The Unintended Consequences of “Ban the Box”: Statistical Discrimination and Employment Outcomes When Criminal Histories Are Hidden

I.  Introduction

Mass incarceration has been an important crime-reduction policy for the past several decades, but it has come under intense scrutiny due to high financial cost, diminishing public safety returns, and collateral damage to the families and communities of those who are incarcerated. There is substantial interest in reallocating public resources to more cost-effective strategies, with greater emphasis on rehabilitating offenders. Due in part to this change in focus, individuals are now being released from state and federal prisons more quickly than they are being admitted. According to the most recent data, more than 637,000 people are released each year (Carson and Golinelli 2014). However, recent data also suggest that approximately two-thirds of those released will be rearrested within 3 years (Cooper, Durose, and Snyder 2014). This cycle signals the country’s failure to help reentering offenders transition to civilian life and limits our ability to reduce incarceration rates. Breaking this cycle is a top policy priority.

Both theory and evidence suggest that connecting ex-offenders with jobs can keep them from reoffending. The classic Becker (1968) model of criminal behavior suggests that better employment options reduce crime. In practice, increasing the availability of jobs for reentering offenders reduces recidivism rates (Yang 2017; Schnepel 2018). But finding employment remains difficult for this group. Part of the reason ex-offenders have difficulty finding employment is that, on average, they have less education and job experience than nonoffenders. However, as Pager (2003) and others have shown, employers discriminate against ex-offenders even when other observable characteristics are identical. This is likely due to statistical discrimination.¹ Ex-offenders are more likely than nonoffenders to have engaged in violent, dishonest, or otherwise antisocial behavior, and, based on current recidivism rates, are more likely to engage in similar behavior in the future.² Ex-offenders also have higher rates of untreated mental illness, addiction, and emotional trauma (Raphael 2010; Wolff and Shi 2012; Justice Center 2016). These are all valid concerns for employers seeking reliable, productive employees. But this reasoning is little comfort to someone coming out of prison and hoping to find gainful legal employment. In addition, since black and Hispanic men are more likely to have criminal records, making a clean record a condition for employment could exacerbate racial disparities in employment.³

If even a few ex-offenders are more job ready than some nonoffenders, then employers’ statistical discrimination against those with criminal records hurts the most job-ready ex-offenders. This has motivated the “ban the box” (BTB) movement, which calls for employers to delay asking about an applicant’s criminal record until late in the hiring process.⁴ Advocates of BTB believe that if employers cannot tell who has a criminal record, job-ready ex-offenders will have a better chance at getting an interview. During that interview, they may be able to signal their otherwise-unobservable job readiness to the employer. This could increase employment rates for ex-offenders and thereby decrease racial disparities in employment outcomes.

However, this policy does nothing to address the average job readiness of ex-offenders. A criminal record is still correlated with lack of job readiness.⁵ For this reason, employers will still seek to avoid hiring individuals with criminal records. When BTB removes information about a criminal record from job applications, employers may respond by using the remaining observable information to try to guess who the ex-offenders are and avoid interviewing them. Even though ex-offenders could be weeded out after the interview process, interviewing candidates is costly.⁶ Employers would rather not spend time interviewing candidates who they are sure to reject when their criminal history is revealed. Surveys by Holzer, Raphael, and Stoll (2006) show that employers are most concerned about hiring those who were recently incarcerated. Since young, low-skilled black and Hispanic men are the most likely to fall into this category (Bonczar 2003; Yang 2017), employers may respond to BTB by avoiding interviews with this group. Even black and Hispanic men without a record would lose opportunities with employers who are worried that these applicants have a record but are forbidden from asking. As a result, racial disparities in employment could increase rather than decrease.

This paper estimates the effect of BTB policies on employment for young, low-skilled black and Hispanic men. To do this, we exploit variation in the adoption and timing of state and local BTB policies to test BTB’s effects on employment outcomes, using individual-level data from the 2004–14 Current Population Survey (CPS). We focus on the probability of employment for black and Hispanic men who are relatively young (age 25–34)⁷ and low skilled (no college degree), as they are the ones most likely to be recently incarcerated. This group contains the most intended beneficiaries of BTB as well as the most people who could be unintentionally hurt by the policy. If BTB does not exacerbate statistical discrimination by employers and only helps ex-offenders, then we would expect BTB to increase employment among groups that include a lot of ex-offenders. If, however, BTB reduces employment for this group and no others, that is strong evidence that employers are statistically discriminating, and the damage to innocent bystanders within this group is greater than the aid given to ex-offenders.

