The broken windows theory of crime suggests that physical disorder in neighborhoods leads to social disorder and eventually serious crime [1
]. In efforts to reduce serious crime, proponents of the theory have developed a broken windows policing strategy, which was made famous by New York City’s “quality-of-life policing” strategy [2
]. Broken windows policing targets low-level misdemeanor crimes to prevent serious crime [4
]. While the effectiveness of the strategy has been debated and its use is controversial (see [6
]), within public housing, an evolution of broken windows policing has made its way into the lives of residents through a process of legal banishment. Banishment policies grant police the authority to formally prohibit individuals from entering public housing properties and arrest them for trespassing if they then violate the ban.
Public housing agencies (PHAs) justify banishment by arguing that it is a strategy for reducing serious crime in public housing. In addition to attempting to stymie social disorder through the issuing of formal bans, this policy grants police the opportunity to more easily control drug possession and potential sales since banned individuals can be arrested for trespassing and subsequently searched if they enter public housing. In this way, banishment serves two purposes for police: it allows them to remove potential criminals and makes it easier to enforce drug laws.
Despite the widespread use of banishment policies (see [7
]) and the evaluation of policing efforts in public housing [8
], an empirical evaluation of the impact of banishment on reducing crime or making drug arrests has not been performed. This study is the first to explore the effect these bans have on crime and drug arrests in public housing. As will be explained below, this strategy, which has been shown to be disproportionately used in disenfranchised communities [17
], empowers the police [7
] and can result in citizens being permanently excluded from spaces even if they have been invited. The result of these policies can have serious social consequences for the banned individuals, their families, and the communities in which it is used. Given the potential social costs, understanding the effectiveness of banishment enforcement in public housing is therefore critical. Thus, the current study adds to the extant literature on broken windows policing broadly, the policing of public housing generally, and banishment in public housing specifically.
More precisely, we extend on the work done by Torres [18
] which investigated the perceived effectiveness of banishment and police in Kings Housing Authority (KHA) and found that public housing residents are more likely to find banishment and police effective if they trusted the police. Notwithstanding the significance of perceptions toward banishment’s effectiveness, we turn our attention here to address whether issuing bans predicts reductions in property and violent crimes in KHA.1
We also explore whether issuing bans predicts increases in drug and trespass arrests. We rely on crime data from 19 communities in one southeastern U.S. city: six public housing communities and 13 surrounding communities. We find that this brand of broken windows policing does work to reduce crime, albeit relatively small reductions and only for property crime. Furthermore, we find that banishment results in an increase in trespass arrests. Both of these findings raise questions about whether or not PHAs and police departments should continue to use banishment. On the one hand, banishment has been shown to modestly reduce property crime. However, it generates a significant increase in trespass arrests, which brings into question its usefulness as a deterrent, increases the number of low level arrests in neighborhoods that are disproportionately composed of people of color, and does not significantly reduce violent crime.
Our analyses are based on a sample of 19 neighborhoods located within a southeastern U.S. city. These neighborhoods include six public housing neighborhoods and 13 non-public housing neighborhoods. The six public housing neighborhoods represent the population of all public housing neighborhoods in the city except three elderly assisted living public housing buildings. The non-public housing neighborhoods were selected based on their proximity to the public housing communities. All non-public housing neighborhoods within a half-mile radius of the public housing communities were used. Data were collected at the neighborhood level over a 12-year period (2001–2012). Banishment policies were introduced to the city in 2004.
This study relies on data comprised of bans (2004–2012), trespass arrests, drug arrests, FBI Part I property and violent crimes, and measures of concentrated disadvantage (2001–2012). All relevant crime data were provided by neighborhood and year and came from the local police department.
Our crime models predict property crime and violent crime. Property crime is measured as the total incidents of reported Part I property crime by neighborhood and year. Similarly, violent crime is the total incidents of reported Part I violent crime by neighborhood and year. We also generated two sets of arrest models that predict drug arrests and trespass arrests. Both arrest variables are measured as the total number of each type of arrest by neighborhood and year. All crime and arrest variables came from the police department overseeing the public housing neighborhoods in this city and were log transformed to reduce positive skewness.
