Empowering youth through summer jobs

One Summer Chicago program

Editor's Introduction

Summer jobs reduce violence among disadvantaged youth

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When young adults do not have access to jobs they are more likely to be involved in violent activity that can injure or kill those involved. This suggests that there is something about having a job that keeps young adults from participating in violent activity. This study looks specifically at summer employment and aims to show that summer jobs lower the rate of youth related violence. These findings can encourage state and local governments to develop summer job opportunities for young people.

Paper Details

Original title
Summer jobs reduce violence among disadvantaged youth
Sarah Heller
Original publication date
Vol. 346 no. 6214 pp. 1219-1223 
Issue name


Every day, acts of violence injure more than 6000 people in the United States. Despite decades of social science arguing that joblessness among disadvantaged youth is a key cause of violent offending, programs to remedy youth unemployment do not consistently reduce delinquency. This study tests whether summer jobs, which shift focus from remediation to prevention, can reduce crime. In a randomized controlled trial among 1634 disadvantaged high school youth in Chicago, assignment to a summer jobs program decreases violence by 43% over 16 months (3.95 fewer violent-crime arrests per 100 youth). The decline occurs largely after the 8-week intervention ends. The results suggest the promise of using low-cost, well-targeted programs to generate meaningful behavioral change, even with a problem as complex as youth violence.


Every day in the United States, acts of violence kill almost 150 people and injure over 6000 more (12). This “public health crisis” (3) disproportionately involves youth, who are twice as likely as adults to be both victims and perpetrators of violence (4). The problem is most concentrated among disadvantaged minority youth; violent-crime arrest rates for African-American juveniles are five times as high as that of their white counterparts (5).

Poverty scholar W. J. Wilson identifies one major cause of these racial violence disparities among young people: joblessness (6). His argument adds to decades of social science investigating how poor job prospects cause crime, from weakening social bonds to generating psychic strain to reducing the perceived cost of punishment (710). Policy discussions often conclude that public employment and training programs are a solution to youth violence on the grounds that “nothing stops a bullet like a job” (11).

The empirical literature on youth employment programs, however, suggests that the practical applications of this idea are limited (12). Several major employment programs fail to reduce delinquency among youth (1314). The two experimentally evaluated interventions that do lower crime, at least during the program, involve such intensity and expense that their benefits fail to outweigh their costs (1516). Attempts to provide shorter, more scalable employment services have, if anything, increased adolescents’ criminal behavior (17). The theoretical promise of using employment interventions to fight youth violence does not appear to translate easily into empirical reality; only very high levels of investment seem able to reduce crime (supplementary materials, section 2.1) (18).

But, one widespread type of youth employment program has not yet been rigorously evaluated: summer jobs (19,20). Despite some promising observational studies (21), there is little convincing causal evidence on the effects of these short-term, low-cost programs and, to my knowledge, no experimental evidence on whether summer jobs can reduce crime (supplementary materials, section 2.1).

This paper presents the results of a large-scale randomized controlled trial that tests a public summer jobs program in Chicago called One Summer Plus (OSP). OSP offers 8 weeks of part-time summer employment at Illinois’ minimum wage ($8.25/hour). Local community organizations place youth in nonprofit and government jobs (for example, summer camp counselors, workers in a community garden, or office assistants for an alderman). Youth are assigned job mentors—adults who help them learn to be successful employees and to navigate barriers to employment—at a ratio of about 10 to 1. Half the treatment group also receives social-emotional learning (SEL) based on cognitive behavioral therapy principles, aimed at teaching youth to understand and manage the aspects of their thoughts, emotions, and behavior that might interfere with employment (supplementary materials, section 2.2).

The study randomly assigns 1634 8th- to 12th-grade applicants enrolled in 13 high-violence Chicago schools to program (jobs-only or jobs + SEL) or control conditions (22). Youth in the jobs-only group are offered 25 hours per week of paid employment; youth in the jobs + SEL group are paid for 15 hours of work and 10 hours of SEL weekly. Control youth are excluded from the program but free to pursue other opportunities.

