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Vol.:(0123456789)
Journal of Quantitative Criminology
https://doi.org/10.1007/s10940-019-09434-9
1 3
ORIGINAL PAPER
Measuring theDirect andSpillover Eects ofBody Worn
Cameras ontheCivility ofPolice–Citizen Encounters
andPolice Work Activities
AnthonyA.Braga1 · LisaM.Barao1· GregoryM.Zimmerman1· StephenDouglas1·
KellerSheppard1
© Springer Science+Business Media, LLC, part of Springer Nature 2019
Abstract
Objectives Existing research on the effects of body-worn cameras (BWCs) have found
largely consistent results regarding direct significant reductions in citizen complaints and
often also report reductions in use of force reports. However, few studies have examined
possible spillover effects onto untreated officers. This study explicitly tests for direct and
spillover effects of BWCs on the civility of police-citizen encounters and police work
activities.
Methods This study assesses the direct effects of BWCs on citizen complaints, police use
of force, and police proactivity and discretion during a 1-year randomized controlled trial
in the Boston Police Department. Through a simultaneous quasi-experimental design, this
study also investigates whether BWC deployment results in spillover effects onto control
officers in treated districts as compared to comparison officers in untreated districts.
Results Findings indicate that the use of BWCs reduces citizen complaints and police use
of force but has no appreciable impact on officer activity or discretion. Furthermore, results
indicate significant spillover reductions in citizen complaints for control officers in treated
districts.
Conclusions The results of this study suggest that a limited BWC adoption may generate
spillover deterrent impacts as officers and citizens perceive an increased threat that inap-
propriate and illegal behaviors will be captured on video even when BWCs are not actually
present during an encounter. Partial BWC implementation seems like a cost-effective alter-
native to full implementation. However, police executives and policy makers need to think
carefully about possible negative externalities generated by uneven BWC coverage.
Keywords Body-worn cameras· Spillover effects· Citizen complaints· Use of force·
Police behavior· Police proactivity
* Anthony A. Braga
a.braga@northeastern.edu
1 School ofCriminology andCriminal Justice, Northeastern University, 360 Huntington Avenue,
Boston, MA02115, USA
Journal of Quantitative Criminology
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Introduction
Body-worn cameras (BWCs) have been rapidly adopted by police departments in the
United States in response to long-simmering police-minority community tensions that were
exacerbated by a string of police killings of unarmed black men in cities such as Ferguson,
Missouri; Baltimore, Maryland; North Charleston, South Carolina; and New York City
(Lum etal. 2015; White 2014). Citizen demands for greater accountability and increased
transparency of officer actions during these events fueled calls for BWCs to be placed on
police officers. To meet this demand, the U.S. Department of Justice (2015) made $20
million dollars in grants available to facilitate the adoption of BWCs by police depart-
ments, which was further supported by a variety of federal, state, and local investments
in BWC acquisition and training. It is notable that the BWC grant program was created by
the Obama Administration and continued under the Trump Administration, bringing the
4year total amount invested to approximately $70 million. Indeed, the International Asso-
ciation of Chiefs of Police (2014) signaled the developing importance and future wide-
spread use of this technology by producing a model BWC policy guide. A 2015 survey by
the Major City Chiefs and Major County Sheriffs associations found that 19% of its mem-
bers had already implemented BWC programs and some 77% planned to do so in the near
future (Lafayette Group 2015). According to the 2016 Law Enforcement Management and
Administrative Statistics (LEMAS) survey, nearly half (47%) of 15,328 general-purpose
U.S. law enforcement agencies1 had adopted BWCs (Hyland 2018).
Most general-purpose law enforcement agencies have implemented BWCs on a limited
scale. For those agencies that reported the adoption of BWCs, the 2016 LEMAS survey
found there were approximately 119,000 BWCs currently in service (29 BWCs per 100
full-time sworn officers) and that an additional 86,000 BWCs would be deployed within the
next 12months (21 BWCs per 100 full-time sworn officers) (Hyland 2018). More than half
(57%) of these agencies reported that BWCs were fully deployed to all intended person-
nel. Among those organizations that reported partial deployments, 63% reported that insuf-
ficient funding precluded full deployment. For the more than 8000 general-purpose law
enforcement agencies that did not deploy BWCs on officers (53% of 15,328), most cited the
expense of implementation such as video storage and disposal costs (77%), hardware costs
(74%), ongoing maintenance and support costs (73%), and training costs (39%) (Hyland
2018). A recent set of case studies by the Police Executive Research Forum (2018) suggest
that partial adoptions of BWCs are the economic reality in many police departments. For
instance, the Phoenix, Arizona Police Department reported that BWCs were deployed on
only 10% (350) of its patrol officers, but with an annual operating expense of $2883 per
camera, cost the city $1,009,050 per year. Since limited deployments are driven by the high
costs of BWC programs, police departments need to test different deployment schema to
maximize any desirable effects of the technology.
It is possible that a limited but strategic deployment of the technology might generate
adequate coverage if the presence of BWC on selected officers impacts the behavior of
other officers who are not outfitted with the equipment. As such, a series of randomized
experiments have considered the possibility that behavioral outcomes for non-BWC control
officers were “contaminated” by interactions with BWC treatment officers (e.g., Ariel etal.
1 General-purpose law enforcement agencies include municipal, county, and regional police departments;
sheriffs’ offices with law enforcement duties; and primary state and highway patrol agencies (Hyland 2018).
Journal of Quantitative Criminology
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2015; Braga etal. 2018b; White et al. 2018; Yokum etal. 2017). The study authors con-
sidered contamination issues as a possible threat to the measurement of the direct effects
of BWCs on officer behavioral outcomes, a typical concern in experimental design. In this
study, we consider whether these contamination effects actually represent “spillover ben-
efits”—that is, unintended positive impacts extended from police-citizen encounters where
the BWCs are present to police-citizen encounters not covered by BWCs (see also Ariel
etal. 2018a, b). Although the aforementioned evaluations did not explicitly measure the
existence of these spillover effects, they indirectly raised the possibility that the BWC treat-
ments generated positive effects on untreated officers. This possibility is critical and sug-
gests that the limited deployment of BWCs can have effects beyond the officers wearing
BWCs, thus impacting the behavior of officers more broadly.
Accordingly, the Boston, Massachusetts, Police Department (BPD) implemented a
pilot BWC program in 2016 to guide further policy and program development guidance to
inform a much larger implementation of the technology on its patrol force. The evaluation
of the pilot program was explicitly designed to measure both direct and spillover effects
of BWCs on the civility of police-citizen interactions and police officer work activities via
randomized controlled trial and quasi-experimental designs. We begin by briefly reviewing
the theoretical justifications that support equipping police officers with BWCs, the avail-
able evaluation evidence on the impacts of BWCs on selected behavioral outcomes, and the
work pursued in prior evaluations to understand the existence of possible spillover BWC
program effects. We then present the methods, data, and models used in the BPD rand-
omized controlled trial and quasi-experiment. Relative to control officers, we find that the
placement of BWCs on treatment officers generated statistically-significant reductions in
citizen complaints and use of force reports but did not alter police proactivity or general
work activities. We also find evidence for the existence of spillover reductions in citizen
complaints against “contaminated” control officers relative to untreated comparison offic-
ers in districts without BWCs present. In the concluding section, we consider the theoreti-
cal and policy implications of our results.
