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A randomized control trial evaluating the effects of 
police body-worn cameras 

David Yokum a b ' 1,2 , Anita Ravishankar 3 '^' 1 , and Alexander Coppock 0,1 

a The Lab @ DC, Office of the City Administrator, Executive Office of the Mayor, Washington, DC 20004; b The Policy Lab, Brown University, Providence, Rl 
02912; 'Executive Office of the Chief of Police, Metropolitan Police Department, Washington, DC 20024; d Public Policy and Political Science Joint PhD 
Program, University of Michigan, Ann Arbor, Ml 48109; and 'Department of Political Science, Yale University, New Haven, CT 06511 

Edited by Susan A. Murphy, Harvard University, Cambridge, MA, and approved March 21, 2019 (received for review August 28, 2018) 

Police body-worn cameras (BWCs) have been widely promoted as 
a technological mechanism to improve policing and the perceived 
legitimacy of police and legal institutions, yet evidence of their 
effectiveness is limited. To estimate the effects of BWCs, we con¬ 
ducted a randomized controlled trial involving 2,224 Metropolitan 
Police Department officers in Washington, DC. Here we show 
that BWCs have very small and statistically insignificant effects 
on police use of force and civilian complaints, as well as other 
policing activities and judicial outcomes. These results suggest 
we should recalibrate our expectations of BWCs' ability to induce 
large-scale behavioral changes in policing, particularly in contexts 
similar to Washington, DC. 

body-worn cameras | field experiments | policing 

P olice body-worn camera (BWC) programs are rapidly 
spreading across the United States. In 2015, the US Depart¬ 
ment of Justice awarded over $23 million in funding to support 
the implementation of BWC programs throughout the country 
(1), and a nationwide survey found that 95% of large police 
departments either have already implemented or intend to 
implement a BWC program (2). Much of the expansion has been 
motivated by a series of high-profile, officer-involved shootings, 
many of which were captured in bystander video and shared 
across social media. Stakeholders such as the American Civil 
Liberties Union, Campaign Zero, and Black Lives Matter have 
urged the police to equip BWCs as a technological solution to 
improve policing, or at least to document police practices and 
civilian behavior to resolve disputes (3, 4). 

The widespread support for BWCs is due, in large part, to 
their anticipated effects on behavior. Both officers and civil¬ 
ians on the street may comport themselves differently if under 
the watchful lens of a camera. A wide range of research, dat¬ 
ing back to the classic experiments at Hawthorne Works (5), 
has suggested that people act differently when they believe 
they are being watched, from increasing work productivity and 
charitable giving (6-9) to encouraging honesty (10), promot¬ 
ing adherence to recycling rules (11), stimulating voter turnout 
(12), and reducing theft (13). Across these settings, monitoring 
appears to shift behavior into alignment with socially acceptable 

In the policing context, cameras are expected to encour¬ 
age officer adherence to departmental protocols and deter 
police from engaging in unprofessional behavior or miscon¬ 
duct, especially unjustified use of force (14). Similarly, civilians 
interacting with a BWC-equipped officer may be less likely to 
engage in inappropriate or combative behavior. The underlying 
social or psychological mechanisms linking BWCs and behavior 
could include greater self-awareness, heightened threat of being 
caught, or a combination of the two. Whatever the exact mecha¬ 
nisms, commentators sometimes allude to a so-called “civilizing 
effect,” wherein BWCs are predicted to calm all parties involved 
and reduce the likelihood that violence occurs (15). By captur¬ 
ing the police-civilian interaction, the cameras are also expected 
to have evidentiary value, both for internal affairs and criminal 
investigations (15, 16). 

The existing evidence on whether BWCs have the anticipated 
effects on policing outcomes remains relatively limited (17-19). 
Several observational studies have evaluated BWCs by compar¬ 
ing the behavior of officers before and after the introduction of 
BWCs into the police department (20, 21). Other studies com¬ 
pared officers who happened to wear BWCs to those without (15, 
22, 23). The causal inferences drawn in those studies depend on 
strong assumptions about whether, after statistical adjustments 
are made, the treatment is independent of potential outcomes. 
In particular, we would need to believe that, after conditioning 
on a set of pretreatment covariates, BWCs were as if randomly 

A small number of randomized controlled trials (RCTs) of 
BWCs have been conducted, with mixed results. In a series of 
RCTs conducted across several sites in the United Kingdom 
and the United States, BWCs appeared to increase police use 
of force at some sites and decrease it at others (24, 25). Cam¬ 
eras appeared to decrease complaints in some experiments but 
not others (16, 25). Further trials found no detectable treat¬ 
ment versus control differences on measured outcomes (26). The 
extant set of RCTs has typically been limited by either small sam¬ 
ple sizes or shift-level random assignments that introduce the 
potential for within-officer spillover (14, 27). 