The existing employment literature might suggest that this kind of low-dosage jobs program is unlikely to change criminal behavior. But, there is an important difference between summer jobs for in-school youth and the previous literature: The well-studied youth employment programs generally act as tertiary prevention, targeting youth already out of school and struggling in the labor market. Research in domains such as education and health, however, suggests that for many negative outcomes caused at least in part by prior behavior (for example, poor school performance and dropout, or certain types of cancer), primary and secondary prevention—intervening before onset rather than managing or trying to reverse a problem once it occurs—can improve outcomes more effectively, with less intensive treatment (2325)

If this well-established idea that prevention can be more effective than remediation also applies to the employment domain, teaching adolescents how to be successful employees, facilitating connections to employer networks, and providing work experience before they drop out of school might reduce crime with less intensive intervention than is required for already disconnected youth. Offering summer employment at this key point in the life course could make crime a relatively less attractive option, strengthen social bonds, and develop “soft” skills such as self-efficacy and impulse control (72628). Waiting until after dropout to intervene may make it more difficult to reduce violence in particular, given the apparently causal relationship between school dropout and criminal behavior, especially murder and assault (29). Limiting the intervention to summer avoids direct conflicts between work and school. Summer jobs also provide wages and structured activity during a high-crime season when youth might otherwise be idle, both of which may affect crime (3031).

However, the theory on summer jobs is not entirely clear-cut. Additional income could be spent on crime-inducing goods such as drugs and alcohol, and time spent traveling to and from work might increase exposure to criminal opportunities. Even the attempt to keep youth busy (the “incapacitation effect”) may be poorly targeted because most jobs are during business hours, whereas most crime occurs during evenings and weekends. More broadly, a short-term subsidized job might not be enough to generate behavior changes beyond the summer itself. The effects of summer jobs are therefore an empirical question.

Data come from matching study youth to administrative data sources (supplementary materials, materials and methods). Program participation is from provider-tracked attendance records. Student-level administrative records from the Chicago Public Schools capture pre- and post-program academic outcomes from the 2011–2012 and 2012–2013 academic years, respectively. Demographic information on applicants’ neighborhoods comes from matching the Census tract of youths’ home addresses to the 2010 American Community Survey. The main outcome measures are from individual-level Chicago Police Department arrest records covering both juveniles and adults (32). The study uses data through 25 September 2013, which is 16 months after randomization (13 months after the end of the program).

The analysis categorizes arrests by offense type (violent, property, drug, and other). It is common for social interventions to have differential impacts on these different types of crime (313334), likely because some of the underlying causes differ. Violent crime stems from conflicts between people, so problematic cognitive and emotional responses to social interactions—including hostile attribution bias, uncontrolled anger, and “hot” decision-making—are thought to be proximal causes of youth violence in particular (3536). Nonviolent crimes, which involve property or drugs more often than interpersonal conflict, may be relatively more responsive to situational and economic factors (3738). Because OSP could affect how youth perceive and respond to social interactions differently from how it affects their economic situations, opportunities for crime, or drug use, the study estimates program effects separately by crime type.

Average applicant characteristics on a variety of preprogram measures are shown in Table 1. None of the differences across the columns is statistically significant, nor are they jointly significant (F31,1517 = 0.37, P = 0.9995), confirming the success of randomization.


Table 1.  Mean preprogram characteristics for treatment and control groups.  To test baseline equivalence, each characteristic was regressed on treatment indicator and blocking variables using heteroskedasticity-robust standard errors; the P value column reports statistical significance of treatment indicator’s coefficient. Demographic and schooling data are from Chicago Public Schools’ administrative records on pre-program year (2011–2012 school year). Free/reduced price lunch is proxy for family poverty. Days absent are reported as a percentage of days enrolled (average missed, 29 days). Arrest and victimization data are from Chicago Police Department administrative records. Neighborhood characteristics are from 2010 American Community Survey and Chicago Police Department’s community-area crime rates. “Percent unemployed” is percent of civilian labor force over age 16 years looking for work but without a job. Table uses nonmissing data only (5 youth missing school attendance data, 60 missing fall GPA, 1 missing neighborhood violent-crime rate). Gender is not included in the table because it is captured by the blocking variables; 38% of the sample is male.