Literature Review
Deterrence andSelf‑Awareness
Two theoretical perspectives—deterrence and public self-awareness—have been advanced
to support the placement of BWCs on police officers to enhance the civility of police-citi-
zen encounters (Ariel etal. 2015). Deterrence theory proposes that offenders refrain from
perpetrating crimes when they perceive the costs of illegal acts to exceed the benefits of
those acts (Zimring and Hawkins 1973). The available empirical evidence suggests that
offender perceptions of apprehension risks and the certainty of punishment determines
whether particular interventions generate deterrent impacts (Nagin 2013). The threat of
BWCs capturing inappropriate or illegal behaviors on video during encounters may stimu-
late a deterrent effect by modifying both officer and citizen perceptions of detection and
punishment risks (Ariel et al. 2017). As Tilley (1993, p. 5) suggests, the presence of a
camera in social settings “reduces… [noncompliance] by deterring potential offenders who
will not wish to risk apprehension and conviction by the evidence captured on videotape or
observed by an operator on a screen on which their behavior is shown.”
Journal of Quantitative Criminology
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The presence of BWCs during police-citizen interactions may also stimulate desirable
behaviors such as treating others in respectful and procedurally-just ways (Ariel et al.
2015; Demir etal. 2018). Public self-awareness theory posits that, when people are being
observed, they are more likely to compare their immediate behaviors to established internal
social norms, comply with rules, and exhibit socially-desirable behavior (Duval and Wick-
lund 1972). Mirrors, audiences, video and audio recording devices, and other environmen-
tal cues stimulate self-awareness (Silvia and Duval 2001). The presence of BWCs may
prompt police officers and citizens to compare their behavior to expected social norms and
standards. In turn, this introspection makes it more likely for officers and citizens to adjust
their actions to fit normative behavior during their encounters (Farrar and Ariel 2013).
The available empirical evidence suggests that the presence of BWCs may indeed mod-
ify certain police officer and citizen behaviors during encounters (Lum etal. 2015; White
2014). However, it remains unclear whether self-awareness, deterrence, or both theoretical
perspectives generate the observed improvements in the civility of police-citizen encoun-
ters. It is also unclear whether the presence of a BWC influences officer work behaviors
such as their use of discretion when considering the use of arrests to resolve incidents
(Rowe etal. 2018), or their willingness to engage proactive policing tactics, such as making
self-initiated calls and completing citizen stops, to control crime (Katz etal. 2014; Wallace
etal. 2018). Consistent with the key outcome variables in this randomized controlled trial,
the impacts of BWCs on citizen complaints, officer use of force reports, and police work
activities are considered below.
The Impact ofBWCs ontheCivility ofPolice‑Citizen Encounters
A recent systematic review of the existing evaluation evidence suggests that BWCs pro-
duce reductions in citizen complaints against officers (Lum etal. 2019; see also Malm
2019).2 For instance, the well-known Rialto, California randomized experiment reported
that citizen complaints were reduced by 88% during treatment shifts when officers wore
BWCs, relative to control shifts when the same officers did not wear BWCs (Ariel etal.
2015). Randomized controlled trials in Orlando, Florida (Jennings et al. 2015) and Las
Vegas, Nevada (Braga etal. 2018b) reported 65% and 25% reductions, respectively, in the
prevalence of citizen complaints against BWC treatment officers relative to non-BWC con-
trol officers. Quasi-experimental evaluations in Phoenix, Arizona (Hedberg etal. 2017) and
Mesa, Arizona (Mesa Police Department 2013) estimated that citizen complaints against
officers decreased by 62% and 40%, respectively, for treatment officers wearing BWCs rela-
tive to non-BWC comparison officers. A small number of controlled evaluations have not
found significant reductions in citizen complaints (e.g., Yokum et al. 2017; White etal.
2018; Grossmith etal. 2015); however, these exceptions do not alter the general consen-
sus that BWCs generate positive impacts on citizen complaints against officers (Lum etal.
2019).
The empirical evidence is somewhat less clear on the impacts of BWCs on officer use
of force during police-citizen encounters (Lum etal. 2019). The Rialto randomized experi-
ment revealed that officer use of force reports decreased by 59% during BWC treatment
2 It is worth noting here that it remains unclear whether observed reductions in citizen complaints reflect
actual changes in the civility of police-citizen encounters. Complaint reductions may also reflect changes
in citizen reporting behaviors driven by a decreased propensity to file frivolous complaints against officers
(see Lum etal. 2019 for a discussion).
Journal of Quantitative Criminology
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shifts when compared to control non-BWC shifts (Ariel etal. 2015). Moreover, an exten-
sion of the Rialto experiment revealed sustained effects of BWCs on lower levels of use of
force over time (Sutherland etal. 2017). When comparing BWC treatment officers to non-
BWC control officers, the Orlando randomized controlled trial found a 53% reduction in
the incidence of response-to-resistance reports (incidents involving non-lethal implements;
Jennings etal. 2015) and the Las Vegas randomized controlled trial reported a 41% reduc-
tion in police use of force reports (Braga etal.2018b). The Mesa quasi-experimental eval-
uation also reported that BWCs were associated with a 75% reduction in use of force com-
plaints against treatment officers relative to control group officers (Mesa Police Department
2013). In contrast, several rigorous studies exist that report null effects of BWCs on officer
use of force (e.g., Headley etal. 2017; Peterson etal. 2018; Yokum etal. 2017; White etal.
2018).
A recent evaluation suggests that these conflicting findings may be a product of vari-
ation in officer compliance with established BWC activation policies. A multisite rand-
omized controlled trial including some 2122 officers across eight police departments found
no reduction in officer use of force and an increase in assaults on officers during treatment
shifts when officers were equipped with BWCs, relative to control shifts when officers did
not wear BWCs (Ariel etal. 2016b). However, in the three sites with high compliance to
a BWC policy that required officers to notify citizens that they were being recorded at the
beginning of the encounter, use of force by BWC officers decreased by 37% during treat-
ment shifts relative to control shifts (Ariel etal. 2016a). Conversely, in the five sites with
low compliance to the BWC policy, there was a 71% increase in officer use of force dur-
ing treatment shifts relative to control shifts (Ariel etal. 2016b). The authors speculated
that unrestrained discretion may cause increased aggressive behavior if BWCs are activated
when police-citizen encounters are escalating in a negative direction. In contrast, the verbal
notification of video recording at the outset of police-citizen interactions may deter aggres-
sive behavior and stimulate civility before these encounters escalate in unfortunate ways.
The Impact ofBWCs onPolice Ocer Work Behaviors
A growing number of studies have examined the effects of BWCs on police officer work
behaviors and discretion. Outfitting police officers with BWCs could possibly increase their
inclination to make arrests. Survey research suggests that officers view the technology as
improving the arrest and prosecution of criminals through the creation of video evidence
on events that transpired during police-citizen encounters (Goodall 2007; ODS Consulting
2011). Other studies suggest that officers express concern over the use of BWC footage to
monitor their performance and fear being reprimanded for not making arrests or not issu-
ing citations when videos reveal citizen violations of the law (Police Executive Research
Forum 2014; Ready and Young 2015). To other observers, the placement of BWCs on
officers may reduce officer willingness to engage proactive policing tactics and lead to “de-
policing” in high crime areas that need police attention (MacDonald 2016). The available
evaluation evidence on the impacts of BWC on police work behaviors is decidedly mixed
(Lum etal. 2019).
A brief review of a small number of well-known BWC evaluations illustrates the con-
flicting findings on police work activity outcomes. The Las Vegas randomized controlled
trial did not find any changes in self-initiated calls but reported increases in call events
that resulted in arrests and citations for the BWC treatment officers relative to the con-
trol officers (Braga etal. 2018b). In the Phoenix quasi-experiment, Hedberg etal. (2017)
Journal of Quantitative Criminology
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also reported increased arrests when comparing BWC treatment officers to control officers.
However, in a randomized controlled trial in Spokane, Washington, Wallace etal. (2018)
did not find an increase in arrests but did find an increase in self-initiated calls by BWC
treatment officers relative to control officers. An experimental analysis found that BWC
officers were less likely to perform stop-and-frisks and make arrests but were more likely
to give citations and initiate encounters in Mesa (Ready and Young 2015). Yet, relative to
non-BWC control officers, Grossmith etal. (2015) found no effects on stop-and-frisks by
BWC officers in the London (UK) randomized cluster trial, and both Headley etal. (2017)
and Peterson etal. (2018) found no effects on traffic stops by BWC officers in the Hal-
landale, Florida quasi-experiment and the Milwaukee, Wisconsin randomized experiment,
respectively.
