As noted in Chapter 1, proactive policing developed as part of an important set of innovations in American policing, growing out of concerns in the late 20th century that the police were not achieving crime prevention goals through standard approaches. Many of the proactive policing strategies that are the focus of this report began with the primary goal of doing something about problems of crime and disorder. Even approaches that included other key aims, such as community-based policing, shared as an important concern the solving of community problems such as crime. In this chapter, we turn to the crime and disorder control impacts of proactive policing strategies. The chapter begins by reviewing the mechanisms through which these strategies are seen to affect crime and other problems. It then discusses each of the four general approaches to prevention described in Chapter 2 and reviews the evidence regarding the specific proactive policing strategies that fall under each approach. Research on the relationship between proactive policing and crime is substantially more developed than the other outcomes addressed by the committee. In light of that, we discuss a selection of highly influential research findings in detail and summarize the other key literature. Finally, the chapter lays out the committee’s key conclusions about these findings and the strength of the evidence for crime prevention outcomes.
The diverse array of programs that are included under the “proactive policing” rubric all seek to harness one or more crime-prevention mecha-
nisms. We review below three basic mechanisms: reduction in criminal opportunities, deterrence, and increases in perceived legitimacy of the law and law enforcement.
The environment for potential offenders may be viewed as consisting of an array of criminal opportunities, some enduring (a gas station that could be robbed) and some transitory (a heated argument in a bar). Each opportunity is characterized from the potential offenders’ perspective in terms of the effort, potential reward, and likelihood of apprehension and punishment (Clarke, 1980; Cook, 1979, 1986; Clarke and Cornish, 1985; Nagin, 2013; Nagin, Solow, and Lum, 2015). Problem-solving interventions often focus on attending to these opportunities (or potential crimes) to stop offending before it occurs. At the most basic level, some proactive programs seek to limit criminal opportunities, such as when police assist in making the case for closing a nightclub that tends to have a high rate of violence or when officers are involved in negotiating gang conflicts before the shooting starts. Other proactive programs address crime opportunities directly by “hardening” them, or increasing the cost and effort it would take for an offender to take advantage of a potential target. Such actions might include problem-solving activities by the police, including using situational crime-prevention measures (Clarke, 1997; Cornish and Clarke, 2003) or crime prevention through environment design (Jeffrey, 1971; Newman, 1972). For example, the police can encourage residents to use locks, doors, gates, guards, or cameras. The police can also work with businesses to make potential criminal opportunities more visible to guardians (e.g., removing obstructions that block police view of an alley or the interior of a neighborhood store). The police can also proactively try to reduce the potential for criminal opportunities to emerge by adjusting the routines of individuals so that potential offenders and victims do not meet (or at least do not meet without the presence of a guardian). For example, the police might request that schools release children at different times to reduce opportunities for bullying or fights. This type of opportunity-reduction strategy arises from routine activity and crime-pattern theories (see Cohen and Felson, 1979; Brantingham and Brantingham, 1993, respectively).
In addition to removing or hardening opportunities for crime, police may proactively try to prevent crime by changing an offender’s risk perception of being apprehended if the offender takes advantage of a crime opportunity. For example, police agencies may choose to proactively increase foot patrol in a crime hot spot in an effort to reduce the rate of vandalism, car theft or break-ins, burglaries, robberies, assaults, or other crimes. The heightened police presence and visibility aims to increase an offender’s perception that he may be apprehended if he takes advantage of crime opportunities at that hot spot. Although individual offenders at a hot spot may vary in their perceived risk of apprehension (and that perception may
also vary for different types of crimes, times, locations, or situations), hot spots policing is believed to alter offenders’ average perceived risk of apprehension, resulting in fewer offenders exploiting opportunities at that hot spot and lowering the crime rate at that location.
This adjustment in a would-be offender’s perceived risk of detection or apprehension is hypothesized to occur through the prevention mechanism of deterrence (Nagin, 2013). The crime reduction value of deterrence is influenced not only by the perceived risk of apprehension (a cost), but also relatedly from a rational calculation of a multitude of costs and benefits associated with that criminal opportunity (see Clarke, 1997; Clarke and Cornish, 1985). An offender’s calculation may be constrained by many factors (intoxication, lack of available information, cognitive deficits, etc.) that are specific to the offender. As a result, the outcome of proactive policing deterrence efforts may be partially stochastic. But in terms of aggregate criminal behavior, deterrence is hypothesized to occur when offenders perceive their risk of apprehension to be high and the perceived benefits do not outweigh those risks.
Deterrence is the primary prevention mechanism in the logic models underlying the place-based and person-focused approaches to proactive policing.1 In hot spots policing, for example, deterrence is created by increasing police presence in places with high levels of concentrated opportunities or routines for criminal offending, thus conveying an increased sense of apprehension and discouraging offenders from taking advantage of those opportunities. Or police may increase the number of pedestrian or traffic stops on a street with high levels of gun violence. Police officers often exercise discretion and do not take enforcement actions against all illegal activity. However, a decrease in discretion with a concomitant increase in lawful stops supported by reasonable suspicion can have a corollary benefit of increasing a would-be offender’s perception that she might be stopped and possibly searched for a weapon (as well as apprehended for carrying the weapon), thus deterring her from carrying that weapon (and, in turn, using that weapon in a crime). In focused deterrence policing, a strategy for the person-focused approach, authorities make direct contact with potential high-risk offenders in an attempt to transform a vague and generalized threat of arrest into an explicit, personalized, and highly salient warning that arrest is imminent if the individuals persist in offending. Other examples of deterrence may be less direct, as we will discuss below.
1Chapter 2 defines the four approaches identified by the committee and discusses typical proactive policing strategies that focus on each approach. Table 2-1 summarizes the committee’s conceptual framework of broad approaches and the strategies for them. The logic model that informs an approach is summarized in that table and discussed in more detail in the section of Chapter 2 for that proactive policing approach.
Aside from deterrence (and in some cases related to deterrence), community-based policing activities are believed to prevent crime not necessarily because they increase the perceived risk of apprehension among potential offenders (although they could) but because they help to increase social and informal control through collective efficacy and increased guardianship (i.e., a community’s or citizens’ willingness to step in to control the behavior of others in the community) (see Sampson, 2011). Some mechanisms typical of the community-based approach attempt to reduce citizen fear and uncertainty and stop citizen withdrawal from aspects of community life that may create informal social control (see Skogan, 1988). Other proponents for a community-based approach have hypothesized that police can prevent future offending by increasing community members’ perceptions of the legitimacy of the law and legal authorities such as the police and the courts. Tyler (2006), for example, hypothesized that the use of procedural justice during officer and citizen exchanges (i.e., how officers treat and interact with an individual) will increase citizens’ compliance with the law in the future.
As discussed in Chapter 2, the police engage in many proactive crime prevention practices that are grounded in these prevention mechanisms. We now turn to a review of the scientific evidence for these interventions and close with a critical assessment of this body of evidence. Note that deterrence mechanisms, as well as related mechanisms that make criminal opportunities less attractive, have the advantage that they do not necessarily entail the imposition of additional punishment, such as arrest or prosecution. Further, if potential offenders perceive a higher risk of arrest, greater potential for detection and disapproval by other community members, or the reduction and availability of opportunities (and rewards) for crime, then both arrests and crime may actually decrease (Nagin, 2013).
Emerging theoretical paradigms and empirical findings on the concentration of crime and disorder at small “hot spot” locations (see Brantingham and Brantingham, 1982, 1984; Sherman, Buerger, and Gartin, 1989) led Sherman and Weisburd (1995) to explore the practical implications of police proactively targeting crime hot spots with preventive patrol. With cooperation from the Minneapolis Police Department they developed a large experimental field study to challenge the conclusions of the well-known Kansas City Preventive Patrol Experiment (Kelling et al., 1974) that varying the levels of police patrol at places has little value in preventing or controlling crime. They also sought to show that proactively focusing
police efforts on crime hot spots presented a new and promising approach for preventing crime.
The Minneapolis field study addressed two limitations of the earlier Kansas City experiment. The design of the earlier experiment, which involved just 15 patrol beats, had limited the statistical power of the results. A second limitation was that the treatment condition was diffused across relatively large areas—entire police patrol beats—which meant that the level of treatment intervention applied at hot spots within these beats may have been too diluted to generate the hypothesized deterrent effect. In the Minneapolis redesign, the researchers first analyzed the addresses of calls for police service and then set appropriate boundaries, based on the researchers’ observations, to define “microgeographical locations” where service calls clustered. Each of the resulting 110 crime hot spots was considerably smaller than a patrol beat (refer to Box 2-1 in Chapter 2 for the definition of hot spot areas). The 110 hot spots were grouped into five statistical blocks based on natural cutting points within the distribution of “hard crime” calls for service frequencies. The within-block randomization procedure created two equal groups of 55 hot spots in the treatment group and 55 hot spots in the control group. Changes in the number of calls for service between the treatment year and a baseline year were calculated for each hot spot, then the statistical differences in the year-to-year changes were compared between the set of hot spots in the treatment condition and the set of control hot spots.
Based on the observations of trained researchers, the treatment hot spots received two to three times as much police patrol presence when compared to the control hot spots. The study authors noted that there was some breakdown in the treatment applied during summer months due to officer vacations and peak calls for service to the police department. They therefore conducted a sensitivity analysis with varying comparison dates to account for the lack of dosage during the summer months. Using a series of analysis-of-variance models, the authors reported that the police patrol treatment generated between 6 percent and 13 percent reductions in calls for service in the treatment hot spots relative to calls for service in control hot spots. These reduction percentages passed tests for statistical significance. Analyses of systematic social observation data on disorderly behavior in both treatment and control hot spots, collected by trained researchers during the treatment year, found that observed disorder was only half as prevalent in treatment hot spots relative to control hot spots (Koper, 1995).
The Minneapolis Hot Spots Patrol Experiment established the potential importance of crime hot spots for policing (see below for confirmatory evidence in later studies), and it challenged the conventional logic that had assumed that police patrol could not be effective. However, the question remained whether concentrating on such places would merely shift crime
from place to place (e.g., see Reppetto, 1976). The first hot spots study to examine the problem of displacement directly was the Jersey City Drug Market Analysis Experiment (Weisburd and Green, 1995). The study identified 56 drug hot spots of varying sizes, ranging from a group of addresses to a group of street segments evidencing similar drug activities. These were then randomly allocated either to a treatment group that received a systematic problem-oriented response to drug crime or to a control group that received the normal reactive responses typical of drug enforcement at the time. The randomized controlled trial compared calls for service at the treatment and control drug hot spots during a 7-month pre-intervention baseline period to calls for service during a 7-month post-intervention assessment period. The analysis revealed statistically significant differences in the pre- and post-intervention levels of calls for service between the treatment and control groups; in treatment drug markets, calls for service for disorder increased 8 percent, whereas calls for service in the control drug markets increased 20 percent.
The research team also used a randomized design method to compare calls for service over the same experimental periods at the two-block buffer zones surrounding the treatment and control drug hot spots. The analysis revealed that for public morals and narcotics calls, the level of calls in the buffer catchment areas for the experimental sites decreased, compared with the level of calls in buffer catchment areas for control sites, and the decrease was statistically significant. Calls regarding public morals declined by 34 percent in experimental catchment areas and increased by 3 percent in catchment areas for control sites. For narcotics, calls in the experimental site catchment areas declined by 12 percent while in control site catchment areas the level of calls for narcotics increased by 57 percent. To assess drug market activity in the area surrounding each treatment or control hot spot, the Jersey City Drug Market Analysis Experiment research team replicated the initial drug market identification process to identify drug markets in the area surrounding each hot spot in the original set. They estimated that drug market activity was half as likely to occur in areas surrounding treatment-condition hot spots as in areas surrounding the control condition hot spots.
The Police Foundation and the Jersey City Police Department subsequently collaborated on a controlled study to determine whether proactive policing targeted at two high-activity crime hot spots would result in immediate spatial displacement of crime incidents to areas surrounding the targeted location or would instead lead to diffusion of crime-control benefits into surrounding areas (Weisburd et al., 2006b). The study used crime mapping and database technologies, supplemented with observations from police officers and researchers, to identify two hot spots for the treatment condition: one location with active street prostitution and another with an active street-level drug market. To measure possible crime-displacement
or benefit-diffusion effects associated with the proactive policing in these targeted hot spots, the researchers demarcated one- and two-block buffer zones around the hot spots as “catchment areas.” The treatment interventions at the targeted hot spots comprised mostly traditional enforcement tactics (including police crackdowns), along with some situational responses.
The outcomes measured in this experiment were prostitution and drug events as observed by trained members of the research team during 20-minute observation periods in the targeted hot spot and its two catchment areas. More than 6,000 such observation periods were compiled over the course of the study. For the prostitution hot spot and its catchment areas, the research team used a quasi-experimental design in which trends in observed prostitution events were analyzed for a 9-month period and then adjusted for citywide disorder call trends. For the drug-market hot spot and its catchment areas, the quasi-experimental design involved analysis of trends in observed drug-behavior events for a 9-month period, but these trends were adjusted for citywide drug call trends. Pre-test versus post-test changes in the hot spots and catchment areas were evaluated using difference-of-means tests, after the trends in observed events had been adjusted for the citywide trend in the relevant call category.
For the prostitution hot spot, the analysis found a statistically significant 45 percent reduction in observed prostitution events at the location targeted for proactive policing, a statistically significant 61 percent reduction in such events in catchment area 1 (the one-block buffer zone), and a statistically significant 64 percent reduction in catchment area 2. For the drug-crime hot spot location, the analysis found a statistically significant 58 percent reduction in observed drug behavior within the hot spot, a 33 percent reduction (statistically not significant) in catchment area 1, and a statistically significant 64 percent reduction in catchment area 2. Consistent with these findings, ethnographic research in the neighborhoods and interviews with arrested offenders suggested that the intensified policing in the hot spot did not simply displace potential offenders into surrounding areas. Displacement did not occur, this ancillary research suggested, because the diminished opportunities and increased risks associated with moving were judged by potential offenders to exceed potential gains from moving their criminal behavior to areas immediately adjacent to the hot spot location.
A number of reviews of hot spots policing evaluations have consistently documented that this strategy has reduced crime in hot spots without displacing crime incidence to other locations. In fact, many of the evaluations reported a diffusion of crime-control benefits from targeted areas to the proximate areas (see, e.g., Sherman and Eck, 2002; Weisburd and Eck, 2004). Relative to other crime-prevention programs oriented toward intervening at larger geographic aggregations, such as neighborhoods and cities,
rigorous evaluations of hot spots policing program are facilitated by the relative ease through which an adequate number of specific hot spot locations can be randomized to treatment and control conditions. In the 2004 report Fairness and Effectiveness in Policing: The Evidence, a National Research Council (NRC) study committee was unambiguous in its conclusions regarding the effectiveness and importance of hot spots policing, concluding that “studies that focused police resources on crime hot spots provide the strongest collective evidence of police effectiveness that is now available” (National Research Council, 2004, p. 250).