This table presents a mean (average) breakdown of the social and economic backgrounds of the participants in the experiment. Because the goal of a randomized controlled trial is to show how a treatment or intervention effects a relationship, ensuring that both groups, the control group and the treatment group, share similarities is important.

This table is meant to show how this sample is relevant to the study.

Control mean

This column presents the mean indicators for participants who are part of the control group—those who are NOT randomly assigned to the summer jobs program.

The control group is important because it will be compared with the treatment group—those who are randomly assigned to the summer jobs program.

Treatment mean

This column presents the mean indicators for participants who are randomly assigned to the summer jobs program. If you look at the different indicators for the control and treatment groups you see that there is not much difference.

p value

Although we as readers of this table can notice that there do not seem to be any major differences between the control and treatment means, it is necessary to use statistics to establish whether this is true.

In statistical tests, when a p value is greater than .05 it is safe to assume that there is no statistical significance. In this case, the statistical test is attempting to see whether there are differences in the socio-economic indicators between the control and treatment groups.

As you look down the column of p values notice that all of the p values are greater than .05. This means that for all of these socio-economic indicators, both the control and treatment groups present very similar backgrounds.

Applicants are on average just over age 16 years (minimum, 14 years; maximum, 21 years), and almost all are African-American. Over 90% are eligible for free or reduced price lunches (a proxy for family poverty), with average grade point averages (GPAs) around a C in the prior fall semester. Study youth missed 18% of the preprogram school year, or around 6 weeks. About 20% had been arrested at baseline, and just over 20% had been victimized. Applicants live in highly disadvantaged neighborhoods: Unemployment averages over 19%; a third of households are under the poverty line; and violent crime rates are extremely high (more than 2100 incidents per 100,000 people).

The main text presents intent-to-treat (ITT) estimates, which measure the average difference between those randomly assigned to treatment and control groups. Three quarters of treatment youth actually participate (supplementary materials, section 2.3, and table S1). Because not all youth who are offered the program enroll, the ITT understates the effect of the program on those who choose to participate. This treatment-on-the-treated effect is discussed and estimated in the materials and methods section and section 2.4 of the supplementary materials. Program impacts are shown both for the treatment group as a whole and each treatment arm.

During the 16-month follow-up period, ~17% of the control group (n = 155 youth) is arrested for any crime, with an average of 0.30 arrests per youth. The main ITT results are presented in Fig. 1. Violent-crime arrests among the treatment group decrease by 43% relative to the control group (0.0395 fewer arrests, or almost 4 fewer per 100 youth; P = 0.022). There are no significant changes in other types of arrests (39). The results are robust to accounting for the number of hypothesis tests conducted, allowing youth outcomes to be correlated within schools and using a nonlinear specification for count data (supplementary materials, section 2.5). Although the study was not powered to detect heterogeneous treatment effects across subgroups, there is suggestive evidence that arrests fall more among youth at higher risk of violence (supplementary materials, section 2.7).


Fig. 1.  ITT program effect on crime by arrest type.  Shown are the control group mean, regression-adjusted treatment mean, difference between the two (ITT), and 95% confidence interval for the difference by arrest type. Data are from Chicago Police Department administrative arrest records through 16 months after randomization. ITT was calculated by using ordinary least squares regression with heteroskedasticity-robust SEs, controlling for baseline covariates and blocking variables. Percent change is relative to the control mean. ***P < 0.01, **P < 0.05, *P < 0.10


This figure is showing the effects of the summer jobs program on rates of different kinds of crime. The researcher gathered data on these crimes from the Chicago, Illinois, Police Department 16 months after the study population was randomized into either participating in the summer jobs program (treatment group) or not participating in the summer jobs program (control group).

Average arrests per youth (top)

This bar graph shows the average number of arrests for violent crime, property crime, drug crime, and other miscellaneous crimes per youth and according to the control mean and the treatment mean.

In looking at the violent crime bars we can see that for the control mean, there are 0.091 arrests per youth compared with 0.051 arrests per youth for the treatment mean.

Intent to treat program (bottom)

This bar graph is showing whether we can statistically claim that the summer jobs program has an effect on arrest rates by comparing the control mean and treatment means.

