Ambiguity in Criminal Punishment∗

Timothy C. Salmon†

Southern Methodist UniversityAdam Shniderman‡

Texas Christian University

July 2017

Abstract

There has been substantial prior field research on how the incidence of criminalbehavior responds to changes in the probability of punishment. The results of this re-search are at best mixed in regards to its conformance to the predictions of standardexpected utility theory. One possible cause for these mixed results is that punishmentprobabilities in the field are ambiguous rather than uncertain. The presence of thisambiguity could in part explain some of these conflicting results. As a step towardsinvestigating this link, we conduct an experiment on tax compliance intended to try tounderstand how individuals respond to ambiguous punishment probabilities and in par-ticular to how they respond to shifts in ambiguous versus known probabilities. We findthat when probabilities are known and shift, the standard model works well to explainthe response. When the probabilities are ambiguous and shift, the behavioral responseis minimal. We also use these experiments as a means of testing whether ambiguityaversion might be present in suffi cient degree to be exploitable in how enforcement pro-cedures are advertised to increase their effectiveness at minimal cost. We find at bestweak evidence in favor of ambiguity aversion and thus little support for the notion thatenforcement regimes could take advantage of ambiguity aversion.JEL Codes: C91, K42 Key Words: Ambiguity; Criminal Behavior; Deterrence

1 Introduction

Policy makers have three well known levers to use in attempting to deter crime - the severity,certainty and celerity (speed) with which punishments are enforced. There has been sub-stantial research regarding which of these levers is most effective at deterring crime. Thereis often, however, little agreement in the scientific literature on even the most basic of issues

∗Funding for this project was provided by the TCU Research and Creative Activities Fund and by SMUDedman College of Humanities and Sciences . We thank seminar participants at the 2016 North AmericanMeetings of the ESA and the 2017 ASSA Meetings for many helpful suggestions. We in particular thankour discussant at the ASSA meetings, Sera Linardi, for a very useful report. Approval for all experimentsin this paper was obtained from the IRB’s at both SMU and TCU. All subjects signed consent forms priorto participation.†Southern Methodist University, Department of Economics, 3300 Dyer Street, Suite 301 Umphrey Lee

Center, Dallas, TX 75275-0496. tsalmon@smu.edu, Phone: 214-768-3547, Fax: 214-768-1821.‡Texas Christian University, Department of Criminal Justice, 2855 Main Drive, Scharbauer Hall, Suite

4200, Fort Worth, TX 76129. adam.shniderman@tcu.edu, Phone 817-257-6420.

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related to crime deterrence. This study is aimed at trying to better understand one poten-tial explanator for that disagreement, the presence of ambiguity in regard to punishments,and to investigate the nature of decision making in the presence of ambiguity.

A rational choice model of criminal behavior involves a potential criminal weighing thebenefits of a criminal act against the potential consequences. Becker (1968) laid out therational choice model that has served as the basis for much of the subsequent work on crimedeterrence. If one assumes a risk averse individual, this standard model predicts that makingthe punishment for a crime more severe would have a stronger deterrent effect than increas-ing the probability that the individual will be apprehended or that the punishment will berealized. Perhaps paradoxically, Becker and the criminologists whose work is rooted in theBeckerian model have often concluded the opposite to be true based on field investigations.They often find that changing the severity of punishment has little deterrent effect (Deckerand Kohfeld (1990); Doob and Webster (2003); MacCoun and Reuter (1998); Nagin (1978);Nagin (1998); von Hirsch, Burney, and Wikstrom (1999)), while increasing the probabilityof apprehension is sometimes found to have a deterrent effect (Eide (2000); Witte (1983)).However, this issue remains unsettled as other studies often find no effect or even the oppo-site effect (Huff and Stahura (1980); Humphries and Wallace (1980); Loftin and McDowall(1982)). Despite the mixed evidence, many criminologists have concluded that changes incertainty of apprehension have a much greater deterrent effect than changes in the severityof punishment (Durlauf and Nagin (2011); Nagin and Pogarsky (2001); Paternoster (1987);Witte (1980); Zimring and Hawkins (1973)).

Our focus in the current study is to try to better understand the effects of changingthe probability of apprehension on behavior to see if we can provide an explanation forsome of these mixed results. While there have been a large number of studies on thisissue, there is still no clear conclusion regarding whether or not such policies are effective.Some of the more prominent examples of these studies involve examining policing policies,such as attempts to increase the size of the police force, which one imagines increases theprobability that criminals will be caught and prosecuted. Beginning in 1994, PresidentClinton took steps to add 100,000 new offi cers by the year 2000 through the CommunityOriented Policing Services (COPS) Offi ce. Over the course of his presidency, PresidentClinton awarded nearly $10 billion in federal grants to police agencies in all 50 states to putmore police on the streets. This policy was implemented with great confidence regardingits ability to reduce crime, however, its actual effects have been the subject of much debateand controversy. In short, the results on the effectiveness of the policy are mixed at best.

Eck and Maguire (2000) reviews 27 studies examining the effects of changing the numberof police on crime rates and found no consistent relationship between the number of policeon the streets and the levels of violent crime. Studies in this sample provided evidencesuggesting both that increasing the number of police is associated with a reduction in crimeand that increasing the number of police is associated with an increase in crime. However,these studies suffer from endogeneity problems, making it diffi cult to clearly identify acausal relationship between the policy changes and the incidence of crime. There havealso been several field experiments conducted on this issue that one would expect wouldresolve the causality questions. These field experiments have generally found no evidencethat increased police presence deters criminal conduct. The Kansas City Preventive PatrolExperiment examined the effect of changes in police patrol (in vehicles) on crime rates. The

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experiment found that changes in police strength had no significant effect on crime rates(Kelling, Pate, Dieckman, and Brown (1974)). The Newark Police department examinedthe effect of changes in foot patrols on crime rates and residents’perceptions of crime inthe city. The results in Newark were identical to those in Kansas City —changes in footpatrols had no impact on the crime rate (Sherman, Gottfredson, MacKenzie, Eck, Reuter,and Bushway (1998)). However, as George Kelling, director of both studies, notes, theseexperiments examine the impact of particular policing techniques on crime rates, ratherthe number of police (Kelling, 1995 ). It therefore isn’t clear that these changes shouldhave had much of an impact on the probability of a criminal being caught. Additionally,these experiments have been criticized for both design, implementation, and evaluationshortcomings (Sherman, Gottfredson, MacKenzie, Eck, Reuter, and Bushway (1998)).

Taking an alternative approach, Levitt (2002) employs a variety of instrumental variablesto try to obtain a causal result. The instruments for police strength tested include mayoraland gubernatorial election cycles as well as firefighter hiring. However, Kovandzic andcolleagues have criticized his use of these techniques and proxy measures (Kovandzic etal., 2016). They contend that the use of mayoral and gubernatorial elections are weakinstruments of police growth and therefore are unreliable for use in assessing the impact ofpolice levels on crime.

