Abstract
Objectives
The New York City Police Department’s “Summer All Out” (SAO) initiative was a 90-day, presence-based foot patrol program in a subset of the city’s patrol jurisdictions.
Methods
We assessed the effectiveness of SAO initiative in reducing crime and gun violence using a difference-in-differences (DiD) approach.
Results
Results indicate the SAO initiative was only associated with significant reductions in specific property offenses, not violent crime rates. Foot patrols did not have a strong, isolating impact on violent street crime in 2014 or 2015. Deployments on foot across expansive geographies also have a weak, negligible influence on open-air shootings.
Conclusions
The findings suggest saturating jurisdictions with high-visibility foot patrols has little influence on street-level offending, with no anticipatory or persistent effects. Police departments should exercise caution in deploying foot patrols over large patrol jurisdictions.
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Change history
03 August 2021
A Correction to this paper has been published: https://doi.org/10.1007/s11292-021-09483-w
Notes
Because this was not a permanent transfer, New York State labor laws would mandate remuneration for employees traveling to participate in this department-sponsored initiative. Contractually, participating officers were entitled to 2 hours and 30 minutes of “travel time” to travel to, and from, their temporary assignments. Monies granted for “travel time” are payable to NYPD officers at their regular hourly rate. Although incurred travel time is not calculated at a traditional overtime rate, it is still subject to normal overtime reporting protocols. The “travel time” rate for an NYPD officer with more than 5.5 years of service is $44.77 per hour, which equates to approximately $112 of overtime earnings per officer, per day. Assuming officers worked traditional 8-hour shifts with steady days off, we would expect a total of 60 work appearances during the intervention phase.
The details of “Operation 25” were found in a pamphlet published internally by the NYPD. Wilson (2013) offers a more in-depth appraisal of the program.
Crime remained unchanged in one experimental beat.
The NYPD does not publish their staffing metrics. We only received aggregated summary statistics of deployed SAO personnel.
Because precinct commanders were given discretion in their deployment of SAO officers, the spatial reach of each precinct’s SAO contingent within precincts is largely unknown. It is unlikely that deployment of foot patrols was intended to evenly saturate the precinct aerial unit. Despite this, the distribution of SAO officers was widespread enough to warrant the designation of the precinct jurisdiction as the primary unit of analysis.
Anecdotal evidence gleaned from interviews with participating officers indicates that many policed street segments on foot—alone. In general, the diffuse dispersal of individual foot patrol units improved the spatial reach of SAO officers within precincts.
The magnitude of disengagement cannot be overstated. In 2014, the NYPD initiated approximately 150,000 fewer stops of individuals suspected of criminality than in the previous year. Data is publicly accessible on the following webpage: https://www1.nyc.gov/site/nypd/stats/reports-analysis/stopfrisk.page
The federal monitor’s reports on police stops in New York City suggest a widespread practice of underreporting. Some estimates suggest nearly half of all stops remain undocumented. In spite of the monitor’s findings, the sharp reduction in street stops following Floyd is still noteworthy, even if it may be an overestimate. Access to the monitor’s semi-annual reports can be found here: http://nypdmonitor.org/monitor-reports/
The SAO initiative was also designed to combat crime occurring in Police Service Areas (PSAs). Officers assigned to PSAs patrol New York City Housing Authority (NYCHA) facilities and grounds. Because NYCHA properties are scattered throughout the City of New York, some PSA boundaries span several precincts. Many NYCHA developments are nested within precinct jurisdictions subjected to the initiative, though jurisdictional responsibility lies with the PSA. Officers assigned to precincts typically police all areas within precinct boundaries except NYCHA property. Some SAO officers were deployed to saturate PSA jurisdictions via foot patrols. Because the units of analysis are large and we did not know a priori the deployment strategy of PSA officers, we do not compare PSA crime to precinct crime.
