One of the most striking features of crime in America is its disproportionate concentration in disadvantaged, racially segregated communities. For example, in 2008, the homicide rate in Hyde Park, the economically and racially mixed neighborhood that is home to the University of Chicago, was 3 per 100,000. In adjacent Washington Park, where over half of residents are poor and 98 % are African-American, the homicide rate was nearly 20 times higher. In its explanation of the riots of 1967, the Kerner Commission cited the destructive role of “the black ghettos where segregation and poverty converge on the young to destroy opportunity and enforce failure. Crime, drug addiction, dependency on welfare, and bitterness and resentment against society in general and white society in particular are the result” (Kerner et al. 1988, p.10). Neighborhood environments potentially can affect criminal behavior through several mechanisms, including peer groups and social interactions (Cook and Goss 1996; Gaviria and Raphael 2001; Glaeser et al. 1996), as well as the quality of local public goods such as schools and police (Becker and Murphy 2000).

A large body of non-experimental empirical research documents that youth and adults living in more disadvantaged, disordered neighborhoods are at elevated risk of engaging in crime even after statistical regression adjustment is made to account for individual-level observable socio-demographic characteristics and other risk factors. In a recent review of the “neighborhood effects” literature, Sampson et al. (2002) concluded that the evidence linking neighborhood processes to crime is stronger than evidence linking neighborhood processes to other outcomes such as health. This non-experimental research raises the question of whether moving people out of areas of concentrated poverty can prevent them from becoming involved in criminal activity.

This question is difficult to answer with non-experimental methods because most families have some degree of choice over where they live and with whom they associate. There necessarily remains much uncertainty about the degree to which non-experimental studies are able to isolate the causal effects of neighborhood environments themselves on criminal behavior from the impacts of hard-to-measure individual or family attributes associated with both residential selection and criminal propensities. Experimental methods that generate exogenous variation in neighborhood environments can provide more plausibly causal estimates of the impacts of neighborhoods on criminal behavior (for a summary of this methodological literature, see Cook et al. 2008).

In this paper, we discuss what is known about the long-term effects of moving from a very distressed to a less-distressed neighborhood, drawing on new data from the U.S. Department of Housing and Urban Development’s (HUD) Moving to Opportunity (MTO) randomized residential mobility experiment. A randomized lottery provided families—living in high-poverty public housing at five sites (Baltimore, Boston, Chicago, Los Angeles, and New York)—with the opportunity to move to lower-poverty neighborhoods with a housing voucher. We utilize administrative and survey data collected as part of the “long-term” study of MTO families measuring outcomes 10–15 years after baseline. Our paper builds on the “interim” MTO study by Kling et al. (2005), which focused on MTO youth—the age group at highest risk for crime involvement—and examined outcomes of those who were aged 15–25 at 4–7 years after baseline to answer three key questions: (1) does moving youth out of areas of concentrated poverty prevent involvement in crime; (2) do these neighborhoods effects vary over time; and (3) do the effects differ by gender?

That study found that the offer of an MTO housing voucher reduced lifetime violent-crime arrests by 32% and property-crime arrests by 33% for females in the experimental group relative to their control group counterparts. In contrast, for males in the experimental group, the offer of a voucher increased lifetime property-crime arrests by 32% relative to controls and the associated reduction in lifetime violent-crime arrests was not statistically significant; however, in the first 2 years after random assignment, violent-crime arrests for males offered an experimental voucher were statistically significantly lower (by 34%) than for controls. Overall across types of crime, females in the experimental group experienced a significantly lower (by 37%) number of arrests relative to controls while the slightly higher number of arrests for experimental group males relative to controls was not statistically significant. Using interim MTO data, Ludwig and Kling (2007) found that racial segregation appears to be the most important neighborhood characteristic in predicting youth violence involvement, more so than a neighborhood’s rate of poverty or violent crime, which were generally not statistically significant predictors.

We present new results demonstrating that there is an attenuation over time of these MTO effects on male criminal behavior for the same cohort of youth examined by Kling et al. (2005). We examine new data on these youth covering 10 years after the time of random assignment.¹ Fade-out over the longer-term is apparent for MTO’s interim adverse effects on property offending by male youth and for beneficial, protective effects in reducing youth violence involvement. We present evidence suggesting that this fade-out of MTO crime impacts for males appears to be partly explained by the attenuation of MTO treatment impacts on neighborhood conditions over time.