An ongoing, systematic review of hot spots policing studies, conducted under the auspices of the Campbell Collaboration, provides a detailed analysis and summation of the research results on how this strategy affects crime. The most recent report from this Campbell review covered results from 19 rigorous studies involving 25 evaluations of hot spots policing interventions (Braga, Papachristos, and Hureau, 2014). Of the 19 studies reviewed, 10 used quasi-experimental research designs to evaluate the effects of hot spots policing, and 9 were randomized controlled trials. A majority of the 25 evaluations concluded that the hot spots policing practices studied had generated statistically significant crime control benefits in the treatment areas, compared to control areas. Twenty of the 25 evaluations (80%) reported substantial gains in crime control that were associated with the hot spots intervention evaluated.
This Campbell meta-analysis was able to calculate effect sizes for just 20 main effects tests and 13 displacement and diffusion tests, due to limited information in the original research reports. For the main effect sizes, the meta-analysis calculated a moderate and statistically significant positive overall mean effect. Nine of the 13 displacement/diffusion tests reported effect sizes that favored benefit-diffusion effects over crime-displacement effects. The displacement/diffusion meta-analysis suggests a small but statistically significant overall “diffusion of crime control benefits effect” (Clarke and Weisburd, 1994) generated by the hot spots policing strategies. However, all but one of the crime-displacement and benefit-diffusion tests were limited to examining spatial displacement and diffusion effects that were proximal to the targeted area in space and time. That is, they evaluated whether the more intensive policing in the targeted hot spots was associated with an increase or decrease in crime incidents occurring in the immediately adjacent area during the test period. (Only the Jersey City Drug Market Analysis Experiment examined whether offenders displaced to distal locations beyond areas immediately surrounding the study hot spots.)
An important point about hot spots policing programs that have been evaluated is that the policing practices used in the targeted crime hot spots can vary considerably. These strategies and tactics can include practices typical of a problem-oriented policing strategy and practices typical of zero
tolerance policing such as more frequent arrests for misdemeanors, as well as increased patrol, focused drug enforcement, pedestrian and traffic stops, increased gun searches and seizures, and the use of surveillance technologies (e.g., license plate readers). The Campbell review categorized these varied programs into two different strategies (consistent with the conceptual framework developed in Chapter 2 and summarized in Table 2-1) to control crime in hots spots (Braga, Papachristos, and Hureau, 2014). Programs more typical of a problem-oriented policing strategy involved police-led efforts to change the underlying conditions at hot spots that are perceived to be factors contributing to recurring crime problems (Goldstein, 1990). Consistent with this strategy (as described in Chapter 2 of this report), in these programs the police are not the sole implementers of the selected proactive practice. Instead, city services, businesses, and other stakeholders may partner with the police to address the conditions targeted in the hot spot. The second strategy identified by the Campbell review as characteristic of hot spots policing interventions relied on increasing traditional policing activities in the targeted hot spots, with the intention of preventing crime through general deterrence and increased risk of apprehension.
The meta-analysis included in the Campbell review used these two category types as an effect-size moderator to compare the evaluated programs. Of the 20 tests for main effects size, the review’s authors characterized 10 as evaluating problem-oriented practices applied to hot spots policing and 10 as evaluating intensified traditional policing tactics in the targeted hot spots. Their analysis found that the programs applying problem-oriented policing practices had an overall mean effect size (average effect size across all 10 studies) that was twice the overall mean effect size for the 10 programs that applied increased traditional policing practices.
Hot spots policing has been criticized for having only a short-term impact (Rosenbaum, 2006). As is the case for other proactive policing strategies reviewed below, little is known about the long-term impacts of this strategy. At the same time, if the mechanism for crime control is the visible presence of police (see Nagin, 2013), then the main gains expected would be short-term and police should expect to continue to manage such places in the long term. This was confirmed in a reanalysis of the Philadelphia Foot Patrol Experiment. During the initial experiment, teams of four foot patrol officers, concentrated in 60 violent crime hot spots of Philadelphia, Pennsylvania, were able to reduce violent crime by 23 percent over a 3-month period, compared to equivalent control locations (Ratcliffe et al., 2011). Subsequently Sorg and colleagues (2013) found that the deterrent effect identified during the experiment dissipated rapidly; differences in violent crime between control and experimental areas were no longer present within a short time after the experiment finished. More long-term gains might be expected in the case of problem-oriented hot spots interventions,
which seek to solve underlying problems, or in cases where a hot spots intervention was maintained over a long period of time. But beyond the Philadelphia Foot Patrol Experiment, little evidence exists in the research literature regarding these questions.
Another question for which solid empirical studies are lacking is whether hot spots policing will produce areawide or jurisdictional impacts on crime (e.g., in a city as a whole, or even large administrative areas such as precincts within a city). In some sense, the large number of well-controlled studies, often randomized experiments, within jurisdictions hampers the ability to draw jurisdictional inferences about crime. Randomly allocating hot spots within jurisdictions necessarily makes it very difficult to gain estimates of an overall program effect across the jurisdictions. Hot spots policing programs have generally compared gains in crime hot spots in treatment and control conditions; they have not estimated the potential large-area impacts of this approach. The logic model of the strategy implies there should be such impacts, given the effects on hot spots and the diffusion-of-benefits impacts noted in a series of studies. Of course, the level of jurisdictional impacts would depend on the scope of the hot spots policing program. However, the possibility of distal displacement of crime makes the investigation of jurisdictional impacts particularly important.
The importance of considering the jurisdiction-level effects of a hot spots policing approach, as well as other geographically focused policing approaches, also follows from consideration of the possible opportunity costs of concentrating police presence. The additional officers that are assigned to the hot spots would otherwise be patrolling lower-crime areas or perhaps engaged in other productive activities that would presumably reduce crime. So the reduction in crime in hot spots logically comes at a cost to other policing activities, assuming that overall police resources are fixed. The case for a hot spots model requires a demonstration not only that additional policing of hot spots reduces crime in those areas but also that in effect, the additional police are more productive assigned to hot spots than they would be in their alternative assignment. None of the evaluations of hot spots policing has measured this sort of opportunity cost as it relates to jurisdictional outcomes.
Weisburd and colleagues (2017) used an agent-based model to compare overall crime prevention impacts in a simulated borough of a city with four beats. The model produced meaningful areawide crime-prevention benefits in the experiments with hot spots patrol as compared to randomized patrol in a jurisdiction. For instance, high-intensity hot spots policing, where half of the police officers assigned to a beat spent all of their time in the top five hot spots in that beat, reduced the incidence of robbery by 11.7 percent at the borough level, 11.5 percent at the police-beat level, and 77.3 percent at the hot-spot level in comparison to random police patrol. That study did
identify distal displacement to areas farther from hot spots, though the distal displacement impacts were small. While these results follow the general logic model for hot spots policing, actual field experiments are needed to draw strong inferences about areawide impacts of the approach.
Summary. A large number of rigorous evaluations, including a series of randomized controlled trials, of hot spots policing programs have been conducted. The available research evidence suggests that hot spots policing interventions generate statistically significant crime-reduction impacts without simply displacing crime into areas immediately surrounding the targeted locations. Instead, hot spots policing studies that do measure possible displacement effects tend to find that these programs generate a diffusion-of-crime-control benefit into immediately adjacent areas. Our knowledge base on the crime-reduction impacts of hot spots policing programs is still developing, however. The available evaluation literature has generally not analyzed crime displacement and diffusion effects beyond areas proximate to targeted hot spot locations. Moreover, the research literature does not provide estimates of the systemwide or large-area impacts of hot spots policing when implemented as a crime-control strategy for an entire jurisdiction. The long-term crime-reduction benefits of this approach have also not been established, as hot spot policing program evaluations have focused on estimating short-term crime prevention impacts.
Predictive policing, as discussed in Chapter 2, is—in terms of crime and place—“the use of historical data to create a spatiotemporal forecast of areas of criminality or crime hot spots that will be the basis for police resource allocation decisions with the expectation that having officers at the proposed place and time will deter or detect criminal activity” (Ratcliffe, 2014, p. 4). However, predictive policing is a relatively new strategy, and policing practices associated with it are vague and poorly defined (Perry et al., 2013; Santos, 2014). Additionally, because the forecasts (and crime analysis more generally) need to be combined with effective practices and tactics targeted at predicted locations or to predicted individuals, there are few studies to date that have tried to parse out the effects of the analysis or forecast itself as a proactive activity. While predictive policing has gained considerable name recognition as a new policing strategy, it is difficult to distinguish predictive policing in any meaningful way from hot spots policing, with the exception that the predictive policing forecasts are usually generated using sophisticated software programs that claim a predictive capability. This raises two questions: First, does the software significantly enhance the ability of existing analytical approaches in the identification
of crime hot spots? Second, are there police tactics employed in predicted areas that are more effective than or different from patrol tactics usually employed in hot spots policing?
One example to consider is a study by Hunt, Saunders, and Hollywood (2014), which examined the impact of predictive modeling on preventing property crimes. Predictions on locations of future crimes were derived monthly for the Shreveport, Louisiana, Police Department, which were then used to drive a strategic decision-making model that included increasing officer awareness of hot spots in roll call and using predictions to implement a broken windows approach (see Wilson and Kelling, 1982). Four selected high-crime districts were randomly allocated to experimental and control groups (two each), and two medium-crime districts were also randomly assigned. Control areas used traditional hot spot mapping of past property crimes to direct an existing operational unit for proactive activities. Hunt and colleagues found no evidence that crime was reduced more when police used the software-driven predictive modeling, compared to control areas that used more traditional crime-mapping techniques to direct operations to crime hot spots. However, the authors suggested a number of possible explanations for their null findings, including concerns regarding the selected policing tactics, the implementation of the strategy, low statistical power due to the small sample size, and a lack of resources in the experimental group.
Mohler and colleagues (2015) conducted one of the few other known published studies of the crime prevention impact of predictive policing technology in Los Angeles, California, and in Kent, England. Rather than comparing fixed experimental and control crime hot spots, they compared days in which directed patrol was deployed using predictive policing algorithms to days in which conventional forms of crime mapping and analysis were used, randomly allocating days to either predictive policing or conventional mapping and analysis. Contrary to the findings of Hunt, Saunders, and Hollywood (2014), Mohler and colleagues (2015) found that use of their predictive forecasting led to an average 7.4 percent reduction in crime compared to the days officers used hot spots derived from conventional crime mapping by analysts, which showed no statistically significant reduction in crime.
These two studies present a common challenge in evaluating the impact of technology on police crime-control effectiveness, especially in proactive contexts. Although both studies attempted to directly test and compare the impact of one analytic technology with another, the effects were still mediated by the agencies implementing the approach. This is one important limitation of drawing inferences from only a few evaluation studies. Mohler and colleagues’ (2015) study in two locations might be considered stronger in this regard, although officers in Los Angeles and Kent still had to act
upon the technology to create the effect. Both sets of maps in this study looked identical despite their underlying data and analysis being different, which suggests that predictive algorithms are not substantially more precise in directing traditional police proactivity than more conventional forms of crime mapping.
One clear problem in assessing the outcomes of these studies is to determine the baseline of “traditional” crime analysis against which to draw conclusions regarding the efficacy of newer predictive algorithms. The ability of crime analysts varies substantially from place to place, along with the software and data quality they can access. They are rarely, if ever, asked to identify small square grids of only a few hundred feet on each side in their normal work day. So determining whether predictive algorithms are a significant enhancement to existing methods of hot spot detection is hampered by variability in the existing approaches. The findings may be different in these studies because standard practice differs.
Another limitation of these studies is that the policing tactics adopted appear to be in most locations a traditional patrol response. In other words, rather than new practices and tactics emerging from predictive policing, to date the strategy has consisted of more-honed spatial resource allocation models whose location forecasts are then linked to traditional crime-prevention policing activities.
A study that presents some insights into the impact of predictive and crime analytic technology is Kennedy, Caplan, and Piza (2011). The authors examined the use of a different predictive crime analytic approach—risk terrain modeling—in enhancing a place-based proactive policing approach in five jurisdictions. This quasi-experimental study compared street segments and intersections that received police proactivity using results of risk terrain modeling with control segments derived from propensity score matching that did not receive extra police effort. The analysis found positive effects of this hot spots policing strategy; however, the control segments did not receive targeted patrols, thereby begging the question whether the technology or the directed patrols caused the observed crime reduction. In other words, was the crime reduction caused by standard police patrols that were no different than a traditional hot spots policing approach, or was value added by the software over and above what could be normally achieved by a combination of existing analytical and operational approaches? In short, whether risk terrain modeling either predicts crime or facilitates proactive policing better than other predictive policing models remains to be tested.
Other predictive analytical approaches may be useful, especially the near-repeat techniques that use short-term event patterns to forecast probabilities of future events (Johnson et al., 2009; Gorr and Lee, 2015) or processes such as the Epidemic Type Aftershock Sequence method (a nonparametric self-exciting point process [see Mohler et al., 2011]). These ap-
proaches could be more effective at predicting short-term crime hot spots than traditional crime mapping approaches, though the methods to assess predictive accuracy have not yet been generally agreed upon and different approaches often produce different types of crime forecast from different data sources—further confounding comparisons.
Some of the studies of computer algorithms designed to predict the spatial pattern of crime have been conducted by the same researchers who designed the algorithms. Some of these algorithms and programs have been subsequently commercialized. The possibility of bias in the reported findings from the evaluations cannot be ruled out. Furthermore, the breadth (and arguably, the vagueness) by which predictive policing has been defined means that many studies of it will likely be unique with respect to what they are studying. It may be some time before there is sufficient replication to draw reasoned conclusions about any policing activities targeted to crime prediction areas.
At present, the newness of many predictive policing technologies is such that their accuracy is difficult to determine; moreover, the base rate of crime activity or other benchmark against which these new technologies should be measured has not been established. If the predictive technologies are deemed to be more accurate than, say, a heat map of the previous year’s crime or the manually estimated predictions of a crime analyst, how much should a computer-generated prediction affect the actions of police? In other words, how much influence should a prediction have in the totality of circumstances for reasonable suspicion and for changing the balance of suspicion in predicted crime areas (Ferguson, 2012)? While the advent of big data might increase the accuracy of crime prediction of both crime-prone individuals (whether as perpetrators or as victims) and crime-prone areas, data quality will become an issue (Ferguson, 2015) and “blind reliance on the forecast, divorced from the reason for the forecast, may lead to inappropriate reliance on the technology” (Ferguson, 2012, p. 316).
Summary. At present, there are insufficient robust empirical studies to draw any firm conclusion about either the efficacy of crime-prediction software or the effectiveness of any associated police operational tactics. Furthermore, it is as yet unclear whether predictive policing is substantively different from hot spots policing.
Another technology believed to improve police capacity for proactive intervention at specific places is closed circuit television (CCTV). CCTV is thought to create a general deterrent effect on crime by increasing an offender’s perceived risk of being identified or apprehended for criminal activ-
ity. CCTV can also be used proactively by the police to monitor suspicious situations or disorders that might turn into criminal events. In this way, the police might be able to respond before a tense situation deteriorates into criminality or to use information learned from remote observing of criminal activity to direct street officers where to conduct searches or apprehension of suspects. These are two different applications of CCTV technology, with the general deterrence application conveying a threat of police intervention simply through the presence of the camera, whereas the proactive use involves more specific deterrence through the active direction of officers to imminent or observed criminality.
