Abstract
Objectives
Outfitting police officers with body-worn cameras (BWCs) has been suggested to improve police-community relations. This study evaluates whether the deployment of BWCs on NYPD officers impacted resident perceptions of the police.
Methods
A cluster randomized controlled trial design was used to test the influence of BWCs on resident perceptions of the NYPD in treatment precincts relative to control precincts. Dual-frame randomly selected telephone surveys were used to collect pre-intervention and post-intervention resident perception data.
Results
We find no statistically significant differences between BWC treatment and control precincts in general perceptions of the NYPD or the average assessment of police officer behavior among those who have had recent encounters with the NYPD.
Conclusion
Strong community support for BWC adoption and citizen expectations for videos of controversial policing events suggests the continued use of this technology. However, BWCs should be implemented with other evidence-based programs to enhance police-community relations.
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Notes
See page 27 of the remedial order; http://nypdmonitor.org/wp-content/uploads/2015/09/Floyd-Remedy-Opinion-8-12-13.pdf (accessed January 31, 2021).
Statements made at April 27, 2017, press conference; see https://www.youtube.com/watch?v=tsAJkDNy1-4 (Accessed January 31, 2021).
https://news.gallup.com/poll/1597/confidence-institutions.aspx (accessed September 18, 2020).
https://news.gallup.com/poll/317114/black-white-adults-confidence-diverges-police.aspx (accessed September 18, 2020).
A number of nonexperimental studies have supported the main elements of the process-based model of police legitimacy (see, e.g., Mastrofski et al., 1996; Paternoster et al., 1997; Sunshine & Tyler, 2003; Tyler & Fagan, 2008; Tyler & Wakslak, 2004), and certain field experiments suggest citizen perceptions are positively impacted by officers who engage procedurally just behaviors (Mazerolle et al., 2013; Sahin et al., 2017). However, it is important to note that the existing evidence base is not strong enough to establish causation in terms of the influence of procedural justice on citizen compliance with the law (Nagin & Telep, 2017; Worden & McLean, 2017; National Academies 2018).
Brooklyn had 6 treatment precincts, Bronx had 5 treatment precincts, Manhattan had 5 treatment precincts, Queens had 3 treatment precincts, and Staten Island had 1 treatment precinct. In general, the most appropriate precinct matches were found within boroughs. There were two exceptions. One Bronx precinct was matched to a precinct in Brooklyn, and one precinct in Queens was matched to a precinct in Staten Island.
NYPD BWC policy specifies a variety of situations where the BWC must be activated including crime-in-progress assignments, interior patrols of NYCHA buildings, pedestrian stops, vehicle stops, personal interactions that escalate, interactions with emotionally disturbed persons, arrests, and other law enforcement duties. The NYPD policy instructs officers to notify members of the public that an interaction is being recorded as soon as it is “reasonably practical.” See https://www1.nyc.gov/assets/nypd/downloads/pdf/public_information/body-worn-cameras-patrol-guide.pdf (accessed July 19, 2020).
https://www1.nyc.gov/site/nypd/about/about-nypd/equipment-tech/body-worn-cameras.page (accessed July 12, 2020).
In March 2017, 190 preliminary telephone interviews were completed, and these responses were analyzed before proceeding with the full survey. One question was adjusted to ensure respondents were reliably reporting whether they had a close friend or family member who was an NYPD officer. The average length of the pretest survey completion time was just under 10 minutes which allowed two additional outcome questions to be added to the final instrument. Hart Research Associates estimated that the final survey would not take longer than 12 minutes to complete but did not include a time length measure in the final database provided to the NYPD monitor team.
TargetSmart develops its subject list and their addresses and phone numbers from a proprietary set of data sources including voter registration data, telephone company databases (such as Telco Repository, which is the “Big Five” telecommunications companies’ near real-time database of every phone number in the United States), and other sources. TargetSmart reported that 74% of the 6.2 million listed residents were associated with telephone numbers: 19% cellphone only, 22% cellphone and landline, and 33% landline only. Following AAPOR’s (2010) recommendations, a screened approach was used when considering eligible residents in the 40 experimental precincts to remove the overlap of the dual frame.