We find net negative effects on employment for these groups: young, low-skilled black men are 3.4 percentage points (5.1%) less likely to be employed after BTB than before. This effect is statistically significant ($p<.05$) and robust to a variety of alternative specifications and sample definitions. We also find that BTB reduces employment by 2.3 percentage points (2.9%) for young, low-skilled Hispanic men. This effect is only marginally significant ($p<.10$) but also fairly robust. Both effects are unexplained by preexisting trends in employment, and—for black men—persist long after the policy change. The effects are larger for the least skilled in this group (those with no high school diploma or GED), for whom a recent incarceration is more likely.

We expect BTB’s effects on employment to vary with the local labor market context. For instance, it would be difficult for an employer to discriminate against all young, low-skilled black men if the local low-skilled labor market consists primarily of black men or if there are very few applicants for any open position. We find evidence that such differential effects exist. BTB has a smaller negative effect on black men in places where a larger share of the population is black and a smaller negative effect on Hispanic men in places where a larger share of the population is Hispanic. Consequently, BTB reduces black male employment significantly everywhere but in the South (where a larger share of the population is black). Similarly, BTB reduces Hispanic male employment everywhere but in the West (where a larger share of the population is Hispanic). This suggests that employers are less likely to use race as a proxy for criminality in areas where the minority population of interest is larger, perhaps because discriminating against that entire set of job applicants is simply infeasible.⁸ In addition, we find evidence that statistical discrimination based on race is less prevalent in tighter labor markets: BTB’s negative effects on black and Hispanic men are larger when national unemployment is higher. In other words, employers are more able to exclude broad categories of job applicants in order to avoid ex-offenders when applicants far outnumber available positions.

Our hypothesis is that employers are less likely to interview young, low-skilled black and Hispanic men because these groups include a lot of ex-offenders with recent convictions and incarcerations. This hypothesis suggests that employers will instead interview and hire individuals from demographic groups unlikely to include recent offenders. We find some evidence suggesting that this does indeed happen. Older, low-skilled black men and older, low-skilled Hispanic women are significantly more likely to be employed after BTB.⁹ (These effects support our hypothesis that the racial discrimination at work is statistical, not taste based.) Effects on white men are also positive and significant when BTB targets private firms.

However, total employment might go down when employers are not able to see which applicants have criminal records. BTB increases the expected cost of interviewing job applicants because there’s a higher chance that any interview could end in a failed criminal background check. In addition, while employers might be willing to substitute college graduates or others who are clearly job ready, those individuals might not be willing to accept a low-skilled job at the wage the employer is willing to pay.¹⁰ Consistent with this, we find no effect on employment for men with college degrees. Controlling for local unemployment rates has little effect on our estimates, suggesting that BTB simply shifts employment rather than reducing it—at least in the short run.

We are not the only researchers interested in the effects of BTB on employment. Two other papers, written concurrently with this one, study the effect of this policy. However, ours is the only one to focus on real-world employment outcomes for young, low-skilled men—the group with the most to gain or lose from BTB.

Agan and Starr (2018) exploited the recent adoption of BTB in New Jersey and New York to conduct a field experiment testing the effect of the policy on the likelihood of getting an interview. They used a classic correspondence study design, submitting thousands of job applications from fictitious job seekers. All applicants were young, low-skilled men, with race and criminal history randomly assigned. Agan and Starr found that before BTB white applicants were called back slightly more often than black applicants were. That gap increased sixfold after BTB went into effect. White ex-offenders benefited the most from the policy change: after BTB, employers seem to assume that all white applicants are nonoffenders. After BTB, black applicants were called back at a rate between the ex-offender and nonoffender callback rates from before BTB—that is, those with records were helped, but those without records were hurt. Since the researchers create the applications themselves, they could keep other factors like education constant. The differences in interview rates before and after the policy change are therefore solely due to the changing factors: race and criminal history. The limitation of this approach is that fake applicants cannot do real interviews that lead to real jobs. It is possible that the few ex-offenders granted interviews would be more likely to get the job after BTB implementation than before. However, if employers are reluctant to hire ex-offenders, those applicants might be rejected once their criminal history is revealed late in the process (between the interview and the job offer). These later steps are critical in determining the true social welfare consequences of BTB. Our paper complements this one by showing that these changes in callback rates do result in changes in hiring, with a net negative effect on employment for young, low-skilled black men. We also confirm that young, low-skilled white men are more likely to be hired when BTB laws target private firms.