Prior reviews of controlled evaluations of passively monitored CCTV systems suggest mixed crime-control impacts of CCTV. However, these studies evaluated the effects of CCTV in its general deterrence capacity; they did not specifically evaluate proactive police use of CCTVs. For instance, Welsh and Farrington (2008) completed a meta-review of studies in which CCTV was the main intervention in an area that had at least 20 crimes prior to the CCTV implementation. Also, each study had to involve at least one experimental area and one reasonably comparable control area and, at a minimum, had an evaluation design comprising before-and-after measures of crime in both the experimental and control areas. They concluded that “CCTV has a modest [16 percent] but significant desirable effect on crime, is most effective in reducing crime in car parks, is most effective when targeted at vehicle crimes (largely a function of the successful car park schemes), and is more effective in reducing crime in the U.K. than in other countries” (Welsh and Farrington, 2008, pp. 18–19; see also Gill and Spriggs, 2005).
Over the past decade, a number of additional studies have taken place. The largest U.S. study examined the crime-reduction effects of CCTV use by law enforcement and municipal authorities in Baltimore, MD, Chicago, IL, and Washington, DC (La Vigne et al., 2011). The design was relatively strong because it used pre-post measures and matched comparison areas that were identified on the basis of a variety of place characteristics. However, the definition of treated and control areas introduced measurement error related to the physical placement of the camera, since this study defined a treated area as the entire area within 200 feet of the camera’s location, rather than defining an area as “treated” if it was in the area the camera could actually see (called a “camera viewshed”). Use of actual camera view-sheds to define the treated area has become more common over the past decade, avoiding this problem (see, e.g., Ratcliffe, Taniguchi, and Taylor, 2009; Gerell, 2016; Piza, Caplan, and Kennedy, 2014). La Vigne and colleagues (2011) found that, in the downtown Baltimore area, both property and violent crimes declined by large percentages (between 23% and 35%) in the months following camera implementation. In Chicago, their analysis
indicated that crime was reduced in some areas but not in others. Cameras alone did not appear to have an impact on crime in the District of Columbia. Overall, the results indicate that cameras have the most impact when they are highly concentrated, actively monitored, and integrated into a broader law enforcement strategy. Consistent with previous studies as well as a recent study from Schenectady, New York (McLean, Worden, and Kim, 2013), La Vigne and colleagues (2011) indicated that CCTV cameras are not universally effective; there are factors at each place that contribute to the effectiveness of the CCTV strategy.
As with the use of other technologies such as predictive policing software or license plate readers, it is difficult to disentangle the technology from the efficacy of the associated policing response to the technological stimuli. For example, even if police never respond to crime in the viewshed of a camera, the deterrent effect of CCTV may still be effective for transient offenders new to the area but ineffective in deterring resident criminals who learn by experience about the absent police response. With all of the CCTV studies mentioned, whether and exactly how police were proactively using these cameras was unknown. Given that these evaluations of CCTV systems did not explicitly cite a specific and proactive differential response from police in their discussion of the project implementation, the committee concluded that any response from police services was probably reactive and not a proactive engagement using a team dedicated to responding to CCTV-identified incidents, as was the case with the next study discussed.
Piza and colleagues (2015) used a randomized controlled trial to explicitly test the use of CCTV to support proactive policing in Newark, New Jersey. In the treatment group, 19 cameras were monitored by a dedicated camera operator; two patrol cars had exclusive responsibility for responding to incidents identified by the camera operator. In the control group, 19 cameras were used “normally,” that is, with monitors reporting suspicious activities through the computer-aided dispatch system to patrol officers. The researchers’ experimental analyses suggested that the treatment condition produced “tangible and meaningful crime reductions of violent crime and social disorder” relative to the control condition (Piza et al., 2015, p. 62). Results varied between time periods measured, but they found 40–48 percent reductions in violent crime and 41–49 percent reductions in social disorder—substantively large effects, which they estimated would have occurred less than 10 percent of the time under the null hypothesis of no relationship between CCTV and crime.
As with other studies involving technology, camera systems are often implemented in combination with other initiatives, so parsing out the individual impact of the cameras is difficult. Research designs also vary considerably, and CCTV schemes have been operationalized in myriad
ways, making it difficult to identify an optimal configuration of camera installation and operational support.
Summary. The results from studies examining the introduction of CCTV camera schemes into relatively passive monitoring systems are mixed, but they tend to show modest outcomes in terms of property crime reduction at high-crime locations. The evidence suggests that the use of CCTV systems without a dedicated police operational response may be effective at reducing vehicle crime and less effective at combating violence, although the way the system is implemented and used appears to be important in achieving any crime reduction. CCTV may also be more effective when bundled with other crime-prevention measures. With regard to the use of an operational police presence in the field and dedicated to responding to active monitoring of a reasonable number of cameras, the evidence appears promising. However, the strength of conclusions about this proactive use is constrained because the evidence base consists of a single study.
Problem-oriented policing seeks to identify the underlying causes of crime problems and to frame appropriate responses using a wide variety of methods and tactics (Goldstein, 1979, 1990; Braga, 2008; see Chapter 2 of this volume). Depending on the nature of the crime and disorder problem being addressed, problem-oriented policing interventions may engage a diversity of enforcement, situation prevention, and community engagement strategies. The 2004 NRC report concluded that problem-oriented policing is a promising approach to deal with crime, disorder, and fear; it recommended additional research to understand the organizational arrangements that foster effective problem solving (National Research Council, 2004). This section discusses the evidence showing that even an imperfect implementation of problem-oriented policing—so-called “shallow” problem solving—generates crime-prevention gains (Braga and Weisburd, 2006). However, the committee believes that improvements to the process of problem-oriented policing could produce even stronger crime control effects.
Many evaluations of problem-oriented policing interventions use weaker evaluation designs,2 such as one-group-only pre-post comparisons
2 We use “weaker” here to refer to the relative strength of findings as evidence. For discussion of standards of evidence and how the committee assessed the research literature, see the Chapter 1 section, “Assessing the Evidence.”
of crime and disorder indicators. For instance, in the influential Newport News, Virginia, test of problem-oriented policing, Eck and Spelman (1987) used time series models to evaluate the effectiveness of three problem-solving initiatives. Their analyses suggested that the implemented interventions were associated with varying, statistically significant crime reductions for the targeted crime problems: residential burglaries in an apartment complex, thefts from vehicles parked downtown, and street prostitution–related robberies. However, the strength of these results is limited by very short time series lengths (marginally longer than n = 50 observations), no comparison areas, and no consideration of possible crime-displacement effects. However, there have also been more rigorous tests of the crime-control efficacy of problem-oriented policing.
Researchers from the Center for Crime Prevention Studies at Rutgers University teamed with the Jersey City Police Department to evaluate a problem-oriented policing intervention targeting locations with high rates of violent crimes (Braga et al., 1999). The team identified 24 locations with a high incidence of violent crime, using computerized mapping and database technologies to rank areas, defined by street intersections, with high levels of service calls for, or incidents of, assault and robbery, as well as police and researcher perceptions of more-violent areas. In the randomized block-field design for this experiment, the 24 violent-crime areas were matched into 12 pairs, with one member of each pair allocated to the treatment condition and the other member randomly allocated to the control condition. The treatment condition, which was applied over a 16-month period, combined several practices typical of a problem-oriented policing strategy, including aggressive enforcement against disorder incidents and some situational responses.
The main analyses of effect used count-based regression models to calculate statistical differences for a number of crime activity indicators at each location between a 6-month pre-test period and a 6-month period after the intervention (post-test period). These pre-post differences were then compared for the locations in the treatment condition against their matched control location. The analyses found that locations in the treatment condition had a statistically significant 21 percent reduction in total calls for service, relative to their matched controls, and a 42 percent reduction in reported crime incidents. There were also varying levels of reduction in calls for service and crime incidents for all the crime-type subcategories. Systematic observations were made of social and physical disorder in the 24 locations during the pre-test and post-test periods, and analysis of the data on these observations found that social and physical disorder had been reduced. The research team also analyzed data on measures for displacement of crime behavior and diffusion of crime-control benefits in the two-block catchment areas surrounding each treatment and control location.
These analyses did not find statistically significant support for either crime displacement into the catchment areas or diffusion of crime-control benefits outside the targeted locations.
In another collaboration, researchers from Harvard University teamed with the police department in Lowell, Massachusetts, on a randomized controlled trial to test a problem-oriented policing strategy in reducing crime and disorder incidence at hot spots in Lowell (Braga and Bond, 2008). The researchers used spatial analyses of service calls involving crime or disorder, supplemented by observations on appropriate hot spot boundaries from both police officers and the research team, to identify 34 hot spots. Pairing of hot spots was based on matching for the numbers and types of calls for service, neighborhood demographics, and other location characteristics. In the randomized block field design for the trial, one member of each pair was randomly allocated to treatment, with the other member allocated to the control condition. The problem-oriented policing intervention, which continued for 12 months, consisted mainly of aggressive disorder enforcement tactics but also included some situational responses.
The main analysis used by Braga and Bond (2008) applied count-based regression models to the pair-wise differences between a number of crime and disorder indicators measured during the 6-month pre-test and post-test periods before and after the 12-month intervention. The pre-post differences for the matched pairs were then analyzed for overall mean differences between the treatment condition and controls. (The same design was used in the Jersey City trial described above.) The authors found that the problem-oriented intervention resulted in a statistically significant 19.8 percent reduction in total calls for service, relative to the control condition. They also found varying levels of reductions for all their crime-type subcategories. Systematic observations were made during the pre-test and post-test periods for measures of both social disorder and physical disorder, and analysis of the data from these observations found that both types of disorder decreased at treatment hot spots relative to their matched controls. A mediation analysis of the core treatment elements suggested that the crime and disorder gains were driven by situational responses, such as razing abandoned buildings and securing vacant lots, rather than increased misdemeanor arrests or police-led social service actions.
Both the Jersey City and Lowell experiments documented proactive policing interventions similar to the usual practices in the field for a problem-oriented policing strategy; that is, the problem-solving component involved only weak or “shallow” problem analysis, with only limited development of responses to address the problems after analysis. Despite this gap between the ideal for a problem-solving approach and these actual implementations, the problem-oriented policing strategy was found to be effective in reducing crime and disorder in the treated hot spots in both cities. These
findings suggest that it may not be essential for achieving crime reduction outcomes to implement problem-oriented policing interventions exactly as the strategy was defined by Goldstein (1979, 1990). It may be enough to focus police resources on risks that the problem-oriented policing project identifies, such as risks typically associated with crime hot spots (Braga and Weisburd, 2006).
Taylor, Koper, and Woods (2011) implemented a randomized controlled trial comparing the effectiveness of both directed patrol and problem-oriented policing interventions at hot spots of violent crime in Jacksonville, Florida. The authors identified 83 hot spots of nondomestic violence and randomly assigned them into three conditions: directed patrol, problem-oriented policing, and the control condition. In the problem-oriented intervention, teams of officers and crime analysts conducted problem analysis and problem solving at selected hot spots, employing such situational crime-prevention measures as installing or improving lighting, erecting road barriers, and repairing fences. The police officers typically worked with business owners and rental property managers to improve security measures and business practices, along with other means to collaborate on crime prevention. Many of these collaborative activities, such as conducting surveys in the community and various modes of outreach to community members, can be viewed as community organizing. Other responses to the problems identified included providing social services (such as improved youth recreational opportunities), stricter enforcement of municipal codes, nuisance abatement, and even aesthetic improvements in the community, such as cleaning up parks and removing graffiti. Across the 22 locations assigned to the problem-oriented policing condition, the participating teams implemented 283 discrete problem-solving measures. The researchers found that this problem-oriented policing intervention was associated with a 33 percent drop in street violence during the 90-day assessment period after the intervention, relative to control areas. Statistically nonsignificant reductions in crime were associated with the directed patrol intervention relative to the control condition.
A review of evaluations of problem-oriented policing by Weisburd and colleagues (2008) for the Campbell Collaboration examined findings on crime and disorder outcomes (see also Weisburd et al., 2010). Although this review covered a large number of empirical evaluations, it identified only 10 as having randomized experimental or quasi-experimental study designs. The reviewers’ meta-analysis found that the problem-oriented policing programs tested by these 10 more rigorous evaluations had produced a combined modest but statistically significant decrease in outcome measures for crime and disorder. Similar results were obtained when the randomized experiments and the quasi-experimental evaluations were analyzed separately.
This review also reported on crime reduction effects found in evalu-
ations with just a pre-post comparison design, which did not include a comparison group and were therefore less rigorous in methodology than the random experiments and quasi-experimental studies. Of the 45 pre-post evaluations reviewed, 43 had reported beneficial crime-prevention effects attributed to the problem-oriented policing intervention evaluated. Furthermore, the crime-reduction effects found by these pre-post comparisons were much larger than the effects found by the 10 evaluations with more rigorous research designs.
Finally, it is important to note that evaluations of problem-oriented policing have looked at the impacts of the approach on the specific problems examined, often at specific places. There is often an absence of assessment of possible displacement outcomes, and there has not been study of whether a problem-oriented approach used widely in a city would reduce overall crime in that jurisdiction.
Summary. Despite the popularity of problem-oriented policing as a crime-prevention strategy, there are surprisingly few rigorous program evaluations of it. Much of the available evaluation evidence consists of non-experimental analyses that report finding strong impacts on crime. The far fewer randomized experimental evaluations generally show smaller, but statistically significant, crime reductions generated by problem-oriented policing interventions relative to the control condition. Program evaluations largely examine the short-term impacts of problem-oriented policing on crime and disorder outcomes, and there is little evidence regarding displacement or possible jurisdictional impacts of this approach. Program evaluations also suggest that it is difficult for police officers to fully implement problem-oriented policing. Many problem-oriented policing projects are characterized by weak problem analysis and a lack of non-enforcement responses to the problems identified. Nevertheless, even these limited applications of problem-oriented policing have generated crime prevention impacts.
While regarded by some as a distinct approach to crime prevention (Buerger and Mazerolle, 1998), the committee views third party policing as aligned with a problem-solving approach, since police using this strategy seek to persuade or coerce organizations or nonoffending persons, such as public housing agencies, property owners, parents, health and building inspectors, and business owners, to take some responsibility for preventing crime or reducing crime problems. Community organizations have long advocated for the use of civil remedies to control crime and disorder problems (Roehl, 1998), and some observers suggest that code enforcement and nuisance abatement strategies represent important mechanisms for
residents and the police to “coproduce” public safety (Blumenberg, Blom, and Artigiani, 1998).