We collaborated with the Metropolitan Police Department of the Dis¬ 
trict of Columbia (MPD) to design and implement an RCT to evaluate the 
effects of BWCs citywide. Specifically, as part of MPD's deployment of BWCs 
to its police force, approximately half of all full duty patrol and station 


Police departments are adopting body-worn cameras in hopes 
of improving civilian-police interactions. In a large-scale field 
experiment (2,224 officers of the Metropolitan Police Depart¬ 
ment in Washington, DC), we randomly assigned officers to 
receive cameras or not. We tracked subsequent police behav¬ 
ior for a minimum of 7 mo using administrative data. Our 
results indicate that cameras did not meaningfully affect 
police behavior on a range of outcomes, including complaints 
and use of force. We conclude that the effects of cameras are 
likely smaller than many have hoped. 

Author contributions: D.Y., A.R., and A.C. designed research, performed research, 

analyzed data, and wrote the paper. 

The authors declare no conflict of interest. 

This article is a PNAS Direct Submission. 

Published under the PNAS license. 

Data deposition: The cleaned dataset sufficient for reproducing the difference-in-means 

estimates of the treatment effects have been deposited in the Open Science Framework, h/. 

1 D.Y., A.R., and A.C. contributed equally to this work. 

2 To whom correspondence should be addressed. Email: 

This article contains supporting information online at 10. 

1073/pnas. 1814773116/-/DCSupplemental. 

Published online May 7, 2019. 1814773116 

PNAS | May 21,2019 | vol. 116 | no. 21 | 10329-10332 


officers were randomly assigned to wear BWCs, while the other half 
remained without BWCs. With 2,224 MPD members participating in the trial, 
this study is the largest randomized evaluation of BWCs conducted to date. 
Our project was deemed "not human subjects research" by the Yale Univer¬ 
sity IRB (protocol no. 2000020390), as all study activities were carried out 
by MPD. 

The primary outcomes of interest were documented uses of force and 
civilian complaints, although we also measure a variety of additional 
policing activities and judicial outcomes. All outcomes were measured 
using administrative data. Before obtaining outcome data, we developed 
a detailed write-up of the methodology and planned statistical analyses 
(a preanalysis plan) and publicly shared it on the Open Science Framework. 
The preanalysis plan is included in SI Appendix. 

Our study encompassed the entire department and included geographic 
coverage of the entire city. We identified eligible officers within each of the 
seven police districts (as well as several specialized units) based on the fol¬ 
lowing criteria: The officer was on active, full duty administrative status and 
did not have a scheduled leave of absence during the study period, held 
a rank of sergeant or below, and was assigned to patrol duties in a patrol 
district or to a nonadministrative role at a police station. Eligible officers 
within each district or special unit were then randomly assigned to one of 
two groups: (/) no BWC (control) or (//') with BWC (treatment). Specifically, 
treatment entails assignment of an eligible participant to wear and use a 
BWC in accordance with MPD policy. MPD General Order SPT-302.13 specifies 
that "[mjembers, including primary, secondary, and assisting members, shall 
start their BWC recordings as soon as a call is initiated via radio or commu¬ 
nication from OUC [Office of Unified Communications] on their mobile data 
computer (MDC), or at the beginning of any self-initiated police action." 
The general order enumerates the range of events for which officers are 
required to activate their BWCs; this list is included in SI Appendix. 

Randomization was implemented using a block-randomized assignment 
procedure. This approach, which uses pretreatment information to group 
officers into blocks before randomly assigning a fixed number of cameras 
to officers in each block, increases the statistical power of the experimen¬ 
tal design and enforces treatment-versus-control balance on the covariates 
according to which blocking occurs. We applied a two-level blocking 
approach: The "major" blocks were the seven police districts and three 
special units, and the minor blocks were constructed using a clustering algo¬ 
rithm based on the background characteristics of the officers (28). Based 
on the eligibility requirements noted above, our sample consisted of 2,224 
MPD members, with 1,035 members assigned to the control group and 1,189 
members assigned to the treatment group. 