There is also a literature that attempts to use lab experiments to examine how be-havior responds to shifts in enforcement regimes, which should be expected to have highlevels of internal validity and allow researchers to be able to observe clearly the behavioralmechanisms behind any effect from changing probabilities in punishment. While this too isa substantial literature with contributions across several decades, (Hill and Kochendorfer(1969); Schildberg-Hörisch and Strassmair (2012); Mungan and Klick (2015); Nagin andPogarsky (2003); Vitro and Schoer (1972)), the picture one gets from this literature is thatidentifying these effects of increasing punishment probability on crime incidence is quitediffi cult and that to date, no clear conclusions can be drawn. DeAngelo and Charness(2016) provides a more recent examination of how changing enforcement regimes affectsbehavior with a special focus on how the fact that individuals have chosen an enforcementregime respond while being monitored in the way they chose. They find that individualsdo respond in the manner predicted by the Becker model though they also respond to com-plexity in how the enforcement regime is explained by transgressing less often than whenthe enforcement regime is explained in a clearer manner.

In addition to the endogeneity problems in identifying these effects, we propose thatthere is a deeper specification issue that may be driving some of the conflicting field resultswhich has to do with the model of decision making used at the foundation of deterrenceresearch. The Becker model of criminal behavior is based on a classical model of deci-sion making under uncertainty. In this model, an agent chooses among actions knowingthat conditional on his choice, different events may then occur according to specific andknown probabilities. An important difference between this model and the world a potentialcriminal operates in is that the probabilities of getting caught and punished are not welldefined, and may even be unknowable. This changes the decision making paradigm to oneinvolving ambiguity, rather than uncertainty. The key difference between the two environ-ments is that in an uncertain environment a decision maker knows the probabilities withwhich events will occur, while in an ambiguous environment the decision maker does not

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know these probabilities. The latter seems quite a reasonable assumption about the waycriminal justice operates. In the face of ambiguity such as a criminal not understanding theprobability of getting caught or not understanding how an increase in police enforcementcould change that probability, it isn’t clear that one should observe the classical responsepredicted by the Becker model. Individuals could respond to the greater complexity in thechoice environment by ignoring shifts they don’t understand or perhaps, in a manner thatcould be considered consistent with the results in DeAngelo and Charness (2016), by overresponding to the presence of the additional complexity.

The notion that individuals might over respond to the complexity of an ambiguous choiceenvironment is accounted for in part by a concept known as ambiguity aversion (Gilboaand Schmeidler (1989); Camerer and Weber (1992); Fox and Tversky (1995); Keren andGerritsen (1999)). This concept is best explained using a canonical experiment known asthe Ellsberg paradox (Ellsberg (1961)). As a demonstration of the core idea, consider an urnconsisting of 30 red balls and then 60 additional balls that are either black or yellow but inunknown proportion. If you ask an individual to first bet on whether a ball drawn at randomwill be black or red then that will measure the person’s belief regarding whether the numberof black balls is greater than or less than the number of red, which is 30. If the individualchooses to bet on red, then that suggests that they must think there are fewer than 30 blackballs in the urn. If the person believes there are fewer than 30 black balls then he mustbelieve there are more than 30 yellow balls in the urn. Consider then offering that sameindividual the option to bet on a draw from that same urn as to whether the draw will be redor yellow. They should now choose to bet on yellow as they previously revealed a belief thatthere are more yellow balls than red. If they instead again bet on a draw for a red ball thenthe person is deemed to be ambiguity averse. This notion of ambiguity aversion essentiallyinvolves an individual always forming a pessimistic belief about an event for which theydo not know the probability. Substantial evidence exists showing that individuals expresspreferences of this sort and there are accompanying papers that demonstrate the importanceof ambiguity aversion in various domains (Becker and Brownson (1964); Butler, Guiso, andJappelli (2014); Curley, Eraker, and Yates (1984); Dimmock, Kouwenberg, Mitchell, andPeijnenburg (2016); Easley and O’Hara (2009); Fellner (1961); MacCrimmon (1968); Hoy,Peter, and Richter (2014); Oechssler and Roomets (2014); Slovic and Tversky (1974)).

The reason that ambiguity aversion is important is that if individuals do act accordingto such preferences then the manner in which the increased presence of capable guardiansis presented to individuals can alter the effectiveness of interventions on deterrence. Forexample, if it is generally known that the probability of getting caught for a crime has someminimum and maximum values then an ambiguity averse individual’s choice is likely to bemost impacted by the maximum value. Policies aimed at adjusting the average or minimumvalue should be expected to have limited effectiveness since in an ambiguous situation,agents won’t be able to accurately assess the average and their pessimism would lead themaway from paying attention to the minimum. Alternatively, the deterrence effect of aprogram is maximized by raising the possible upper end of enforcement possibilities even ifthe average isn’t shifted. If ambiguity is the correct depiction of the field choice environmentthen that insight could be helpful in designing enforcement regimes. In regard to thefield evidence, the lack of a consistent response to policies aimed at shifting enforcementprobabilities could be attributed to ambiguity as potential criminals may be paying attention

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to things other than what the researchers expected in choosing how to respond to shifts inenforcement regimes.

We note that Segal and Stein (2006) argue strongly for the importance of thinkingabout ambiguity in the context of criminal trials. Their main interest is in arguing thatdue to the fact that criminal sentencing is an ambiguous process and defendants will beambiguity averse, prosecutors are able to take advantage of defendants by getting them toagree to disadvantageous plea deals. They provide an argument to attempt to demonstratethat defendants are in general ambiguity averse but this is not clear evidence. If they arecorrect, then their claim would support our hypothesis regarding the ambiguity aversion ofpotential criminals being exploitable to deter them from breaking the law in the first place.Thus while ambiguity aversion may disadvantage defendants in trials, it may also allow lawenforcement to decrease the rate at which crimes are committed.

In this study, we will use a laboratory experiment that will examine how individualsrespond to changes in apprehension probabilities when those probabilities are known andwhen they are ambiguous. The experiment will also examine the degree to which ambigu-ity aversion might drive behavior in the ambiguous environment. Although we noted thatprior research has established that there are situations in which individuals will behave ina manner consistent with ambiguity aversion, these studies are mostly framed in regard topotential gains. When dealing with criminal punishment, the issue should be in regard topotential losses and it isn’t clear that individuals will treat gains and losses similarly. Thereis in fact other recent evidence that suggests substantial skepticism on the broader applica-bility of ambiguity aversion. Kocher, Lahno, and Trautmann (2015) investigate whetherambiguity aversion drives behavior in a broader range of situations than the common ex-amples in the literature and find that there are relatively few configurations of a choiceenvironment in which ambiguity aversion will emerge. This is an important finding for theliterature as it makes it clear that one has to be careful regarding making overly broadclaims about the presence of ambiguity aversion. We use a laboratory experiment as thebasis for our examination as it is necessary to obtain the clear identification we need of howchanges in detection probability affect behavior. We see this as an initial small scale proofof concept that is necessary to establish the validity of these ideas before one would find itworthwhile to engage in testing equivalent policy changes in the field.