Spillover Eects ofBWCs
Methodological discussions of the findings of selected BWC randomized experiments
have considered the extent to which the measurement of direct effects of the technology
have been undermined by the diffusion of the BWC intervention from treatment officers
to control officers (e.g., see Ariel etal. 2015; Braga etal. 2018b; Yokum etal. 2017). The
diffusion of treatment into control conditions contaminates the counterfactual contrasts
between treatment and control subjects and, as such, threatens the internal validity of the
randomized experiment (Ariel etal. 2018; Cook and Campbell 1979). This undermines the
statistical analysis of causal effects by violating the stable unit treatment value assumption
(SUTVA) that assumes that the effect of a treatment on a given observational unit is not
related to the intervention assignments of observational units (Rubin 1980). For example,
in the Rialto randomized controlled trial, the same officers worked both the BWC treatment
shifts and the no-BWC control shifts; therefore, the experimental officers may have carried
over BWC treatment effects into the control shifts (Ariel etal. 2015). Indeed, the evaluators
noted that there was possible treatment contamination as the control shifts also experienced
reductions in citizen complaints and officer use of force incidents. In a later multi-site rand-
omized experiment that also used shifts as the units of analysis, Ariel etal. (2017) referred
to this phenomenon as “contagious accountability” and suggested that the adoption of
BWCs by a subset of officers could impact the behaviors of the entire police department.
BWC randomized experiments that use officers as the units of analysis experience dif-
fusion of treatment effects when the BWC treatment officers respond to the same calls for
service as the control officers (Ariel etal. 2018). The Spokane BWC randomized controlled
trial reported that control conditions were contaminated by the presence of a treatment
officer in roughly 20% of calls during the intervention period; after BWC deployment, the
percentage of control officers with a complaint declined by 50% and percentage of control
officers with a use of force report declined by 39% (White etal. 2018). The Las Vegas
BWC randomized experiment found that about 19% of the calls handled by control offic-
ers were contaminated by the presence of BWC treatment officers; however, the evaluators
reported a small reduction of only 5% in the percentage of control officers with a complaint
and a small increase in the percentage of control officers with a use of force report (Braga
et al. 2018b). The Washington DC Metropolitan Police Department BWC randomized
experiment suffered from very high levels of contamination of control conditions: roughly
70% of calls involving control officers had treatment officers present (Yokum etal. 2017).
Given this high level of contamination, it is not surprising that the DC evaluation reported
Journal of Quantitative Criminology
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no pre-post differences between treatment and control group officers for complaints, use of
force reports, and a range of police officer activity outcomes.
While such contamination undermines experimental design and complicates the ability
of statistical analyses to generate valid effect sizes, contamination effects are also meaning-
ful in their own right when conceptualized as “spillover effects.” For example, evaluations
of crime prevention programs have observed spatial spillover crime reduction benefits, in
particular when areas surrounding but not directly protected by implemented interventions
are benefitted themselves (Clarke 1989; Guerette and Bowers 2009). These “diffusion of
benefits,” the opposite of crime displacement, occur when the reach of crime prevention
programs is overestimated by prospective offenders (Clarke and Weisburd 1994). Relevant
to the current study, the placement of BWCs on police officers could generate spillover
benefits by deterring inappropriate and illegal actions and/or by stimulating desirable
behavior among officers not outfitted with the cameras.
Deterrence theory suggests that spillover effects may be generated by the modifica-
tion of the objective risk of potential officer antisocial behavior being recorded by another
officer and subsequently detected by superiors, which in turn influences untreated offic-
ers’ perceived risk of apprehension. Spillover deterrent effects could also be generated by
increased perceived severity of formal punishment from superior officers and informal
punishment from friends, family, and broader society via public shaming on social media,
doxing (i.e., the malicious release of identifying and social information), death threats, and
the like. Indeed, if a BWC video is released and “goes viral,” the negative officer behavior
can be viewed over and over again. In contrast, public self-awareness theory suggests that
the presence of BWCs on other officers may stimulate untreated officers to behave in ways
consistent with societal norms (e.g., this is how everyone is supposed to act) and more-
recently endorsed departmental norms governing use of force and procedural justice rather
than norms that may be historically bounded in traditional police culture (e.g., this is tradi-
tionally how I have seen other officers talk and act) (see, e.g., Silver etal. 2017).
Video surveillance has become a prominent feature of modern society as cameras have
been woven into the fabric of everyday life given the ubiquity of smartphones, closed-
circuit televisions (CCTV), drones, and other technologies (Evans 2015; Foucault 1977;
Ganascia 2010; Haggerty etal. 2011). High quality videos of police-citizen encounters can
be instantaneously shared with thousands or millions of viewers. To some observers, the
saturation of cameras forms a reciprocal system of social control, the synopticon, in which
“the many” watch “the few” (Doyle 2011, p. 283; see also Mathiesen 1997). Indeed, the
“new visibility” of police work in officers’ operational environment (Brown 2016; Gold-
smith 2010) could also be generating a “contagious accountability” effect beyond the mere
presence of BWCs on particular officers in the department. As such, studies designed to
measure the existence of BWC spillover effects need to include separate comparison groups
of untreated officers that, to the extent possible, isolate these general societal changes in
video surveillance from the specific influence of BWCs on untreated officers who respond
to the same events as treated officers.
None of the randomized experiments reviewed above were explicitly designed to deter-
mine whether changes in complaints and use of force reports generated by control officers
were driven by spillover BWC treatment effects. These studies did not contrast contami-
nated control officer outcomes relative to outcomes for a counterfactual group of non-con-
taminated comparison officers. As such, any suggestion of a cross-group spillover effect is
based on speculation rather than an explicit statistical analysis of causal effects. We pro-
vide an explicit test of spillover effects below. In many ways, this paper is a modest empiri-
cal attempt to answer the call by Ariel etal. (2018b) to implement BWC evaluation studies
Journal of Quantitative Criminology
1 3
that consider partial inference, or the effect of treatment of one unit on the treatment effects
of another unit.
Methods, Data, andModels
The BPD implemented a BWC pilot program in September 2016 that involved the random
allocation of 100 BWCs to officers who wore these cameras for a 12-month intervention
period. The BPD developed and implemented a policy to guide officer use of the BWC
technology during the pilot program.3 Distinctive features of the policy included: a require-
ment that BWC officers notify citizens that the interaction was being video-recorded at the
outset of the encounter; guidelines to seek consent from citizens before recording in resi-
dences during non-warrant or emergency situations; and detailed guidelines on the occur-
rences when video-recording was mandatory during the delivery of police services. During
the 1-year intervention period, BPD officers outfitted with the BWCs generated roughly
38,200 videos that covered more than 4600h of police work in Boston neighborhoods.
Boston Mayor Martin Walsh and then BPD Commissioner William Evans committed
to a rigorous assessment of the pilot program and engaged a research team from North-
eastern University to design and execute an impact evaluation. This pilot was intended to
help answer policy questions about how the BWC system would operate if and when fully
implemented and to address concerns of officers and community members on the use of
the technology. The research team sought to measure the direct and spillover effects of
the BWCs on the civility of police-citizen encounters and officer work activities. A rand-
omized controlled trial was used to test the direct impacts of BWCs while a quasi-experi-
mental design was used to assess BWC spillover impacts.