As anticipated in our preanalysis plan, some officers who were assigned 
cameras did not install or use them, and some officers who were not 
assigned cameras nevertheless obtained them. We estimate two compliance 
measures: the number of videos uploaded to the video database by treat¬ 
ment officers and the average length of the videos in minutes, as compared 
with control officers. If officers complied with the randomization proto¬ 
col, we would expect that officers assigned BWCs would make vastly more 
videos per year, as well as have a longer average length of videos, than their 
counterparts in the control group. On average, treatment officers uploaded 
about 665 videos annually (compared with 14 videos uploaded among con¬ 
trol officers). The average video recorded by a treatment officer was over 
11 min long, while the average video recorded by a control officer was 
just 0.8 min long. For both manipulation check measures, the treatment 
assignment is both substantively and statistically significant (p < 0.001). We 
conclude that compliance with the study protocol was high. 

Following best practices in settings encountering two-sided noncompli¬ 
ance, we conducted all of our analyses according to the original random 
assignment (29). Our experiment thus recovers estimates of the effect of 
being assigned to a BWC on a variety of outcomes (the intention-to-treat 

Measurement Strategy. We assessed the effect of BWCs on four families of 
outcome measures: police use of force, civilian complaints, policing activity, 
and judicial outcomes. 

i) Police use of force was based on officers' self-reported use of force (in 
accordance with MPD policy). It included a count of all use of force inci¬ 
dents as well as measures of serious uses of force (as defined by MPD 
policy), nonserious uses of force, and use of force incidents by the race 
of the subject of force. 

//) Civilians can file complaints in two ways: with MPD itself or with the 
independent Office of Police Complaints. Our measure was the total 
number of complaints associated with an officer from both sources. 

We also disaggregated the complaints by disposition: sustained, not 
sustained, or unresolved due to insufficient facts. 

Hi) The policing activity category included traffic tickets and warnings 
issued, reports taken from particular types of calls for service, arrests 
on specific charges (e.g., disorderly conduct, traffic violations, assaults 
against a police officer), and injuries sustained by officers in the line of 
duty. We used these measures to evaluate the effects of BWCs on officer 
discretion and activity, as well as on civilian behavior. 
iv) Finally, we examined the effects of BWCs on judicial outcomes, mea¬ 
sured by whether MPD arrest charges are prosecuted by the US 
Attorney's Office (USAO) or the Office of the Attorney General (OAG) 
and the disposition of those charges. Our examination of this set of 
outcomes was constrained by limitations in the available data. Namely, 
we did not have access to the full datasets managed by the USAO, OAG, 
and the courts. We instead had access to a subset of these data available 
to MPD, which captures only the initial charges on which an individual 
was arrested. A consequence is that we were unable to track court out¬ 
comes for any changes to those initial charges. As this limitation applies 
to both control and treatment groups, however, we were still able to 
conduct a preliminary analysis on the evidentiary value of BWCs. 

Due to logistical constraints, MPD deployed cameras on a district-by- 
district basis over the course of 11 mo. Officers in two of the seven police 
districts received cameras in late June 2015, with the deployment to the 
remaining districts taking place from March to May 2016. By integrating 
randomization directly into the BWC deployment process, we were able to 
conduct this study at marginally low cost to MPD. 

To address the staggered deployment process, the data collection period 
varies for each police district, based on the start date of BWC deployment 
in that district. All outcomes were obtained at the officer level and trans¬ 
lated into yearly rates. These rates were calculated from the date that the 
cameras were first deployed in each district. We calculate these rates before 
and after the intervention based on a window of 212 d, because 212 is the 
number of days between deployment and the end of the study period for 
the district that was the last to receive cameras. The pretreatment and post¬ 
treatment periods are of the same length for all districts; the pretreatment 
measurements come from the same 212-d window (in the previous year) as 
the posttreatment measurements, to account for seasonality in policing and 
desensitization to the treatment over time. 

Because all of our outcomes are unconditional event counts translated 
into yearly event rates per 1,000 offices, our measurement procedure avoids 
the posttreatment bias that would be associated with measuring various 
conditional quantities. For example, we might want to measure the frac¬ 
tion of an officer's civilian interactions that include use of force, but, since 
the officer-citizen interaction is posttreatment, we cannot condition on it 
without the risk of bias. 