The dynamic pattern of MTO crime impacts seems more concordant with a behavioral model emphasizing contemporaneous rather than past neighborhood conditions in driving crime, or what Sampson (2012) calls “situational” rather than “developmental” neighborhood effects. The situational neighborhood effects hypothesis suggests that the offending behavior even of adolescents who have been exposed for many years to distressed neighborhood environments may respond to changes in community contexts.² Our results are consistent with some of the previous situational neighborhood effects research suggesting that even modest changes to the “in the moment” decision-making environment can substantially affect criminal behavior. Other examples include work by Ronald Clarke and others on ‘situational crime prevention’ (Clarke 1995; Homel and Clarke 1997; Cornish and Clarke 2003), the discussion by Zimring (2011) of the determinants of New York City’s crime drop, and the recent cognitive behavioral therapy study by Heller et al. (2013).

The next section briefly reviews the candidate mechanisms through which neighborhood environments might influence crime and violence. The third section provides a very brief review of previous non-experimental studies. Section four discusses the MTO experiment, section five discusses our data sources and analytic methods, section six presents our main empirical findings, and the final section discusses the implication of our results for public policy and other attempts to carry out long-term follow-ups of randomized social experiments.

Many theories of crime suggest that people engage in crime because they lack impulse control, future orientation or other non-academic factors (what researchers variously call “non-cognitive” or social-cognitive skills), or because people have poor earnings prospects in the legal labor market (perhaps due to low levels of either academic or non-academic skills) and so view criminal behavior as a superior alternative (Gottfredson and Hirschi 1990; LaGrange and Silverman 1999). These theories imply that the accumulated exposure of young people to neighborhood environments is important in affecting risk of criminal involvement by changing people’s development of academic or non-academic skills.

Neighborhood environments may shape the developmental environments in which children grow up partly by affecting the quality of local public schools, which previous research suggests varies dramatically across areas (Rivkin et al. 2005). Neighborhood social conditions may also affect the developmental environments children experience if for example neighborhood adults or peers generate human capital externalities (Borjas 1995), or if local adults act as role models that change the incentives that young people perceive for investing in human capital (Wilson 1987).

MTO could have effects on risky or criminal behavior mediated through MTO’s impacts on household environments important for child development. Parental unemployment, substance use, poor mental health, exposure to community violence, and inadequate housing may be risk factors for child maltreatment. Each of these risk factors could be affected by MTO. Previous research also suggests that neighborhood social conditions (such as crime and violence) may change the way that parents monitor and supervise their children (Furstenberg et al. 1999).

These “developmental neighborhood effects” hypotheses imply that MTO children who are relatively younger at baseline (and so will experience more exposure to new neighborhood environments at any given follow-up point) should be more affected by MTO moves than those who are older at baseline. This is particularly true if there are developmentally “sensitive” or “critical” periods (Knudsen et al. 2006; Shonkoff and Phillips 2000; Shonkoff et al. 2012). Sensitive periods are hypothesized to be ages in which development of certain skills or developmental processes are particularly susceptible to environmental influences, which in our case is the social environment of the neighborhood, but are not necessarily the only times in which those skills or processes can be modified. Critical periods are thought to be ages at which some skills or developmental processes are shaped, after which they are largely fixed.

Other neighborhood effect theories implicitly argue instead that contemporaneous neighborhood environments should be most important for affecting criminal behavior by young people. For example, urban planners and criminologists have been concerned with the possibility that some building designs contribute to crime, for example, through the construction of enclosed stairwells in public housing buildings that are difficult for local residents to monitor. Neighborhoods may also vary in the willingness of local adults to monitor public space and enforce shared values as in the “collective efficacy” model of Sampsonet al. (1997) (see also Coleman 1988).