We measured the number of bans issued in public housing neighborhoods by year. Because the formal use of banishment began in 2004, ban data were collected for the years 2004 through 2012. Only bans issued within one of the six public housing neighborhoods chosen for the study were recorded. This city has various public housing neighborhoods, including assisted living developments for the elderly. Bans issued to these properties were excluded from the study, as were bans issued to a now demolished public housing property. This resulted in excluding a maximum of 13 percent of total bans in 2008 and a minimum of 1 percent in 2012. Two of the public housing communities were combined due to the inability to obtain separate socio-demographic variables for each within the 2000 Census and 2008–2012 American Community Survey 5-Year Estimates (ACS), as each survey places both communities under the same block group. This is explained by the fact that the two public housing communities are physically adjacent. For non-public housing neighborhoods, the number of bans was set to zero for all years. Bans for each public housing neighborhood by year are found in Table 1
Table 1. Bans and population by public housing neighborhood by year.
Our full regression models controlled for concentrated disadvantage
, which refers to the geographic concentration of poverty and associated social conditions (see [48
]). Concentrated disadvantage has been found to influence crime in low-income communities (see [46
]). The following neighborhood-level socio-demographic variables were used as indicators of concentrated disadvantage: (1) median family income; (2) percentage of families with income below the poverty line; (3) percentage of population with less than a high school education; (4) percentage of households on public assistance; (5) unemployment rate; (6) percentage of female single parent households; (7) percentage of households with income below $30,000. These data came from the 2000 and 2010 U.S. Census [53
] and the 2008–2012 American Community Survey (ACS) 5-year Estimates [55
]. Since annual data for these variables could not be obtained, linear interpolation was used to generate yearly estimates. Principal component analysis was conducted to generate a component score for concentrated disadvantage
using a single extracted component. Four of the variables were transformed to reduce skewness prior to extraction. The first component explained 84 percent of the joint variance and was the only component with an eigenvalue greater than one. All of the component loadings for the single component were larger than 0.74 with five of the seven loading higher than 0.90.
Ideally, a measure of neighborhood instability should be included as an additional control variable. Neighborhood instability is thought to lead to a neighborhood’s inability to police itself because of high residential turnover. Neighborhoods with more stability therefore should have lower crime rates, while neighborhoods with a more transitory population—more neighborhood change—should have greater crime and disorder because the higher rates of residential turnover disrupt social networks. There is some evidence for the association between neighborhood instability and crime (for example, see [56
]). Typical measures of neighborhood instability such as the proportion of renters/owners and the proportion of vacant homes are problematic with our data because 100 percent of public housing residents are renters, by definition. We therefore did not use a measure of neighborhood instability given the inability to construct an efficient measure.
presents descriptive statistics for the variables used in our models. The within neighborhood minimum and maximum values have been de-meaned (i.e., the group mean is subtracted and the grand mean is added), which is why some of the variables have negative values. We also controlled for the year of the study in our regression models.
To test our hypotheses, we used sets of Arellano–Bond dynamic panel models to predict the crime and arrest variables of interest. In the full crime models, meant to test our first set of hypotheses, we separately predicted property and violent crime as a function of bans issued net of covariates. These models are beneficial when the data has more panels than years, when one or more of the explanatory variables are expected to be endogenous, and when issues of autocorrelation are likely to be present [47
The following equation was used to estimate the full crime models:
where yit">yit represents the dependent variable (property or violent crime) for neighborhood i">i at time t">t, Bit">Bit is the number of bans, Cit">Cit is the concentrated disadvantage, Yt">Yt is the year, Tit">Tit is the number of trespass arrests, Dit">Dit is the number of drug arrests, uit">uit is the error term (composed of the unobserved neighborhood effects and the residual errors such that uit=νi+eit">uit=νi+eit), and the β">β values are the regression coefficients. By taking first differences, the Arellano–Bond estimator eliminates the fixed unobserved neighborhood specific effects along with any endogeneity issues they might potentially introduce. To deal with issues of autocorrelation, the models use a lagged dependent variable (LDV) as well as additional lags of the dependent variable, which act as instruments to eliminate potential endogeneity introduced by the first-differenced LDV. Notice that the ban, trespass arrest, and drug arrest variables have been lagged by one time unit. We are interested in determining whether crime levels are influenced by the number of bans and amount of low-level enforcement from the previous year.