Our experiment is modeled on a situation involving potential tax evasion though the taxframe is not central to the story.1 Our subjects engage in a task for which they earn piecerate pay. Earnings are subject to a tax that is pure deadweight loss to the subjects. We allowthe subjects to self-report their earnings with any reported earnings being taxed at a highrate. The self-reporting option allows them to misreport their earnings to obtain a lessertax bill. We include the possibility that their report may be audited with misreportedearnings incurring a fine. In our treatments, we vary what the subjects know regardingthe audit probability. In some cases they know the audit probability and thus they aredealing with uncertainty. In other cases they only know the set from which the probability

1Tan and Yim (2014) is an example of a paper which investigates tax evasion issues specifically using anexperiment. They investigate tax evasion in the face of a fixed probability of monitoring versus a case inwhich the monitor has discretion over when to monitor which someone could see as similar to our settinginvolving ambiguity. On the other hand, one cannot test our questions from their data given that theirexperiments were designed to test different issues.

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might be drawn but they have no information about how the probability is drawn fromthat set. This latter situation is one with ambiguity. Our findings will show that subjectsrespond as predicted to changes in known probabilities which provides vindication for theclassical Becker model and is consistent with the results from DeAngelo and Charness(2016). When probabilities shift in an ambiguous way, we find no clear behavioral response.This is consistent with the field studies which also provide evidence of a muddled responseto changes in enforcement regimes. Finally, we examine the behavior of the subjects todetermine if they exhibit ambiguity aversion in an exploitable degree but we find only weakand limited support for ambiguity aversion which is contrary to most of the prior literatureon ambiguity aversion but roughly consistent with the results from Kocher, Lahno, andTrautmann (2015).

2 Experiment Design

We seek to determine how ambiguity in the probability of apprehension affects behavior.This involves allowing subjects an opportunity to engage in some form of transgressivebehavior that benefits them with the possibility that the behavior could be detected andpunished leading to financial losses. To make certain that subjects see the losses as real, theexperiment design needs to maximize the subjects feelings of entitlement to the money theyrisk losing through apprehension and punishment. Consequently, our experiment involvessubjects engaging in a real effort task to earn money and includes an element in which theycould lose some of their earnings in a fine for engaging in dishonest behavior. We explaineach of these elements, in turn, as well as our treatments.

There are two types of subjects in our experiments: workers and tax collectors. Thereis a single tax collector per session; all other subjects are workers. In each round of theexperiment, workers engage in a task for piece-rate earnings. This task is based on one usedin Erkal, Gangadharan, and Nikiforakis (2011) and then in Ku and Salmon (2012). Subjectsare asked to take random sequences of 4 letters and transform them into a numerically codedversion using a provided code. Every encoding workers complete correctly earns them 1.5ECUs (Experimental Currency Units) which translated into $1.50 as the exchange ratein the experiment was 1 ECU=$1. Workers would have 4 minutes to complete as manyencodings as they wished to in the production phase of a period.

At the end of the production phase, workers are asked to report to the tax collector howmuch they earned. Workers are allowed to enter any amount they wish. The amount theyenter is subject to a 40% tax. Therefore, subjects could under report their earnings to saveon their tax bill. The downside to doing so is that there is a chance that the worker mightbe audited. This chance and how it is presented to the subjects depends on the round andthe treatment, further explained below. If a worker is audited and found to have reportedearnings at least as high as he or she actually earned, they simply pay the 40% of theirreported earnings in taxes. If a worker under reports, then he or she must pay the entiretax bill owed plus a fine - equal to the difference in the tax they claimed to owe and theamount they actually owed multiplied by 1.25. If a worker is not audited in a round, thenthey simply pay the 40% tax on whatever income they chose to report. The tax revenueis deadweight loss to the subjects. It is not redistributed in any way. Of course real taxesare collected by a government and spent on programs that do distribute the money in some

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Blue Red Green

Known 30% 40% 50%Ambiguous 30% / 50% 40% 30% / 50%Ambiguous Shift 30% / 40% / 50% 10% / 40% / 70% 30% / 50% / 70%

Table 1: Audit probabilities for each treatment.

way back to the populace and so real tax fraud could be seen as harming individuals. Sinceour experiment doesn’t possess this element, this might lead to more tax fraud than if thetaxes benefitted other people in some way. While this is true, that effect should be expectedto be orthogonal to the treatments and therefore not impact our comparative statics whichare the measurements of interest, not the overall level of tax fraud.

The role of the tax collector is largely passive. He or she doesn’t perform the auditsbut the results of all audits performed in a round are shown to the tax collector. The onlyaction of the tax collector is to then press a button labeled “Levy all Fines.”The purposeof the subject in this role is so that when workers lie about their earnings, they see it aslying to another subject in the experiment, rather than the experimenter. At a minimum,workers will know that another subject will observe their lying, so that it might increasethe possibility that they see it as a moral transgression. The tax collector is paid a fixed feeof 10 ECUs for their performance of this job. We wanted to give them something active todo during the experiment so we still allowed to complete encodings but at a reduced rate of.5 ECUs per encoding. The tax collector earned a lower piece rate because their earningsare not subjected to taxes. The lump sum 10 ECU payment on top meant that those inthe role of tax collector should in the end earn more money than the workers.

The probability of an audit depends on the treatment as outlined in Table 1. Subjectsparticipate in only one treatment. Our first treatment is the Known Probability treatment(Known). In it there were three possible audit probabilities, 30%, 40% and 50% with theprobability being associated with a round color. The color of a round was determined atrandom and the color could be either blue, red or green. The audit probability is 30% inblue rounds, 40% in red and 50% in green. In this treatment, subjects are told the roundcolor when making their income report and so they know exactly what the audit probabilityis when making their choice. They do not know the audit probability in the productionphase, only at the income reporting phase.

In our Ambiguous Probability Treatment (Ambiguous), again there are three possibleround colors. In red rounds, the audit probability is known to be 40%. In green and bluerounds, subjects know that all blue rounds have a common probability as do all greenrounds with one being 50% and the other 30%. We do not inform them of which is whichnor did we provide them any explanation of a mechanism that would have made the choice.Thus the audit probability is ambiguous in rounds with these two colors as subjects do notknow the probability of the audit nor do they know the likelihood of any particular auditprobabilities.