The first direct evaluation of third party policing occurred with the Oakland Police Department’s Beat Health Program (refer to Box 2-3 in Chapter 2). This intervention took a problem-solving approach designed “to control drug and disorder problems, in particular, and restore order by focusing on the physical decay conditions of targeted commercial establishments, private homes, and rental properties” (Mazerolle, Price, and Roehl, 2000, p. 213). This randomized controlled trial compared the Beat Health intervention (the treatment condition) with the routine policing practices of a regular patrol division as the control condition (Mazerolle, Price, and Roehl, 2000). A street block that included a residential or commercial property referred to the Beat Health police unit as having a drug problem or other indicators of blight became eligible for inclusion in the trial. For the trial, 100 such street blocks were randomly assigned to either the Beat Health intervention or the control condition (n = 50 for each condition). A difference-of-differences design was used for the analysis of effect, with a pre-test period of 21.5 months before the 5.5-month intervention period and a post-test period of 12 months after the intervention. In addition to the indicators of effect within the street-block units, crime displacement and control-benefits diffusion effects were assessed in catchment areas extending 500 feet out from the problem address on each street-block unit. The analysis showed that the units in the Beat Health program had a statistically significant 7 percent reduction in drug calls relative to units in the control condition (in which drug calls actually increased by 55%), but there were no statistically significant differences in other categories of service calls. The effects were also more prominent in residential treatment blocks than in commercial areas. The analysis of effects in catchment areas showed an overall (across all catchment areas in the treatment condition) diffusion of crime-control benefits, compared to catchment areas for the control condition (Mazerolle, Price, and Roehl, 2000).
In San Diego, the police worked with the Code Compliance Department (the third party in this intervention) to encourage property owners to fix drug-related problems—for example, by evicting offending tenants (Eck and Wartell, 1998). When the police identified a property as having persistent drug activity, the Code Compliance Department could use San Diego’s nuisance abatement legislation to fine the property owners or close their properties for up to 1 year. To evaluate this intervention, Eck and Wartell (1998) used a randomized controlled trial in which properties identified by the police as having a drug-related problem were randomly assigned to one of two treatment groups (n = 42 and n = 37) or to the control condition (n = 42). Property owners in one treatment group received a letter from police describing enforcement action and offering assistance;
property owners in the other treatment group met with a narcotics detective and were threatened with nuisance abatement. The main outcome for this trial was incidence of post-intervention official crime at each problem property, measured as the aggregate of five 6-month consecutive periods (a total of 30 months post-intervention). Property owners in the meeting treatment group experienced large reductions (declines of almost 60%) in reported crime, whereas the property owners in the letter-receiving group experienced smaller crime reduction effects (a decline of 13%).
As we noted in Chapter 3, third party policing’s use of coercive mechanisms to influence business and housing owners may raise privacy concerns. Descriptive research also suggests that overly coercive applications of third party policing strategies may produce unintended harmful consequences for community members (Desmond and Valdez, 2013).
A related approach to third party policing is the development of Business Improvement Districts (BIDs). BIDs rely not only on policing resources but also on private security, often including guards and CCTV. A quasi-experimental evaluation of 30 BIDs created in Los Angeles during the 1990s found that expenditures on private security were effective in creating a sustained reduction in crime (Cook and MacDonald, 2011). The authors found the data closely fit a linear dose-response curve: on average, an additional $100,000 spent on private security annually resulted in an incremental reduction of six robberies, four assaults, and five burglaries. Given standard estimates of the social cost of these crimes, the benefit-cost ratio exceeded 20. The crime-reduction effects were coupled with reductions in the numbers of arrests for these crimes, thus providing a further cost savings to the criminal justice system in Los Angeles County. The authors found no evidence of geographic displacement of crime to areas outside the BID resulting from the private security within the BID (Cook and MacDonald, 2011).
Summary. There are only a small number of evaluations of third party policing programs, but these evaluations have assessed the impact of third party policing interventions on crime and disorder using randomized controlled trials and rigorous quasi-experimental designs. The available evidence supports a conclusion that third party policing generates statistically significant short-term reductions in crime and disorder; there is more-limited evidence of long-term impacts in evaluations of BIDs. Implementations of this strategy, whether measured in an experimental evaluation of Oakland’s Beat Health Program or in a quasi-experimental evaluation of BIDs, did not displace crime incidence to nearby areas outside the intervention boundary. Indeed, the Oakland evaluation showed a diffusion of crime-control benefits to nearby areas (i.e., crime measures decreased in the
nearby area). However, little is known about possible jurisdictional impacts of adopting these approaches.
Focused deterrence strategies have been implemented to halt ongoing violence by gangs and other criminally active groups, disrupt disorderly and violent drug markets (known as Drug Market Intervention or DMI), and prevent continued criminal behavior by individual repeat offenders.3 The 2004 NRC policing report described the then-available scientific evidence on the crime reduction value of focused deterrence practices as “promising” but “descriptive rather than evaluative” (National Research Council, 2004, p. 241), and the 2005 NRC report on firearms violence suggested the evidence was “limited” but “still evolving” (National Research Council, 2005, p. 10). A recent Campbell Collaboration systematic review identified 24 evaluations of focused deterrence strategies that used comparison groups (Braga, Weisburd, and Turchan, in press). The Campbell review meta-analysis suggested that focused deterrence strategies were associated with an overall, statistically significant, moderate crime-reduction effect. However, program effect sizes varied by program type, with gang violence reduction strategies generating larger crime-reduction impacts and drug market intervention smaller impacts.
In an earlier Campbell review, Braga and Weisburd (2014) noted that existing evaluations of focused deterrence programs used quasi-experimental tests, and many of these had weaker study designs that depended upon non-equivalent comparisons. The reviewers expressed concern over the lack of randomized controlled trials and called for more rigorous evaluations of focused deterrence programs. As of the writing of this report, their call for more rigorous research on this strategy has not been answered. However, many of the quasi-experimental evaluations completed since the first iteration of the Campbell review have employed more rigorous methods. The evolution in rigor of quasi-experimental evaluation techniques is evidenced by the difference in the study designs used to evaluate separate implemen-
3 The committee decided not to review repeat offender programs for two reasons. First, these programs were common in the 1980s but have generally been replaced by programs using a focused deterrence strategy as reviewed here. Second, there has been no additional research evidence on repeat offender programs beyond the research reviewed in the 2004 NRC report. That report concluded that available studies represent “only indirect examinations of their effect on reducing crime, and conclusions about their crime reduction effectiveness rely on ancillary assumptions about the effectiveness of selective incarceration and incapacitation” (National Research Council, 2004, p. 241).
The initial evaluation of Operation Ceasefire in Boston, sponsored by the U.S. Department of Justice (DOJ) in the 1990s, used a quasi-experimental design to compare youth homicide trends in that city with trends in other major U.S. cities and in other large cities of New England. (Braga et al., 2001). The main outcome variable for assessing the program’s impact was the average number of homicide victims per month, ages 24 and under, between January 1, 1991, and May 31, 1998. Supplementing this assessment of outcome were analyses of Operation Ceasefire’s effect on citywide, monthly counts of gun assault incidents and service calls reporting gunshots fired, as well as monthly gun assault incidents by youths in one high-risk policing district. The effect of Operation Ceasefire on these outcome variables was analyzed using Poisson and negative binomial regression models that controlled for potential confounders (covariates) such as secular trends, seasonal variations, youth population trends and employment rate trends in Boston, robbery and adult homicide trends, and youth drug arrest trends. Program impact was estimated using a dummy variable in the regression models, with June 1996 through May 1998 as the post-implementation period.
The analyses in this first Operation Ceasefire evaluation found that the program was associated with statistically significant reductions not only in the youth homicide rate but also in the other indicators of serious gun violence. The regression models estimated, after controlling for the potential covariates, that a 63 percent reduction in the monthly count of youth homicides could be attributed to the program. The regression modeling also attributed to the intervention a 25 percent reduction in citywide gun assault incidents, a 32 percent reduction in citywide shots-fired calls for service, and a 44 percent reduction in the monthly count of gun assaults by youth in the high-risk district (Braga et al., 2001).
As noted, this evaluation of Operation Ceasefire also compared the youth homicide trend in Boston with the trends in 39 major U.S. cities, as well as 29 New England cities with populations greater than 60,000 (Braga et al., 2001). After controlling for the covariates listed above, the regression analysis found only three cities—Dallas, Texas; Jacksonville, Florida; and Virginia Beach, Virginia—that had statistically significant reductions in youth homicide trends (monthly counts) during the Operation Ceasefire implementation period. In four other cities—Los Angeles, California; New York City, New York; Philadelphia, Pennsylvania; and Tucson, Arizona—reductions in monthly counts of youth homicides were statistically significant at some point in the entire time series but not during the implementation of the Boston intervention. However, for all these
other major U.S. cities, the researchers concluded that for corresponding time periods, the trajectories of the youth homicide time series were distinct from the youth homicide trajectory in Boston. Based on these findings, Braga and colleagues (2001) concluded that the trend in youth homicide reduction associated with implementing Operation Ceasefire was distinct from the trends in most other major U.S. cities.
To assess whether implementation of Operation Ceasefire coincided with the start of the 63 percent decrease in Boston monthly youth homicides, a companion study by Piehl and colleagues (2003) analyzed in more detail the time series of youth homicide counts. They applied an econometric model to evaluate all possible monthly break points in the time series, while controlling for trends and seasonal variations, for the maximal monthly break point associated with a significant change in the series’ slope (trajectory). This analysis found that the “optimal break” in the time series occurred during the summer months of 1996, after Operation Ceasefire was implemented in January of that year.
This first evaluation of Operation Ceasefire has been reviewed by a number of researchers who have made their own assessments of the relationship between the implementation of the intervention and the trend in the youth homicide rate in Boston during the 1990s. One reviewer suggested that some of the decrease in youth homicides may have occurred without the intervention because violence in general was decreasing in most major U.S. cities during this period (Fagan, 2002). To illustrate his point, Fagan graphed the time series for youth gun homicide in Boston and other Massachusetts cities, showing that a general downward trend in gun violence was occurring even before Operation Ceasefire.
Shortly after Fagan’s review, Rosenfeld, Fornango, and Baumer (2005) used a growth-curve analysis to examine predicted homicide trend data for the 95 largest U.S. cities during the 1990s. This analysis produced some evidence that the reduction in the youth homicide rate in Boston after Operation Ceasefire began was steeper than elsewhere, but the authors concluded that given the small number of youth homicide incidents, their statistical models did not support any strong conclusion about Operation Ceasefire effectiveness. However, a review of the Rosenfeld, Fornango, and Baumer (2005) analysis by Berk (2005) raised a number of concerns about their statistical and methodological analysis. Yet another reviewer agreed with the original evaluation that Operation Ceasefire was associated with a substantial reduction in the youth homicide rate in Boston but concluded that uncertainty remained about the extent of the intervention’s (causal) effect on youth violence throughout Boston, given the complexities of analyzing citywide data on homicide rates (Ludwig, 2005).
A 2005 report by an NRC study committee concluded that the Operation Ceasefire evaluation was compelling in associating the intervention
with the subsequent decline in youth homicide. However, that study committee agreed with other reviewers in suggesting that many complex factors affect youth homicide trends, making it difficult to specify the nature (i.e., a statistical association versus a causal connection) of the relationship between the Operation Ceasefire intervention and subsequent changes in youth offending behaviors (National Research Council, 2005). Because the evaluation was not a randomized, controlled experiment, the design does not rule out the possibility that alternative factors, including complex interactions among the covariates that were considered in the regression analysis, may have been more important causal factors in the observed trend in youth homicides in Boston than the Operation Ceasefire intervention.
Braga, Hureau, and Papachristos (2014) conducted a quasi-experimental evaluation of a reconstituted Boston Ceasefire program implemented during the mid-2000s in response to a growing problem of gang violence. Propensity scores were used to match treated Boston gangs (n = 16) to untreated Boston gangs (n = 37) that were not connected to the treated gangs through rivalries or alliances. The impact of the Ceasefire program was assessed using difference-in-differences estimators calculated from growth-curve regression models to compare gun violence trends during the 2006–2010 study period for the gangs in the treatment condition to their matched untreated gang. This evaluation found that total shootings involving the directly treated gangs were 31 percent less than total shootings in which the untreated gangs were involved. Braga, Apel, and Welsh (2013) used a similar evaluation methodology and found that the Ceasefire treatment condition also was associated with spillover deterrent effects on untreated gangs that were socially connected to treated gangs by rivalries or alliances. Total shootings involving these socially connected but untreated gangs decreased by 24 percent relative to total shootings by matched comparison gangs.
Other versions of the focused deterrence strategy have also employed rigorous quasi-experimental approaches. For instance, the seminal focused deterrence strategy, the Drug Market Intervention, was implemented to control disorderly and violent drug markets operating in High Point, North Carolina. In a recently completed quasi-experimental evaluation, Corsaro and colleagues (2012) analyzed longitudinal data to estimate the intervention’s effects by comparing violent crime trends in treated neighborhoods with trends in matched comparison neighborhoods, also in High Point. This evaluation reported modest 12–18 percent reductions in violent crime in the treated areas relative to control areas (Corsaro et al., 2012). More recently, Saunders and colleagues (2014) applied a synthetic control group quasi-experimental design to evaluate the High Point Drug Market Intervention Program and reported a 21 percent reduction in general crime
rates in treated areas with little evidence of spatial displacement of crime incidence to nearby areas.
The Project Safe Neighborhoods (PSN) intervention was implemented to test the hypothesis that Chicago’s homicide and gun violence problem could be improved by intervention tactics targeting the population at high risk of being either a victim or offender of gun violence (Papachristos, Meares, and Fagan, 2007). To test this hypothesis, the researchers selected two adjacent police districts on Chicago’s West Side to receive the intervention (the treatment districts). In these districts, the rates of murder and gun violence in 2002 were more than four times the city average. Two other of Chicago’s 25 police districts were selected via propensity-score matching as controls. Thus, neither the treatment nor the control districts were randomly selected. The PSN intervention, which began in May 2002, followed two principles: (1) Enforcement activities should be highly specific and targeted to those most at risk of being a gun-violence victim or offender. (2) Serious effort had to be made toward changing attitudes of those at risk with the law and law enforcement and toward changing the thinking by young men that would justify using a gun (the “normative side” of gun violence).
The PSN intervention comprised four component policing practices: (a) increasing federal prosecution for convicted felons who carried or used a firearm, (b) seeking longer sentences for successful federal prosecutions, (c) activities to curtail the supply of illegal firearms (gun recoveries by special teams composed of officers from both the U.S. Bureau of Alcohol, Tobacco, and Firearms and the Chicago Police Department), and (d) offender notification meetings—a practice associated with the procedural justice strategy—to communicate messages about deterrence and social norms to the potential offender population. The offender notification meetings were directed at recently released former prison inmates who had involvement in gun or gang violence and were returning to the treatment districts. These randomly selected offenders were informed that as convicted felons, they were vulnerable to federal firearms laws that carried mandatory minimum sentences if they were apprehended carrying a gun. On the constructive side, returning offenders were also offered social services and were encouraged by community members and other former offenders to change their life pattern.
In the quasi-experimental design used to evaluate the PSN intervention, monthly and quarterly counts of homicide incidents between January 1999 and December 2004 were the measures used to quantify the key outcome variable (Papachristos, Meares, and Fagan, 2007). Other outcomes included monthly and quarterly counts of gun homicide incidents, gang homicide incidents, and aggravated assault incidents in the treatment districts, relative to the control districts.