It is possible that high-crime neighborhoods might have policing of lower quality or quantity compared with more affluent areas. Whether or not such variation in policing exists depends in part on the degree to which policymakers choose to allocate additional police resources to the highest-crime neighborhoods (Sherman 2002), as well as on the intensity of patrol activities in different areas, the degree to which community members are willing to work with police to solve cases, and how police use their discretion to make arrests. If youth move to neighborhoods with more or more intensive policing, MTO could increase the likelihood of a youth being arrested for any given level of actual criminal activity. Previous research raises the possibility that minorities may be at particularly elevated risk for being arrested, even after controlling for frequency of involvement with criminal behavior and other risk factors such as neighborhood type, family income, and educational history (Huizinga et al. 2007).

A large literature suggests that contemporaneous peer influences should affect decisions about engaging in crime, or what Jencks and Mayer (1990) call “epidemic models,” which emphasize the power of peers to spread behaviors. Such contagion effects can arise from learning criminal behavior from peers, pure preference externalities (individuals enjoy imitating their peers), stigma effects and social norms (the negative signal from criminal behavior declines when more people do them), and physical externalities (for example, higher rates of crime reduce the chances of getting arrested because of congestion effects in law enforcement); see Kleiman (1993), Cook and Goss (1996), Glaeser and Scheinkman (1999), Brock and Durlauf (2001), Manski (2000), and Moffitt (2001). Some epidemic models predict peer influences on youth criminal behavior that vary with the prevalence of peer criminal behavior within a community, potentially leading to nonlinearities in peer effects or “tipping points.”

Although most behavioral models predict that MTO moves should reduce youth involvement with risky or criminal behavior, Jencks and Mayer’s discussion implies that other outcomes are possible. Competition models emphasize the competition between neighbors for scarce resources like grades or jobs. Failure in the competition for pro-social rewards may lead youth to compete instead for anti-social rewards, which could elevate risk for criminal involvement. Relative deprivation models focus on negative psychological impacts from experiencing a decline in one’s relative material or social standing (Luttmer 2005). These theories about the potential adverse effects of moving into a less distressed, disadvantaged neighborhood also seem to emphasize contemporaneous over cumulative or lagged neighborhood conditions experienced by young people.

Kling et al. (2005) discuss possible explanations for the gender differences they observe for MTO’s impacts on criminal offending. Male and female youth might move to different neighborhoods. Minority males might face greater discrimination than females in their new neighborhoods or they might sort into higher risk peer groups. Males might adopt a more confrontation strategy in adapting to their new environments whereas females might turn to adults for support. Lastly, males may be more likely than females to take advantage of their comparative advantage in their new neighborhood to commit property offenses. In their view, the comparative advantage in property offenses is the explanation that seems most likely.

The non-experimental empirical literature reveals mixed results on the importance of these theoretical neighborhood mechanisms in affecting risky and criminal behaviors. Case and Katz (1991) found strong relationships between one’s own risky and delinquent behaviors and that of one’s peers for illegal drug use, alcohol use, and criminal offending in the Boston Youth Survey. However, Esbensen and Huizinga (1990) found that the level of disorganization of the neighborhood was not associated with neighborhood-level prevalence or frequency of drug use. Studies of a sample of young black women in Chicago found some relationship between pregnancy risk and low neighborhood socioeconomic status (Hogan and Kitagawa 1985) and evidence that this risk was related to lower contraceptive use (Hogan et al. 1985). The proportion of managerial workers in a census tract has been shown to be related to teen childbearing (Brooks-Gunn et al. 1993; Crane 1991), but Case and Katz (1991) did not find direct evidence of peer influences on out-of-wedlock childbearing.

The non-experimental research provides stronger support for an association between neighborhood attributes and involvement with crime or violence. An influential non-experimental study on this question is Sampson et al’s (1997) analysis of data from the Project on Human Development in Chicago Neighborhoods (PHDCN). Their analysis found one of the best predictors for involvement in violence is a neighborhood’s degree of informal social control combined with social cohesion and trust—what they term “collective efficacy.”

Collective efficacy is found to have a robust association with violence even after controlling for a rich set of individual-level characteristics, and seems to mediate the effects of other neighborhood attributes such as socioeconomic composition (Sampson and Raudenbush 1999; Morenoff et al. 2001; Sampson et al. 2005). Similar patterns of results have been reported in multiple studies including Hirschfield and Bowers (1997), Warner and Rountree (1997), Bellair (2000), Wikström and Loeber (2000), Beyers et al. (2001), and Simons et al. (2004). Sampson et al (2002) provide an excellent survey of such studies. A more recent observational study drawing on PHDCN data presents suggestive evidence of a non-linear relationship between youth violence involvement and exposure to violent peers, where the effect of exposure to additional violent peers declines at higher levels of peer violence (Zimmerman and Messner 2010).

