRV scores, as well as a quadratic on age at sentence.

*** p

differences among sentence types were not important as we found in our analyses above.

The only two coefficients that are significant at the 10% level are those for the 4th quarter

after sentence and after release. According to these, a prisoner is about 23 percentage

points less likely to be working in a formal job in the 4th quarter after receiving the

sentence or after being released from prison. Some of the coefficients switch sign but we

cannot tell whether it is because prisoners are really more likely to be working (some

of the point estimates are sizeable in magnitude) or because of the imprecision of our

estimates. We do note, however, that in both 2SLS approaches, the point estimates for

employment effects trend to more positive effects of prison on employment over time,

starting most negative in the 4th quarter and moving to most positive in the 20th quar-

ter, suggesting yet another axis along which effects of incarceration in prison may be

heterogeneous.

All in all, the employment results are not supportive of effects of incarceration in

prison vs. probation on employment outcomes. These conclusions must be tempered

by the fact that our standard errors are too large to give very precise estimates, and

as a result our results are not inconsistent with incarceration effects. However, the

2SLS results are consistent with the descriptive statistics and reduced-form regressions

discussed above.

7 Conclusion

Whether and how being incarcerated in prison affects one’s future behavior are questions

that criminologists have asked for decades. This paper leverages discontinuities in the

probability of being sentenced to prison arising from the structure of the Michigan Sen-

tencing Guidelines to provide new estimates of the total effects of incarceration on future

recidivism and employment outcomes. The sentencing guidelines provide a framework in

which low-level offenders (classified in Grids D, E, and F, i.e. low-severity crime classes)

may receive a prison sentence if their prior record scores (PRV) are at or above a certain

cutoff determined by the specific grid and the offense severity level. This setup leads to a

fuzzy RD design in which the running variable is the PRV scores. To estimate the causal

37

effect of receiving a prison sentence relative to probation, we perform reduced-form and

instrumental-variable analyses based on the logic of instrumental variables applied to the

fuzzy RD setting. We conduct two types of IV analyses: one in which we pool all cutoffs

together to construct a single binary variable indicating whether the individual’s PRV

score is at or to the right of the pooled cutoff. This indicator is used as an instrument

for the dummy indicating the receipt of a prison sentence. In the second IV approach,

we construct 11 IVs in the same way, one for each of the 11 cutoffs present in Grids D,

E, and F of the Michigan Sentencing Guidelines.

From our analytical sample of around 21,000 observations within a bandwidth around

the cutoff of 16 points of the PRV scores, we are able to identify significant incapacita-

tion effects particularly for recidivism. Being sentenced to prison reduces the likelihood

of committing a new crime by at least 14 percentage points relative to an offender sen-

tenced to probation. This effect is present 1, 3, and 5 years after sentence. After release,

we find null prison effects in all time frames. Hence, our results suggest that, at the

cutoff, the main effect of sentencing offenders to prison operates through incapacitation.

That is, our results indicate that individuals getting a prison sentence behave the same

as individuals receiving probation after release. One interpretation of these two results

taken together is that either criminogenic and crimino-suppressive mechanisms are both

null or that the two types of effects roughly cancel each other out. While we cannot

distinguish between the various mechanisms that might bring about those effects, our

results do suggest the importance of incapacitation effects. If it were to generalize, this

would also be an important conclusion from a policy perspective, as it suggests that

sentencing offenders on the margin between prison and probation to prison only reduces

their average future offending during the time they spend in prison.

Our IV strategy is less successful in identifying the effects of incarceration on em-

ployment, as the estimates are fairly imprecise. Nonetheless, the estimates suggest that

initially there is a strong negative effect on the probability of having a formal job in

the 4th quarter after sentence and in the 4th quarter after release (which is only signif-

icant at the 10% level). Longer term effects are not statistically significant. We find no

38

statistically significant effect in the 12th quarter and then a slight positive but still not

statistically significant effect in the 20th quarter.

One reading of our results is that they suggest that future research should pay closer

attention to sources of heterogeneity in the effect of incarceration in prison, as some

of our results suggest the potential for considerable effect heterogeneity in the effect

of prison. First, although our results differ from those of some prior studies (see for

example, Mueller-Smith, 2014, who finds positive effects of incarceration on recidivism

and negative effects on employment using a different identification strategy), this may

be because we are estimating effects for a different subpopulation of offenders, in our

case only individuals within a certain window of the cutoffs. Second, the reduced-form

analysis presented in this paper provides evidence that crossing the cutoff has significant

effects on the outcomes that vary in sign depending on the cutoff analyzed. This suggests

that individuals convicted of more or less severe crimes may be affected by prison differ-

ently. Finally, we found some suggestive evidence that the effect of prison on employment

starts out negative and seems to turn positive over time, suggesting that there is treat-

ment effect heterogeneity across different time frames for the outcome. Unfortunately,

our research design and setting are poorly positioned to examine effect heterogeneity

directly. Although we use multiple cutoffs as multiple instruments in