For instance, in the pre-intervention survey, men ages 18–24 were weighted according to their 2010 ACS proportional representation: 18% of control precinct residents and 17% of treatment precinct residents. Weight calculations for the pre-intervention and post-intervention landline samples and cell phone samples in the treatment and control precincts were estimated separately and then combined via stratified sampling techniques. The weighting used for landline samples and cellphone samples accounted for differential nonresponse by telephone usage group.
We used AAPOR Response Rate 5 (RR5) to calculate our survey response rates: this is the number of complete interviews divided by the number of interviews (complete plus partial) plus the number of non-interviews (refusal and break-off plus noncontacts plus others). https://www.aapor.org/AAPOR_Main/media/MainSiteFiles/Standard_Definitions_07_08_Final.pdf (accessed February 17, 2021).
As noted in Braga, MacDonald, and McCabe (2021), only 18 officers (0.5% of 3,889) appeared in both the treatment group and control group during the intervention period. The movement observed included 12 officers moving from control to treatment conditions and 6 officers moving from treatment to control conditions.
Stata 15.1 was used to execute the analyses in this study. Since the survey data were weighted to more accurately reflect precinct populations in our analyses, the “svy” series of commands were used. Unfortunately, the CFI and SRMR goodness-of-fit statistics cannot be estimated with the weighted data. In models run with the svy prefix, standard errors are reported as “linearized standard errors.” These are synonymous with robust standard errors when not using survey data. As summarized by StataCorp (2019: 6), “By default, svy computes standard errors by using the linearized variance estimator— so called because it is based on a first-order Taylor series linear approximation... In the nonsurvey context, we refer to this variance estimator as the robust variance estimator, otherwise known in Stata as the Huber/White/sandwich estimator; see [P] robust.” As such, we report these commonly used goodness-of-fit statistics based on confirmatory factor analyses of the unweighted data. There were no substantive differences between the unweighted and weighted data in the factor loadings when estimating the latent variables included in this study. Comparative tables are available upon request from the authors.
We follow convention in referring to small mean differences as those that are less than .20 standard deviations. While randomization by design should mean that treatment and control groups are on average comparable, there is always the chance that some differences will emerge. Randomization does not ensure perfect comparability in a single experiment. What matters is how different the groups are on pre-existing differences. As such, statisticians recommend using a comparison of average differences, like a standardized effect size, rather than a test statistic and p value (Imai et al., 2008).
Survey respondents were slightly more likely to be female and, on average, in their mid to late 40s than the general residential population. More than half of respondents were high school graduates and many reported having earned a 4-year college or higher degree. Less than 20% of participants reported living in NYCHA housing, and fewer than 20% also said that they had a friend or family member currently in the NYPD.
It is worth noting here that the pre-intervention and post-intervention survey responses represent repeated cross-sectional data (newly sampled subjects interviewed each time over two data collection periods) rather than pure panel data (the same subjects interviewed each time over two data collection periods). In this study, the unit of experimentation is the precinct, so we consider subjects as exposed to the BWC intervention if they lived in the treatment precincts.
This evaluation used cluster randomization, a variation of the classic experimental design in which clusters (groups) of subjects, rather than individual subjects, are randomly allocated to treatment and control conditions (Mosteller & Boruch, 2002). Following convention on a statistical analysis of cluster randomized controlled trials, we clustered standard errors on groups (matched pairs) using STATA statistical software (Rogers, 1993). This approach is advantageous because it allows the errors to vary differently between clusters, rather than assume they are fixed. An alternative approach would be to estimate with the model with a group-level random effect. This alternative approach, however, assumes that the clusters are random draws of the population of precincts in NYC, when in fact the study was setup to provide a balanced comparison of the impact of BWCs on outcomes in precincts with the highest levels of interactions between the NYPD and civilians (see Campbell et al., 2007).
For instance, reverse coding involved switching the scale to run from “very satisfied to “very dissatisfied” to run from “very dissatisfied” to “very satisfied.” As such, negative coefficients on the DID estimator would then be interpreted as treatment conditions that generated a negative effect on the selected outcome relative to control conditions over the pre-intervention and post-intervention periods.