Bans, drug arrests, and trespass arrests have the same goal of reducing crime. We caution that this suggests the potential for multiple treatments at work; however, our analysis allows us to isolate the effect of each type of treatment. Both drug arrests and trespass arrests were used before the start of banishment in public housing. Since bans are set to 0 in public housing from 2001–2003 and 0 for all non-public housing sites, we are able to determine if bans influence crime, once implemented, independent of drug and trespass enforcement. It is necessary here to reiterate the uniqueness of issuing bans as a policing tool. Bans are civil punishments, not criminal punishments that prohibit individuals from returning to the property. This is a more proactive approach to deterrence than arresting individuals for committing a criminal act such as possessing drugs or trespassing. Because all of these policing tactics can potentially influence crime but do so in different fashions, we control for drug and trespass arrests so we can estimate the independent effect of bans on crime. Unlike the majority of program evaluative studies, which assume a dichotomous treatment (a ban law is either present or absent for each neighborhood in a given year), our regression models treat bans as a continuous measure that enhances precision and provides a better look at the impact of bans. If two different public housing neighborhoods for which the ban law is in effect enforce and issue bans differently, our models will capture this.
We tested Hypothesis 2A by predicting trespass arrests as a function of lagged ban variables (the equation shows only the first difference of bans as a predictor, but second, third, and fourth differences were tested as well in separate models). The following equation for the full trespass arrest model was used:
Similarly, we tested Hypothesis 2B by predicting drug arrests as a function of lagged ban variables. The following equation for the full drug arrest model was used, which included lagged trespass arrest variables to determine if trespass arrests potentially mediate a relationship between bans and drug arrests:
It should be noted that only two additional lags of the dependent variable were used to create instruments to avoid over-identifying the models. Though Arellano–Bond models typically use all possible lags of the dependent variable to ensure that autocorrelation is removed, tests for autocorrelation show that any autocorrelation has been sufficiently removed from our models. Also, the variance inflation factors for the variables used in our models all had values lower than three, indicating that multi-collinearity was not an issue.
We begin by looking at the trend in bans (see Figure 2
). As discussed above, bans were formally introduced in 2004 to public housing communities, but as we can see from the figure, their usage by officers varied in the decade following their introduction. The use of bans generally rose in public housing after being formally introduced in 2004, peaking in 2010.
looks at property crimes over time in public and non-public housing communities. Though it is generally lower in public housing, it appears to have decreased in public housing in the period after 2004, especially when compared to non-public housing communities. To test if this apparent effect is significantly due to bans, we used three separate regression models presented in Table 3
, all three of which are nested in the model presented as Equation (1) above.
Table 3. Arellano–Bond dynamic panel-data models predicting property crime.
As we can see, the number of bans issued in a given year significantly reduces property crime, even after the covariates are added. This finding supports Hypothesis 1A (additional support for H1A using the synthetic control method for counterfactual analysis can be found in Appendix A
). Notice, however, that doubling the number of bans issued in a given year only reduces the number of property crimes by approximately five percent in the following year (2−0.076=0.95">2−0.076=0.95
). Surprisingly, we do not find an effect of disadvantage or drug and trespass enforcement on property crime independent of the other effects. Though tests for autocorrelation show that second order and larger autocorrelated errors have been removed, it should be noted that when placebo controls were added in the form of leads of the ban variable, a significant lead effect was discovered. Models including up to four leads found that a two-year lead in bans significantly predicts a decrease in property crime. This calls into question the causal claims that can be made regarding bans and property crime. Though we find that significant independent negative correlation exists between number of bans issued and subsequent property crime with the Arellano–Bond models, we cannot claim that bans cause a reduction in property crime and not the other way around. That being said, our synthetic control models in Appendix A
demonstrate that a divergence in property crime between public housing neighborhoods and a synthetic control case does occur in the expected direction after the institution of bans, supporting our causal claim from H1A.
When we turn our attention to violent crime (see Figure 4
), there does not appear to be an obvious trend, inside or outside of public housing, despite the general decrease in violent crime experienced by the nation as a whole during this time. Using the Arellano–Bond models to predict violent crime, we find that the number of bans in a given year does not significantly predict violent crime in the following year (or two, three, or four years later) in any of our models (see Table 4
). Given this result, we do not find support for Hypothesis 1B. As it turned out, none of the variables significantly predicted violent crime in our models.