The BPD provides policing services directly to Boston residents through 11 district sta-
tions. The Youth Violence Strike Force (YVSF, informally known as the “gang unit”) is
comprised of plainclothes officers who use proactive policing tactics to prevent outbreaks
of gang violence. As will be described further below, 10 districts were matched into 5 pairs
based on a range of relevant variables including crime, calls for service, arrests, field inter-
rogation observation (FIO) reports, citizen complaints, number of officers assigned, popu-
lation demographics, and levels of neighborhood concentrated disadvantage.4 The research
team randomly allocated one district from each matched pair to the BWC treatment group.
YVSF was also non-randomly assigned to the BWC treatment group.5 The randomized
3 https ://www.bwcsc oreca rd.org/stati c/polic ies/2016-07-12%20Bos ton%20-%20BWC %20Pol icy.pdf
(Accessed November 21, 2018).
4 Since there was an odd number of policing districts, one district would necessarily be excluded from the
matched pairs. BPD District C-6 (South Boston) was not included in the matching process because it was
not a good match for the other districts. This was primarily due to the unique presence of a majority white
population with higher levels of concentrated disadvantage. It is also important to note here that District
A-15 (Charlestown) is a subcommand of District A-1 (Downtown) and not a stand-alone BPD policing dis-
trict. As such, District A-15 was not included in the matching exercise as there is no other similar subcom-
mand in Boston.
5 The non-random selection of the YVSF stemmed from two complementary interests. First, the BPD
wanted to develop policy and programmatic information on the issues involved in assigning cameras to
plainclothes officers relative to uniformed officers. Second, during conversations with community groups
on the BWC implementation, community leaders generally recognized YVSF as a key BPD unit engaged in
proactive policing activities centered on youth living in disadvantaged minority neighborhoods. These lead-
ers requested that YVSF officers also wear BWCs during the pilot program.
Journal of Quantitative Criminology
1 3
controlled trial compared outcomes for treatment officers who were randomly allocated
BWCs relative to control officers who did not receive the technology. The quasi-experi-
mental design compared outcomes for control officers who experienced varying levels of
BWC intervention through contamination processes in treatment districts to outcomes for
matched comparison officers in control districts that did not have the BWC technology pre-
sent during the intervention period.
Randomized Controlled Trial Design
The randomized controlled trial design required the random allocation of the BWC technol-
ogy to officers within the 5 treatment districts and YVSF. The BPD provided the research
team with a database of n = 281 eligible officers from these assignments who worked the
day (Patrol, 7:30 AM–4:00 PM; YVSF, 8:30 AM–5:00 PM) and first half (Patrol and
YVSF, 4:00 PM–11:45 PM) shifts as of September 1, 2016. The BPD excluded officers
who were responsible for administrative duties, medically-incapacitated, on military leave,
or assigned to other responsibilities that did not primarily involve law enforcement work
on the street. The database included information on age, race, sex, and time on the job.
The research team also collected information on citizen complaints and officer use of
force incidents generated by these officers for 3years prior to the start of the pilot program
(2013–2015) through databases maintained by the BPD Bureau of Professional Stand-
ards. BPD official data sources were used to develop officer activity measures during the
12-month pre-intervention period. Key officer activity measures included mean monthly
responses to call events, mean monthly crime incident reports, mean monthly arrests, and
mean monthly Field Interrogation Observation reports (FIOs, representing documented
police-citizen encounters).
A computer algorithm was used to randomly allocate the n = 281 officers to treatment
and control groups within the 5 treatment districts and YVSF. The initial randomiza-
tion was used to divide the officers into two nearly equivalent-sized experimental groups
(n = 140 treatment officers and n = 141 control officers); n = 100 officers within the treat-
ment group were then randomly assigned to wear the BWC technology at the outset of the
pilot program. The BPD was committed to maintaining 100 active BWC officers working
in Boston communities for the entire 12month pilot program. The n = 40 treatment officers
that did not receive BWCs were trained in the BWC policy and operations of the technol-
ogy. As described below, these officers served as “alternates” to the treatment officers out-
fitted with BWCs as attrition occurred over the course of the study period.
Randomization provides a simple and convincing method for achieving comparability
in the treatment and control groups (Shadish etal. 2002). If randomization is done cor-
rectly, the only systematic difference between treatment and control groups should be the
presence or absence of the treatment. To test the balance between the treatment and con-
trol groups on key officer variables, we used independent samples t tests and standardized
mean differences, known as Cohen’s d (Cohen 1988). Table1 presents basic descriptive
information on officers participating in the experiment and the results of these tests; for
binary variables, means are expressed as percentages. A positive t test indicates that the
treatment group has a higher mean than the control group. Covariate imbalance would be
exhibited by Cohen’s |d| in excess of .20 and a |t| in excess of 1.96. The equality of vari-
ances was tested and confirmed for all variables. This reveals that the randomization cre-
ated balanced treatment and control groups. The balanced treatment and control groups
supports the internal validity of the design and suggests that the randomized controlled
Journal of Quantitative Criminology
1 3
trial was well positioned to isolate the impact of body worn cameras on the study outcome
measures.
Attrition ofOcers
Attrition represents a threat to the internal validity of randomized experiments as it could
affect the equivalence of treatment and control groups and introduce bias into the analy-
sis of experimental data (Campbell and Stanley 1963). In general, attrition from the BWC
treatment group during the randomized controlled trial was very modest; only n = 21 treat-
ment officers ceased wearing BWCs before the August 31, 2017 end of the intervention
period (14.9% attrition from n = 140 treatment officer group) and were replaced by trained
alternates. Over the course of the 1year pilot program, n = 18 control officers (12.8% attri-
tion from the n = 141 control officer group) were no longer in an active duty assignment
eligible for BWC use.
Table 1 Summary characteristics
of officers in treatment and
control groups, N = 281
N = 140 officers in the treatment group and N = 141 officers in the con-
trol group. SD = Standard Deviation. Continuous variables are summa-
rized by means and standard deviations while categorical variables are
represented by percentages
* = p < .05, ** = p < .01
Officer characteristics Balance diagnostics
Mean (SD) t d
Treatment 49.8% – –
Control 50.2%
Male 91.1% .19 .011
Female 8.9%
White 65.1% − 1.04 .062
Black 25.6% .58 .034
Hispanic 7.5% .70 .041
Asian/other 1.8% .46 .027
Mean age 40.4 (9.8) − 1.18 .071
Mean years on job 12.2 (9.1) − 1.13 .067
Mean yearly complaints .22 (.21) 1.01 .049
Mean yearly use of force .12 (.19) .12 .006
Mean monthly calls 38.78 (33.04) 1.29 .077
Mean monthly crime incidents 9.92 (8.44) 1.56 .092
Mean monthly arrests 5.71 (6.81) 1.08 .064
Mean monthly FIO reports 2.79 (3.97) − 1.25 .074
Day shift 43.4% .53 .031
First half 56.6%
B-2 21.7% − .98 .058
B-3 19.6% .86 .042
D-4 18.9% − .73 .043
D-14 13.9% 1.23 .073
E-18 13.5% 1.02 .050
YVSF 12.5% − 1.77 .105
Journal of Quantitative Criminology
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Table2 presents the reasons for officer attrition from the randomized experiment. The
officers left due to an assignment change that did not involve BWC use (the most com-
mon reason for attrition), medical incapacitation, promotion, and leaving the department
via retirement or resignation. The n = 21 treatment officers who left the program had worn
the BWCs for an average of 13.6weeks (slightly more than 3months), ranging from only
9 days to 28.6 weeks. As such, n = 121 treatment officers (86.4% of 140) actually used
BWCs for varying time periods while performing their law enforcement duties during the
pilot program.
To address the observed attrition issue, we used intention-to-treat (ITT) analyses based
on the initial random assignment to treatment. ITT analyses provide fair comparisons
between treatment and control groups because it avoids the bias associated with the non-
random loss of study participants (Hollis and Campbell 1999). As such, all n = 140 treat-
ment officers and n = 141 control officers were included in the analyses presented here.