The researcher uses a regression technique to test this. Like we did in Table 1, we have to look for the p values to determine whether there is a statistical significance. In this chart we see that the difference between the treatment and control group for violent crime arrests is significant at the .05 level.

There are no significant differences for the other crimes.

An important question concerns what mechanisms drive this considerable behavioral change. One hypothesis for why prior youth employment programs require high intensity to succeed is that disadvantaged adolescents may lack the “soft skills” to engage with less intensive pro-social programming (40). If so, OSP’s SEL curriculum—which focuses on emotion and conflict management, social information processing, and goal setting—could be a key driver of the violence decrease. Because SEL was randomly assigned, the study can separately identify any additional role of SEL.

ITT violence effects by treatment group are shown in Table 2. Not only is the difference between groups statistically insignificant, but the magnitude is also tiny (1% of the control mean). The nearly identical point estimates suggest that the statistical similarity across groups is not just the result of limited power to detect subgroup differences. Instead, it appears that both groups of youth experienced very similar drops in violence. The same is true for other crime types (supplementary materials, section 2.6, and table S4).


Table 2.  ITT effect on violent-crime arrests by treatment group. Results are from regression of number of violent-crime arrests on separate treatment group indicators, baseline covariates, and block fixed effects. Bottom row shows the magnitude and SE of the difference in effect across treatment arms. Heteroskedasticity-robust standard errors are in parentheses. ***P < 0.01, **P < 0.05, *P < 0.10


If you recall from the author’s discussion of the design of this experiment, the treatment in this experiment includes two levels. Half of the participants in the summer jobs program are only involved in the summer jobs program. The other half of the summer job participants, however, are also randomly selected to be involved in social-emotional learning (SEL) to help manage their thoughts and emotions.

This table is looking at whether we can identify anything statistically significant in the effects of the SEL on violent crime activity.

Difference between groups

In looking at the difference between the two groups we notice that the p value is higher than .10. This indicates that there is not significant difference between the effects of the summer jobs only treatment group and the summer jobs + SEL group.

Neither group has more of an effect on reducing violent crime arrests than the other.

Jobs only

When looking at the effect of summer jobs on violent activity, we see that the p value is less than .10, which indicates significance.

Jobs + SEL

When looking at the effect of summer jobs and the SEL on arrests for violent activity we see that the p value is less than .05, which indicates significance.

Although the experimental design can only directly isolate the role of SEL, another potentially important mechanism is testable indirectly: whether the decrease in violence is a mechanical result of youth having less time to engage in crime while working over the summer (an “incapacitation” effect). If so, and youth returned to their prior behavioral patterns immediately after the program ended, one would expect to see a large violence drop during the program period, after which there would be no treatment-control difference. This is not the case. The ITT violence decrease during the 3 months between random assignment and the end of the program is proportionally large but statistically insignificant (–0.005 violent-crime arrests, P = 0.39, control mean = 0.01). During the following 13 months (excluding the program period), treatment reduces the number of violent-crime arrests by –0.035 (P = 0.03, control mean = 0.08).

The time path of the violence decrease is shown in Fig. 2 in greater detail. It graphs the cumulative treatment effect over time, with each point adding an additional month of data to the prior effect. The drop in arrests becomes statistically different from zero around month 6, 3 months after the end of the program, and continues to grow through month 11, after which it flattens out. The downward slope of the effect makes it clear that the bulk of the drop in violence accrues between months 5 and 11, well after the end of the program at month 3.


Fig. 2. Time path of violence decrease. Shown is the regression-adjusted cumulative difference in the number of violent-crime arrests between treatment and control youth by month. Random assignment lottery occurred at month 0; program ended at month 3. Regressions include baseline covariates and blocking variables. Confidence intervals were calculated by using heteroskedasticity-robust SEs.


This figure is demonstrating the rate by which violent crime arrests decreased over a 13-month time period.

Month three is important to note because that is the month that the summer jobs program ends. You can see how the line slopes downward from month three onward. This indicates that the rate of violent crime arrests drops once the program ends. It continues to drop through the following months.

95% Confidence interval

The gray shaded area that surrounds the line is called the 95% confidence interval. In statistical analysis the 95% confidence interval is a way to define a range of values that we can be 95% certain contains the population mean or average.