The research team analyzed not only the overall effects of the PSN treatment but also the effectiveness of the four component interventions. Through regression modeling on individual outcome growth curves, they estimated that the overall PSN intervention in the two treatment districts was associated with a statistically significant 37 percent reduction in homicides, compared with the control condition. They also found that the PSN intervention as a whole was associated with statistically significant decreases in gun-related homicides and aggravated assaults. There was also a decrease in gang-involved homicides, but this decrease was not statistically significant.
Of the four PSN component practices, the offender notification meetings were associated with the largest, statistically significant effect on homicide reduction, relative to the control condition. That is, the treatment districts with higher proportions of offenders who attended a forum experienced larger declines in homicides relative to control districts. The study also found modest but not statistically significant reductions in homicide rates, relative to the control condition, for two other components: intensifying federal prosecutions of felons apprehended with a firearm and curtailing the supply of illegal guns (quantified as the number of guns recovered by the special teams). The regression analysis did not show an association between declines in homicides in the treatment districts and the fourth PSN component, increasing the length of sentence associated with federal prosecutions (Papachristos, Meares, and Fagan, 2007).
In a supplemental analysis of the PSN intervention (described further in the procedural justice section of this chapter), Wallace and colleagues (2016) studied recidivism among former offenders who attended an offender notification meeting. The authors applied a survival analysis technique to the data on offender recidivism and found that offenders who attended one of the PSN meetings were 30 percent less likely to be arrested again, compared with a similar group of recently released former offenders from the same neighborhood who had not attended a meeting. Furthermore, the analysis found that the PSN treatment condition was associated with reduced recidivism rates for prior offenders, whether or not they were gang members, but the reduction in recidivism was greater for offenders who had only one felony conviction when they attended a PSN meeting.
Summary. A growing number of quasi-experimental evaluations have found that focused deterrence programs generate statistically significant crime reduction impacts in areas under the treatment condition. Unfortunately, there have been no randomized experimental evaluations of focused deterrence interventions, and although there are some noteworthy exceptions, the overall methodological rigor of focused deterrence evaluations needs to be strengthened. However, consistent crime-control impacts have been
reported both for short- and longer-term outcomes—not only by controlled evaluations that tested program effectiveness using outcomes such as reductions in gang violence and street crime driven by disorderly drug markets but also by non-experimental studies that examined repeat offending by individuals.
One of the first studies to examine whether the increase in the use of a stop, question, and frisk (SQF) strategy in New York City reduced crime was carried out by Smith and Purtell (2008). They used an interrupted time series, lagging SQF stop rates to crime rates. Their analysis found that SQF may have dissimilar effects across different types of crime or locations. The SQF strategy seemed to be associated with citywide reductions in incidents of robbery, murder, burglary, and motor vehicle theft but not with reduction in incidents of assault, rape, and grand larceny. Smith and Purtell (2008) also examined impacts of SQF in precincts with “impact zones” in which stop and frisk activity was concentrated. In those precincts, stops were found to be associated with reductions in robbery, assault, and grand larceny, although the authors point out that there are declining returns to scale for both the city and for precincts with impact zones.
Rosenfeld and Fornango (2014) critiqued Smith and Purtell’s (2008) methods, arguing that other factors may have contributed to their findings. Unlike the earlier Smith and Purtell study, Rosenfeld and Fornango (2014) used yearly rates of crime and SQF stops across all 75 precincts in the New York Police Department and limited their analysis to robbery and burglary. Per their critique of Smith and Purtell (2008), they included measures of precinct-level economic disadvantage, immigration, and residential stability. Their results indicate that there are no statistically significant correlations between SQF and burglary or robbery and only marginally significant negative relationships between stops lagged 2 years behind precinct burglary rates (Rosenfeld and Fornango, 2014, p. 11). Both of these studies were based on non-experimental data and are therefore vulnerable to all the problems inherent in the use of such data to make causal inferences.
Perhaps the most important of these problems is separating cause from effect. One way of disentangling cause from effect in non-experimental data is through the use of instrumental variable (IV) regression. The valid use of IV regression requires the identification of a source of variation in the application of SQFs that affects the crime rate only through its effect on the frequency of use of SQF. This approach is one of the two analyses used by Weisburd and colleagues (2016), who drew from an earlier study showing that SQFs in New York were used as a hot spots policing strategy (Weisburd, Telep, and Lawton, 2014). Employing an adaptation of Bartik’s
Instrument (see Bartik, 1991), they used frequency of stops occurring in the same borough but in different precincts as an instrument and found a deterrent effect of SQFs at a microgeographic level. Interpreting their results in terms of numbers of SQF stops, they found that in the year with the highest number of SQF stops (686,000), their models predicted a reduction of 11,771 crimes, or a 2 percent decrease in crime at the city level, attributable to SQF.
The second analysis used by Weisburd and colleagues (2016) was a space-time interaction model known as bivariate Ripley’s K (see Diggle et al. ; this analysis was also used by Wooditch and Weisburd ) to examine the daily impact of SQF on crime. Similar to the Bartik (1991) analysis, they found that SQFs had a deterrent effect on crime, at least within a limited time frame (less than 5 days).
There is also a separate body of research on the effectiveness of SQF in targeting places with serious gun crime problems and focusing on high-risk repeat offenders. Koper and Mayo-Wilson (2006, 2012) have reviewed studies of police tactics intended to reduce firearms violence. In these studies, the police employed various aggressive enforcement approaches ranging from traffic and pedestrian stops to car checks at locations with high concentrations of gun crime. But unlike zero tolerance tactics that depend on indiscriminate arrest for even minor offenses, the enforcement tactics were tailored to increase the risks for carrying firearms illegally in crime hot spots, and the evaluations found that such tactics had positive crime-prevention outcomes (see, e.g., McGarrell et al., 2001; Sherman, Shaw, and Rogan, 1995).
A recent study of an intervention to reduce gun crime in St. Louis, Missouri, reported similar crime-reduction outcomes (Rosenfeld, Deckard, and Blackburn, 2014). This study evaluated the effect of directed patrol and self-initiated enforcement efforts conducted at firearm violence hot spots in St. Louis. Thirty-two violent crime hot spots were randomly allocated to two different treatment conditions (directed patrol only, directed patrol with enforcement activities), as well as one control condition (no special treatment). For the directed patrol with enforcement activities, officers were asked to remain in a hot spot for approximately 15 minutes each time, following the Koper Curve principle (see Koper, 1995), and to engage in a variety of self-initiated activities. These included making arrests; conducting vehicle, pedestrian, and business checks; carrying out foot patrol; and other problem-solving techniques. The researchers found that directed patrol with these self-initiated activities reduced total firearm violence by 20 percent at the treatment area relative to the control areas. Firearm assaults decreased by about 55 percent, but there was no significant change in robbery using a firearm. However, the authors attributed their findings to the increased certainty of arrest and the increase in occupied-vehicle checks that resulted
from the self-initiated activities, not specifically from pedestrian checks or SQF.
Two randomized experiments in Philadelphia to examine the effects of foot patrol in small, violence-prone hot spots generated some valuable insights into the link between pedestrian stops (also called field investigations, many of which included frisks) and violent crime. While neither the Philadelphia Foot Patrol Experiment (Ratcliffe et al., 2011) nor the subsequent Philadelphia Policing Tactics Experiment (Groff et al., 2015) were designed to explicitly test the impact of SQF or pedestrian stops in particular, the association between pedestrian stops conducted by the foot patrol officers in both experiments is illuminating. In the first experiment, after 3 months violent crime was reduced by 23 percent in 60 randomly selected crime hot spots. The authors noted that whereas pedestrian stops changed by less than 1 percent in control areas, the intervention sites that had two groups of officers patrolling in pairs for 16 hours a day, 5 days a week, saw a 64 percent increase in pedestrian stops. In the intervention areas that demonstrated the clearest evidence of crime reduction, there was a “substantial jump in proactive activity for foot patrol officers” (Ratcliffe et al., 2011, p. 821).
In contrast, during the Philadelphia Policing Tactics Experiment, foot patrol officers in violent crime hot spots were unable to replicate the gains demonstrated in the Philadelphia Foot Patrol Experiment. The authors (Groff et al., 2015) noted a number of differences related to implementation and dosage. The later experimental areas were larger, foot patrol officers were veterans rather than rookies, and most of the foot patrol sites were only patrolled for 8 hours a day compared to 16 in the earlier experiment. All of this translated to differences in pedestrian stops, with no significant increases in police activity in foot patrol areas and a suggestion that “the veterans were less aggressive in their enforcement than the officers with less experience from the Philadelphia Foot Patrol Experiment who increased pedestrian and vehicle stops” (Groff et al., 2015, pp. 44–45). Thus, while there were implementation differences between the experiments, the first experiment’s foot patrol areas had substantial increases in pedestrian stops and proactive activity and were associated with significant crime-reduction gains.
Summary. Non-experimental analyses of SQF programs implemented as a general, citywide crime control strategy have found mixed outcomes. A separate body of experimental and quasi-experimental evaluation research examines the effectiveness of SQFs and other self-initiated enforcement activities by officers in targeting places with serious violence or gun crime problems and focusing on high-risk repeat offenders. Often, these studies do not specifically isolate the impact of SQF on crime. Evaluations of these
focused uses of enforcement tactics that have included pedestrian stops report meaningful and statistically significant crime reductions at targeted locations, though the estimated jurisdictional impact (when measured) has been modest.
As a proactive crime prevention strategy, community-oriented policing tries to address and mitigate community problems (crime or otherwise) for the future and build social resilience, collective efficacy, and empowerment to strengthen the infrastructure for the coproduction of safety and crime prevention. There can be overlap between community-oriented and problem-oriented policing programs, given that the community can be involved in specific problem-solving efforts. This overlap is not surprising, as the basic definitions of community policing used by police departments often include problem solving as a key programmatic element (see, e.g., Trojanowicz and Bucqueroux, 1994; Skogan and Hartnett, 1997).
Three extensive reviews of the crime-control impacts of community-oriented policing are worth mentioning. In an update to an earlier comprehensive review of crime-prevention programs (see Sherman, 1997), Sherman and Eck (2002) reviewed 23 studies on the effects on crime and victimization of community-oriented policing programs such as neighborhood watch, community meetings, door-to-door contacts, police storefronts (substations in the community), increasing information flow to citizens, and legitimacy policing (which is reviewed in the next section). The authors concluded that some community-oriented policing efforts were “promising” in reducing crime and victimization, such as those that increased community participation with planning and priority setting about specific crime problems or from door-to-door visits by the police. However, many other community-oriented policing approaches did not appear to be effective, such as monthly newsletters, education programs, or community meetings. The strongest research, which used randomized controlled trials to examine monthly community newsletters, education efforts, and home visits after domestic violence, found no statistically significant effects on crime reduction in the treatment condition compared with the control condition (Sherman and Eck, 2002).
The 2004 NRC study on policing (National Research Council, 2004) also reviewed the research on community-oriented policing and concluded that broad-based, community-oriented policing programs (i.e., community meetings, newsletters, education programs) generally do not reduce crime but may improve other important outcomes, such as citizen views of the po-
lice (see Chapter 5 of this report). Any observed crime-prevention impacts were more directly associated with other strategies such as problem-oriented policing, implemented within a community-based policing approach. That NRC study also included foot patrol as a community-based policing tactic.
A Campbell systematic review sponsored by the UK National Policing Improvement Agency identified 25 eligible studies, which evaluated 65 controlled tests of community-oriented policing programs (Gill et al., 2014). This review collected 114 eligible outcome measures across five types of outcome categories—citizen satisfaction, legitimacy of police, citizen perceived disorder, citizen fear of crime, and official crime and victimization. Forty-seven official crime and victimization outcomes across the 25 studies were identified. This systematic review only included studies with at least one comparison group or lengthy pre- and post-time series analysis, and only one study was identified as a randomized controlled trial. Of the 65 controlled tests of community-oriented policing programs, the authors were able to calculate odds ratios for 37 tests to be included in a meta-analysis. Their conclusion from this meta-analysis was that community-oriented policing programs had limited effects on crime.
These three reviews, across a period of more than two decades, seem to have arrived at similar conclusions. The direct impact of a community-oriented policing strategy (that is not focused necessarily on problem solving as discussed above) on crime prevention and control remains questionable. Further, evaluation studies on community-oriented policing continue to be carried out with only moderate levels of methodological rigor. Many of these studies compare nonrandomly constituted, large, and often noncomparable geographic areas with and without the program. Such studies suffer from low internal validity and insufficient statistical power, reducing the committee’s confidence in their results.
The committee confirmed these findings, based on the three major reviews discussed above, when we examined research in the Evidence-Based Policing Matrix (the “Matrix”), a continually updated tool on policing intervention studies (see Lum et al., 2011; Lum and Koper, 2017).4 The Matrix only includes evaluations that measure crime-control effects of policing interventions and uses inclusion criteria that are slightly more restrictive than the Gill et al. (2014) review. For example, the Matrix includes neither evaluations that use time series studies without comparison groups nor studies that compare an intervention in a neighborhood with larger, noncomparable units, such as the rest of the jurisdiction (see, for example, Esbensen , which is included in the Gill et al.  review but not in the Matrix). The Matrix also includes only those studies that show at
4 See also http://cebcp.org/evidence-based-policing/the-matrix/ [October 2017].
least some police involvement (so community activities to prevent crime that do not involve the police are not included).
We found 12 studies in the Matrix that meet the definition of community policing described by Gill and colleagues (2014) and that fall under our description of community-oriented policing as described in Chapter 2. The interventions evaluated by these studies included: (1) organizing residents and increasing community involvement in both setting priorities and determining responses to specific problems (Connell, Miggans, and McGloin, 2008; Giacomazzi, 1995; Lindsay and McGillis, 1986; Pate, McPherson, and Silloway, 1987; Tuffin, Morris, and Poole, 2006); (2) general increases in police contact with citizens, including door-to-door contacts, business checks, newsletters, and storefronts (Pate and Skogan, 1985; Wycoff et al., 1985); (3) community-based anti-gang initiatives (Cahill et al., 2008); (4) neighborhood watch (Bennett, 1990); and (5) a combination of many of these practices and tactics (Chicago Community Policing Evaluation Consortium, 1995). Of these 12, two studies used a randomized controlled experimental design (Pate et al., 1985a, in both Newark and Houston) and another two used rigorous quasi-experimental designs (Lindsay and McGillis, 1986; Pate, McPherson, and Silloway, 1987).