Shoag and Veuger (2016) use a difference-in-differences strategy to consider the effects of BTB on residents of high-crime neighborhoods (a proxy for those with criminal records), using those living in low-crime neighborhoods (a proxy for those without criminal records) as a control group. They focus on a subset of BTB cities, and neighborhoods are deemed high or low crime based on preperiod (year 2000) violent crime rates. Using aggregated data, they find that more people are employed in high-crime neighborhoods after BTB relative to employment in low-crime neighborhoods and interpret this as evidence that BTB has a beneficial effect on ex-offenders. However, the compositions of these neighborhoods may have changed over time, and the analysis does not control for residents’ demographic characteristics. A supplementary analysis uses annual data from the American Community Survey (ACS) to consider effects of BTB on the full working-age population, divided by race and gender (but not age or education, which we argue are important in this context). The way the ACS asked about employment changed in 2008, and this change seems consequential (Kromer and Howard 2010). Survey documentation strongly cautions against comparing employment outcomes before and after 2008. Given concerns about the consistency of ACS employment measures during this time period, we believe the CPS is better suited to measuring the impact of BTB. We use the CPS to consider impacts on the groups most likely to be affected by BTB in the full set of places that adopt BTB. We also use individual-level data with a full set of demographic controls to account for the composition of local labor markets. We will show that using our empirical strategy with ACS data gives qualitatively similar but highly attenuated results. When restricting the analysis to 2008 and later (after the survey change), we find statistically significant negative effects of BTB on employment for young, low-skilled black men, consistent with the estimates from the CPS.

BTB policies seek to limit employers’ access to criminal histories. This access itself is relatively new. Before the internet and inexpensive computer storage became available in the 1990s, it was not easy to check job applicants’ criminal histories. This is the world that BTB advocates would like to re-create. Of course, this world differs from our own in many other respects, but nevertheless it is helpful to consider how employment outcomes changed as criminal records became more widely available during the 1990s and early 2000s. A number of studies address this, and their findings foreshadow our own: when information on criminal records is available, firms are more likely to hire low-skilled black men (Bushway 2004; Holzer, Raphael, and Stoll 2006; Finlay 2009; Stoll 2009). In fact, many of those studies explicitly predicted that limiting information on criminal records, via BTB or similar policies, would negatively affect low-skilled black men as a group.¹¹

There is plenty of evidence that statistical discrimination increases when information about employees is less precise. Autor and Scarborough (2008) measure the effects of personality testing by employers on hiring outcomes. Conditioning hiring on good performance on personality tests (such as popular Myers-Briggs tests) was generally viewed as disadvantaging minority job candidates because minorities tend to score lower on these tests. However, the authors note that this will happen only if employers’ assumptions about applicants in the absence of information about test scores are more positive than the information that test scores provide. If, in contrast, minorities score better on these tests than employers would have thought, adding accurate information about a job applicant’s abilities will help minority applicants. They find that in a national firm that was rolling out personality testing, the use of these tests had no effect on the racial composition of employees, although they did allow the firm to choose employees who were more productive.

Wozniak (2015) found that when employers required drug tests for employees, black employment rates increased by 7%–30%, with the largest effects on low-skilled black men. As in the personality test context, the popular assumption was that if black men are more likely to use drugs, employers’ use of drug tests when making hiring decisions would disproportionately hurt this group. It turned out that a drug test requirement allowed nonusing black men to prove their status when employers would otherwise have used race as a proxy for drug use.