Our final treatment is called the Ambiguous Shift Treatment (Shift). In this one, thesubjects face ambiguity in all rounds. In Red rounds the probability is either 10%, 40%or 70%. In blue the possibilities are 30%, 40% and 50%. Green rounds have an audit

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probability of either 30%, 50% or 70%. Again, subjects are told that one of the threepossibilities has been chosen in advance for each color but they have been provided nodetails regarding how those choices were made. The idea in which this treatment representsa shift in ambiguity is to consider red rounds a baseline condition in which the probability ofpunishment is 10%, 40% or 70%. If one wishes to increase the enforcement level, one possibleshift would involve keeping the potential average probability the same but increasing thelowest possible punishment percentage. This would involve the change in probabilities tothe blue rounds in which the average is still 40% but the lowest possible probability is now30% with the top probability falling. Alternatively, one could shift up the overall possibilityof punishment as in the green rounds by moving the bottom and middle probabilities butleaving the top probability unchanged. As we will explain below, these two shifts allow usto identify which element subjects pay attention to when making their income reportingdecisions.2

Our ambiguity comes from the subjects not knowing what the enforcement probabilitywill be but knowing that it could be one of two or three options, e.g. 30% or 50%. Thisis slightly different than the standard ambiguity aversion experiment based on the originalEllsberg urn design. A closer parallel to those experiments would have involved our tellingthe subjects that the audit probability could be potentially anything from the range of 30%to 50%. We chose the simpler design due to the fact that by focusing attention on theendpoints we should increase the impact of someone having either optimistic or pessimisticbias to their beliefs about which probability might be realized. While this is different fromthe design commonly used, it still implements ambiguity in a manner perfectly consistentwith the theory and in a manner we expect to be even more likely to lead to ambiguityaversion affecting behavior.

In all treatments, subjects earn income and report earnings in 9 rounds. While roundcolors were randomly ordered between subjects, each subject faced each round color threetimes. At the end of the experiment one of the 9 rounds was chosen at random to generatefinal payment to the subjects. Subjects earned on average $30.24 including a $10 show upfee. We conducted a total of 13 sessions for these treatments leading to a total of 47 subjectsfrom 5 different sessions in the worker role for the Known treatment, 37 from 4 sessions inAmbiguous treatment and 55 from 4 sessions in the Shift treatment.

3 Hypotheses

There are several issues we need to test in the data in order to provide an answer to theunderlying questions. In this section, we will provide a theoretical characterization of thechoice behavior, as well as explain the hypotheses regarding how that choice behavior mightvary according to the treatments.

For this analysis we will take the earnings, E, of an individual from the encoding taskto be fixed. This should not vary with the round color as subjects do not know the color of

2Given that the only thing that varies across round colors is the audit probability, one could be worriedthat this might lead to some experimenter demand effect in which subjects respond to the round colors bychanging behavior more than they would if the difference weren’t so salient. While possible, the fact thatmost of our important results demonstrate a lack of any change in behavior between round colors suggeststhat there does not appear to have been much of a demand effect.

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a round when generating their income. They only know the round color when choosing howmuch to report. Our main interest is in that reporting decision and how it varies with roundcolors and so we model that choice rather than the choice of E. We will let t represent thetax rate (40% in the experiments) and c ∈ [0, 1] be the fraction of total earnings that aworker claims in their income report where c = 1 means the worker is reporting truthfullyand c < 1 implies under reporting income.3 We will then let p be the audit probability.Given this, the choice problem of a subject when facing their incoming reporting decisionis as follows:

maxc∈[0,1]

(1− p)u [(1− tc)E] + p ∗ u [E(1− t− 1.25(t− tc))]

The first term represents the utility for the worker should the audit not occur. In thiscase, the worker receives their utility from their base earnings, E, less what they pay intaxes based on how much of their earnings they report, ctE. If the audit occurs, then theworker receives their utility from their base earnings less their full tax bill less the fine owedwhich is 1.25 times the difference between their owed and claimed taxes. This leads to anoptimality condition of

1− p1.25p

=u′ [E(1− t− 1.25(t− tc))]

u′ [(1− tc)E]While there is no general analytical solution for c, we can assume a functional form for

the utility function and solve for c computationally. We will assume a standard CRRA utilityfunction, u(x) = xα and provide a characterization of how c∗ varies with α and p. Under theCRRA specification, c∗ doe not depend on E. The characterization of optimal choices canbe found in Figure 1 as we show the optimal c∗ for the various audit probabilities used in theexperiment and for risk aversion parameters on the range of [.1, 1]. The figure demonstratesthat at very low audit probabilities, i.e. 10%, then no individuals should report any incomeunless they are exceedingly risk averse and even then they report essentially 0. Once theaudit probability gets to 50%, then under reporting is not worthwhile for anyone. For theintermediate probabilities of 30 and 40%, the optimal percentage of income reported shouldbe decreasing in α.

We have chosen not to obtain a separate risk measure for our subjects as the Knowntreatment essentially provides this. We saw little value in obtaining a separate measure tocompare with this one. Given that we can expect a range of risk aversion parameters in thepopulation, the analysis above provides us with the basis for our first hypothesis regardingdata from the Known treatment.

Hypothesis 1 In the Known treatment, we expect the propensity for and level of incomeunder reporting to be highest at the 30% audit probability and decreasing as the audit prob-ability increases.

The Known treatment is designed as a test of whether behavior adjusts in the mannersuggested by the standard Becker model when punishment is uncertain and this hypothesis

3 In the experiment, subjects actually could report more income than they earned and a few subjects didso. We allowed for this simply because we didn’t want to impose any restrictions on reporting. Theoreticallythis is dominated so we won’t consider it in the analysis.

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0 .1 0 .2 0 .3 0 .4 0 .5 0 .6 0 .7 0 .8 0 .9 1 .0α

0 .0

0 .1

0 .2

0 .3

0 .4

0 .5

0 .6

0 .7

0 .8

0 .9

1 .0

p = .1p = .3p = .4p = .5 o r .7

c *

Figure 1: Optimal percentage of earnings to report as risk aversion varies.

reflects the standard predictions from that model; people will be more honest when thelikelihood of punishment is higher. We do note, however, that we specifically chose theparameters of the experiment in a range such that this hypothesis should hold. As theanalysis above shows, at low levels of the audit probability, the theory would predict norelation between it and the propensity or severity of under reporting as all will completelyunder report while at high levels of audit probability no one will under report. We choseprobabilities in an intermediate range to allow us to observe a behavioral shift. This factunderscores the importance in designing experiments with parameters that allow for thebehavioral shifts one wants to observe.

Hypothesis 2 In the Ambiguous treatment, workers will under report less in blue and greenperiods than red periods.

Our second hypothesis refers to our Ambiguity treatment. This treatment is intendedto help us understand how individuals will choose in an environment possessing ambiguityin the audit probabilities. Our statement of this hypothesis is premised on the notionthat subjects will be ambiguity averse. If the subjects are ambiguity averse, when facedwith the blue and green periods and knowing that the audit probability could be 30 or50% subjects should place more weight on the possibility of the 50% audit probability andrespond accordingly with less under reporting. If we compare their baseline in those twotreatments to the red periods when the audit probability is known to be 40%, the subjectsshould transgress less often in the periods when the audit probability could be 50%. Thishypothesis then is a basic test of whether our subjects are ambiguity averse to a strong

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enough degree that it will impact their behavior.