Pate and colleagues (1985a) examined two randomized controlled experiments, one in Newark, New Jersey, and one in Houston, Texas, on the impact of community newsletters on fear of crime and residents’ perceptions. Although this may not necessarily be a “community-involved” interaction, it does involve the police increasing communication with citizens, which is one of the foundations of community-oriented policing. In the case of Newark, three conditions were tested using random assignment: households that received a newsletter with local crime statistics, households that received a newsletter without local crime statistics, and households that were not mailed any newsletter. Findings indicated that those who were sent newsletters without crime statistics took significantly fewer crime prevention actions than those not sent a newsletter at all. In Houston, respondents in households that were sent newsletters regardless of whether crime information was included perceived a greater increase in crime than respondents not sent newsletters. Those who were given statistics also had increased levels of worry about victimization than those receiving newsletters without statistics. The study by Pate and colleagues (1985a) thus indicates that increased information to the community, in particular information about crime, may lead members to be less satisfied with police services and more fearful of crime. However, these studies did not measure the impact of newsletters on objective measures of crime or victimization; they only measured community perceptions thereof.
the other eight studies were more modest in methodological rigor. With regard to the two quasi-experimental studies, Pate, McPherson, and Silloway (1987) examined an intervention that used community block clubs, recruitment of community leaders, and other tactics for involving the community. In their evaluation, 21 neighborhoods were first matched on demographic and socioeconomic characteristics and then randomly allocated to one of three conditions: (1) police helping to organize block clubs and recruit community leaders; (2) in addition to organizing clubs and recruiting leaders, police officer activity included tactics such as officers attending block meetings, engaging in special control, and providing further services; and (3) an untreated control group. Neither of the two treatments were found to have a statistically significant impact on burglary. Lindsay and McGillis (1986) also attempted a relatively rigorous quasi-experimental design, in which they matched census tracts in Seattle, Washington, based on preprogram burglary rates. One tract in each matched pair received a community crime prevention program; the other tract did not. Their analysis of outcomes in treated and control tracts found that whereas paired tracts were very similar on burglary rates prior to the intervention, those that received the crime prevention program had significantly lower burglary rates post-intervention (2.45% in treated tracts versus 5.65% in controls). The pre- and post-burglary rates amounted to a 61 percent decline in burglary in treatment tracts, compared to 5 percent in control tracts. The authors also measured the impact of the intervention on displacing crime into adjacent census tracts and found no evidence of such displacement.
Of the eight studies that were more modest in methodological rigor, all but two found positive impacts on crime. These studies commonly compared one large area that was selected for treatment with another that was not selected. Whereas Bennett (1990) found no statistically significant impact of neighborhood watch on crime, and Cahill and colleagues (2008) found mixed results of the impact on crime of a gang reduction program, the other six studies all showed that the interventions reduced crime. However, as with previous reviews of evaluation studies, less confidence should be placed in these findings, given their less rigorous evaluation designs.
The difficulty in evaluating and assessing the evaluation research evidence on the crime prevention impacts of community-oriented policing interventions continues to stem from a number of challenges. Most importantly, studies on community-oriented policing are often carried out using less rigorous evaluation designs. This is likely due to many reasons, the first of which is that agencies often implement interventions before an evaluation plan can be properly designed, or they have less interest in evaluation than in implementation. Second, because community-oriented policing is both a general philosophy (logic model) of proactive policing and a strategy that is decentralized and locally shaped, it has resulted in a variety of activi-
ties—sometimes vague—that can be defined as “community oriented.” Interventions may include multiple components, the dosages of which may be difficult to identify, measure, and track when the intervention is evaluated. Further, because of the multifaceted characteristic of community-oriented policing, identifying the mechanism(s) or activity(ies) that contribute to a finding is also difficult. Was it, for instance, the community collaboration component that created the effect, or simply the police presence and crackdown? In some studies such as that by Koper and colleagues (2010; see also Koper, Woods, and Isom, 2016), which was included in the Campbell review (Gill et al., 2014) but was not among the 12 Matrix evaluations, the enforcement aspect of the intervention was more prominent, which likely led to the statistically significant findings, although the intervention could be considered community oriented. The size of the unit of analysis further complicates evaluations of community-oriented policing. Hot spots studies indicate that police can create deterrent effects when focusing on much smaller geographic units of analysis and tailoring efforts to those crime concentrations. Community-oriented policing, on the other hand, tends to be implemented in larger areas and neighborhoods, which might dilute its effects.
Summary. Overall, the committee did not identify a consistent crime-prevention benefit for programs using a community-oriented policing strategy, as that strategy is defined in Chapter 2. Research evaluations of such programs found mixed effects. Moreover, programs that showed significant outcomes often included tactics typical of other crime-prevention strategies, such as problem-oriented policing, that have been found to reduce crime outcomes. Empirical studies on community-oriented policing also tend to be characterized by relatively weak evaluation designs, although that is not true for all the evaluations reviewed here.
The manner in which police interact with citizens may have important consequences for citizen evaluations of whether they were treated fairly and with dignity and, more generally, for their trust in the police. These perceptions may in turn have behavioral consequences. One is whether citizens comply with any requests or orders made by police officers during encounters. There may also be behavioral outcomes beyond the immediate encounter. Among these is future willingness to cooperate with the police—for example, in providing information about crimes witnessed or reporting such crimes. This section examines the evidence on one specific but very important outcome: whether procedurally just treatment of citizens by the police increases the likelihood of citizens’ subsequent legal compliance. Al-
though, as we noted in Chapter 2, procedural justice advocates also argue that this approach will produce long-term crime-prevention gains in the community, such jurisdiction-level outcomes have not been examined to date. While procedural justice policing might be characterized as a person-based strategy, we include it among the community-based strategies because of its overarching objective of building community trust.
The largest part of the research on procedurally just treatment by the police and legal compliance is based on survey research in which people are asked questions about their perceptions of their procedurally just treatment by police on some or all of the dimensions delineated above, their overall perceptions of police legitimacy, and indicators of criminal offending. Offending is measured by either self-reports of past offending or future intentions to offend. Most surveys are cross-sectional, but a few are panel surveys, usually over two waves. Surveys also measure demographic characteristics of the respondents and their perceptions of factors that might also be associated with perceptions of procedurally just treatment, legitimacy, and/or indicators of offending. An example is respondents’ perceptions of sanction risk. These survey-based studies consistently find that perceptions of procedurally just treatment are positively associated with perceptions of legitimacy, generally of police themselves, net of association of other predictor variables in regression-based studies (Tyler, Schulhofer, and Huq, 2010; Wolfe et al., 2016; Hinds, 2007). With few exceptions (Augustyn, 2015; Cavanagh and Cauffman, 2015) these studies also find that perceptions of legitimacy are negatively associated with self-reported offending or intentions thereof (Fagan and Piquero, 2007; Reisig, Bratton, and Gertz, 2007; Jackson et al., 2012).
Do these associations credibly demonstrate a causal relationship whereby more procedurally just treatment by the police results in improved perceptions of that treatment, which in turn improves perceptions of police legitimacy, which in its turn increases legal compliance? Nagin and Telep (2017) point to four important shortcomings in the survey-based studies and the procedural justice literature more generally that stand in the way not only of credible inferences about causal connections down this envisioned chain of consequences but also the effectiveness of policies to promote procedural justice. These shortcomings can be stated as four limitations in the evidence for causation throughout the above set of hypothesized consequences: (1) The associations observed among the “links” in this supposed chain of consequences may be a reflection of third common causes (sometimes called “confounders”), of reverse causality, or of both. (2) Evidence for a causal link to perceptions of procedurally just treatment from actual treatment in procedurally just ways is very limited, and the constrained body of research draws contradictory conclusions. (3) Evidence on the effectiveness of policies such as training for promoting
procedurally just treatment by police is limited. (4) Evidence that such policies are effective in achieving their ultimate objective—crime reduction—is even more limited. These four shortcomings are discussed in turn below, drawing substantially from the more extended discussions in Nagin and Telep (2017). Following this discussion, the committee discusses earlier reviews by Mazerolle and colleagues (2012b, 2013b) that reach a somewhat different conclusion about the evidence, and we attempt to reconcile the difference in conclusions.
With respect to the first shortcoming, it is important to recognize that perceptions of procedurally just treatment by the police cannot be directly manipulated in a social science experiment. What can potentially be manipulated for the sake of experimentation is the way police treat citizens. This principle has fundamental implications for both causal inference and policy. Concerning causal inference, a key requirement for making credible causal inferences about the effect of procedurally just treatment on legal compliance is that treatment including policy manipulation can credibly be assumed to be exogenous: for example, a policy change as a treatment condition within a randomized experiment or a policy change that is not a direct response to a spike in citizen dissatisfaction with the police or an uptick in crime. Without such exogenous change, the statistical associations observed among perceptions of procedurally just treatment, legitimacy, and legal compliance may reflect third common causes and/or reverse causality, rather than the causal effect of procedurally just treatment on legal compliance that is assumed by the logic model for the procedural justice policing strategy.
Two examples of credible third common cause explanations for statistical associations among procedural justice treatment, legitimacy perceptions, and legal compliance involve social control–based theories and community context. Individuals with larger “stakes in conformity” (Toby, 1957) or with investments in conventional social bonds (Hirschi, 1969) may not only be more legally compliant but may also perceive that agents of the criminal justice system treat them more fairly and are more legitimate. No study we know of accounts either for the independent effect of such factors on legal compliance or, more generally, for the compliance effect of moral commitments to abide by the law. Likewise, the legacy of ill treatment of disadvantaged non-Whites, particularly Blacks, compared to Whites by the police may negatively affect their perceptions of their treatment by the police, independent of their personal experience with police who are trying to be procedurally just. Again, parsing out the effect of procedurally just treatment from the independent effect of legal socialization arising from community context is extraordinarily difficult.
Reverse causality may also account for the measured associations: for example, it may be that legal compliance affects perceptions of legitimacy
and procedurally just treatment, rather than the reverse. One possible form of reverse causality is referred to as “neutralization” (Sykes and Matza, 1957), a situation in which offending is rationalized by the offender as a justified response to poor treatment by the police. More generally, police-community relations are bilateral, with each side affecting the behavior of the other. Just as citizens are reacting to their treatment by the police, so the police are responding to the behavior of citizens. Sorting out the extent to which each party is reacting to the other in this context is extremely difficult.
The committee identified only one study that assessed the association between perceptions of procedurally just treatment and actual treatment as assessed by third parties. Worden and McLean (2014) compared citizen perceptions of their treatment in 539 recorded encounters with the police that were later assessed by trained observers. The correlation of citizen perceptions of procedurally just treatment (e.g., was the citizen given the opportunity to explain themselves?) and the observer’s assessment of such treatment as just was only 0.12. Interestingly, the correlation of perceptions and observers’ assessments of unjust treatment (e.g., was the citizen treated disrespectfully?) was much larger and negative, −0.31. The latter finding is consistent with a small body of studies involving third-party observers of police–citizen encounters in which Mastrofski, Snipes, and Supina (1996, p. 296) conclude: “Our police may be able to do little to enhance their cause but a great deal to hurt it.”
Experimental work by Mazerolle and colleagues (2012b, 2013b), MacQueen and Bradford (2015), and Sahin and colleagues (2016) involved manipulation of officer behavior through a script or protocols that were randomly assigned to the officers for use during traffic stops or in an airport screening process. These studies thus provide an opportunity to compare citizen perceptions with what officers were supposed to do in encounters. In each study, the experimental script/protocol was infused with concepts from procedural justice theory, whereas the control script/protocol was “business as usual.”
These studies reached conflicting conclusions. Mazerolle and colleagues (2012b, 2013b) concluded that the experimental treatment increased citizen perceptions of the fairness of their treatment at the encounter and police legitimacy overall. Sahin and colleagues (2016) found a salutary effect for the encounter itself but not for overall confidence in the police. MacQueen and Bradford (2015) found a backfire effect in which the experimental treatment resulted in more negative views of the encounter and the police more generally. We also note that these experiments were conducted in a very controlled setting in which the potential for hostile interaction was low and that response rates to post-treatment surveys mailed to study partici-
With respect to the third shortcoming listed above, research on the effectiveness of policy intended to promote procedurally just practice by police pertains mostly to training. Rosenbaum and Lawrence (2013) report the findings of a randomized experiment involving Chicago police officers that tested the effectiveness of the Quality Interaction Program (QIP). Results based on pre and post surveys of study participants found no statistically significant impact of the training on officer respect toward civilians or on perceptions of the importance of quality of treatment at traffic stops. By contrast, officer behavior in the videotaped scenarios showed a statistically significant treatment effect in which officers receiving the additional training were more likely to demonstrate respectful and supportive behavior. However, the post-training sample of videotaped officers was very small (n = 34).
Skogan, Van Craen, and Hennessy (2015) examined the effects of the Chicago Police Department’s day-long training program on procedural justice. The program, distinct from the QIP but based on similar principles, included five modules that focused on legitimacy, procedural justice, cynicism, and race. More than 9,000 officers received the in-service training. Based on a comparison of pre- and post-training survey data of participating officers, post-training officer endorsement of various indicators of procedurally just treatment increased. A second, less rigorous analysis found evidence that these effects were sustained longer term.
Robertson and colleagues (2014) examined the effectiveness of a program in Scotland similar to Chicago’s QIP program. The study examined a nonrandomized group of 95 police recruits who received nine sessions of procedural justice training over 12 weeks and 64 control-group officers. The survey-based findings were mixed; the treatment group officers had improved scores in communication skills but decreased score on the item “people should be treated with respect, regardless of their attitude.” In scenarios, officers receiving treatment were more likely to score “good” than the control group officers in terms of their use of procedural justice in practice, but the difference was not statistically significant.
None of these studies examined actual officer behavior in the field, but two recent randomized trials do so. One took place in Manchester, United Kingdom, where Wheller and colleagues (2013) randomly allocated officers to one of three treatment groups differing in the duration and content of procedural justice training or to a comparison group receiving no procedural justice training. Small sample sizes made it difficult to differentiate among treatments. As with the Chicago evaluations, after training, officers in the treatment group significantly improved on some indicators of interest (e.g., building empathy and rapport, fair decision making), but not others
(e.g., perceived value of procedural justice and perceived level of public cooperation). This study went on to evaluate behavior in the field, but only toward victims, not suspected perpetrators. There were some positive impacts of the training on victim perceptions, although these effects were neither consistent across measures of procedurally fair treatment nor large in magnitude. Owens and colleagues (2016) examined the impact of randomly assigned procedural justice–infused training on officer behavior. Officers assigned the treatment were less likely to resolve incidents with an arrest and were less likely to be involved in incidents where force was used.
In summary, knowledge about the effectiveness of procedural justice training is limited and findings are not consistent across studies. However, the results of the Wheller and colleagues (2013) and Owens and colleagues (2016) studies provide encouraging signs of effectiveness in altering officer behavior in the field. Evidence of such effectiveness is important because unless policies can be devised that reliably change behavior of police officers in their delivery of procedurally just treatment, the predicted benefits of such treatment will be out of reach.
Finally, with respect to the fourth shortcoming in the evidence base, only two studies provide indirect tests of the effect of procedurally just treatment on those citizens’ legal compliance. One is an outgrowth of a domestic violence experiment; the other involves a gun violence intervention in Chicago. The domestic violence study by Paternoster and colleagues (1997) used data from the Milwaukee domestic violence experiment (Sherman et al., 1992), in which police responding to misdemeanor domestic violence calls for service randomly assigned suspects between mandatory arrest and non-arrest conditions. For those who were arrested, Paternoster and colleagues (1997) created a survey based on indicators of perceived procedurally just treatment and administered the survey at the time of their booking of the suspects from either treatment group who were arrested. They found that individuals who perceived greater procedurally just treatment were less likely to recidivate for domestic violence.