Estimation Strategy. We use two estimators of the average treatment 
effects: (/) difference-in-means with inverse probability weights to account 
for differential probabilities of assignment by block and (/#) regression of 
outcome on treatment assignment with controls for pretreatment char¬ 
acteristics and inverse probability weights. Specifically, we control for the 
pretreatment value of the outcome (e.g., past use of force), pretreatment 
covariates for the officer, and indicators for each major block. Eq. 1 provides 
the exact specification, as preregistered before the realization of outcomes. 

Yposr — 0o + /3i Z + fa Ypre + 03 Block + /3/iX + e, [1] 

where Z is the treatment indicator (officer assigned camera or not); Y PRE 
is the pretreatment value of the outcome under study; Block is a vector of 
indicator variables for an officer's home district or special unit; X is a vec¬ 
tor of pretreatment covariates that includes race, gender, and length of 
service; and e is the error term. We estimate Eq. 1 using weighted least 
squares regression with inverse probability weights, which are calculated 
as the inverse of the probability of each unit being in its observed condi¬ 
tion (29). We use HC2 robust standard errors for variance estimation (30). 
We conduct our primary analysis among officers in the seven districts of 
DC (n = 1,922). We exclude officers in special units from this analysis, as 
policing activities and camera use patterns may differ between these units 
and the district officers. We conduct this analysis at the officer level, and 
report results as a yearly rate per 1,000 officers. Our analyses were con¬ 
ducted by two independent statistical teams, to help avoid coding errors 
and as a check of convergence in results. 

Data Availablity. The cleaned dataset sufficient for reproducing the 
difference-in-means estimates of the treatment effects will be made 

10330 | 

Yokum et al. 

Fig. 1. Average difference (with 95% confidence interval) between BWC 
and non-BWC groups, per 1,000 officers over a year for police use of 
force, complaints filed against officers, and arrests for disorderly conduct. 
We show findings from both our difference-in-means (DIM) estimator and 
ordinary least-squares (OLS) regression including pretreatment covariates. 

available at the Open Science Framework at We are 
unable to make public the raw data from which the cleaned dataset was 
produced, due to privacy concerns of both officers and civilians. We are also 
unable to release the officer-level covariate information that we use to esti¬ 
mate the covariate adjusted models, as these data would uniquely identify 
individual officers. 


Across each of the four outcome categories, our analyses con¬ 
sistently point to a null result: The average treatment effect 
estimate on all measured outcomes was very small, and no 
estimate rose to statistical significance at conventional levels. 
Because our study has a large enough sample size to detect small 
effect sizes, these failures to reject the null are unlikely to be 
due to insufficient statistical power. Fig. 1 plots the estimated 
average treatment effect (as a yearly rate per 1,000 officers) 
of BWCs on police use of force, civilian complaints, and offi¬ 
cer discretion (as measured by arrests for disorderly conduct). 
Our best guess is that cameras caused an increase of 74 (SE = 
87) uses of force per 1,000 officers, per year. This estimate 
is not statistically significantly different from zero. The effects 
on complaints (57 per 1,000 officers per year, SE = 41) and 
arrests for disorderly conduct (—128 per 1,000 officers per year, 
SE = 277) were also nonsignificant. Effect estimates on court 
appearances, judicial outcomes, domestic violence calls, and 
other measures of police behavior (all null) are included in SI 


We consider here a few possible explanations for our null find¬ 
ings. First and most obviously, it is possible the null finding needs 
no explanation: The devices, in fact, have no effect on behavior. 
Perhaps neither the officer nor civilian involved in an interaction 
are actually aware of or affected by the camera, either due to 
attention being diverted elsewhere or desensitization over time 
to the presence of the cameras. 