Hypothesis 3 When comparing the Known and Ambiguous treatments by color, thereshould be equivalent behavior in Red rounds and Green rounds but more transgressions inBlue rounds in Known than Ambiguous.

Our third hypothesis is based on a more detailed test of the ambiguity aversion conceptallowing us to determine the strength of any potential ambiguity aversion. When comparingbehavior by round color between Known and Ambiguous, the red rounds in both treatmentsshould lead to equivalent behavior as in both the audit probability is known to be 40%. Forblue rounds, the audit probability is known to be 30% in Known but could be 50% in theAmbiguous. Therefore, it is expected that this possibility should lead to fewer transgressionsin the Ambiguity treatment. For green rounds, the audit probability is known to be 50%in Known but could be 30% in Ambiguous. Again though, if subjects are ambiguity aversetheir decisions should be based on a pessimistic view of which probability could be in effectand assume it should be the 50% probability, at least in the case of extreme ambiguityaversion. This means that we might see the same behavior in green rounds between bothtreatments. Of course this is a very strong view of inequality aversion which is unlikelyto hold. It will not be surprising if we instead find more transgressions in the Ambiguitytreatment but how many fewer will be a useful gauge of the level of ambiguity aversionpresent.

Hypothesis 4 In the Shift treatment, we expect that there will be fewer transgressions inred rounds than in blue rounds and there should be equal number between red and greenrounds.

The Shift treatment serves several purposes. The first is as a test for how behavior mightbe affected by ambiguous shifts in enforcement levels in a manner we believe comparable tohow shifts in police enforcement levels might change expectations of punishment likelihoodin the field. In the field and in this case, our subjects will know that some shift has happenedbetween one regime (round) and the next but they won’t know what the shift actually is oreven have a good way of forming expectations over what the new probability is since theyhave no knowledge of the process which determines the probability. They won’t even knowthat the probability of enforcement has gone up only that there is a shift in the potentialprobability of enforcement.4 This treatment is also designed as a way to try to identifywhat element of announcements regarding regime changes might be most likely to impactbehavior, whether it is the minimum possible level, the maximum possible level or somenaive average. Hypothesis 4 is one approach to testing that and it stated assuming thatsubjects are strongly inequality averse and therefore respond only to the highest possibleprobability of detection. Since in both red and green rounds, the maximum detectionprobability is 70%, we hypothesize that behavior should be equivalent. This should hold if

4One might object that in the field, one should know that the probability has gone up even if one doesn’tknow what the original probability was or the magnitude of the shift. For some policies that may be truebut for others maybe not. For example, if a new enforcement regime of how police patrol neighborhoods hascome into place, this could involve an overall increase in police presence but at the same time the distributioncould change so that in some areas enforcement rates could drop even if overall rates increase.

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subjects are strongly ambiguity averse and this is despite the fact that if one takes a naiveexpectation of the probability of audit, the probability is higher in the green rounds thanthe red ones. When comparing red rounds to blue ones, the maximum probability is lowerin blue than red despite the fact that the naive average is the same. Again, if subjectsrespond according to ambiguity averse preferences this means that the red rounds shouldhave a lower likelihood of transgressions than the blue.

While hypothesis 4 is stated under the assumption of ambiguity aversion, there areother possible bases for how subjects will respond to the audit possibility. For example,it is possible that workers take an optimistic view of the probabilities and respond to theminimum possible probability. If so, then we expect red rounds to generate the most underreporting given that the lowest audit probability in those rounds is 10% while the othertwo have the same minimum of 30% meaning we should see the same behavior in both. Ifsubjects just naively average the probabilities, then in both blue and red rounds, the averageaudit probability is 40% and we should observe the same behavior. In the green rounds theaverage is 50% and so we should observe fewer transgressions. The point being that whileour hypothesis is stated on the premise that our subjects are ambiguity averse, it is thecase that this treatment was constructed not just to verify the effects of ambiguity aversionbut more broadly to provide a clear test of whether subjects pay attention to the max, minor average of a set of possible probabilities when they have no information regarding howthose probabilities will be selected.

4 Results

We will provide properly constructed regressions to test each of our stated hypothesesbut it is useful to first get some understanding of the structure of the data by examiningsummary statistics regarding the choice behavior and these are shown in Table 2. For allthree treatments, we provide: the average pre-tax earnings, the propensity to under reportearnings and the percentage by which subjects under report conditional on under reporting.5

To be clear, this last summary statistic examines only those individuals who have chosento under report their earnings. We have provided these summary statistics separately forthose subjects whose pre-tax earnings are above average and those whose pre-tax earningsare below average. While theoretically the earnings level is unimportant to the choice tounder report in the CRRA specification, we still wanted to examine the issue given thatCRRA might not be the behaviorally correct specification and under other forms of riskaversion the optimal level to under report would depend on earnings level.

Examining these statistics provides quite suggestive indications for what our formalresults will be. To quickly summarize; in the Known treatment, there is some indication thatsubjects do under report their income most often in Blue rounds and least often in Greenwhich is as expected. In the Ambiguous treatment, above average earners under reportmost often in Red rounds and less so in Blue and Green which is suggestive of ambiguityaversion but it is not clear that the difference will be large enough to be significant. Belowaverage earners demonstrate no such tendency. In the Shift treatment, subjects overall tend

5To avoid skewing the statistics due to what are clearly mistakes, we eliminate a few observations inwhich workers reported earnings above 100.

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All Below Avg Earners Above Avg EarnersBlue Red Green Blue Red Green Blue Red Green

Known Pre-Tax Earnings 33.500 33.129 32.914 29.000 28.420 28.964 36.554 36.268 35.500Propensity 0.582 0.436 0.338 0.632 0.589 0.418 0.548 0.333 0.286% Under Report 0.372 0.313 0.34 0.355 0.312 0.399 0.385 0.313 0.291Number 47 19 28

Ambiguous Pre-Tax Earnings 33.176 33.505 33.154 26.458 27.458 27.083 36.400 36.446 36.232Propensity 0.586 0.636 0.626 0.500 0.528 0.611 0.627 0.689 0.634% Under Report 0.493 0.569 0.473 0.288 0.423 0.308 0.512 0.624 0.553Number 37 12 25

Shift Pre-Tax Earnings 33.037 33.074 32.907 28.318 28.136 28.111 36.281 36.469 36.203Propensity 0.500 0.438 0.340 0.439 0.439 0.273 0.542 0.438 0.385% Under Report 0.302 0.267 0.274 0.266 0.290 0.323 0.322 0.251 0.251Number 54 22 32

Note: % Under Report is measured conditional on under reporting.