There are two important limitations of this study that stand in the way of interpreting this finding as a causal association. Both follow from the prior discussion. First, procedurally just treatment was not randomly assigned or exogenously manipulated in any way. Second, there were no third-party observers assessing officer treatment. Measures of procedurally just treatment were based solely on the arrestees’ perceptions, which, for reasons previously discussed, may not be closely tied to actual treatment and may also be related to recidivism due to unobserved characteristics of the arrested individual.
Wallace and colleagues (2016) examined the impact on recidivism of offender notification forums infused with procedural justice. The forums were implemented as part of a Project Safe Neighborhoods intervention in
Chicago. The forums lasted 1 hour and sent a message to individuals recently released from prison with a history of violence that further violence would no longer be tolerated. The message was explicitly designed to focus not only on deterrence but also on emphasizing individual choice, respect, and fairness. The evaluation of this intervention compared re-incarceration rates between parolees in two police districts receiving forums to parolees in two comparison districts where there were no forums. Hazard models suggest a significant intervention effect both within neighborhoods (i.e., comparing forum attenders to non-attenders in the same precinct) and between neighborhoods (i.e., comparing forum attenders to non-attenders in comparison precincts). Parolees attending a forum had a longer time on the street (and out of prison), on average, than non-attendees (as described above, a 30% reduction in recidivism). Additionally, forum attendees had lower hazards of committing weapons offenses or murder compared to non-attendees. Effects for violent crime overall and violent property crime were less consistent.
This study (Wallace et al., 2016) is important because it analyzed the impact of an actual policy intervention that addressed a serious crime problem and that was directed at individuals with extensive criminal histories. The difficulty of interpretation involves extracting the contribution of procedural justice to a multipronged intervention involving focused deterrence and access to social service components as other prominent features of the intervention package. Interventions such as this are exemplars of the more general challenge of parsing out the contribution of any one component of a complex intervention, especially in circumstances where the component parts are so heterogeneous. We also note that because participation in the forums was not randomly assigned, the observed associations may be contaminated by selection bias.
The conclusion of our review with respect to the four shortcomings in the evidence base is that the well-documented association of perceptions of procedurally just treatment by police and/or perceptions of police legitimacy with legal compliance, while consistent with a causal linkage across these factors, has many other possible noncausal interpretations that the evaluation designs do not rule out. Further, from a policy perspective, evidence is extremely limited for the effectiveness of training or other policy levers in affecting police behavior vis-à-vis procedural justice.
Our conclusions differ from the more affirmative conclusions of Mazerolle and colleagues (Mazerolle et al., 2012a, 2013a; Higginson and Mazerolle, 2014). We attribute the difference to several factors. First, the reviews by Mazerolle and colleagues examined studies only through April 2010.
Second, they included any study that met other technical inclusion criteria and that stated that one of its purposes was to improve police
legitimacy or that articulated an objective consistent with Tyler’s conception of procedurally just treatment.5 Their expansive inclusion criteria for studies that constitute a test of procedural justice policing (as this committee uses the term) have several important consequences. One is that their meta-analysis leaves unspecified the sources of perceptions of legitimacy. Definitions of what constitutes procedurally just treatment vary across studies. For example, Bottoms and Tankebe (2012, p. 129) argue that it is the quality of dialogue between the citizen and the police officer that is crucial: “legitimacy needs to be perceived as always dialogic and relational in character.” Such a difference in emphasis is important because that difference is crucial not only to pinning down and testing the sources of perceptions of legitimacy but also to designing policies that are effective in promoting legitimacy.
A second consequence of an expansive inclusion criterion is that the legitimacy enhancement objective was only one among many objectives of the interventions included in the review. Thus, while the committee’s discussion above focused on interventions designed to enhance procedural justice through scripts or training, the reviews by Mazerolle and colleagues (2012a, 2013a) included a variety of intervention types, including community-oriented policing, Weed and Seed programs (which include a variety of elements design to “weed” a community of criminal and disruptive influences such as gangs and “seed” pro-social influences), and restorative justice (see Higginson and Mazerolle, 2014). These practices include elements of procedural justice policing but also cover a far broader range of activities than is implied by the definition of procedural justice used by this committee. As a consequence, it is difficult to sort out what part of program benefits are attributable to the procedural justice component of the intervention or practice (Cook, 2015).
Summary. There is a lack of rigorous program evaluations that directly test whether procedural justice policing can reduce crime and disorder. Prior reviews of impact evaluations have included multifaceted programs comprising a broad range of other crime prevention activities that go well beyond procedural justice policing. It is therefore difficult to isolate any crime prevention benefits associated with this approach.
5Tyler’s (1990) hypothesis about the effect of procedural just treatment in improving citizens’ compliance with the law is noted at the beginning of this chapter, in the initial discussion of the logic model for procedural justice policing.
As described in Chapter 2, broken windows policing is a strategy for a community-based approach to proactive policing that developed from Wilson and Kelling’s (1982) propositions about the relationship between disorder and crime. Disorder includes social incivilities (e.g., public drinking, loitering, and prostitution) as well as physical incivilities such as trash accumulations in public areas, vacant lots, and abandoned buildings. If disorder is a cause and not just a correlate of serious crime, Wilson and Kelling (1982) argued, then proactive suppression of disorder would yield another even more important benefit than just improving social order: it would reduce serious crime. This line of reasoning became the rationale, or logic model, supporting broken windows policing tactics.
Broken windows policing is controversial for two reasons. First, the underlying hypothesis of a causal linkage between disorder and serious crime was unproven, even as it spawned an era of greatly expanded policing against disorder in New York City and many other large U.S. cities. Second, the most common implementation of the strategy has been aggressive policing against disorder that involved making large numbers of arrests for minor crimes and expanding the issuance of summons for even less serious legal infractions.
Since the appearance of the Wilson and Kelling (1982) paper, a modestly sized body of research has been conducted addressing the causal linkage between disorder and serious crime or the effectiveness of aggressive policing against disorder in reducing serious crime. We review the research on these two facets of the logic model in turn.
With regard to the causal relationship between disorder and crime hypothesized by Wilson and Kelling (1982), the evidence is mixed. While there is strong evidence that places that have more disorder also tend to have more serious crime, what is uncertain is whether the correlation of crime and disorder across places and also over time is a reflection of a common set of underlying causes, such as poverty, social disorganization, or even ineffective policing,6 or whether the relationship is causal—specifically in the direction that disorder begets serious crime. Empirically distinguishing these alternative explanations for the correlation of crime and disorder has proven difficult.
Studies of the effect of urban blight or disorder on crime have yielded differing conclusions. For example, Skogan (1990) examined the association of neighborhood disorder with robbery victimization and concluded there was a causal relationship, but Harcourt’s (2001) reexamination of
6 This issue is thus another instance of the “third common cause” or confounder problem that we discussed with respect to the evidence base for the causal linkage presumed in the logic model for procedural justice policing (see previous subsection).
Skogan’s data found no comparable association for other crimes such as assault, burglary, or rape. He concluded, therefore, that there was no causal relationship. Eck and Maguire (2006) critiqued Harcourt’s findings, suggesting that they were based on removing those neighborhoods in Skogan’s analyses that had high disorder and crime relationships. Another study by Keizer, Lindenberg, and Steg (2008) that used a number of field experiments found a causal link from disorder conditions to crime, especially when disorder conditions were allowed to spread or linger. Freedman and Owens (2011) used plausibly exogenous changes in the funding formula for the Low Income Housing Tax Credit program as a source of controlled variation in neighborhood disorder. They found that improving the quality of housing in low-income places can cause reductions in violent crime (homicide, rape, robbery, and assault) at the county level, although they found no substantive impact on property offenses (burglary, larceny, auto theft, and arson).
Taylor (2001) used a longitudinal analysis of disorder and crime in 66 Baltimore neighborhoods to support a conclusion similar to Harcourt (2001). Similarly, Sampson and Raudenbush (1999) found that once neighborhood characteristics were taken into account, the association between crime and disorder, including the association for homicide, vanished. This finding is notable because disorder was measured in their analysis based on systematic observation by trained observers. They concluded: “Rather than conceive of disorder as a direct cause of crime, we view many elements of disorder as part and parcel of crime itself” (Sampson and Raudenbush, 1999, p. 638). They also observed that “Attacking public order through tough police tactics may thus be a politically popular but perhaps analytically weak strategy to reduce crime” (Sampson and Raudenbush, 1999, p. 638). Yang (2010), using a longitudinal approach, also questioned a direct and consistent causal link from disorder to crime.
A different conclusion is reached in an evaluation of a citywide blight-reduction project in Philadelphia to remediate abandoned buildings and clean up abandoned lots during the period from 1999 to 2013. More than 5,000 buildings and lots were remediated during that time, and the effect on crime was evaluated by Branas and colleagues (2016). They described the lot clean up this way:
Remediation involves removing trash and debris, grading the land, planting grass and trees to create a park-like setting, and installing low wooden post-and-rail fences with walk-in openings around each lot’s perimeter to show that the lot was cared for, permit recreational use, and deter illegal dumping. Landscapers return approximately once each month to perform basic maintenance. (Branas et al., 2016, p. 2159)
The authors compared changes in local assault rates in treated places with a matched sample of places that were eligible for treatment but did not receive it. The results for the remediation over the first year were a 4.5 percent reduction in gun assault and 2.2 percent reduction in overall assault rate, both highly significant statistically. The remediation treatment also conveyed social benefits that exceeded costs. Nonetheless, drawing inferences from this quasi-experiment is limited because the assignment of the treatment was not in any sense exogenous but rather a choice made by owners (for private lots and buildings). It is unfortunate, in retrospect, that the treatment condition was not assigned in a fashion that would permit stronger inferences about causation. Nonetheless, the findings support a finding that there needs to be stronger experimental research done in this area before one can draw strong conclusions about the causal direction of the disorder/crime relationships.
Alongside this literature of mixed findings about a causal relationship between disorder and crime, just as important in the police context is how the broken windows logic model has translated into police practice and whether those practices are effective in reducing crime. (This is the second facet of the broken windows logic model on which limited evidence exists.) As Braga, Welsh, and Schnell (2015) pointed out, policing to counter disorder can take various forms. The two most common (separately or in combination) have been the use of aggressive policing that uses misdemeanor arrests to disrupt disorderly social behavior and the use of problem-oriented or community-oriented policing practices to address disorderly conditions that are hypothesized to contribute to crime.
With regard to the effect of increased misdemeanor arrests in reducing violent crimes, Kelling and Sousa (2001) used precinct-level data from New York City to examine whether higher rates of misdemeanor arrest were associated with lower levels of crime, after taking account of other characteristics of the precincts. They concluded that aggressive misdemeanor arrests prevented more than 60,000 violent crimes between 1989 and 1998, or a statistically significant 5 percent reduction in violent crime. Kelling and Sousa (2001, p. 9) noted, “the average NYPD [New York City Police Department] precinct during the ten-year period studied could expect to suffer one less violent crime for approximately every 28 additional misdemeanor arrests made.” Corman and Mocan (2005), who also analyzed New York City data, reached a similar conclusion.
Balanced against these findings is a study by Rosenfeld, Fornango, and Rengifo (2007), which found smaller effects of increased misdemeanor arrests on crime incidence, and studies by Fagan and Davies (2003) and Harcourt and Ludwig (2005) that found no evidence of a statistically significant effect. The Harcourt and Ludwig (2005) study is notable because it includes an analysis of data that uses a similar regression technique on
the same dataset used by Kelling and Sousa (2001). Specifically, both studies examined police precinct–level data from New York City for the years 1989 to 1998 and used panel regression methods to estimate the causal contribution of misdemeanor arrest rates to violent crime rates. Harcourt and Ludwig concluded that the substantial crime prevention effect identified by Kelling and Sousa (2001) may be no more than regression to the mean.7 Specifically, they found that the largest increases in misdemeanor arrest rates occurred in those precincts with the largest increase in violent crime in the 1980s and that subsequently these same precincts experienced the largest decrease in crime for reasons unrelated to intensive misdemeanor policing. We note that this Harcourt and Ludwig (2005) critique of Kelling and Sousa (2001) pertains to all the studies based on non-experimental data: the misdemeanor arrest rate in some time period may be driven by the overall crime rate prior to that period, which makes it difficult to distinguish whether the association is a reflection of increased arrest rate causing decreased crime rate, a change in crime rate causing a positively correlated change in arrest rate, or neither of these causal connections occurring consistently over times and places.
Another important shortcoming of these types of studies is that they do not account for the intensity of use of other policing tactics that may also be affecting crime and thereby biasing the estimated impact of the misdemeanor arrest rate in unknown ways. We note that this shortcoming is not the fault of the authors of these studies because data measuring the intensity of use of other policing tactics is not available.
The relationship between misdemeanor arrests and crime has also been studied using experimental and quasi-experimental methods. Two recent meta-analyses of the studies by Braga, Welsh, and Schnell (2015) and Weisburd and colleagues (2015) reach the conclusion that broken windows policing based on increasing the misdemeanor arrest rate is not effective in reducing serious crime. The Braga, Welsh, and Schnell (2015) review also includes studies of interventions that aimed to reduce disorder not by aggressive policing against disorder but by tactics typically used for community-based and problem-solving approaches and designed to change social and physical disorder conditions at particular places. The review authors found that these tactics did have a modest crime-reduction effect.
The Braga, Welsh, and Schnell (2015) review is important because it also speaks to different approaches to policing practices aimed at reducing
7 In this context, regression to the mean refers to the police responding to a random increase in crime at a specific location by increasing the intensity of misdemeanor arrest activity at that location. If crime subsequently subsides at that location, the decline may be in whole or in part attributable to crime randomly returning to its normal level (regressing to the mean) rather than to the increased police activity.
disorder, practices that this report considers as exemplifying the community-based and problem-solving approaches (see Chapter 2). The authors identified a diverse group of 30 controlled tests of police-led interventions to control crime by reducing social and physical disorder, 21 of which used quasi-experimental designs (70%), while 9 used randomized experimental designs. Units of analysis included small places (such as crime hot spots and problem buildings; 46.7% of the tests), small police-defined administrative areas such as patrol beats (26.7% of the tests), neighborhoods and selected stretches of highways (13.3% of the tests), and larger police-defined administrative areas such as precincts and divisions (13.3% of the tests). Twenty evaluations tested the impact of community-based/problem-solving interventions largely designed to change disorderly conditions in places; 10 evaluations tested the impact of aggressive order-maintenance tactics intended to control problem behaviors of disorderly individuals in the areas targeted for treatment. Given the broad definition of “policing disorder” (i.e., policing that is intended to decrease disorder) used by the authors, it is important to note that many of the studies they reviewed appear in other sections of this chapter (e.g., Braga and Bond  is discussed in the problem-oriented policing section; Pate and Skogan  is discussed in the community-oriented policing section; Weisburd et al. [2006b] is discussed under hot spots policing).