Treatment Contamination
The BPD randomized controlled trial attempted to minimize treatment contamination
effects by using different officers in the treatment and control groups. The BPD often oper-
ates one-officer patrol units; as such, interaction between treatment and control officers
during calls for service—and thus the potential for contamination—can be limited during
a typical shift but does occur when two officers work together or back up another officer
on particular calls. As such, our direct estimates of BWC impacts on outcomes measures
are biased towards the null hypothesis of “no difference” between treatment and control
groups. In other words, our estimates are conservative.
BPD calls for service data were used to monitor and assess the extent of possible con-
tamination during the September 2016 through August 2017 intervention period. The
research team eliminated duplicate citizen calls for service for the same event; as such,
the calls for service data represented unique call events. The evaluation team matched
the unique officer identification numbers for officers in the randomized controlled trial to
officer identification numbers in the call data. These data allowed us to determine which
officers were involved in call events as primary officers and as back-up officers during the
intervention period. As such, we were able to estimate the percentage of control officer call
events that involved one or more treatment officers.6
Table 2 Reasons for officer
attrition from RCT Reason Treatment Control
N Percent N Percent
Assignment change 10 47.6 7 38.9
Medically incapacitated 5 23.8 6 33.3
Promotion 3 14.3 3 16.7
Retired/resigned 3 14.3 2 11.1
Total 21 100.00 18 100.0
6 It is possible that BWC officers served as back-up to control officers and did not report their presence to
the BPD dispatcher. Given limited funds, we were not able to conduct a field test of this hidden source of
contamination that was not captured in the call data. As such, our analyses might be biased to an unknown
degree by any BWC officers who did not notify their presence to the dispatcher when backing up control
officers during the intervention period.
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Our analyses suggest modest contamination of control conditions by the presence of
BWC treatment officers in the BPD BWC RCT. During the intervention period, the n = 141
control officers were involved in 64,984 total calls: 46,403 calls as the primary officers
and 18,581 as back-up officers. Treatment officers were present at 23.7% of the same call
events attended by control officers (15,415 of 64,984 call events with control officers). The
percentage of calls per control officer that were contaminated by the presence of a treat-
ment officer ranged from .0% to 87.3% with a mean per control officer percentage of 27.0%
(standard deviation = .205).
Independent samples difference of means t tests suggest an inverse relationship between
call contamination and officer complaints and use of force reports. Control officers experi-
encing at least one complaint during the intervention period (n = 39, mean = 19.5%) had a
significantly lower mean percentage of their calls contaminated by BWC treatment officers
(difference = − 9.8%, t = 2.385, p = .019) when compared to control officers who did not
experience at least one complaint during the intervention period (n = 102, mean = 29.3%).
Similarly, control officers generating at least one use of force report during the intervention
period (n = 17, mean = 19.8%) also had a lower mean percentage of their calls contami-
nated by BWC treatment officers (difference = − 8.5%, t = 1.683, p = .095) when compared
to control officers who did not generate at least one use of force report during the interven-
tion period (n = 124, mean = 28.2%).
Quasi‑Experimental Design
The quasi-experiment was explicitly designed to examine possible diffusion of BWC treat-
ment effects to control officers in the treatment districts by providing a counterfactual group
of untreated matched officers from the control districts. The eligible 10 BPD districts were
matched into 5 pairs based on a qualitative exercise informed by simple quantitative analy-
ses of official 2015 BPD district crime and policing data and 2015 U.S. Census American
Community Survey data for the block groups that comprised the larger district areas.7 Sim-
ple but deliberate matching exercises ensure that any peculiarities found in one sample will
most likely occur in the other as well (see Blalock 1979; Rossi etal. 2004). One district
in each of the 5 pairs was randomly allocated to treatment conditions (Fig.1).8 Relative
to the 5 matched control districts, the 5 matched treatment districts had an overall higher
percentage of black residents and the officers in these districts generated higher numbers of
FIO reports (Table3). Even so, the matched control districts had generally similar policing
work environments when compared to the matched treatment districts.9 The BPD provided
7 An index measuring concentrated social disadvantage was calculated by standardizing and summing the
following block-group level variables from the 2015 ACS: the percentage of families below the poverty
level; percentage of households receiving public assistance; percentage of female-headed households with
children; and percentage of the population unemployed.
8 The 5 control districts were A-1 (Downtown), A-7 (East Boston), C-11 (Dorchester), E-13 (Jamaica
Plain), and E-5 (West Roxbury). The 5 treatment districts were B-2 (Roxbury), B-3 (Mattapan), D-4 (Back
Bay/South End), D-14 (Allston/Brighton), and E-18 (Hyde Park).
9 Districts B-2 and B-3 have majority black residential populations (45.3% and 79.5%, respectively). Fagan
etal. (2016) found a strong association between the percentage of black residents and the number of FIO
encounters reported by the BPD in Boston neighborhoods, controlling for crime and other factors. Two
sample t tests of means and two sample z tests of proportions were performed on the matching covariates
reported in Table3. None of the differences reported between the treatment and control districts were sta-
tistically significant at the p < .05 level (e.g., percent black residents = -20.8% difference, z = .74, p = .459).
Given the small numbers of districts in the two samples (n1 = 5, n2 = 5), the two sample tests were not
Journal of Quantitative Criminology
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the research team with a database of n = 311 patrol and Anti-Crime Unit (ACU) officers10
Fig. 1 Boston Police Department districts included in BWC evaluation
10 ACU plainclothes officers assigned to the control districts were included as counterfactuals for the YVSF
officers in the control group. ACU officers work to apprehend repeat offenders and increase police presence
in crime hot spots within districts. While the foci of ACU activities are broader, the ACU and YVSF engage
in similar proactive policing tactics. The matching exercise included n = 38 eligible ACU officers.
adequately powered to detect bona fide differences. As such, the results of these hypothesis tests were not
robust enough to be reported here.
Footnote 9 (continued)
Journal of Quantitative Criminology
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from the control districts who were actively performing policing duties and worked the day
and first half shifts as of September 1, 2016.
Propensity score matching routines were used to develop balanced groups of matched
control officers from the treatment districts and matched comparison officers from the con-
trol districts (Leuven and Sianesi 2003). Propensity score matching routines summarize
relevant pre-treatment characteristics of each officer into a single-index variable—the pro-
pensity score—and then matches officers in the control districts to control officers in the
treatment districts on values of the propensity score (Rosenbaum and Rubin 1985). Radius
matching with a caliper = .01 was selected from the wide range of available propensity
score matching techniques (Apel and Sweeten 2010). After the maximum propensity score
caliper is established, this algorithm matches all untreated units within the given radius
of a treated units (Caliendo and Kopeinig 2005; Dehejia and Wahba 2002). The propen-
sity score matching routine included the following characteristics: age, race, sex, time on
the job, shift, plainclothes assignment, mean yearly citizen complaints (2013–2015), mean
yearly use of force incidents (2013–2015), mean monthly responses to call events (2015),
mean monthly crime incident reports (2015), mean monthly arrests (2015), and mean
monthly FIO reports (2015).
Stata 15 statistical software was used to execute PSMATCH2 propensity score match-
ing routine. Table4 includes the post-matching means for 133 matched control officers
from the treatment districts and the 268 matched comparison officers from the control dis-
tricts, t-tests and p-values, and standardized bias statistics showing the average difference
as a percentage of the mean standard deviation between the groups (Rosenbaum and Rubin
1985). The results confirm that the matched sample created balanced treatment and com-
parison groups as all p-values are higher than .05 and the bias statistics are less than 20.0
(Austin etal. 2007). The propensity score matching routine indicated that 133 matched
control officers from the treatment districts and the 268 matched comparison officers from
the control districts were in the common support region, ensuring that officers with the
same values of covariates have the same probability of being treated and untreated (Heck-
man etal. 1999).