One way the program might have changed behavior during these later months is by increasing time spent in school, either by developing pro-social attitudes or providing information on how the labor market values education. However, schooling data suggest that this is unlikely to be the key mechanism. There is no treatment effect on days present (or other academic outcomes) during the following school year, with confidence intervals small enough to make changes in attendance an implausible cause of the drop in violence (supplementary materials, section 2.10, and table S7).

Prior research on youth employment suggests that only costly and intensive employment programs can reduce crime. The current study demonstrates that when offered to youth still in school, an intervention need not be lengthy to change behavior; an 8-week summer jobs program reduces violence among an adolescent population living in some of the most violent neighborhoods in the country.

The results are consistent with the idea that employment programs can have a larger impact at lower cost when offered to disadvantaged youth before school exit. There are, however, other possible reasons why this study finds larger effects than previous work. For example, OSP involved an adult job mentor making regular visits to the workplace, whereas most of the evaluated U.S. youth programs do not. The measurement of crime may also matter. If reaching youth before school exit is the key difference, one might expect multiple-year interventions for high school youth that aim to improve both education and employment outcomes to generate even larger impacts than seen here. In fact, they generally find no effects on crime (4142). But, the evaluations of those two programs use self-reported overall crime rates, separating only drug and alcohol use. Given that effects are heterogeneous by crime type, it is possible that these programs also reduced violence, but that the studies aggregated crime outcomes to a level that masked the effect.

The estimates in this paper rely on administrative arrest records, which only capture offenses known to the police. Nationally, about half of violent incidents are reported to police, about half of which result in an arrest (4344). As such, the estimates here may considerably understate the number of violent crimes prevented (supplementary materials, section 2.9).

The fact that both the jobs-only and jobs + SEL versions of the program were equally effective means that SEL cannot be the only operative mechanism. A similar SEL program has reduced violence on its own (45), but the jobs-related programming was enough to generate the steep drop in violence independently. Because replacing 2 hours of work with an SEL curriculum neither improved nor reduced the intervention’s impact, the relevant mechanism is likely to be something common across the two types of programming.

One possibility is that the substance of the SEL curriculum—teaching youth to process social information, manage thoughts and emotions, and set and achieve goals more successfully—was taught equally well on the job. Youth could have learned these skills from interactions with the job mentors, who were part of both treatment arms. Reports from the program providers suggest that the mentors play a large part in helping youth learn to manage conflict in the workplace, in addition to teaching basic job skills. The process of working itself might also be enough to improve self-control, develop self-efficacy, and reduce frustration (all potential determinants of how youth perceive and respond to conflict). One study, which randomly assigned adults to an earnings subsidy program to increase employment, found that treated individuals report a greater sense of control over their lives and less anger about their lack of opportunities (46).

Another possibility is that the relevant mechanism was something else that both groups received: income, a caring adult, job skills, and/or employer connections. The experimental design cannot tease out which program element or elements generate the decrease in violence. Nonetheless, because schooling outcomes show little movement, it is unlikely that changes in perceptions about the value of schooling, or simply the amount of time in school, are the main drivers of the violence drop. The program provides a relatively large income shock, averaging 1,400 USD in neighborhoods where one third of households are below the poverty line and median income is about 35,000 USD. Additional income could change criminal behavior directly or increase parental supervision by reducing how much parents need to work away from home. It is also possible that improved post-program employment plays a role, although the direction of that effect is theoretically ambiguous. Working more could reduce all types of crime through incapacitation or by making it more costly to be incarcerated. But, the increased income could also have mixed effects, for example by reducing economically motivated crimes such as theft while increasing the ability to purchase drugs.

The fact that OSP only reduces violent crime is perhaps most consistent with a role for improvements in self-control, social information processing, and decision-making, which as discussed above are more central to violent behavior than to other types of crime. Other interventions that target these skills through either explicit curricula or mentorship have also reduced youth delinquency with very few contact hours (4748).