We noted above that an important limitation in the studies on the effect on crime rate of increased misdemeanor arrests is that those studies lacked controls for other policing tactics and practices that were being used in conjunction with the tactic of increasing misdemeanor arrests and that might also be affecting the crime rates observed. Interpretation of the results found in the experimental and quasi-experimental studies reviewed by Braga, Welsh, and Schnell (2015) is complicated by another form of this problem: how to parse out the causal contribution of the “broken windows” component of the intervention from the contribution from other components of an intervention intended to reduce disorder. Further complicating matters, as Weisburd and colleagues (2015) emphasized, is that discerning the mechanism by which order-maintenance policing might reduce the more-serious crimes is extremely difficult. We also note that studies included in the Braga, Welsh, and Schnell (2015) meta-analysis are very heterogeneous in terms of the character of interventions and the size of the city or town in which they took place. As that review’s authors suggest, such heterogeneity raises concerns about the interpretability of an effect size that is an amalgam of results from such diverse studies (Braga, Welsh, and Schnell, 2015, pp. 572–573).
Summary. The scientific evidence on the effects of broken windows policing on crime is mixed. In general, the available program evaluations sug-
gest that aggressive practices based solely on increasing the misdemeanor arrest rate to control disorder generate small to null impacts on crime. The better-controlled evaluations of hybrid interventions that incorporate practices typical of place-based and problem-solving approaches in order to reduce social and physical disorder have found consistent short-term crime-reduction effects from the entire intervention. However, the study designs do not allow the contributions of specific tactics to be parsed out from the overall effect of the hybrid intervention.
This review has focused on the effectiveness of several policing strategies that are proactive in the sense that they are anticipatory responses to problematic crime patterns, rather than routine and reactive responses to calls for service. The primary goal of proactive policing is crime prevention, and assessing the evidence that these strategies reduce crime has been the focus of this chapter. Other potential outcomes, such as improving the public’s perception of the police, are considered in the chapters that follow.
The committee’s review of the evidence base focused on evaluations of real-world interventions that were developed and conducted by police departments. While the evidence generated by these interventions is far from complete or definitive, the past three decades have been something of a “golden age” for the production of systematic evidence on what works. The police, more than other criminal justice agencies, have been amenable to running field experiments, and even non-experimental interventions are better documented than in the past, due to the increasing quality and quantity of data on crime and police activities. Although the available evidence still has important gaps and contradictions, this recent trend in research is favorable to the ultimate goal of evidence-based crime policy.
One challenge in developing or reviewing this evidence base is the overlap of the approaches as we defined them in Chapter 2. These approaches were defined to distinguish the key underlying logic models for different strategies. In practice, the broad approaches and the strategies for them, as delineated here and in Chapter 2, are not mutually exclusive, and each of them has fuzzy boundaries when it comes to classifying specific actual programs and interventions used by police organizations. For example, a project to clean up vacant lots that facilitate drug dealing may originate from an intervention plan that could reasonably be said to involve community-oriented policing, problem-oriented policing, or broken windows policing—three proactive policing strategies with separate sections in this chapter. Our review acknowledges these potential ambiguities and overlaps.
A second challenge in assessing the evidence, as discussed above, is that most real-world interventions are quite complex and may include elements
of several strategies, as those strategies are defined in this report. For example the Weed and Seed programs funded by DOJ have been used to assess the impact of “legitimacy policing” on crime, but each of those programs has also included elements of community-oriented policing, neighborhood restoration, and stepped-up law enforcement (Higginson and Mazerolle, 2014; Cook, 2015). Separating out the effect of the “legitimacy” element from the others is not possible, given that each program was implemented as a bundle.
Many of the evaluations to date have been short term, examining crime-prevention outcomes for no more than 1 or 2 years, and often less. Some proactive policing programs have had only short-term goals, for example, suppressing crime in high-crime areas such as hot spots. However, others do not have just short-term goals, but our knowledge base is focused on short-term, rather than long-term, gains among people, places, or communities. Similarly, many of the interventions in the literature examined by the committee are focused on places, and place is a key feature of some interventions whose underlying logic model comports more closely with a community-based, person-focused, or problem-solving approach (as these approaches are defined in this report). In this context, issues of whether crime is displaced to areas nearby are common in evaluations and are reflected in their study designs. However, very little is known about distal displacement of crime across a jurisdiction. Nor are there estimates of jurisdictional impacts for key strategies such as hot spots policing, problem-oriented policing, third party policing, and procedural justice policing. In Chapter 8, the committee provides suggestions on filling these and other knowledge gaps.
Finally, while the evidence base has grown dramatically over the past decade, the interventions that the committee examined are often limited to specific contexts. In some cases—for example, hot spots policing—we had a large enough number of evaluations to draw more general conclusions that are likely to apply in different types of cities in different circumstances. Accordingly, by necessity our discussion of the quality of evidence in this chapter has referred more to the credibility of the design in drawing causal statements about a program’s outcomes than to reasonable extrapolation of those outcomes across different settings. As we note in Chapter 8, much more work needs to be done before one can provide specific policy prescriptions about the use of the approaches this committee reviewed.
With these challenges and caveats as context, the committee has drawn a series of conclusions about the effectiveness of proactive policing strategies in reducing crime and disorder, offered with the proviso that the state of the art is constantly developing. We summarize the key findings below in Table 4-1. Note that “broken windows” and “stop, question, and frisk” are divided into two subcategories, reflecting broad differences in practices
|Policing Strategy||Principal Mechanisma||Strength of Evidence (study design, replication)b||Do Strong Studies Find Significant Positive Effects?||Concerns|
|Hot Spots Policing
Example: Concentrated patrol of microgeographic high-crime places
Example: Data-intensive algorithm for predicting near-term crime in hot spots
|Deterrence||Weak||Mixed||Not yet well defined|
|CCTV (type I)
Example: Passive monitoring of cameras in high-crime area
|CCTV (type II)
Example: Proactive camera surveillance linked to dedicated operational police response
|Deterrence (specific)||Weak||Yes (but only one study)||Only one intervention studied|
Example: Close taverns that have frequent violence
|Opportunity Deterrence||Medium||Yes||Only a small number of potential implementations have been studied|
|Third Party Policing Example: Police coordinate with private security in a Business Improvement District||Opportunity Deterrence||Medium||Yes|
|Focused Deterrence Policing
Example: Police department “calls in” a gang and delivers a personalized “carrot and stick” message
|Deterrence||Medium||Yes||No RCTs, but evidence base includes strong quasi-experiments|
|Stop-Question-Frisk (type I)
Example: High-volume Terry stops throughout jurisdiction
|Stop-Question-Frisk (type II)
Example: High-volume Terry stops in violent-crime hot spots
|Deterrence||Strong||Yes||Studies are confounded with hot spots policing practices, one RCT|
Example: Neighborhood watch, newsletters, and community meetings
|Collective efficacy||Weak||No||Broad category, not well defined|
|Policing Strategy||Principal Mechanisma||Strength of Evidence (study design, replication)b||Do Strong Studies Find Significant Positive Effects?||Concerns|
|Procedural Justice Policing
Example: Train police to improve interactions with public
|Legitimacy||Weak||Mixed||Evaluated interventions typically include tactics from other strategies, so effect of procedural justice component is not determinable|
|Broken Windows Policing (type I)
Example: High-volume arrests for certain misdemeanors
|Broken Windows Policing II (type II)
Example: Clean up vacant lots
|Deterrence, Opportunity, Collective efficacy||Strong||Yes||Evaluations to date do not allow identification of whether impact is due to collective efficacy or deterrence|
NOTES: RCT = randomized controlled trial.
Deterrence: Increase perceived and/or actual likelihood of arrest if an offense is committed.
Opportunity: Curtail availability of attractive opportunities to commit crime.
Legitimacy: Improve community perception of the legitimacy of police actions or of the police force generally.
Collective efficacy: Increase the willingness of citizens to intervene and accordingly strengthen informal social controls.
bStrength of causal evidence:
Weak: Available evaluations have weak design and/or are sparse.
Medium: A few well-done studies done in different contexts with research designs that provide a strong basis for drawing causal conclusions.
Strong: A number of well-done studies conducted in varying contexts with research designs that provide a strong basis for drawing causal conclusions.
within these strategies that lead to differing impacts. Each strategy is described according to which of three mechanisms, hypothesized to potentially reduce crime rates, may apply to that strategy: (1) an increase in the perceived or actual probability of arrest, which would potentially reduce crime rates through deterrence or incapacitation; (2) a reduction in access to or profitability of criminal opportunities; and (3) increases in collective efficacy or police legitimacy. Each strategy-category is then assessed according to the strength of the evidence that at least some of the real-world programs in that category have reduced crime. That assessment is a one-word summary of the much more nuanced discussion in the chapter text and the numbered conclusions below. The last two columns of the table note whether studies found significant positive outcomes for the strategy and any specific concerns of the committee regarding the studies’ designs or results.
The committee found particularly strong evidence for proactive policing programs that take advantage of the strong concentration of crime at crime hot spots. A number of rigorous evaluations, including a series of randomized controlled trials, of hot spots policing programs have been conducted.
CONCLUSION 4-1 The available research evidence strongly suggests that hot spots policing strategies produce short-term crime-reduction effects without simply displacing crime into areas immediately surrounding targeted locations. Hot spots policing studies that do measure possible displacement effects tend to find that these programs generate a diffusion of crime-control benefits into immediately adjacent areas. There is an absence of evidence on the long-term impacts of hot spots policing strategies on crime and on possible jurisdictional outcomes.
In contrast, we could not draw a strong conclusion regarding predictive policing, which draws directly on the insights of hot spots policing but seeks to develop more sophisticated predictive tools.
CONCLUSION 4-2 At present, there are insufficient rigorous empirical studies on predictive policing to support a firm conclusion for or against either the efficacy of crime-prediction software or the effectiveness of any associated police operational tactics. It also remains difficult to distinguish a predictive policing approach from hot spots policing at small geographic areas.
The evidence suggests that the use of CCTV, absent a dedicated operational response on the ground, may be more effective at reducing vehicle crime and less effective at combating violence, though the way the system is implemented and used appears to be important in achieving any crime reduction. There are insufficient studies with regard to proactive use of CCTV with dedicated operational resources to draw any firm conclusions.
CONCLUSION 4-3 The results from studies examining the introduction of closed circuit television camera schemes are mixed, but they tend to show modest outcomes in terms of property crime reduction at high-crime places for passive monitoring approaches.
CONCLUSION 4-4 There are insufficient studies to draw conclusions regarding the impact of the proactive use of closed circuit television on crime and disorder reduction.
There is promising evidence regarding problem-oriented policing programs. Much of the available evaluation evidence consists of non-experimental analyses that suggest strong effects in reducing crime; randomized experimental evaluations generally show smaller, but statistically significant, crime reductions generated by problem-oriented policing programs.
CONCLUSION 4-5 There is a small group of rigorous studies of problem-oriented policing. Overall, these consistently show that problem-oriented policing programs lead to short-term reductions in crime. These studies do not address possible jurisdictional impacts of problem-oriented policing and generally do not assess the long-term impacts of these strategies on crime and disorder.
While there are only a small number of program evaluations of third party policing, the impact of third party policing interventions on crime and disorder has been assessed using randomized controlled trials and rigorous quasi-experimental designs.
CONCLUSION 4-6 A small but rigorous body of evidence suggests that third party policing generates short-term reductions in crime and disorder; there is more limited evidence of long-term impacts. However, little is known about possible jurisdictional outcomes.
The results from evaluations of these offender-focused proactive policing programs, which capitalize on the concentration of crime among a subset of criminals, indicate that this approach does reduce crime rates. A growing number of quasi-experimental evaluations suggest that focused deterrence programs generate statistically significant crime-reduction impacts. While there have been no randomized experiments, and only a few of the quasi-experimental designs are rigorous, the programs from the stronger (as well as the weaker) designs show consistent outcomes.
CONCLUSION 4-7 Evaluations of focused deterrence programs show consistent crime-control impacts in reducing gang violence, street crime driven by disorderly drug markets, and repeat individual offending. The available evaluation literature suggests both short-term and long-term areawide impacts of focused deterrence programs on crime.
SQF programs have generated much controversy. Non-experimental analyses have examined the impact of SQF when implemented as a general, citywide crime-control strategy. A separate body of controlled evaluation research examines the effectiveness of SQF in targeting places with serious gun crime problems and focusing on high-risk repeat offenders.
CONCLUSION 4-8 Evidence regarding the crime-reduction impact of stop, question, and frisk when implemented as a general, citywide crime-control strategy is mixed.
CONCLUSION 4-9 Evaluations of focused uses of stop, question, and frisk (SQF) (combined with other self-initiated enforcement activities by officers), targeting places with violence or serious gun crimes and focusing on high-risk repeat offenders, consistently report short-term crime-reduction effects; jurisdictional impacts, when estimated, are modest. There is an absence of evidence on the long-term impacts of focused uses of SQF on crime.
The committee’s findings regarding community-based interventions provide less optimism for the impacts of strategies using this approach to reduce crime and disorder. Overall, we did not identify a consistent crime-prevention benefit from community-oriented policing programs. Studies report mixed effects, and community-oriented policing programs often include tactics typical of other crime-prevention strategies, such as problem-
oriented policing, that can be seen to generate crime control impacts when they are observed in isolated application. The empirical studies to date on community-oriented policing also tend to have weak evaluation designs. There are even fewer rigorous program evaluations that directly test whether procedural justice policing is associated with crime and disorder reductions. Prior reviews of impact evaluations have included multifaceted programs comprising a broad range of tactics typical of other crime prevention strategies; such programs go well beyond just procedural justice policing. As with community-oriented policing, it is difficult to isolate any crime-prevention benefits specifically associated with the procedural justice policing strategy.
CONCLUSION 4-10 Existing studies do not identify a consistent crime-prevention benefit for community-oriented policing programs. However, many of these studies are characterized by weak evaluation designs.
CONCLUSION 4-11 At present, there are an insufficient number of rigorous empirical studies on procedural justice policing to draw a firm conclusion about its effectiveness in reducing crime and disorder.
Although the available program evaluations suggest that generalized aggressive use of increased misdemeanor arrests as a means to controlling disorder in a broken windows strategy generates small to null impacts on crime, controlled evaluations of place-based practices that use problem-solving interventions to reduce social and physical disorder, another implementation of a broken windows strategy, have consistently reported crime-reduction effects. However, it is unclear whether these effects are due to the reinforcement of community social controls or to the deterrence and opportunity reduction generated by police activities.
CONCLUSION 4-12 Broken windows policing interventions that use aggressive tactics for increasing misdemeanor arrests to control disorder generate small to null impacts on crime.
CONCLUSION 4-13 Evaluations of broken windows interventions that use place-based, problem-solving practices to reduce social and physical disorder have reported consistent short-term crime-reduction impacts. There is an absence of evidence on the long-term impacts of these kinds of broken windows strategies on crime or on possible jurisdictional outcomes.