Table 4. Arellano–Bond dynamic panel-data models predicting violent crime.
To test Hypothesis 2A, we examine trespass arrests over time. From Figure 5
we can see that trespass arrests appear to grow during the years following the institution of the ban legislation in public housing neighborhoods. The trespass arrest regression models in Table 5
demonstrate that though trespass arrests are not significantly correlated with bans in the previous year, they are significantly influenced by the number of bans two years prior, even when we account for a general independent trend of increasing trespass arrests (this relationship does not exist for other lagged ban variables: third-differenced, fourth-differenced, etc., and holds when placebo controls are added in the form of leads; no significant placebo controls were found in models including up to four leads for the ban variable). Notice that in the third model, which predicts trespass arrests using only the LDV and second differenced bans as explanatory variables, the effect of lagged bans is stronger than in the final model. The coefficient for bans is being inflated by a general trend of trespass arrests increasing over time (both in public and in non-public housing, though the trend is stronger in public housing). However, when we control for this trend, Model 4 shows that bans still have a positive significant (p
< 0.10, two-tail) impact on trespass arrests. These models provide support for Hypothesis 2A (additional support can be found in Appendix A
Table 5. Arellano–Bond dynamic panel-data models predicting trespass arrests.
Finally, we examine drug arrests in Figure 6
and Table 6
. Though the variability in drug arrests appears to be higher in non-public housing, according to Figure 6
, there does not appear to be much of a difference between the trends across housing types, and there does not appear to be a consistent change in public housing after the institution of ban legislation. However, when we examine the Arellano–Bond regression models (see Table 6
), we find that just like for trespass arrests, drug arrests are significantly influenced by the bans issued two years prior. In Model 4, which predicts drug arrests using only an LDV and second-differenced bans as explanatory variables, it appears that lagged bans do not influence drug arrests. However, this is because a suppression effect is present due to a general decrease in drug arrests over the period in these neighborhoods. Once we control for this time trend (Models 5 and 6), we see that drug arrests are significantly increased by the bans issued two years prior. Interestingly, lagged trespass arrests do not predict drug arrests independent of lagged bans. Various combinations of lagged trespass variables were included independently and together. Model 6 shows the effects of first and second-differenced trespass arrests on drug arrests in the same model, but the coefficients and standard errors are nearly identical when only one or the other is included by itself. Just like in the property crime models, we need to add a word of caution. Though tests for autocorrelation show that second order and larger autocorrelated errors have been removed, when placebo controls were added in the form of leads of the ban variable, a significant lead effect was discovered. Models including up to four leads found that a one-year lead in bans significantly predicts a decrease in drug arrests. This calls into question the findings regarding a causal relationship between bans and drug arrests given the contradiction in direction of the relationship between the significant lag and significant lead of bans. Additionally, our synthetic control models in Appendix A
do not find a consistent divergence in drug arrests between public housing neighborhoods and a synthetic control case after the institution of bans. Because of these issues, we cannot conclude with confidence that there is a causal connection between bans and drug arrests in public housing.
Our regression models indicate that bans negatively predict property crime. In the context of other broken windows policing strategies, such a finding adds to the research showing that policing disorder can reduce crime [45
]. However, we also found that bans did not predict decreases in violent crime or drug arrests. In fact, bans appear to independently increase drug arrests in subsequent years, but we remain wary of these findings given the significance of a lead placebo control and the lack of findings using a synthetic control (see Appendix A
). Despite support for bans predicting reductions in property crime, the magnitude of such reductions appear to be relatively small. Our models found that police must double the amount of bans issued to see a return of only a 5% reduction in property crime. This finding is consistent with other research such as Braga and colleagues’ [45
] meta-analysis of 30 broken windows strategies, which found that such strategies tend to have modest returns.