The MTO experiment was designed to test the impact of moving families living in public housing projects in the most disadvantaged neighborhoods in American cities into neighborhoods with much lower poverty rates using private housing vouchers. Eligibility was limited by design to families living at baseline in public housing units operated by local government housing authorities. In 1994, HUD began randomly assigning eligible low-income families with young children who volunteered to participate in MTO into three different groups:

The experimental group (or low-poverty voucher group) was offered a housing voucher that could only be used in neighborhoods where the poverty rate was 10 % or less according to the 1990 census.³ This group was also provided with counseling to help locate an appropriate unit and neighborhood.

In total, 4,600 families representing about one-quarter of the universe of eligible families in the target public housing projects signed up for MTO between 1994 and 1998 (Goering et al. 1999, table 5). Although all families assigned to the experimental and Section 8 groups were offered housing vouchers, only around 47 % in the experimental group and 63 % in the Section 8 group used the voucher to move. Despite less than complete compliance with the MTO treatment, the random assignment of MTO families into treatment and control groups alleviates concerns about selection effects (see further discussion below). Furthermore, these utilization rates are consistent with rates observed in studies of other housing voucher programs (Olsen 2003; Rubinowitz and Rosenbaum 2000). Some families did not use their voucher because they could not find an affordable unit within the time limits of the program. Finding affordable housing may have been particularly challenging for families in the experimental group because they were restricted to searching in low-poverty census tracts. The tight housing markets of some of the MTO cities during this time period also contributed to the difficulty of finding suitable units.

A baseline survey that HUD administered to all families when they applied for MTO provides baseline characteristics of the adults who were assigned to the three different groups. Averaged across the five MTO study sites, about two-thirds of all the participants were African-American and about one-third were Hispanic. However, in two of the sites, Chicago and Baltimore, the participating families were overwhelmingly African-American, while the other three demonstration sites (Boston, Los Angeles, and New York City) participants were more evenly mixed between African-American and Hispanic.

Concerns about crime and safety play an important role in motivating families to participate in MTO. Around 40 % reported living with someone who had been victimized in the last six months. Three-quarters of the respondents reported a desire to get away from drugs and gangs; half reported they wished to find better schools for their children as their primary or secondary reason for moving.

Table 1 presents the baseline characteristics of the sample of youth that is the focus of this paper—those who were ages 15–25 at the end of 2001 and ages 17–28 as of the end of the follow-up period for this paper, or 10 years after random assignment (n=4,643). As detailed below, these youth were not eligible for the youth survey that was part of the MTO long-term (10–15) evaluation because they were over age 20 as of December 2007—the point at which eligibility for the survey sample was determined. In other published work on the long-term evaluation, this group is known as “grown children”. This is essentially the same cohort studied using data from the interim MTO evaluation (4- to 7–year follow-up) by Kling et al. (2005), although there are a few differences in the two samples. However, we have added youth whose families were randomized in 1998, the last year of MTO recruitment. In addition, we have excluded a small number of youth who were 18 or older at baseline, and we have decided to include youth even if they moved to other jurisdictions at some point after random assignment. As expected, due to the random assignment of families to the treatment and control groups, baseline characteristics of youth generally do not differ by treatment status. An omnibus F test fails to reject the null hypothesis that the full set of baseline characteristics controlled for in our analysis (listed in Appendix Table 3) is the same for youth in the experimental group and the control group (P=0.74) or the Section 8 group and controls (P=0.43).

The distribution of behavioral outcomes is quite different for boys versus girls. At baseline, parents were more likely to report behavioral and emotional issues for boys than for girls. Nearly 20% of boys (compared with some 10% of girls) had recently been suspended or expelled from school. Behavioral/emotional, learning, and physical health problems were all about twice as prevalent among boys as girls. Violent crime arrests were somewhat higher for experimental and Section 8 boys than for controls, but pre-random assignment differences could occur by chance. We also control for pre-random assignment arrests in our analysis, although as mentioned above, there is no overall pattern of pre-randomization differences between the control group and either the experimental or Section 8 group. Because previous MTO studies have found that boys and girls also respond differently to MTO-assisted moves into less distressed neighborhoods (Kling et al. 2005; Kling et al. 2007), we follow previous MTO work and analyze the data separately by gender.