In another related paper, Bartik and Nelson (2016) hypothesize that banning employers from checking job applicants’ credit histories will negatively affect employment outcomes for groups that have lower credit scores on average (particularly black individuals). The reasoning is as above: in the absence of information about credit histories, employers will use race as a proxy for credit scores. They find that, consistent with statistical discrimination, credit check bans reduce job-finding rates by 7%–16% for black job seekers. As with BTB policies, one goal of banning credit checks was to reduce racial disparities in employment, so this policy was counterproductive.

Our study therefore contributes to a growing literature showing that well-intentioned policies that remove information about racially imbalanced characteristics from job applications can do more harm than good for minority job seekers.¹² Advocates for these policies seem to think that in the absence of information, employers will assume the best about all job applicants. This is often not the case. In the examples given above, providing information about characteristics that are less favorable, on average, among black job seekers—criminal records, drug tests, and credit histories—actually helped black men and black women find jobs. These outcomes are what we would expect from standard statistical discrimination models. More information helps the best job candidates avoid discrimination.

The availability of criminal records is just one facet of an ongoing debate about data availability. Improvements in data storage and internet access have made a vast array of information about our pasts readily available to those in our present, including to potential employers, love interests, advertisers, and fraudsters. This often seems unfair to those who, like many ex-offenders, are trying to put their pasts behind them. The policy debate about whether and how to limit this data availability is complicated both by free speech concerns and by logistical issues—once information is distributed publicly, what are the chances of being able to make it private again? Even so, a great deal of effort has gone into defining who should have access to particular data, often with the goal of improving the economic outcomes of disadvantaged groups.¹³ As this and related studies have shown, well-intentioned policies of this sort often have unintended consequences, and providing more information is often a better strategy.

This paper proceeds as follows: section II provides background on BTB policies. Section III describes our data. Section IV presents our empirical strategy. Section V describes our results. Section VI presents robustness checks. Section VII discusses and concludes.

II.  Background on BTB Policies

When allowed, employers commonly include a box on job applications that applicants must check if they have been convicted of a crime, along with a question about the nature and date(s) of any convictions. Anecdotally, many employers simply discard the application of anyone who checks this box. BTB policies prevent employers from asking about criminal records until late in the hiring process, when they are preparing to make a job offer. The first BTB law was implemented in Hawaii in 1998, and, as of December 2015, similar policies exist in 34 states and the District of Columbia. President Obama banned the box on employment applications for federal government jobs in late 2015.

BTB policies fall into three broad categories: (1) those that target public employers (i.e., government jobs only), (2) those that target private employers with government contracts, and (3) those that target all private employers. We will refer to these as “public BTB,” “contract BTB,” and “private BTB” policies, respectively. Every jurisdiction in our sample with a contract BTB policy also has a public BTB policy. Similarly, every jurisdiction in our sample with a private BTB policy also has a contract BTB policy. Thirteen percent of jurisdictions adopt a contract and/or private BTB policy during this time period. Our analysis focuses primarily on the effects of having any BTB policy, but we consider differential effects by policy type in section V.E.

Public BTB laws can affect both public and private sector employment. These policies were typically implemented as a result of public campaigns aimed at convincing employers to give ex-offenders a second chance. Public BTB policies were intended in part to model the best practice in hiring, and there is anecdotal evidence that this model, in combination with public pressure, pushed private firms to adopt BTB even before they were legally required to. Several national private firms, such as Walmart, Target, and Koch Industries, voluntarily banned the box on their employment applications during this period, in response to the BTB social movement.¹⁴

Public BTB laws might also affect private sector employment because workers are mobile between the two sectors and likely sort themselves based on where they feel most welcome. Ex-offenders who would have been employed in the private sector might not get those jobs if they target job openings in the public sector due to a public BTB law; if applicants change their application strategies and where they spend their time interviewing for jobs, then these policies could quickly have meaningful impacts on private sector employment. Because BTB likely affected jobs in both sectors, we will focus on the net effect of BTB policies on the probability that individuals work at all. We believe this is the most relevant policy question. However, we also consider the effect of BTB on public sector employment specifically in section VI.D.