NYPD officials did not explicitly disclose their selection criteria for participating jurisdictions. The composition of the treatment group suggests indicators of violence were considered, which are often weighted by other precinct characteristics such population size and density. Many of the NYPD’s 77 precinct jurisdictions never received a summer contingent of surplus guardianship. Other regions of the city with similarly pressing crime and disorder concerns were not included; this is due, in part, to the limited availability of personnel to saturate all jurisdictions equally. This supports, to a certain degree, the “randomness” of precinct selection.
Four precincts were excluded from the control group. The Central Park Precinct is an expansive recreational environment without an official residential population. Victims of crime are representative of the ambient population visiting the park, which precludes any accurate assessment of per capita crime rates. Likewise, the 14th and 18th Precincts in midtown Manhattan typically have large ambient populations far surpassing their residential populations. The 121st Precinct in Staten Island was summarily excluded because this area was not officially recognized as a precinct jurisdiction until the summer of 2013.
Empirical testing of common group trends is akin to a placebo treatment procedure whereby crime outcomes are regressed on interactions between a treatment indicator and a full series of T − 1 dummies for months (St. Clair and Cook 2015). Coefficients on the interaction terms represent the conditional outcome distribution over time. Statistically significant differences should only arise when the treatment group enters into the treatment condition. Alternatively, one could test for nonequivalence of the group-level trends using only pre-intervention outcomes (Ryan 2009). In either setting, the pre-period coefficients associated with several of New York City’s major crime indices were indistinguishable from zero, supporting the assumption of trend equivalence.
As New York City’s major crime indices drop to historic lows, differences in crime rates across time show greater volatility—in percentages—than in their actual counts. CompStat evaluations typically compare counts of crimes in one jurisdiction with itself in the previous year. Even meager differences over time in aggregate offense counts, if small, can produce large percentage changes. We contend that police officials might overestimate the severity of even a modest crime spike. Baseline deviations in crime are not likely to persist, or be demonstrative of a significant historical divergence in trend.
Violent crime is a composite index comprising murder/non-negligent manslaughter, rape, robbery, and felonious assault. Later, we disaggregate composite measures to examine the effect of the SAO initiative on specific crime types.
The data that support the findings of this study are available from the NYC OpenData portal (https://data.cityofnewyork.us/Public-Safety/NYC-crime/qb7u-rbmr).
Hospital physicians and superintendents are mandated to report bullet wounds to police authorities, and any failure to do so is a class “A” misdemeanor according to the New York State Penal Law (see, e.g., § 265.25).
The NYPD’s shooting database did not record any incident-level data for three jurisdictions over the 60-month observation period. The 17th, 19th, and 111th Precincts did not report any open-air shooting incidents during our window of observation; these were removed from our group of controls.
Index crime is comprised of “seven major” crime types: murder/non-negligent manslaughter, rape, robbery, assault, burglary, grand larceny, and grand larceny auto. These crimes are regularly tracked and monitored as part of the NYPD’s CompStat system.
In all instances, log(.) denotes the natural logarithm. The absence of crime reports in any particular month is imputed with a value of 1 to facilitate this transformation.
Note, we adjust for obvious controls such as population and area, even though they do not assist with the identification of our causal parameter of interest. If any observed precinct characteristics do change across time, they change slowly. For example, the 121st Precinct in Staten Island was not officially recognized as a precinct jurisdiction until late 2013. The 121st Precinct absorbed sector boundaries within neighboring precincts to alleviate their workload. In general, the inclusion of precinct-level controls does not appreciably influence our results. In fact, double-differencing in this context produces results similar to the standard fixed effects estimator, and so our models will silently exclude many time-invariant controls once we allow for the estimation of precinct- and time-specific intercepts. Also, our equations are insensitive to the inclusion of precinct population weights.
Perhaps one could delineate a theoretical framework for a surge in violence in response to the imminence of the intervention. If public announcements are perceived early, it signals to offenders the “absence” of formal guardianship in public spaces in the weeks before the onset of foot patrol deployments.