This section discusses the data sources analyzed in the present paper, which come from longitudinal arrest records and in-person parent surveys collected for the long-term MTO evaluation to measure outcomes through 10–15 years after the time of random assignment. Given the randomized experimental design, our analysis methods are straightforward. We begin by presenting “intention to treat” (ITT) estimates, which represent the effects of being offered the chance to move through MTO. Since not all families offered a MTO voucher actually moved through the program, the ITT will understate the effects of actually moving through MTO. Accordingly, we also present estimates that use the randomized treatment group as an instrument for actually moving with an MTO voucher to estimate the effects of moving for those families who actually moved—the so-called “treatment on the treated” (TOT) estimates.

Using data collected through 10–15 years after random assignment, we find that MTO generates large differences in average neighborhood conditions across randomly-assigned groups that shrink over time. We also show that, in the years immediately following random assignment, MTO generates substantial reductions in violent-crime arrests but sizable increases in property-crime arrests, primarily among males. These MTO effects on crime generally seem to attenuate over time as the MTO effect on neighborhood conditions attenuates. We also find that among the youth who are 15–25 at the end of 2001, there is little evidence that those who were relatively younger at baseline benefit more from MTO than those who were older at baseline. Taken together, these findings suggest that what Sampson (2012) calls “situational” neighborhood effects may be relatively more important than “developmental” neighborhood effects.

This paper presents a long-term (10-year) follow-up of the effects of the MTO residential mobility experiment on youth who were ages 15–25 at the end of 2001 (the group studied by Kling et al. (2005) about 4–7 years after random assignment). We find large and statistically significant reductions in violent-crime arrest rates among male youth assigned to the experimental rather than control group, concentrated during the first 4 years following random assignment, and adverse effects on property-crime arrests, which are also concentrated during the first few years after random assignment.

Given the significant effects on Section 8 male property-crime arrests at the beginning and end of the follow-up period, a natural question is why there were no effects in the intervening years. The standard errors around our estimates do not let us rule out the possibility that there were some modest sustained impacts on arrests over time for these youth. Additionally, the experimental-control ITT for property-crime arrests in years 9–10 is not quite statistically significant (p=0.11) but is also large as a fraction of the control mean—about 25 %.

Why do the MTO impacts on arrest rates for male youth in the experimental group – particularly the beneficial effects on of violent-crime arrests —attenuate over time? One candidate explanation for the changes over time in MTO’s effects on arrests among experimental group males is that they are driven by the size of MTO’s effect on contemporaneous neighborhood conditions, and that the attenuation of these effects on arrests over time is due to the attenuation of MTO’s effects on neighborhood environments. Figure 1 shows the pattern implied by the results presented in Table 2 for how MTO’s effect on violent-crime arrests for males changes in response to the effect on neighborhood minority concentration. There appears to be a relationship between the size of the neighborhood “dose” and the size of the arrest “response”, with a pattern suggesting that generally larger reductions in violent-crime arrests occur during periods when the MTO effect on neighborhood conditions (in this case, census tract share minority) is larger.

Another hypothesis that a criminologist might consider stems from the well-known age–crime curve: perhaps this cohort of youth is simply “aging out” of their crime-prone years, so that our study sample is no longer engaged in criminal activity towards the end of our 10-year follow-up period (the average age of the youth in our sample 10 years after random assignment is almost 23). Perhaps over time, there is just no crime to be prevented through changing neighborhoods? Yet this explanation does not square well with the data presented in Table 2, which shows that the control means for violent- and property-crime arrests are higher in the later years of the follow-up period.

A different candidate explanation is that crime rates themselves were changing over the course of the study period, since MTO began enrolling families in 1994—not long after the start of the sizable drop in crime rates observed over the 1990s nationwide (see, for example, Levitt 2004 for a discussion and candidate explanations). However, because MTO was structured as a random assignment experiment, secular changes that affected all places equally should have similar effects on the offending patterns of youth assigned to control and treatment conditions.