Analytical Approach
Since randomized experiments control for confounding factors by design, analyses of
experimental data do not require extensive statistical modeling to ensure rival causal
Table 3 Comparison of treatment
and control BPD districts, 2015 Treatment Control
N 5 5
Mean population 64,126.2 54,831.0
Mean percent black population 37.5 16.7
Mean percent hispanic population 17.8 24.1
Mean concentrated disadvantage index .342 − .361
Mean calls per 100K population 56,863.2 60,861.8
Mean index crime rate per 100K population 3212.0 2993.4
Mean FIO reports 2539.4 1587.2
Mean arrests 1210.6 1221.4
Mean officers assigned 83.6 84.0
Journal of Quantitative Criminology
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influences are identified and controlled (Weisburd 2010). As such, we used independent
samples t tests and standardized mean differences (Cohen’s d) to test the direct impact of
the BWCs on treatment officer outcomes relative to control officer outcomes during the
12-month intervention period. However, the relatively small number of officers in the ran-
domized experiment makes it challenging to estimate the true impact of the BWC treat-
ment (see Cohen 1988; Lipsey 1990). The standardized mean difference test only had an
estimated statistical power of .39 to detect a small standardized effect size of .20 using a
two-tailed test with α = .05. The impact of BWCs on treatment officer outcomes relative to
control officer outcomes was also estimated through a difference-in-differences (DID) esti-
mator (Card and Krueger 1994). The use of a DID estimator in a panel regression model
with 12- month pre-intervention and 12-month intervention period observations for each
officer had the benefit of increasing the statistical power of the research design (281 offic-
ers × 2 observations each = 562 total observations) to detect potentially small effect sizes.
For a two-tailed test with α = .05, the DID impact analysis had an estimated statistical
power of .65 to detect a small standardized effect size of .20 and statistical power of .99 to
detect a moderate standardized effect size of .40.
The DID estimator evaluates the difference in a treatment officer’s post-intervention out-
comes at time t compared with their pre-intervention outcomes, relative to the same dif-
ference for the control officers in the experiment. The equation for our panel regression
models was:
As shown in Eq.(1), (Yit) represents our outcome measure for each individual officer (i)
during a specific observation period (t). The regressor Groupi is a dummy variable identi-
fying whether an individual officer (i) was in the treatment group (1) or not (0). The omit-
ted group comprises control officers in the experiment. The regressor Periodt is a dummy
variable for whether the officer outcome was measured during the intervention period (1)
or during the pre-intervention period (0). Our primary interest is on coefficient β3, which
(1)
Yit
=𝛽0+𝛽1Group
i
+𝛽2Period
t
+𝛽3
(
Group
i
×Period
t)
+u
i
Table 4 Balancing control officers in treatment districts and comparison officers in control districts through
propensity score matching
N = 401, Results based on radius matching propensity score model (caliper = .01). There were n = 133 con-
trol officers in treatment districts and n = 268 comparison officers in treatment districts
Characteristics Treated Untreated % bias t test p > |t|
Male .914 .935 − 7.5 − .68 .498
White .621 .664 − 8.9 − .75 .456
Age 36.669 39.726 − .6 − .05 .960
Years on the job 11.621 11.769 − 1.6 − .14 .885
Plainclothes .121 .131 − 2.8 − .28 .781
Day shift .42 .48 − 12.1 − .96 .337
Mean yearly complaints .207 .179 7.3 .56 .579
Mean yearly use of force .121 .120 .2 .02 .985
Mean monthly calls 41.340 36.255 15.4 1.29 .198
Mean monthly crime incidents 9.711 10.780 − 12.7 − 1.05 .296
Mean monthly arrests 5.489 5.271 2.7 .22 .824
Mean monthly FIO reports 2.886 2.295 14.9 1.25 .213
Journal of Quantitative Criminology
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conforms to the product of the group dummy with the period dummy and represents the
DID estimate of the effect of BWCs on the officer outcome measure. To ensure that the
coefficient variances were robust to violations of the homoskedastic error assumption of
linear regression models, robust standard errors were used.
The yearly pre-intervention means suggested that citizen complaints and officer use
of force reports were distributed as rare event counts (see Table1). Indeed, the average
officer participating in the BWC experiment experienced a citizen complaint against them
roughly once every 4.5years (.22) and generated a use of force report roughly once every
8.3 years (.12). As such, Poisson panel regression models were used to estimate direct
treatment impacts on these outcomes.11 Ordinary Least Squares (OLS) panel regression
models were used to estimate treatment impacts on mean monthly responses to dispatched
call events, mean monthly self- initiated call events, mean monthly crime incident reports,
mean monthly arrests, and mean FIO reports during the intervention and pre-intervention
study periods.
The DID panel regression models were used to analyze possible diffusion of BWC
treatment impacts on outcomes during the intervention and pre-intervention periods for
the matched control officers in the treatment districts relative to the matched untreated
officers in the control districts. These models included the inverse probability of treat-
ment weighted propensity score value (IPTW = 1/propensity score) for the officers in the
matched groups. The IPTW covariate controls for observable differences between the
officers in the matched treated and untreated groups, given the variables used to estimate
the propensity score (Imbens and Wooldredge 2009). Since direct impacts and spillover
impacts are logically linked, it is important to note here that the results of diffusion of
BWC treatment models are only presented for outcomes showing a direct BWC treatment
effect in the randomized controlled trial.
Results
The standardized mean difference analyses suggested small direct impacts of BWCs on
citizen complaints (d = − .137, SE = .061, p = .021) and, at the less restrictive p < .10 level,
officer use of force reports (d = − .109, SE = .092, p = .067) for treatment officers relative
to control officers during the intervention period. In practical terms, the group of treatment
officers generated 19 fewer complaints and 10 fewer use of force reports relative to the
group of control officers when wearing BWCs during the intervention period.12
Table5 presents the results of the DID panel Poisson regression analyses of the direct
impact of BWC on citizen complaints and use of force reports for treatment officers rela-
tive to control officers. The DID estimators suggested stronger BWC impacts on citizen
11 Post-estimation likelihood ratio tests confirmed that these outcomes were distributed as Poisson rather
than negative binomial processes. For the citizen complaints model, the likelihood χ2 (df = 1) = .78,
p = .188. For the officer use of force reports model, the likelihood χ2 (df = 1) = 1.75, p = .093.
12 These intervention period differences are slightly larger than what was reported in an unpublished pre-
liminary impact evaluation report (see Braga etal. 2018a). The discrepancy is due to a reporting lag in the
entry of complaints and use of force reports into the data systems maintained by the BPD Bureau of Profes-
sional Standards when the preliminary data were provided to the research team in September 2017. There
are no time constraints limiting when complainants can file Internal Affairs Division complaints against
BPD officers. Officer use of force reports are investigated and reviewed by an established chain of com-
mand.
Journal of Quantitative Criminology
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Table 5 Impact of BWC on Citizen complaint counts and Officer use of force report counts: panel poisson regression models
DID Differences-in-differences, Coef. Coefficient, RSE Robust standard error (clustered by officer)
*p < .05, **p < .01
Variable Randomized controlled trial Quasi-experiment
BWC direct effects BWC diffusion effects
Complaints Coef. (RSE) Use of Force Coef. (RSE) Complaints Coef. (RSE) Use of Force Coef. (RSE)
BWC impact (DID) − .704 (.341)* − 1.009 (.509)* − .483 (.245)* − .701 (.449)
Group (1 = treated) .848 (.557) 1.279 (.751) .619 (.484) 1.158 (.788)
Period (1 = intervention) .388 (.212) − .051 (.343) .925 (.747) .647 (.387)
Inverse propensity score – – .026 (.351) − .574 (.505)
Constant − 2.141 (.374)** − 1.901 (.552)** − 2.784 (.752)** − 2.003 (.791)**
Log pseudolikelihood − 321.294 − 224.976 − 490.284 − 313.548
Wald χ2261.28** 278.09** 298.64** 390.21**
Wald df 3 3 4 4
Observations (officers × period) 562 562 802 802
Number of officers 281 281 401 401
Journal of Quantitative Criminology
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complaint and officer use of force report outcomes. Exponentiating the Poisson regres-
sion coefficients into incidence rate ratios suggests that the placement of BWCs on treat-
ment officers resulted in a statistically-significant 50.5% reduction in citizen complaints
(IRR = .495, p = .039) and a statistically-significant 63.6% reduction in officer use of force
reports (IRR = .364, p = .047) relative to control officers when comparing pre-intervention
and intervention time periods.