Under deterrence and opportunity theories, reductions in property crime would not be surprising given the argument concerning how property offenders take into account the threat of sanctions [59
]. If property offenders wish to offend in public housing, being banned would limit the opportunity to commit such offenses should offenders feel as though there is an increased likelihood of being caught on the property and arrested for trespassing. Still, reductions in property crime could be a function of the incarceration of a handful of offenders who committed the disproportionate share of property offenses in public housing. This would be supported by research that suggests that a small fraction of the population accounts for a very high percentage of crime [62
]. Beyond incarceration, should a property offender be a resident of public housing, there would be grounds for an immediate eviction, which would remove the offender from public housing in the same manner as incarceration would. Though the significance of a placebo control (number of bans at time t+1) undermines claims to causal direction, we remain confident that a causal relationship between bans and property crime exists, especially given the supporting evidence in Appendix A
This study did not find support for bans predicting reductions in violent crime. There are several plausible reasons for this. First, much violent crime is spontaneous and “expressive” rather than “instrumental” (see [65
]). As such, one may be less likely to be deterred from violent crime by the threat of trespass arrests. In addition, assuming these neighborhoods are similar to other high-crime neighborhoods, much of the violence in these neighborhoods is likely a result of a very small percentage of residents. For example, studies have found that as little as 0.3 percent of a city’s population can account for over 60 percent of the city’s homicides (for a review, see [65
]). More specifically, one study on homicides in Los Angeles public housing communities found that residents contributed more to the violence in public housing than non-residents [42
]. If a few residents are contributing a significant proportion of the violence, banning outsiders might not affect violent crime. It is only when these individuals are removed from the network (either through incarceration, aging-out, or death) that violence will decrease. This insight results in the underlying logic of focused deterrence strategies. Focused deterrence strategies attempt to locate chronic violent offenders and maximize the risks of offending by providing them with incentives and disincentives [68
]. The violent crime-reduction benefits of this tactic have been well established (see [70
]). Not only is it possible to reduce violent crime under this approach, but police legitimacy may increase as well, as police use more procedural justice tactics in focused deterrence strategies [74
Given the ability of bans to aid in generating drug arrests, we hypothesized that bans would increase drug arrests as it becomes easier for officers to investigate individuals on public housing property, even without probable cause for drug possession or distribution. We found mixed support for this and cannot conclude with confidence that a causal relationship between bans and drug arrests exists. While there is evidence that bans increase drug arrests in subsequent years, the fact that a two-year lead of bans is also statistically significant in our model raises doubts about the true relationship between bans and drug arrests.
Still, the results indicating that bans can lead to an increase in trespass arrests poses concern. We find that an increase in bans that leads to a 5 percent reduction in property crime the following year corresponds to an 8 percent increase in trespass arrests in two years, even though trespass arrests do not appear to reduce either property or violent crime independently. Therefore, increasing trespass arrests appear to be a necessary byproduct of ban legislation. Additionally, the high level of trespass arrests that emerge post-legislation in public housing may challenge any claims that banishment acts as a deterrent. For a policy that is intended to keep banned individuals away, the message is quite clear that many come back to public housing, whether it is to offend or not, and are arrested for trespassing. Ultimately, PHAs, police departments, and residents will have to decide whether the returns are worth the potential legal and social costs. We certainly should expect that the social consequences are most felt by banned individuals and those they know within public housing; however, these consequences should not be ignored for a number of reasons. Socially, it is well documented that banishment can disrupt families [75
]. For example, Torres [18
] found that 40 percent of public housing households know at least one friend or family member that has been arrested for trespassing. Furthermore, processing trespassing offenses can clog an already over-burdened criminal justice system. In addition, court cases dealing with banishment in public housing involve disputing the legality of banishment when it is used on those with intent to see family (see [21
Moreover, the findings of this study need to be understood in the context of who resides in these public housing communities. African-Americans make up over 97 percent of the public housing population in this study [54
]. Therefore, in this southern city, communities of color are disproportionately affected by ban policies. One clear consequence of these policies is an increase in trespass arrests. It follows that policies like banishment, that operate in communities disproportionately comprised of racial and ethnic minorities, contribute to the persistent racial disparities in the criminal justice system, including imprisonment (see [38
]). Thus, our findings that banishment produces only meager benefits in terms of reductions in property crimes while generating trespass and drug arrests must be considered in light of the work of Fagan and colleagues [17
] that found racially selective enforcement
of banishment in New York City public housing. Still, despite the already tense relationship between police and many disadvantaged communities of color, there has been evidence that even in predominantly African-American public housing communities using banishment, residents can find the police to be effective [18
]. Ultimately, future studies should consider whether banishment builds or hinders collective efficacy and whether it decreases or increases fear of crime.