III.  Data

Our analysis considers BTB policies effective by December 2014. Figure 1 maps the cities, counties, and states with BTB policies by that date.¹⁵ Information on the timing and details of BTB policies comes primarily from Rodriguez and Avery (2016). The details of local policies used in this analysis are listed in Table 1. When information about a policy’s effective date was available, we used that date as the start date of the policy; otherwise, we used the date the policy was announced or passed by the legislature. If only the year (month) of implementation was available, we used January 1 of that year (the first of that month) as the start date.

Information on individual characteristics and employment outcomes comes from monthly CPS data for 2004–14.¹⁶ The CPS is a repeated cross section that targets those eligible to work. It excludes anyone under age 15 as well as those in the Armed Forces or in an institution such as a prison. Each monthly sample consists of about 60,000 occupied households; the response rate averages 90% (CPS 2016). Excluding those who are incarcerated could affect our analysis: if BTB increases recidivism and incarceration by making it more difficult to find a job, some of the people now unemployed because of the policy will be excluded from the CPS sample. Any such sample selection will bias our estimates upward, so that BTB policies look more helpful than they are.

The CPS provides information on age, sex, race, ethnicity, education level, and current employment (if employed and employer type). Since our hypotheses center on statistical discrimination by race and ethnicity, we limit our analysis to individuals who are white non-Hispanic, black non-Hispanic, or Hispanic (hereafter referred to as white, black, and Hispanic, respectively). We consider three levels of educational achievement: no high school diploma, no college degree, and college degree.¹⁷ We code someone as “employed” if they answer yes to the question, Last week, did you do any work for pay? This should be the most reliable measure of employment for our population of interest, for whom temporary, seasonal, or informal jobs are common. We restrict our sample to those who are US citizens and who do not consider themselves retired.¹⁸

Our goal is to measure the effect of BTB on individuals in the local labor market, so we assign treatment at the level of metropolitan statistical areas (MSAs). All individuals are matched to states, and about three-quarters are matched to MSAs.¹⁹ We consider individuals treated by BTB if their state has a BTB policy or if any jurisdiction in their MSA has a BTB policy. For individuals living outside an MSA, only state-level policies matter. To the extent that this approach codes some MSA residents as treated by BTB when they were not, this will bias our results toward finding no effect of the policy.

Our primary group of interest is young (age 25–34), low-skilled (no college degree) men. We focus on this group for several reasons. First, the age profile of criminal offenders is such that most crimes are committed by young men. In 2012, 60% of criminal offenders were age 30 or younger (Kearney et al. 2014). So, employers concerned about job applicants’ future criminal behavior should be most concerned about younger individuals. Second, employers report the most reluctance to hire individuals who were recently incarcerated (Holzer, Raphael, and Stoll 2004), and those who are recently released tend to be young because they were young when they were convicted.²⁰ Third, the vast majority of ex-offenders have a high school diploma (or GED) or less.²¹

There are 855,772 men aged 25–34 in our sample; 503,419 of those have no college degree. In that subset, 11.9% are black, 14.0% are Hispanic, and the remaining 74.1% are white. Forty-six percent of the young, low-skilled men in our sample live in areas that were treated by BTB as of December 2014.

Summary statistics for the full working-age male population (age 25–64) in the CPS are shown in Table 2. Summary statistics for our primary population of interest—low-skilled men aged 25–34—are presented in Table 3.

Individuals affected by BTB policies are not randomly distributed across the United States. As Table 3 shows, those affected by BTB are much more likely to live in metro areas. Table A1 shows the effect of preperiod (2000) state characteristics on the likelihood of at least one jurisdiction in that state adopting a BTB policy by December 2014. States with BTB policies are more urban, have more black residents, have more college-educated residents, and have residents with higher earnings. When all of these characteristics are considered together, the strongest predictor of having a BTB policy is having a larger black population, although this effect is small: a 1 percentage point increase in the state black population increases the probability that BTB is adopted in that state by 1.75 percentage points (2.5% of the average probability). The remaining characteristics are statistically insignificant.²²

We are particularly interested in whether the local labor markets in non-BTB places are good counterfactuals for those in places that adopted BTB. Focusing on metro areas only, we find that the local unemployment rate in 2000 has a weak relationship with the probability that an MSA ever adopted BTB: a 1 percentage point increase in local unemployment increases the probability of adopting BTB by only 1.5 percentage points, and that effect is statistically insignificant. Similarly, the local preperiod unemployment rate had a small and insignificant effect on the timing of BTB adoption. Results are in Table A3.