Table5 also presents the results of the quasi-experimental analysis of potential diffu-
sion of BWC treatment effects. The results suggest varying spillover benefits in the civility
of police-citizen encounters for control officers who were present in the same districts as
BWC treatment officers. The DID estimators report that matched control officers in treat-
ment districts experienced a statistically-significant 38.3% reduction in citizen complaints
(IRR = .617, p = .048) and a non-significant decrease in use of force reports (IRR = .496,
p = .119) relative to matched untreated officers in control districts when comparing pre-
intervention and intervention time periods.13 The standardized mean difference analy-
sis found a small diffusion impact of BWCs on citizen complaints (d = − .118, SE = .041,
p = .018) for matched control officers in the treatment districts relative to matched untreated
officers in the control districts during the intervention period. In contrast, the standardized
mean difference comparison suggested null spillover effects on officer use of force reports
matched control officers from the treatment districts relative to matched untreated officers
in the control districts during the intervention period (d = − .026, SE = .061, p = .600).
The standardized mean difference analyses (not shown here) did not reveal any statis-
tically-significant impacts in the officer activity outcome measures for treatment officers
relative to control officers during the intervention period. These null findings were con-
firmed by the DID panel OLS regression analyses (Table6). These analyses suggest that
the placement of BWCs on treatment officers did not change the monthly mean number
of dispatched calls received, calls that were self-initiated, the crime incident reports com-
pleted, arrests made, and FIO encounter reports when compared to the same monthly mean
activity outcomes for the control officers over the course of the pre-intervention and inter-
vention periods. Consistent with these results, BPD officers who wore BWCs during the
RCT did not change their level of activity in any significant way during the 1 year pilot
program.
Conclusion
This study used a randomized controlled trial in conjunction with a quasi-experimental
design to estimate the direct and spillover impacts of BWCs on citizen complaints, officer
use of force reports, and police work activities. Results indicate that outfitting BPD offic-
ers with BWCs generated modest but statistically-significant decreases in citizen com-
plaints and use of force reports relative to control officers. Findings from the quasi-exper-
imental design suggest that the placement of BWCs on treatment officers also generated
13 Note that the program impacts were robust across a variety of matching algorithms and caliper/band-
width selections: radius matching (caliper .1, .01); Gaussian kernel matching (bandwidth = .01, .001),
Epanechnikov kernel matching (bandwidth = .1, .01), and simple nearest neighbor matching. Although the
estimates differed slightly across the varying propensity score matching methods, the BWC treatment statis-
tically-significant spillover effect on officer complaints remained robust while the spillover effect on officer
use of force reports never reached the less restrictive p < .10 level of significance.
Journal of Quantitative Criminology
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Table 6 Impact of BWC on mean monthly officer activities: randomized controlled trial, panel OLS regression models
DID Differences-in-differences, Coef. Coefficient, RSE robust standard error (clustered by officer)
*p < .05, **p < .01
Dispatched calls Officer-initiated calls Crime incidents Arrest reports FIO reports
Variable Coef. (RSE) Coef. (RSE) Coef. (RSE) Coef. (RSE) Coef. (RSE)
BWC impact (DID) − 1.687 (1.369) − .870 (.789) − .055 (.808) .018 (.061) .456 (.351)
Treatment group (1 = treated) 3.846 (2.684) 2.264 (1.388) 1.621 (1.591) .126 (1.21) − 1.048 (.775)
Period (1 = intervention) .548 (1.242) .336 (.697) − .795 (.716) − .074 (.048) − .981 (.279)**
Constant 16.451 (2.325)** 7.979 (1.72)** 8.941 (1.363)** 1.720 (.086)** 3.067 (.618)**
Overall R2 .014 .015 .017 .016 .017
Wald χ28.64* 8.66* 9.38* 8.48* 18.43**
Wald df 3 3 3 3 3
Observations (Officers × Period) 562 562 562 562 562
Number of Officers 281 281 281 281 281
Journal of Quantitative Criminology
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statistically-significant spillover reductions in complaints against control officers in treat-
ment districts relative to complaints against matched comparison officers in untreated dis-
tricts. Though use of force reports for control officers in treated districts decreased relative
to matched comparison officers in untreated districts, this reduction was not statistically
significant. Lastly, this study found no direct effects of BWCs on BPD officer work activ-
ity or discretion measures after assessing possible pre-post changes to dispatched calls
received, officer-initiated calls, crime incident reports, arrests, or FIO encounter reports for
treatment officers relative control officers.
Like many program evaluations, this study has at least two noteworthy limitations. First,
since this assessment only involved one police agency with its own organizational culture
and unique environmental factors, the results may suffer from limited external validity and
not be generalizable beyond the BPD (Shadish etal. 2002). Nonetheless, as suggested by
our literature review, the results of this study are consistent with the direct and contami-
nation effects that have been reported in other locations which bolsters confidence in the
generalizability of our findings. Second, this and many other BWC evaluations continue
to be limited by the “black box” nature of the research designs applied (Ariel etal. 2018a,
b). Existing program evaluations have thus far been limited in their ability to explore the
underlying mechanisms that lead to observed behavioral changes. As such, little is known
about how and why BWCs affect the behaviors and actions of citizens and officers alike. We
do not know whether the observed changes in Boston and elsewhere are generated through
deterrence, public-awareness, both mechanisms, or some other theoretical explanation.
While observing desirable changes to bottom-line outcomes is clearly important, future
research should be designed to our enhance our understanding of the processes through
which behavioral changes are achieved in order to develop more refined, and possibly more
effective, departmental BWC policies and practices.
While a growing body of evidence suggests consistent impacts of BWCs on the civility
of police-citizen encounters, the existing program evaluation literature on the effects of
BWCs on police officer work activities and discretion is still developing and largely sug-
gests heterogeneous results (Lum etal. 2019). Indeed, our study found null effects on these
(available) outcome measures, while other studies reported increases in arrests and cita-
tions (e.g., Braga etal. 2018b) and mixed impacts of the BWCs on various measures (e.g.,
Ready and Young 2015). The observed heterogeneity in study outcomes may be linked
to variations in BWC activation policies, officer compliance to BWC policy requirements,
and the organization and community contexts in which the studies occurred. For instance,
Ariel etal. (2016a) found that variations in compliance to BWC activation policies across
police departments in their multisite randomized experiments influenced the number of
assaults on BWC officers. As such, a comprehensive and systematic review of these kinds
of moderators across studies that might explain the observed heterogeneity in study find-
ings seems warranted. Such an examination would shed some much-needed light on why
variation exists by uncovering the salient factors that seem to affect officer proactivity and
discretion outcomes.
This study finds that the limited implementation of BWCs in police departments may
indeed stimulate broader “contagious accountability” suggested by Ariel et al. (2017)
through the possible modification of the behaviors of officers not equipped with BWCs.