Table 2: Summary Statistics

to under report least in the Green rounds most in blue though the difference between Redand Blue is not as pronounced as in the Known treatment. If we look by earnings group,the below average earners behave exactly the same in Blue and Red but under report lessoften in Green. The above average earners change their behavior more between Blue andRed than between Red and Green. The indication is that below average earners may beresponding to the naive average enforcement probability while the above average earnerscould be again showing mild evidence of ambiguity aversion. We will use the regressionsthat follow to determine which of these differences are significant.

Our first set of regressions is not designed to test one of our hypotheses, but rather toensure that a particular element of the design worked as intended. Since subjects did notknow the color of a round when producing, their pre-tax income levels should not dependon round color. Also, in order for us to compare across treatments it is helpful for pre-taxincome to also not depend on treatment. Table 3 provides a set of regressions to test whetherpre-tax earnings were effected by treatment or round color. The regressions are all randomeffects panel regressions with standard errors clustered at the individual level. To allow forease of interpreting the results, we provide one specification which includes all treatmentsand then separate specifications for each individual treatment. The first specification allowsfor determining whether earnings depends on treatment. The regressions for each treatmentallow us to determine if earnings depend on round color inside of the treatments. We findtreatment and color variables all to be insignificant indicating that the experiment designwas successful in delivering the property that pre-tax earnings depend on neither treatmentnor round color.

Our first formal hypothesis concerned the Known treatment and simply stated that thepropensity to under report should depend on the round color with the ranking being Blue≥ Red ≥ Green. Table 4 provides the regressions to formally test this hypothesis. Weprovide three different specifications of this regression. The first is a random effects logit

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(1) (2) (3) (4)All Known Ambiguous Shift

Ambiguous 0.028(1.712)

Shift 0.669(1.447)

Green -0.282 -0.272 -0.141(0.437) (0.448) (0.262)

Blue 0.391 -0.240 -0.082(0.309) (0.338) (0.290)

Constant 31.03∗∗∗ 31.00∗∗∗ 31.23∗∗∗ 31.78∗∗∗

(1.099) (1.128) (1.349) (0.971)

Obs 1,368 468 369 531Clusters 152 52 41 59Robust clustered standard errors in parentheses, *** p<0.01, ** p<0.05, * p<0.1

Table 3: Regressions on earnings by treatment and then by round color for eachtreatment.

regression with standard errors clustered at the individual level and a dependent variablebeing a binary variable for whether or not the individual reported earnings below their trueearnings in a round. The second specification is a linear probability version of the samespecification. The third version examines only the set of individuals who chose to underreport and uses as the dependent variable the percentage by which they under reported.The first two specifications speak to the question of whether the individuals under reportwhile the third speaks to the issue of the degree to which they under report if they do. Wealso provide a second set of these regressions that include a dummy variable to separateout those who earned less than the average in pre-tax earnings and then interactions withthe round colors. This allows us to determine if low and high income earners behaveddifferently. This leads us to our first result.

Result 1 In the Known treatment, the propensity of subjects to under report responds toround color as hypothesis 1 predicted.

Not surprisingly, hypothesis 1 is not rejected as overall subjects under report more oftenin Blue rounds than Red and then under report less often in Green rounds than Red. Whenwe split out how low versus high earners behave, we see that high and low earners dorespond differently. High earners under report more often in Blue rounds compared to Redbut they show no change in behavior between Red and Green rounds. For the low earners,they show exactly the opposite in that they evidence no difference in behavior between Redand Blue rounds but do under report significantly less often in Green rounds compared toRed.6 These results indicate that in a world in which punishment probabilities adjust in a

6These claims can be verified by checking the significance of the combined terms of Blue + (LE*Blue)and Green + (LE*Green) which result in p−values of 0.329 and 0.027 for specification 4 and 0.336 and 0.030for specification 5.

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(1) (2) (3) (4) (5) (6)Logit Report LP Report % Under Rep Logit Report LP Report % Under Rep

Blue 1.614∗∗∗ 0.149∗∗∗ 0.099∗∗∗ 2.562∗∗∗ 0.214∗∗∗ 0.132∗∗∗

(0.481) (0.045) (0.031) (0.744) (0.064) (0.043)

Green -1.136∗∗ -0.099∗∗ 0.008 -0.613 -0.046 -0.032(0.520) (0.046) (0.030) (0.669) (0.050) (0.033)

LowEarn 3.124∗∗ 0.265∗ 0.047(1.517) (0.140) (0.079)

LE*Blue -2.037∗∗ -0.162∗ -0.066(0.908) (0.083) (0.058)

LE*Green -1.194 -0.131 0.085(1.041) (0.096) (0.057)

Revenue 0.004 <0.001 <0.001 0.033 0.002 <0.001(0.045) (0.004) (0.004) (0.047) (0.004) (0.004)

Constant -0.896 0.425∗∗∗ 0.245∗∗ -3.238∗ 0.244 0.222(1.676) (0.139) (0.115) (1.913) (0.148) (0.136)

Obs 423 423 190 423 423 190Clusters 47 47 35 47 47 35Robust clustered standard errors in parentheses, *** p<0.01, ** p<0.05, * p<0.1

Table 4: Regressions examining Known treatment.

known manner, then the Becker model should on average be expected to do a good job ofexplaining/predicting behavioral changes though there may be some heterogeneity in regardto strength of response.

Our second hypothesis concerned the Ambiguous treatment and involved trying to de-termine if our subjects evidenced behavior consistent with ambiguity aversion. Table 5provides the regressions to test this hypothesis and the regressions have the same structureas before but include only data from the Ambiguous treatment. This leads to our secondresult.

Result 2 In the Ambiguous treatment, we find no change in propensity to under report forlow or high earners based on round color. We do find that conditional on under reporting,subjects under report slightly less in the blue/green ambiguous rounds.

Our regression specifications here compare behavior in Red rounds to Blue and Greencombined as subjects should have seen little difference between the two. Overall, we findno significant differences in behavior between Red rounds and the other two. We continueto find no difference when we separate out effects for low and high earners.7 While inthe summary statistics it appeared possible that the behavior of the high earners couldbe consistent with ambiguity aversion, the difference between the Red rounds and theothers was not strong enough to be significantly different. We do find that conditional onunderreporting, the subjects are underreporting less in Blue and Green rounds than in Red

7The test of the signicance for the linear combination of (Blue or Green) +(LE*BorG) results in a p−valueof 0.464 for specification 4 and 0.549 for specification 5.