One key insight from the data is that incapacitation alone—the mechanical reduction in free time during the summer—cannot explain the program’s success. Violence reductions are large and statistically significant during the 13 months after the program is over, and the point estimate is 7 times larger at the end of the follow-up period than at the end of the summer. This pattern is not consistent with the idea that behavior only changed during the initial 8 weeks of the program; something about youths’ summer experiences also changed their future behavior.

As in any social experiment, external validity is not guaranteed. The study sample is fairly representative of low-income, African-American youth living in urban neighborhoods who are still enrolled in school. Many other cities have successfully implemented summer jobs programs, suggesting that the basic approach is one that may not be difficult to scale (although displacement effects that reduce the number of jobs available to nonprogram youth become a bigger concern in larger-scale programs). A better understanding of how broadly these results will generalize requires replications in other cities with different service environments and youth populations. Policymakers should proceed with caution until future studies can establish exactly what works for whom, how long effects persist, and whether the program’s benefits outweigh its costs (supplementary materials, section 2.11).

In the meantime, this study provides causal evidence on the effects of a widespread but under-studied intervention. The results echo a common conclusion in education and health research: that public programs might do more with less by shifting from remediation to prevention. The findings make clear that such programs need not be hugely costly to improve outcomes for disadvantaged youth; well-targeted, low-cost employment policies can make a substantial difference, even for a problem as destructive and complex as youth violence.

Supplementary Materials


Materials and Methods

Supplementary Text

Tables S1 to S8

References (5396)

References and Notes

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  2. Numbers are daily averages from the 5 most recent years of violence-related fatalities (from death certificates) and nonfatal injuries (from emergency room reports).

  3. Center for Disease Control and Prevention, STRYVE to Prevent Youth Violence Website, 2014; available at www.cdc.gov/features/youthviolence/index.html.

  4. Authors’ calculations for ages 10 to 24 years versus over 24 are from 2012 Federal Bureau of Investigation (FBI) Uniform Crime Reports, Census data, and (1).

  5. Office of Juvenile Justice and Delinquency Prevention, OJJDP Statistical Briefing Book, U.S. Department of Justice, Washington DC, 2014; available at www.ojjdp.gov/ojstatbb/crime/JAR_Display.asp?ID=qa05261.

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  12. The focus here is on youth programs because disadvantaged youth are at such disproportionate risk of violent offending. There have been many public efforts to provide vocational or on-the-job training, job search assistance, and remedial education to adults as well. Those programs’ crime effects are also mixed (49), perhaps in part because the largest employment impacts tend to be among adult women—a group with very low levels of criminal involvement (supplementary materials, section 2.1).

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  18. Although there is a consensus that generating measurable changes in youth outcomes requires comprehensive and expensive intervention, conclusions about how much investment is desirable differ by author (19, 40, 49, 50).

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  22. Youth were individually randomized within a blocked design, in which blocks were defined by school and gender. All analyses control for the blocking variable. Materials and methods are available as supplementary materials on Science Online.

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  25. The emphasis on those already exhibiting symptoms of the underlying problem is true of most major programs focused on youth employment. The youth elements of the National Supported Work Demonstration, JOBSTART, the National Guard ChalleNGe, and the Job Training Partnership Act all focus on high school dropouts (13, 16, 17, 51). Job Corps requires applicants to need additional education, training, or vocational skills—all signs that they are already experiencing difficulties in the labor force (15). Year Up serves youth no longer in school (52). There are well-evaluated programs for high school youth that integrate employment programming with long-term educational interventions [such as (41, 42)]. However, because they are also lengthy and intensive—and aim to improve educational attainment directly, which may have an independent impact on crime (29)—they do not provide a test of the hypothesis proposed here: that low-dose, low-cost employment interventions could have a larger effect than suggested by the existing employment literature when used as primary and secondary prevention.

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  32. Additional results on violent victimizations are provided in supplementary materials, section 2.7.

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  39. The reliance on official arrest data means that violent crime is a better-measured outcome; nationally, violent crimes are 2.5 times more likely to result in an arrest than are property crimes (43). Differential arrest probabilities also help explain why the control means for property and drug arrests are around half as large as for violent-crime arrests, despite the fact that nonviolent crimes are more common (43). The supplementary materials, section 2.9, discusses how underreporting might affect the results.

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