We should acknowledge some of the limitations of the current study. First, we want to emphasize that this study involves a limited number of neighborhoods from a single city and therefore suffers from lack of power and is sensitive to noise. We attempted to increase the power by using dynamic panel models that rely on multiple differences and by treating the stimulus (ban legislation) as a continuous variable that varies dramatically within the treatment cases (public housing neighborhoods) from panel to panel. Nevertheless, we are relying on repeated measures of a panel consisting of data from only 19 neighborhoods, and we fully recognize this limitation. Yet, maybe even surprisingly given the small sample, we find significant effects that support two of our four hypotheses. In addition, in these cases, several different analytic strategies—albeit each with their own sets of problems and limitations—produce consistent findings. Therefore, while we recognize the small sample size to be a serious limitation, we are confident these data tell an interesting and consistent story, especially with respect to the influence of bans on trespass offenses and property crimes.
Second, we did not control for spatial lag whereby contiguous areas influence adjacent areas’ levels of crime and arrests (see [46
]). Spatial lags could be used to determine if bans displace crime. However, under the context of public housing, this may not be important; the goal of banishment is to keep crime out of public housing, so if crime increases in non-public housing communities as a result of banishment, it is of no concern to PHAs. However, while public housing officials may not care if banishment displaces crime, police departments do. Knowing such information may be useful in developing strategies for dealing with displacement. With that, this study could merely offer speculative support of any displacement effects. In looking at Figure 3
, it appears that non-public housing neighborhoods experienced a period of increased property crime following the start of banishment. However, the average amount of property crime experienced in non-public housing neighborhoods after banishment began is not clearly above the average amount of property crime experienced by non-public housing neighborhoods before banishment began. Further, while we might expect that this displacement could vary by crime types (i.e., robbery versus aggravated assaults), we looked at additional plots (not shown) and found similar results. Thus, there were no consistent patterns of heightened levels crime in non-public housing neighborhoods following the implementation of banishment above what these neighborhoods experienced before banishment was implemented. While future studies will need to address displacement explicitly, these descriptive results suggest that banishment does not displace crime in the long term. It is possible that banishment is ineffective at totally displacing the criminally active who have ties to the public-housing community; thus, there may be some displacement, but crime is not totally displaced (see [84
]). Again, we found definitive evidence that bans lead to increases in trespass arrests, which implies that a number of people are not deterred by the ban itself and return to public housing. Thus, there may be a number of offenders who are tied to the public-housing community and not willing to offend elsewhere. The literature suggests this situation would result in a lack of displacement because of the inability of potential offenders to seek alternative opportunities (see [85
]) or their preference for committing offenses close to their home or previous home [88
], which in this case would be public housing.
Third, we did not use calls-for-service, police-initiated or citizen-initiated, which could help determine both the proactivity of police officers and their visibility in the community. In a study of the consequences of assigned beats, Kane [92
] found that officers on a permanent beat increase police-initiated calls-for-service. Since the studied communities have strong community policing components and community policing requires officers be accountable to their assigned beats, one would expect the studied communities to have more proactive officers and more police-initiated calls for service. Citizen-initiated calls-for-service may also be higher in public housing if residents know community police officers are likely to respond, therefore increasing police presence in public housing communities only. Still there is no reason to suspect that police visibility dramatically influenced crime levels in these neighborhoods. The neighborhoods had community policing initiatives implemented in them for years prior to enacting the banishment policy, and permanently assigned officers routinely made foot patrols in the neighborhoods. The frequency of the patrols did not increase after the banishment policy was enacted; however, the police now had a new strategy to pursue when trying to prevent crime. Finally, while PHAs may be more concerned with long-term reductions in crime that come from banishment, building models with monthly data would help solve the endogeneity issues from aggregate, within-year models and help determine the short-term effects of banishment.
Despite our limitations, this is an important first step in understanding the logic and merits of banishment in public housing. Of importance for the sake of this test of broken windows theory is that it utilized variables capturing the context of local conditions. In the case of banishment, it calls forth a civil punishment, bans, that are unique to the policy and to the site. Attempts to address crime reduction strategies where public housing communities are included must account for differences in how public housing communities are policed compared to how non-public housing communities are policed. The use of bans in this study is something exclusive to public housing, and this can only be explained by banishment.