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(1) (2) (3) (4) (5) (6)Logit Report LP Report % Under Rep Logit Report LP Report % Under Rep

Blue or Green -0.301 -0.032 -0.084∗∗∗ -0.795 -0.066 -0.061∗

(0.568) (0.046) (0.030) (0.769) (0.059) (0.031)

LowEarn -0.769 0.020 -0.118(2.058) (0.178) (0.112)

LE* BorG 1.340 0.107 -0.080(1.065) (0.091) (0.073)

Revenue 0.193∗∗ 0.018∗∗ 0.004 0.202∗ 0.020∗∗ 0.002(0.097) (0.009) (0.005) (0.104) (0.009) (0.005)

Constant -5.277 0.021 0.412∗∗ -5.265 -0.034 0.511∗∗∗

(3.275) (0.280) (0.164) (3.808) (0.342) (0.181)

Obs 333 333 202 333 333 202Clusters 37 37 28 37 37 28Robust clustered standard errors in parentheses, *** p<0.01, ** p<0.05, * p<0.1

Table 5: Regressions examining Ambiguous treatment.

rounds which could be seen as very minor evidence in favor of ambiguity aversion but thatwould be very weak support for ambiguity aversion.8

For our third hypothesis we want to test how behavior compares between Known andAmbiguous treatments to provide a more detailed look at the possibility of ambiguity aver-sion. Table 6 provides the regressions to provide that comparison. Data from both treat-ments are included and the structure of the regressions are again the same as in the priortwo tables though we find it more convenient to present the results in the form of separateregressions for Low and High Earners. These regressions provide the support for our thirdresult.

Result 3 In comparing behavior in the Known and Ambiguous treatments, low earnerstreat each colored the round the same in both treatments. The high earners under reportmuch more often in Red rounds in the Ambiguous treatment than the Known treatment andunder report much less often in the Blue rounds in the Ambiguous treatment than in theKnown treatment.

As explained before, the Red rounds are identical in the Ambiguous and Known treat-ments, so identical behavior is expected. This holds for Low Earners but not for HighEarners, as High Earners under report much more frequently in the Ambiguous treatmentthan in Known. This is unexpected and we have no clear explanation for the behavior. Inthe blue and green rounds, Low Earners still show no response to treatment. The HighEarners on the other hand are less likely to under report in Blue rounds in the Ambiguous

8One might be tempted to conclude that the reason we fail to find support for ambiguity aversion isbased on the fact that our design induced ambiguity over two possible probabilities rather than a continuousrange. While it could be the case that ambiguity aversion impacts behavior only with that very specificimplementation, that would support our core interpretation of our results which is that one shouldn’t expectambiguity aversion to be exploitable in the field.

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(1) (2) (3) (4) (5) (6)Low Earners High Earners

Logit Report LP Report % Under Rep Logit Report LP Report % Under Rep

Ambiguous -0.785 -0.042 -1.723 3.800∗∗∗ 0.320∗∗∗ 2.275(1.311) (0.127) (1.955) (1.412) (0.113) (2.200)

Revenue 0.136∗∗ 0.011∗∗ 0.525 0.230∗∗∗ 0.017∗∗∗ 0.480(0.055) (0.005) (0.511) (0.063) (0.005) (0.469)

Green -1.879∗∗ -0.181∗∗ -0.257 -0.567 -0.035 0.067(0.858) (0.081) (0.501) (0.660) (0.048) (0.359)

Blue 0.513 0.046 -0.083 2.700∗∗∗ 0.210∗∗∗ -0.410(0.576) (0.055) (0.408) (0.762) (0.063) (0.586)

Ambig*Green 1.697 0.159∗ -8.280 0.436 0.015 -8.616(1.066) (0.096) (8.164) (0.944) (0.071) (8.569)

Ambig*Blue -0.952 -0.083 0.187 -3.122∗∗∗ -0.246∗∗∗ 0.503(0.769) (0.069) (0.463) (0.936) (0.075) (0.661)

Constant -3.056 0.257 -14.390 -10.620∗∗∗ -0.272 -16.98(1.899) (0.178) (14.300) (2.656) (0.192) (16.88)

Obs 540 540 461 621 621 467Clusters 60 60 57 69 69 60Robust clustered standard errors in parentheses, *** p<0.01, ** p<0.05, * p<0.1

Table 6: Regressions comparing Known and Ambiguous Treatments.

treatment than in the Known treatment. Again the difference in this case is that in Known,the subjects knew the audit probably was 30% while in the Ambiguous treatment it couldhave been 30 or 50%. The indication is that the High Earners are responding to either themaximum possible audit probability or just the increase in the naive expectation of an in-crease in the audit probability. In Green rounds, High Earners behave equivalently betweenthe two treatments. Had they been making their decisions on the naive average probability,the fact that the audit probability could have been 30% or 50% in the Ambiguous treatmentshould have led to increased transgressions relative to the Known treatment in which theaudit probability was certain to be 50%. This behavior is therefore consistent with the ideathat they are responding to the top possible audit probability rather than the minimum oraverage. This provides another minimal bit of evidence suggesting that ambiguity aversioncould be present in a small degree for the above average earners but, again,the evidence isnot strong.

Our final hypothesis focuses on the Shift treatment and is based on trying to test moreexplicitly if behavior is a function of maximum, minimum or the naive average audit prob-ability. The analysis of this treatment also provides more generally an indication for howindividuals respond to ambiguous shifts in probabilities. The regressions to test these issuesare shown in Table 7 which again have a similar structure to p previous regression tablesbut are based on data only from the Shift treatment. This leads to our fourth and finalresult.

Result 4 Hypothesis 4 is rejected for Low Earners but not for High Earners.

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(1) (2) (3) (4) (5) (6)Logit Report LP Report % Under Rep Logit Report LP Report % Under Rep

Blue 0.440∗ 0.060∗ 0.048 0.722∗∗ 0.100∗∗ 0.060(0.245) (0.035) (0.045) (0.288) (0.042) (0.069)

Green -0.735∗ -0.098∗ 0.012 -0.375 -0.052 -0.018(0.415) (0.054) (0.043) (0.530) (0.074) (0.038)

LowEarn -0.179 -0.034 -0.068(0.891) (0.125) (0.071)

LE*Blue -0.733 -0.099 -0.034(0.520) (0.071) (0.075)

LE*Green -1.003 -0.115 0.088(0.828) (0.108) (0.102)

Revenue -0.028 -0.003 -0.006∗ -0.047 -0.006 -0.008∗∗

(0.043) (0.006) (0.004) (0.048) (0.007) (0.004)Constant 0.320 0.538∗∗∗ 0.463∗∗∗ 1.037 0.637∗∗ 0.534∗∗∗

(1.396) (0.196) (0.112) (1.709) (0.249) (0.128)Obs 495 495 207 495 495 207Clusters 55 55 41 55 55 41Robust clustered standard errors in parentheses, *** p<0.01, ** p<0.05, * p<0.1

Table 7: Regressions examining Shift treatment.