Our review of the DiD literature suggests there is no clear consensus regarding the optimal lead-lag structure. DiD studies investigating anticipatory effects often assess anywhere from one-to-three lead effects before treatment exposure (e.g., Autor 2003; Cavalcanti et al. 2019; Green et al. 2014; Grinols and Mustard 2006; MacDonald et al. 2016). It is also not uncommon to find DiD evaluations report lead effects more than three periods before program/policy adoption (Azoulay et al. 2019; Venkataramani et al. 2019). In other settings, anticipatory effects are largely ignored and the authors only incorporate a static intervention dummy (Braga et al. 2018; Larsen et al. 2015).
The classic DiD framework with two groups and a standardized time index for post-treatment months could only be estimated separately by year. One-way cluster robust standard errors, clustering on precinct, are less conservative than least-squares estimates assuming independent and identically distributed errors. We also estimated nonparametric variance-covariance matrices adopted by Driscoll and Kraay (1998), which are amendable to settings with dependence across cross-sectional units. This alternative uncertainty estimator is not appreciably different than standard “sandwich” estimators that cluster on precinct.
The calendar month immediately prior to program implementation in both years serves as the reference period. Excluded periods include June in 2014 and May in 2015.
We do not model months earlier than January in both years.
Few open-air drug and weapon-related offenses occur across months. Non-ignorable differences in pre-treatment reporting trends may be partially responsible for any observed anticipatory effects. Drug and/or weapon-related crime reporting is typically fueled by geographically-focused arrest-generating activities. For example, the staffing of specialized units dedicated exclusively to narcotics enforcement has dwindled heavily in recent years, and as a result, their intensity has been concentrated in more drug-prone regions of the city. Anecdotal evidence suggests narcotics-related activity intensified in the pre-intervention period, as heightened SAO guardianship would typically disrupt the execution of “plainclothes” operations. Further, narcotics-related arrests, in general, have been declining over time. Most of the observed drug and/or weapon-related offenses in our sample involve crimes of simple possession. In particular, most reports involving drug possession are consistent with personal use—not distribution. Similarly, most weapon-related offense reports are consistent with non-firearm-related possession (e.g., knives and other blunt instruments). The SAO model of crime prevention was not designed to be an arrest-generating intervention strategy. Rather, most officers were encouraged to prevent crime by exercising their visible presence on street segments. We argue that any increase in drug and weapon-related reporting are unlikely to be the result of intensifying visible foot patrols.
Restricting burglary complaints to a subset of street offenses is limiting. Too few burglaries occur in public domains. To illustrate, larcenies from vehicles used by persons for commercial or business purposes would be classified as a burglary according to the New York State Penal Law (see, e.g., §140.00 definition of “building”). Offenses of this type typically occur on visible street segments when the vehicle is unattended, and would be classified as a “street” burglary for crime reporting purposes. Less than 5% of burglaries for the years under study were listed as street offenses. Log-linear leastsquares estimates would be affected by small per capita rates and low cardinality over time.
Assessing crime displacement to nearby street segments is a complicated endeavor due to large units of analysis. Absent the precise deployment of foot patrols to micro-locations within precinct jurisdictions, we cannot directly quantify how the widespread surge in police presence affected adjacent beats or sectors.
The coefficients in the pre-period were positive and relatively large in magnitude. The “absorbing” influence of pre-period dummies (i.e., “lead” indicators) has been observed in other place-based evaluation strategies, particularly those where self-selection of jurisdictions into treatment was suggested. In their analysis of Operation Impact in New York City, MacDonald et al. (2016) observed that effects were weaker once they modeled the two periods before program exposure.
Some reported crime metrics were more infrequent than others across time. Coefficients associated with several non-composite crime metrics (e.g., drug/weapon offenses), have small offense counts at the street-level, and thus their rates will typically have high variance. On the other hand, the NYPD’s composite crime indices (e.g., index crime) is more precisely estimated, as indicated by their tighter confidence bands.