The BPD trained 140 treatment officers on the technical aspects of BWC operations and
departmental policy for authorized usage and some 121 officers wore BWCs over the
course of the 1-year intervention period in 5 treatment districts. Roughly 24% of the call
events attended by the 141 control officers had BWC officers directly present and these
treatment officers were generally present in the control officers’ work environment in the
Journal of Quantitative Criminology
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5 treatment districts. Relative to matched comparison officers in the 5 control districts, our
evaluation suggests that the direct benefits of the BWC intervention on citizen complaints
(and, perhaps to a lesser degree, use of force incidents) diffused from the treatment offic-
ers to the control officers. In essence, the presence of BWCs in specific command areas
seemed to modify encounter behaviors for treatment and control officers alike. Moreover,
due to the publicity associated with the rollout of the cameras in the 5 treatment districts,
the behavior of citizens in these neighborhoods may have also been influenced by the mis-
taken belief that control officers in encounters were outfitted with cameras when these
officers were not.
Some rigorous evaluations have acknowledged the issue of treatment contamination of
control conditions and assessed these spillover effects by considering contemporaneous
declines in selected outcomes for the control group during the intervention period (e.g.,
Ariel etal. 2015; Braga etal. 2018b; White etal. 2018). In this study, the availability of
counterfactual conditions and matched comparison officers to compare outcomes for con-
taminated control officers provided a much more definitive appraisal of the existence of
the spillover benefits generated by BWCs. Future evaluations of the impacts of BWCs on
behavioral outcomes should explicitly consider the existence of spillover effects and be
designed to isolate and measure both the direct and indirect impacts of the technology.
Doing so would better position social scientists to establish the overall impacts of the adop-
tion of BWCs on police officer behavior and avoid extensive treatment contamination of
control conditions that undercut the establishment of treatment effects that may, in fact,
exist (e.g., Yokum etal. 2017). Moreover, research may be unintentionally discounting the
benefits of BWCs by not accounting for potential spillover effects. Researchers should con-
sider the careful recommendations made by Ariel etal. (2018) on a variety of methodolo-
gies that could be employed to measure these kinds of spillover effects in future program
evaluations.
Crime policy scholars have long acknowledged the existence of diffusion of crime con-
trol benefits in evaluations of crime preventions that generate crime reductions that extend
to unprotected areas and individuals (Clarke 1989; Clarke and Weisburd 1994; Guerette
and Bowers 2009). Deterrence is considered a key mechanism in generating diffusion
effects, as prospective offenders are dissuaded from committing crimes when they believe
that the risks of detection and arrests are much greater than actual apprehension risks for
a particular crime opportunity. The results of this study suggest that a limited adoption of
BWCs by a police department may generate spillover deterrent impacts as officers and citi-
zens perceive an increased threat that inappropriate and illegal behaviors will be captured
on video even when BWCs are not actually present during an encounter. Similarly, the
incomplete introduction of BWCs may signal to non-BWC officers that their behaviors are
being scrutinized and influence them to be more mindful of departmental policies govern-
ing appropriate behavior. These spillover self-awareness effects could be enhanced by the
regular presence of BWC officers during their responses to calls for service. Partial imple-
mentations of BWCs in police work areas could also stimulate more desirable behaviors by
civilians during encounters with non-BWC officers as they may believe responding officers
are equipped with BWCs when they are not.
The existence of beneficial spillover effects has important implications for how depart-
ments execute BWC programs. In particular, strategic deployment of cameras may help
some departments manage the costs associated with implementation. Departments may be
able to achieve similarly powerful positive benefits through only partial BWC deployments.
Police executives should be mindful that deterrent impacts can decay over time (Sherman
1990) and, as such, regular publicity of the general presence of BWCs should accompany
Journal of Quantitative Criminology
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partial deployments to maximize potential spillover effects onto untreated police-citizen
encounters. In police work areas where officers frequently patrol in two-officer cars or in
specialized units with multiple officers working the same assignments, the benefits of one
camera seem likely to diffuse to other present officers. This would eliminate the need for all
officers to be outfitted with BWCs. For routine patrol deployments that include one-officer
units, departments can assign more cameras to areas with higher rates of complaints, calls
for service, and/or proactive stops to ensure that these high-risk environments receive more
comprehensive coverage. Additionally, varying officer BWC assignments may increase
other officers’ uncertainty regarding who may or may not be wearing a camera, thus
increasing any associated deterrent effects (Sherman 1990). Police departments could also
consider assigning BWC to specific officers (such as “rookie” officers during their proba-
tionary periods), officers with high numbers of complaints and/or use of force reports (such
as those flagged in early intervention systems), or even those officers who are top perform-
ers in the agency (e.g., to capture “good policing” for training purposes).
The initial purchase, setup, and deployment of BWCs to approximately 2200 officers
in the BPD is anticipated to require approximately $8.5 million over the course of 3years,
after which the Mayor’s Office estimates annual costs will be about $3.3 million (City of
Boston Mayor’s Office 2018). While costs in smaller departments may be recouped through
savings associated with reduced civil litigation, the cost-effectiveness of BWCs may be less
clear in larger departments where initial and ongoing expenses are much more substantial
(Police Executive Research Forum 2018). Since use of force events and citizen complaints
are relatively rare events, it is unclear as to whether avoided civil litigation will compen-
sate for the significant investments required by larger police departments to place BWCs
on all officers with assignments that involve encounters with the public (Police Executive
Research Forum 2018).
As noted at the outset of this article, the rapid diffusion of BWCs in police departments
across the United States has been powerfully influenced by calls for increased police trans-
parency and accountability. Nonetheless, it is difficult to ignore that there are other, more
pragmatic, reasons for police departments to quickly implement this technology—BWC
videos reflect the officers’ gaze, and can serve to counter narratives recorded on smart-
phones by members of the public, and potentially reduce organizational liability. For
instance, Crow etal. (2017) recently surveyed community members on their support for
the adoption of BWCs by their police departments, hypothesizing that respondents who
were satisfied with the police would see less need for BWC oversight, and thus less sup-
portive of BWCs overall. Their results suggested otherwise, leading them to conclude that,
“community members who believe the police are doing a good job and treating people
fairly are more likely to support BWCs, not as a mechanism to correct bad police behav-
ior, but as a tool to combat negative views of the police that result from the rare bad act
caught on cell phone video” (Crow etal. 2017, p. 605). The notion that BWCs might be
used as prophylactic strategy—a countering gaze against smartphone videos— is consist-
ent with Foucault’s (1977) model of competing gazes. It also suggests that there might be
little backing for partial BWC adoption strategies by police departments and their support-
ers who are concerned about capturing officer video evidence that counter citizen claims of
police misconduct.
The achievement of broader goals that are hard to measure and figure into cost–ben-
efit estimates, such as enhancing police transparency, accountability, and legitimacy, could
very well make the high costs of BWCs worthwhile investments for police departments
struggling with these issues. And the absence of BWC video capturing a highly contro-
versial police-citizen encounter could result in diminished police legitimacy, generate
Journal of Quantitative Criminology
1 3
expensive overtime costs when managing associated citizen protests, and be particularly
detrimental should protests become destructive riots. Officers without BWCs who receive
frivolous complaints won’t have video and audio evidence to exonerate them. Further, the
disproportionate deployment of BWCs to increase coverage in higher-activity, disadvan-
taged minority neighborhoods could result in strong negative public reactions to partial
BWC deployment schemes. Still, the findings of this study suggest that partial imple-
mentations of BWCs could generate very desirable changes to police-citizen encounters
through both direct impacts and spillover impacts. Future studies should assess the cost-
effectiveness and completeness of video coverage of police-citizen encounters for partial
BWC implementation schemes relative to the full adoption of BWCs on all officers in work
assignments that interface with the public.
Acknowledgements This work was supported through research funds provided by the City of Boston and
the Rappaport Institute for Greater Boston. The authors would like to thank Mayor Martin Walsh, Police
Commissioner William Evans, Superintendent Kevin Buckley, Superintendent Frank Mancini, Superinten-
dent John Daley, Amy Condon, Desiree Dusseault, and Dawn Mello for their support and assistance in the
completion of this research report. The conclusions presented here are those of the authors and do not rep-
resent the official position of the City of Boston, Boston Police Department, or the Rappaport Institute for
Greater Boston.
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