Overall, this is a policy that has been adopted primarily by urban areas in states with larger black populations, but the local labor market conditions do not appear to have affected whether or when BTB was adopted by particular jurisdictions. Even so, adoption of BTB was a local choice, and the results of this study speak to the effects of BTB in the types of jurisdictions that adopted the policy by December 2014. Given that areas that do not adopt BTB look somewhat different from those that do adopt BTB, we conduct robustness checks that use only similar jurisdictions as control groups. We also pay close attention to the parallel trends assumption of our difference-in-differences identification strategy.

IV.  Empirical Strategy

We consider the effect of BTB policies on the probability that individuals are employed based on a linear probability model. We use the following specification:

Our preferred specification fully interacts all of the control variables with race. This is equivalent to running the regressions separately by race (in fact, we will sometimes present results separately by racial group when that makes a table more readable). Allowing this additional flexibility (where the effect of all controls can vary with race) reduces our statistical power and often has little effect on the estimates. However, for some subgroups it makes a difference. We view this fully interacted specification as the most conservative approach. For the sake of transparency we will show how the main results change as each set of controls is added.

For each 25–34-year-old man in our sample, the full set of controls adjusts for the average employment probability for men of the same race/ethnicity within his MSA, the employment trend for that race/ethnicity group in his MSA, monthly region-specific employment shocks (such as the housing crash), and his individual characteristics. Any remaining variation in his likelihood of employment would come from idiosyncratic, individual-level factors (e.g., an illness or a fight with a supervisor) or MSA-specific shocks that do not affect nearby MSAs, such as adoption of a BTB policy. Our identifying assumption is that the adoption and timing of BTB policies are exogenous to other interventions or local job market changes that might affect employment, so that, in the absence of BTB, employment probabilities would evolve similarly to those in nearby MSAs without the policy. The most likely threat to identification is that BTB policies were voluntarily adopted by areas that were motivated to help ex-offenders find jobs. The timing of these policies likely coincides with new local interest in hiring those with criminal records. This should bias our estimated effects upward, toward finding positive effects on young, low-skilled black and Hispanic men.

V.  Results

Figure 2 shows a coefficient plot of results from equation (1) for young, low-skilled white men. The Y-axis shows the effect of BTB on the probability of being employed; the X-axis shows the year relative to the effective date of the BTB policy. Year t is the effective date of BTB. Year $t-1$ is the excluded category, and so that coefficient is forced to be zero. The coefficient for $t-4$ includes 4 years or more before the policy change; similarly, the coefficient for $t+4$ includes 4 years or more after the policy change. The dashed lines show 95% confidence intervals around the coefficients.

BTB appears to have no effect on employment for young, low-skilled white men. Estimates are near zero before BTB and remain near zero after BTB.

Figure 3 shows the coefficient plot for black men. Estimates are less precise due to the smaller sample, but they are still informative. For black residents, the “effect” of BTB on employment during the preperiod is basically flat; if anything, it appears that employment for black men may have been increasing slightly 2–3 years before BTB was implemented, consistent with the possibility that BTB jurisdictions are positively selected in terms of local efforts to support young, low-skilled black men. But the year before BTB, there was no impact on employment for this group, and after BTB goes into effect, employment begins to fall. This negative effect of BTB worsens over time.

Figure 4 shows the coefficient plot for Hispanic men. Again the estimates are noisy, but they are fairly flat before BTB. After BTB, it appears there is a reduction in employment, but it is short lived. By 3 years after BTB is implemented, the effect on employment has returned to zero.²⁶

To consider the outcomes from figures 2–4 more rigorously, Table 4 presents our main results for men aged 25–34 with no college degree. We consider the effect of BTB for each race subgroup (white, black, Hispanic). Each column adds control variables from equation (1) and/or restricts the sample of analysis.