Over the 60-month observation period, the SAO policy dummy intermittently indexes a subset of precinct jurisdictions during two discrete but qualitatively similar iterations (i.e., \( {SAO}_{pt}^{14} \) and \( {SAO}_{pt}^{15} \)). Again, the variable SAOpt is a dummy equal to unity if a precinct participated in the SAO initiative at any time and it was in the post-exposure epoch (i.e., the 90-day intervention phase). We dub SAOpt a static effect because it is a simple dummy intervention. Our goal is to assess the effects of the SAO initiative on open-air gun violence absent any time-varying treatment structure.
The NYPD has eight patrol boroughs. The boroughs of Brooklyn, Queens, and Manhattan are split into a northern patrol borough and a southern patrol borough. Each has clearly demarcated borders and is headed by a separate borough commander in charge of patrol operations. This is a qualitatively different hierarchical position in the NYPD rank structure. A precinct commander is in charge of patrol operations within the confines of his or her assigned precinct. The borough commander will oversee all precinct commanders within the same patrol borough. Matching SAO jurisdictions with their patrol borough counterparts overlooks city sections where shootings do not cluster. Many of the future and previous receivers of the SAO initiative were sampled by NYPD executives from within the same patrol borough, offering a more homogenous counterfactual grouping.
Shooting lead coefficients close to the SAO effective dates were mostly positive in both years, and a bit more precisely estimated in 2015. Though anticipatory effects were of substantive interest in this evaluation, we were also concerned with selection of SAO jurisdictions into treatment on the basis of past outcomes. The latter concern is entirely plausible and is one of the reasons we modeled the shooting data more rigorously than the NYPD’s standard crime metrics.
Any precinct-specific linear or higher order polynomial trend fully absorbs the persistent effect observed in 2014.
Augmenting visible guardianship on street segments might affect the perception of offending risk in non-SAO jurisdictions if foot patrols concentrated near the periphery of SAO precinct borders—or beyond. Discarding all neighbors thus compares SAO precincts with those jurisdictions that are more geospatially remote. We have no evidence that a nonadjacent counterfactual would be influenced by the widespread surge in foot patrols within SAO precincts. As well, if SAO officers were deployed on foot directly from their assigned SAO precincts—and not from their previous administrative facilities—then marked vehicular travel to and from SAO precincts would not inadvertently create the impression of more police presence within non-SAO precincts. The perception of police intensity in comparison areas is a noteworthy critique in experimental studies and biases results towards zero (see Larson 1975). Our understanding of the intervention suggests SAO exposure respected precinct boundaries, though we cannot completely rule out treatment spillover.
Operation Impact was in effect from January 2003 to mid-July 2014.
The NYPD mandated that all SAO officers receive, in aggregate, a 1-day refresher course to reacclimate members to street-level patrol work. We have no evidence that attendees received detailed instruction regarding any community-derived intelligence specific totheir individually assigned jurisdictions.
Maintaining the perception of increased guardianship over time is not easy. The NYPD did not sanction any governing body to ensure the visibility of SAO officers during the intervention phase. Supervision of SAO personnel was relegated to the supervisory staff permanently assigned to participating SAO jurisdictions. Thus, as the rank-and-file staff increased due to the influx of SAO personnel, the supervisory component did not. Throughout the initiative, patrol supervisors were thus in charge of supervising regular patrol duty operations and ensuring the continued visibility of the SAO contingent on foot. This greatly increases the “span of control” of supervisory members at the local level and should not be understated. We have no evidence that precinct-level supervisors were making frequent or varied visits to SAO officers on foot. In sum, if foot deployments were too sparse and sufficiently interrupted by officer absence from their assigned posts, then the perception of “more presence” is even more diluted.
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Bilach, T.J., Roche, S.P. & Wawro, G.J. The effects of the Summer All Out Foot Patrol Initiative in New York City: a difference-in-differences approach. J Exp Criminol 18, 209–244 (2022). https://doi.org/10.1007/s11292-020-09445-8
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DOI: https://doi.org/10.1007/s11292-020-09445-8