Second, Washington, DC may be different from other places 
in important ways. Perhaps BWCs have no effect in the nation’s 
capital, but they do in other municipalities. We are sympa¬ 
thetic to this possibility, but we also note that, as BWCs 
were randomly assigned within each of the seven police dis¬ 
tricts, we conducted the equivalent of seven mini-experiments. 
Despite substantial district-to-district heterogeneity in baseline 
outcomes, we observe small, insignificant effects in all seven 

A third explanation for the null findings considers the possi¬ 
bility that other factors are masking the true effect of the BWCs: 
The cameras do affect the measured outcomes, but these effects 
are being hidden by interference across units, or spillovers from 
treated to control officers. Approximately one-third of calls were 
responded to by control officers only, one-third by treatment 

officers only, and the last third by a mix of treatment and control 
officers. This distribution of calls indicates that control officers 
were frequently performing their duties without cameras nearby. 
As a check of whether the introduction of cameras affected 
both treatment and control officers, we examined time trends 
for documented uses of force and civilian complaints before and 
after cameras were deployed (analysis presented in SI Appendix). 
We observed no differences in precamera versus postcamera 
outcomes for either group. 

Finally, the true effect of BWCs may be masked by the 
widespread presence of nonpolice cameras (e.g., civilians’ cell 
phones). Civilians regularly record encounters with MPD mem¬ 
bers with their own cameras, and closed caption television 
(CCTV) is widespread. Perhaps the BWCs do not change behav¬ 
ior at the margin, simply because there is no more room to have 
an effect. To explore this possibility (we note that this analysis 
was not preregistered), we examined the effect of treatment on 
use of force at night, when exposure to nonpolice cameras is 
lower. We also found no effect of cameras on this alternative 
dependent variable. 

Other researchers have suggested that BWCs may fail to 
affect results because of nonadherence: Officers, for a variety 
of reasons, may not use their assigned cameras according to 
departmental policy (15, 22, 26). Officers may fail to activate the 
camera, for example. We have no indication that nonadherence 
was a widespread problem in our experiment. For 98% of the 
days in 2016, MPD averaged at least one video (and often many 
more) per call for service associated with a treatment officer. 
Further, even for the 2% of days in 2016 in which the number 
of videos uploaded was less than the number of incidents for 
which we would expect them, the difference is minimal, with 96% 
average adherence based on our measure. That said, effects may 
depend on the level of discretion officers are given to activate the 
cameras, although evaluation of that possibility will have to await 
further experiments. 

We acknowledge that BWCs may have had effects that are 
not measurable with administrative data. For example, it may be 
the case that there were uses of force that were previously going 
unreported, and those have now dropped with the introduction 
of BWCs. However, because our data do not capture unreported 
uses of force, we are unable to detect this kind of change. As 
a matter of speculation, however, we find it implausible that we 
would measure very small effects on reported outcomes but that 
the true average effect on unreported outcomes is large. 

In summary, we measured the average effects of BWCs on 
documented uses of force and civilian complaints as well as a 
variety of additional policing activities and judicial outcomes. 
Our sample size was unusually large, enhancing our ability to 
detect differences, should they exist. In addition, our compar¬ 
ison groups were constructed from an individual-level officer 
randomization scheme, which avoids several problems of infer¬ 
ence present in other methodologies used to date. We are 
unable to detect any statistically significant effects. As such, 
our experiment suggests that we should recalibrate our expec¬ 
tations of BWCs as a technological solution to many policing 

ACKNOWLEDGMENTS. We thank Katherine Barnes, JD, PhD, Donald Green, 
PhD, Bill Egar, PhD, Jennifer Doleac, PhD, and Donald Braman, JD, PhD, 
and reviewers from The Lab @ DC and its partners for valuable feedback. 
We thank the many individuals who participated in briefings and shared 
their thoughtful insights and opinions with us. This study would not have 
been possible without the Metropolitan Police Department of the District of 
Columbia. They welcomed our research team and were committed to under¬ 
standing, as rigorously as possible, the impacts of the BWC program. Special 
thanks go to Chief Cathy Lanier (ret.). Chief Peter Newsham, Matthew 
Bromeland, Commander Ralph Ennis, Heidi Fieselmann, Derek Meeks, and 
all the sworn members who dutifully adapted to a new, complicated pro¬ 
gram and participated in the study. We also thank the Executive Office 
of the Mayor, especially Mayor Muriel Bowser, City Administrator Rashad 
Young, Deputy Mayor for Public Safety and Justice Kevin Donahue, and 

Yokum et al. 

PNAS | May 21, 2019 

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Chief Performance Officer Jennifer Reed, for dedicating their support, time, 
and resources to advancing evidence-based governance and policy in the 
District. Thanks to Objectively for layout and web design. We thank the 

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