Column 1 shows the effects of BTB in the full sample, controlling only for MSA fixed effects. With no additional information about the individual or the time period, BTB is associated with a lower probability that low-skilled white men are employed. This association is larger for black men and slightly smaller for Hispanic men.

Column 2 adds detailed information about the individual, including age fixed effects, fixed effects for precise years of education, and whether he is currently enrolled in school. This reduces the magnitude of the above-described effects slightly, but qualitatively they are very similar.

Column 3 begins to add information about labor market trends, with time-by-region fixed effects; time is the month of the sample, and region is the census region. The estimates are now more plausibly interpreted as causal effects. As expected, controlling flexibly for labor market shocks is important, as our sample period (2004–14) includes the Great Recession. Many BTB policies are implemented at the state level, so we cannot control for month-specific state-level shocks. However, most of the non-BTB labor market shocks we are worried about, such as the housing crash, affected MSAs throughout the census region. These fixed effects should absorb that type of variation.²⁷

Controlling for time-by-region fixed effects wipes out the correlation between BTB and employment for white men, reducing that coefficient to a small and statistically insignificant negative 1 percentage point. The effect on black male employment is a statistically significant 3.2 percentage points ($p<.01$). The effect on Hispanic men is also negative 1 percentage point and statistically insignificant.

Column 4 further controls for non-BTB labor market trends with MSA-specific linear time trends. This makes the estimate slightly more precise but has little effect on the estimates.

The effects of the controls and time trends might vary with race—for instance, the employment trend for black men in a particular MSA might be different from the trend for white men. Column 5 presents the results of a fully interacted model, where the effects of all of the control variables in equation (1) are allowed to differ across race/ethnicity groups (white, black, and Hispanic). This reduces our statistical power substantially but is the most conservative approach to isolating the effect of BTB. It is equivalent to running the regressions separately by race. Based on these estimates, BTB reduced employment by a statistically significant 3.4 percentage points (5.1%) for black men and by a marginally significant 2.3 percentage points (2.9%) for Hispanic men. This is our preferred specification.

One concern about using non-BTB jurisdictions as controls is that they tend to be less urban and have smaller black populations than places that adopt BTB. Even after controlling for preexisting trends, they might not be good counterfactuals for the places likely to adopt BTB. Columns 6 and 7 restrict the sample to places that are similar to BTB-adopting labor markets.

Column 6 considers only individuals living in MSAs—that is, it excludes individuals living in more rural areas. (In our data set, those individuals could still have been affected by state-level policies.) Since BTB-adopting jurisdictions tend to be more urban, perhaps it makes the most sense to compare them only with similarly urban places. Under this restriction, we lose about one-third of our original sample. We have less statistical power, but the effect on black and Hispanic men is similar to before: BTB reduces employment by 2.9 percentage points for black men ($p<.05$) and by 2.3 percentage points for Hispanic men ($p<.10$).

Column 7 restricts attention to only jurisdictions that adopted BTB by December 2014. If some types of places are more motivated to help ex-offenders or reduce racial disparities in employment and thus to adopt BTB, labor market trends might be fundamentally different than they are in other places. This compares apples with apples, so to speak—we consider only individuals who live in places that eventually adopt BTB and rely on variation in the timing of policy adoption to identify BTB’s effect. This reduces our sample to under half of what it was originally, so we again lose statistical power, but the magnitudes of the estimates are very similar to those in column 5. BTB has no significant effect on white male employment but reduces the probability of employment by 3.1 percentage points for black men ($p<.05$) and by 2.0 percentage points for Hispanic men (not statistically significant).

Some readers might be concerned that our specification does not control sufficiently for local labor market shocks. To address this, column 8 adds a time-varying control for the MSA unemployment rate. Since this applies only to individuals living in an MSA, we restrict the sample to that population, as in column 6. Controlling for unemployment when our outcome variable is the probability of employment raises obvious endogeneity concerns—if BTB reduces local employment overall (due to the increase in expected hiring costs), then controlling for the unemployment rate could mask that effect. However, if BTB simply shifts employment from one group to another, leaving the overall unemployment rate unchanged, then controlling for the local unemployment rate might not make a difference. As column 8 shows, controlling for MSA-level unemployment has little effect on our estimates. This suggests two things: (1) our estimates are not the result of local labor market shocks unrelated to BTB and (2) at least in the short run, BTB shifts employment from one group to another rather than reducing the total number of people employed.