Because we rely on administrative records on arrests to MTO youth, rather than directly measure youth criminal behavior, our analysis could be affected if the likelihood that a crime results in arrest varies systematically between more and less disadvantaged neighborhoods. The interim follow-up survey in MTO asked household heads about the likelihood that police respond to 911 calls, with a pattern of responses that suggests police may be more responsive in lower-poverty areas. If the probability of arrest is indeed higher in lower-poverty areas, our analysis would understate any protective MTO effects to prevent crime and overstate any adverse effects of MTO moves on criminal behavior. That is, our analysis may understate the beneficial effects on violent crime and overstate adverse effects on property crime. However, it is not entirely clear why this pattern should change over time, and so it is not clear that differential enforcement can explain the evolution of MTO effects on arrests over time. It could be the case that low-income, minority youth as in MTO learn over time to better “blend in” or interact with law enforcement in low-poverty areas. But this explanation would predict that the beneficial MTO effect in reducing violent-crime arrests in the few years right after random assignment should actually increase rather than decrease (in absolute value) over time.

Perhaps a more plausible explanation for the adverse effect of MTO on property-crime arrests is that there is simply more valuable loot to steal in less racially and economically segregated areas compared with the more disadvantaged communities in which the control group families reside. This hypothesis also provides an explanation for why the MTO effect on property offending declines over time—because the treatment-control difference in neighborhood conditions converges over the 10-year study period. Another possibility is that fade-out represents acclimation to the new neighborhoods. For example, males moving to new neighborhoods may initially act out and steal items, but this behavior may stop once they become accustomed to the neighborhood and form social connections.

More generally, our pattern of findings seems to be more consistent with the relative importance of “situational” neighborhood effects that depend on the environments in which decisions to engage in crime or not are made, rather than to “developmental” neighborhood effects that influence the quality of the developmental environments children experience growing up. The developmental neighborhood hypothesis has the additional testable prediction that MTO youth who are relatively younger at baseline should be more responsive to MTO moves than those older at baseline, because they experience larger neighborhood changes during a more developmentally “plastic” life stage. To test this hypothesis, we interact a linear term for baseline age with treatment assignment among our sample of youth 15–25 as of the end of 2001 and find no pattern of statistical significance (i.e. the effect of MTO on the criminal behavior of younger youth does not differ from the effect on older youth).

The findings described above also fit the pattern of previous studies, including studies from the MTO interim evaluation, where treatment group females fare better (or at least are no worse off) than their control counterparts and males are arrested less for violent crimes but are actually arrested more for property crimes. Kling et al. (2005) examined variation by gender in three candidate explanations when reviewing the gender differences in the interim MTO results: mobility patterns, discrimination, and adaptability. They largely ruled out the first two explanations because neither varied systematically by gender. Our results are consistent: Table 2 shows that (1) the impacts on neighborhood characteristics by gender are quite similar, especially earlier in the post-randomization period when effects on criminal behavior are strongest, and (2) the effects on neighborhood racial composition, while statistically significant, were more modest than the effects on neighborhood economic composition, and even experimental group youth who moved with a voucher lived in high-minority neighborhoods. Kling et al. (2005) find some evidence that MTO youth differ in their adaptability to new neighborhoods, however, and point to a comparative advantage in property offending that affects males more than females due to lower achievement test scores and higher school absence rates, less adult supervision, and more friends who have engaged in risky and delinquent behavior.

Furthermore, the findings presented here are consistent with the idea that neighborhood conditions may have an important influence on the violent criminal behavior of youth in particular, and also with the idea that contemporaneous rather than lagged neighborhood conditions (particularly minority composition), i.e. situation neighborhood effects, may be the most important determinant of the neighborhood’s influence on violent behavior. Our analysis does not isolate the specific mechanisms through which neighborhood conditions might affect youth violence, but the exercise of tracking youth over the long term that we present here begins to narrow down the range of mechanisms that are consistent with the data. Our findings are also consistent with the optimistic view that even the criminal behavior of adolescents who have been exposed to distressed neighborhood conditions for extended periods may be sensitive to changes in the offending environment. The young people growing up in our nation’s distressed urban neighborhoods, even those who have already reached their peak offending ages, appear to be affected in important ways by their current situation.