Hypothesis 4 is predicated on the notion that in the Shift treatment, subjects shouldrespond primarily based on changes in the top probability of audit. This would lead toequivalent behavior in Red and Green rounds but greater probability of underreportingin Blue rounds. For the overall sample, this is rejected. There is very weak response ofmore under reporting in the Blue rounds compared to Red and then less in Green roundscompared to Red. When we look at the data by high vs low earners, we find that forhigh earners, they evidence behavior consistent with hypothesis 4. There is a significantdifference in behavior between Blue and Red rounds but not between Red and Green. Thiswould be consistent with the high earners basing their behavior on the high audit probabilityas it is 50% for the Blue rounds and then 70% for Red and Green. This result weakensa bit when one tests for the difference between Blue and Green rounds as the behavior isdifferent between these two9. Taken together the indication is that the high earners maybe responding to both the change in the high end of the possible audit probabilities as wellas the naive average which shifted from 40% in the Blue and Red rounds to 50% in theGreen rounds. For the low earners, we again find no evidence consistent with ambiguityaversion. The behavior for these subjects is completely identical between Blue and Redrounds indicating no response at all when the upper end of the audit probability goes from50 to 70%. There is however a marginally significant drop in likelihood of under reportingbetween Red and Green rounds indicating that behavior does change at least moderatelyas the naive average shifts.10

9P−value of this test is 0.022.10P−value of the relevant test is 0.071.

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For the low earner segment of the population, their response to any shift in enforcementregimes was minimal at best. While the high earners shifted a bit more, even their responseswere generally sluggish. As described in the introduction, field studies on changes in en-forcement regimes also generally find either counterintuitive behavioral changes or a lackof a change in behavior due to enforcement regime changes. Alternatively, in the Knowntreatment we find sharp shifts in behavior due to regimes shifts. The comparison of thesetwo findings suggest that when a policy change leads to an ambiguous shift in an alreadyambiguous enforcement regime then the response is not as strong as when the shift is fromone clear probability to another.

5 Conclusion

The intent of this study was to determine the effect of ambiguity in punishment regimeson the tendency for individuals to engage in dishonest acts. Our interest in ambiguitywas twofold. First, there exists substantial prior literature suggesting that individuals areambiguity averse and so we wanted to examine the degree to which ambiguity aversionmight drive the behavior in a frame regarding rule breaking. Second, we wanted to examinehow shifts in ambiguous enforcement regimes might affect behavior.

Our first treatment is a baseline case designed to examine how individuals would reactto shifts in enforcement regimes under the standard assumption of uncertainty, or whenthe probability of detection is known. In this case, our subjects responded as predicted bya standard model in that as the probability of detection was increased; the propensity toengage in dishonest behavior decreased. Our second treatment made the detection probabil-ities ambiguous in the sense that the subjects knew the detection probabilities were drawnfrom a specific set but they didn’t know how leaving them not knowing the actual detectionprobabilities they faced. This was designed to determine if the subjects were ambiguityaverse or if they would react based on a pessimistic belief that the highest detection proba-bility in the set was the one most likely to be in effect. We found little evidence consistentwith that hypothesis. The individuals in our experiment who earned more than the averagemight be seen as mildly ambiguity averse but the effect is not statistically significant andthere is definitely no effect on those earning less than the average. This is a very impor-tant result from the perspective of designing or perhaps in advertising enforcement regimes.Were individuals ambiguity averse, then an enforcement agency could be well served byadvertising enforcement regimes in an ambiguous manner in hopes that people take thepessimistic belief regarding their likelihood of apprehension and respond accordingly. Ourresults suggest that such a strategy is unlikely to elicit the desired effect.

Our final treatment looked at how shifts in an ambiguous enforcement regime wouldimpact behavior. Our treatment was designed to determine if individuals respond morestrongly to the max, min or naive average detection probability in the ambiguous set. Ourfindings again suggest that ambiguity aversion is certainly not driving the behavior forlow earning subjects but again may be influencing that of high earning subjects. For bothgroups though, we found that any behavioral responses were moderate as we shifted betweenambiguous enforcement regimes.

This moderate response to shifts in ambiguous regimes is important and it is informativeto compare it carefully to how behavior shifted in the treatment involving only uncertainty.

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In the treatment where probabilities are known, one of our shifts in detection probabilitywas to move from a 40% detection rate to 50%. We observed a substantial reduction indishonest behavior. In our treatment involving a shift in ambiguous regimes, we had twocases in which one might see the average detection probability to be 40% and a third whereit was 50%. We do not, however, find a reliably strong response to that shift overall nor ifwe look at high versus low earners separately. The implication is that individuals respond atbest more sluggishly, if at all, when enforcement regimes are changed from one ambiguousregime to another compared to how they respond to similar shifts in regimes involvingonly uncertainty. This result may help explain why many shifts in enforcement regimes inthe field have been less effective than anticipated and provides important insights for howone might design and frame future regime changes in a way that might make them moreeffective.

Our results imply that simply announcing changes in an enforcement regime in anambiguous manner, such as “more police will be on patrol”or “IRS agents will be carefullyscrutinizing more tax filings,”should not be expected to be effective. Indeed we cite severalfield studies in the introduction that demonstrate the principle that simply announcingambiguous changes in enforcement regimes has unpredictable and uncertain effects. Theissue may well be that simply announcing a shift from a regime with an unknown detectionprobability to a new regime with a detection probability that will also be unknown is diffi cultfor individuals to process and respond to. If those in the target population have no concreteknowledge about the new detection probability, how is it supposed to have an impact ondeterrence? We can return to the notion of ambiguity aversion to see that one perhapsperceived benefit of leaving the detection rates ambiguous is the hope that individuals willtake a pessimistic prior and over respond to such an announcement. However, we find nosuch response in our data which is corroborated by the mixed evidence in the field.

If a law enforcement authority wants to announce a regime shift in a way that shouldbe expected to be effective, our results suggest that quantifying the detection rates or atleast the change might be more effective. For example, instead of announcing that theIRS would be evaluating an increased number of tax filings, the agency could announcespecific targets for how many additional filings would receive deeper scrutiny by an agent.This would communicate to potential tax evaders the actual increase in their chance ofdetection, or at least a closer approximation, which allows them to respond in the expectedway. Police departments could not realistically pre-announce the patrol patterns of newoffi cers to convey increases in crime detection and apprehension rates; however, they couldmake a point of announcing increases in apprehension rates to try to make the impact ofthe increased enforcement quantifiable. Other enforcement agencies could likely find similarways of presenting any alterations to enforcement regimes aimed at increasing deterrence.

While our results are suggestive that providing policies with more specifics would lead toenhanced deterrence, we note that it is important to proceed with caution when interpretingnew and unexpected results like ours to the field. It is important to solidify findings byreplicating them in other domains and populations prior to implementing such suggestionswith great confidence. We see our results as an important step to shifting policy makers’focus to the ambiguity inherent in enforcement regimes and encourage both policy makersand researchers to consider carefully how this ambiguity might be limiting the effectivenessof deterrence policies. As the issue of how ambiguity in enforcement influences deviant

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behavior becomes better understood and the recognition that enforcement regimes involveambiguity rather than uncertainty gains greater recognition, we expect that it will help inrefining the design and framing of enforcement policies.

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