Overall, these results tell the same story as the graphs described above. It is reassuring to find such similar effects across most specifications and samples. In particular, our robustness samples including only metro areas or only BTB-adopting places show extremely similar effects. The fully interacted model is required to detect BTB’s effect on Hispanic men, but that effect is also robust to different sample definitions. We see no significant effect of BTB on white men without college degrees in this age group.

VI.  Robustness

VII.  Discussion

Ban the box has arisen as a popular policy aimed at helping ex-offenders find jobs, with a related goal of decreasing racial disparities in employment. However, BTB does not address employers’ concerns about hiring those with criminal records and so could increase discrimination against groups that are more likely to include recently incarcerated ex-offenders, particularly young, low-skilled black and Hispanic men.

In this paper, we exploit the variation in adoption and timing of state and local BTB policies to estimate BTB’s effects on employment for these groups. We find that BTB reduces the probability of employment for young black men without a college degree by 3.4 percentage points (5.1%) and for young Hispanic men without a college degree by 2.3 percentage points (2.9%). The effect on black men is particularly robust across different specifications and samples.

These effect sizes may seem large, but they are consistent with those found in related studies. Holzer, Raphael, and Stoll (2006) found that the last hire was 37% more likely to be a black man when firms conducted criminal background checks, while Bartik and Nelson (2016) found that banning credit history checks reduced the likelihood of finding a job by 7%–16% for black job seekers. Given relatively high turnover rates in the low-skilled labor market, it does not take long for increases or decreases in hiring rates to result in a large change in employment.³⁵ For instance, in a similar context Wozniak (2015) found that allowing drug testing by employers increased employment for low-skilled black men by 7%–30%.

In light of these other studies and estimated turnover rates, our estimates are plausible and may actually be somewhat small. Indeed, our effects are likely biased upward (toward finding positive effects of BTB) for two reasons. First, jurisdictions that adopt BTB are typically more motivated to help ex-offenders find jobs, and this motivation alone should increase employment for those with criminal records. Second, the CPS excludes individuals who are incarcerated, so if some of the men who are unemployed as a result of BTB commit crime and are sent to prison, they will not be included in our sample.

Most work on statistical discrimination posits that employers will infer applicants’ productivity correctly, on average, and so small differences in criminal histories across black and white men should have smaller effects on employment outcomes than larger differences would. In this framework, where employers think of productivity as a continuous measure and the likelihood of hiring an applicant (or the wage someone is paid) increases with their expected productivity, this might be correct. However, if employers are comparing multiple applicants for a single job opening, even small differences in expected productivity across racial groups could have large effects on hiring. If a criminal record is correlated with low productivity and black men are more likely to have a criminal record, then when faced with identical applications from a black man and a white man, an employer will assign lower expected productivity to the black applicant every time and always choose the white applicant. This decision-making process, where applicants are not judged in a vacuum on the basis of their expected productivity but are compared with other applicants, can explain the apparently large effects of policies like BTB on hiring and employment, even when real-world differences in criminal histories are relatively small.³⁶

This is the first paper to consider the effects of BTB on the employment of young, low-skilled black and Hispanic men, but our findings are consistent with theory and other research about statistical discrimination in employment. We find evidence that BTB has unintentionally done more harm than good when it comes to helping disadvantaged job seekers find jobs. More research on the dynamics of job application behavior and the differential effects across law types would be helpful in understanding how job applicants and employers respond to this and similar labor market policies. Understanding how these actors interpret and utilize information in employment decisions can help us design better policies going forward.

Increasing employment rates for ex-offenders is a top policy priority, for good reason, but policy makers cannot simply wish away employers’ concerns about hiring those with criminal records. Policies that directly address those concerns—for instance, by providing more information about job applicants with records or improving the average ex-offender’s job readiness—could have greater benefits without the unintended consequences found here.