In addition to the generalized structural equation models (GSEM), we also used factor score regressions with a Bartlett predictor and two-step GSEMs to calculate the DID estimators for the latent variable outcomes. While there are limitations to each approach, the findings did not differ substantively across the three modeling strategies. Some statisticians suggest that factor score regressions produce biased estimates (Hoshino & Bentler, 2013). Other analysts suggest that GSEMs diminish bias and better fit the data relative to factor score regressions (Devlieger et al., 2015). However, in a simultaneous model, which estimates both the measurement part of the model (production of the latent variable) and the structural part of the model (the additional predictors) at the same time, the measurement part of the model can be affected by the inclusion of covariates (Devlieger & Rosseel, 2017). Two-step GSEMs avoid the problems associated with simultaneous estimation by predicting the measurement model and then constraining the parameters of those variables to their original values when running the full model. However, doing this ignores some of the errors produced in the measurement piece, so standard errors may be underestimated (Bakk & Kuha, 2017).
The exclusion rates varied across the regression models, ranging from 1.5% to 8.0% with an average of 6.5%. Sub-questions generated higher rates of exclusions given the smaller number of respondents who answered affirmatively to the larger question. For instance, a smaller number of respondents reported being stopped by the police and, as such, missing responses on sub-questions on their stop experiences generated a larger percentage of missing values. To determine whether any statistically significant differences between included and excluded cases existed for the covariates used in our main models, simple t test comparisons were used. No statistically significant differences were noted between the missing and included cases. As such, these analyses suggested that the data were missing at random and listwise case deletions were appropriate to address these modest missing data problems.
Statistical power was calculated from the computed effect sample size that reweights the total sample size (n) by the number of observations per cluster (m=2), the number of matched pairs (k=20), and the intraclass correlations between clusters and pairs (ICC=r1, r2) according to the following formula: effective sample= (n) / (1 + (m-1)*r1+(k-m)*r2). We set the ICC for clusters (r1) to be 0 since the same people were not purposively interviewed in the pre- and post-BWC periods. As a result, the formula for effective sample size is equivalent to the following: (n) / (1 +(k-m)*r2). If the ICC (r2) is equal to 1, then the effective sample becomes the average number of observations for a matched pair. If the ICC is equal to 0, the effective sample size becomes the total sample size (n) (see Kerry & Bland, 1998). For the ICC per pair (k), we rely on a mixed effect regression that estimates the correlations within pairs.
For instance, a p value = .05 for a particular statistical comparison suggests that 5% of all tests will result in false positives (e.g., proportion of all tested subjects who do not have a disease who will be identified as having the disease). In contrast, a q value = .05 for a particular statistical comparison suggests that 5% of statistically significant results will be false discoveries (e.g., the proportion of all subjects identified as having the disease who do not actually have the disease).
As mentioned earlier, NYPD policy requires officers to notify citizens that an interaction is being recorded “as soon as reasonably practical.” BWC officer compliance with this policy requirement was not quantifiable. The surveys conducted in this research study assumed that NYPD officers outfitted with BWCs were indeed notifying citizens that encounters were being captured on video. However, when officers are not required to provide notification, research suggests most citizens are not aware that the encounters are being recorded by BWCs (White et al., 2017).
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Acknowledgements
The Braga and MacDonald currently serve on the federal monitor team pursuant to the court orders in Floyd et al. v. City of New York, et al., 08 Civ. 1034 (AT);Ligon, et al., v City of New York, et al., 12-CV-2274 (AT); and Davis et al., v. City of New York, et al., 10-CV-00699 (AT). The analyses and opinions expressed in the article reflect those of the authors only and not any other entity. The work reported in this paper was funded by the City of New York as part of the court orders. The authors would like to thank Peter Zimroth, Richard Jerome, other monitor team members, and the NYPD for their assistance with this research.
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Braga, A.A., MacDonald, J.M. & Barao, L.M. Do body-worn cameras improve community perceptions of the police? Results from a controlled experimental evaluation. J Exp Criminol 19, 279–310 (2023). https://doi.org/10.1007/s11292-021-09476-9
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DOI: https://doi.org/10.1007/s11292-021-09476-9