Increasing Cooperation With the Police Using Body Worn Cameras

Introduction

On April 7, 2015, a white North Charleston police officer was charged with murdering Walter Scott, an unarmed black man, after shooting Scott eight times. The incident was caught on a bystander’s video contradicted several parts of the officer’s initial account (New York Times, 2015). Following this and similar incidents, police departments have been pushing to procure and implement the use of Body Worn Cameras (BWCs). At least 15 states are currently considering “BWCs Bills,” requiring police officers to wear these devices on the line of duty. Many believe that BWCs will greatly affect public health, at least through the minimization of use of force—a concern that the Scott incident brings to light more than ever before in late modernity.

Despite great promise, the level of excitement over this hypothesis overwhelmingly exceeds our evidence-base on the efficacy of these devices, on virtually all fronts. With only a few notable exceptions reviewed hereunder, there is in fact a limited body of published, rigorous, evaluation research on the effects that BWCs might have in policing (Lum, Koper, Merola, Scherer, Reioux, 2015; White, 2014). Using BWCs in police operations can potentially be linked to behavioral changes in police–public encounters, such as reduced reported use of force (e.g., Ariel et al., 2016a; Ariel et al., 2016b; Ariel, Farrar, & Sutherland, 2014; Jennings, Lynch, & Fridell, 2015). However, what about other outcomes?

A somewhat neglected avenue of research thus far has been on the possibility that BWCs could affect police legitimacy. One manifestation of enhanced police legitimacy is an elevated likelihood of reporting crimes to the police (Sunshine & Tyler, 2003). The more we trust the police—whether because they are viewed as “more just” or because they are perceived to be more effective, or both (Tankebe, 2013)—the more we are likely to cooperate, come forward when we have witnessed a crime, and ask for assistance in emergency situations. How would BWCs come into play here? If the public believes that officers that are “being watched” by BWCs are more likely to provide them with what they consider a more professional service than officers who are not under BWCs surveillance, they might be more likely to cooperate. It is logical to assume that an individual will be more willing to come forward and report a crime to the police, if that person experiences an elevated perception of police professionalism. In other words, if BWCs introduce enhanced police accountability, greater transparency, or improved utility, then the public will view the police as more legitimate—and the behavioral display of this legitimacy is increased cooperation.

However, testing the effect of BWCs on reporting behavior presents methodological challenges. Citywide or neighborhood-level assessments, with crude before-after analyses, cannot unmask this effect of BWCs, as alternative explanations to the treatment effect cannot be ruled out (Shadish, Cook, & Campbell, 2002). Comparison groups are needed. At the same time, a test in which BWCs are randomly allocated to officers (i.e., when the officer is the unit of analysis of the test) presents measurement difficulties as well, because crime reporting variations are unlikely to be attributed to particular officers, or even a group of officers. A more useful unit of analysis for testing the treatment effect on crime is a small geographic unit: the street segment level. Street segments present a palatable option for studying the effect of BWCs on crime reporting, for two major reasons, both of which are associated with consistency. First, there is ample evidence which suggests that crime levels—especially in hotspots—remain stable in terms of their spatiotemporal location (Weisburd, Bushway, Lum, & Yang, 2004), including the overall number of crime incidents they experience over time (Weisburd et al., 2006). Therefore, if treatment is allocated to some street segments but not others (preferably through a random allocation of units), the untreated segments can serve as viable counterfactuals, to which the treatment effect can be compared. Second, and specifically for the framework of BWCs research, street segments are likely to receive a similar “dosage” of police attention (e.g., similar number of patrol hours and policing style), which is conditional primarily on the number of incidents the streets experiences: “hotter” hotspots receive more response policing, while “cooler” hotspots receive less (Ariel, Weinborn, & Sherman, 2016). Thus, these features—consistency of both crime patterns and overall police intervention—create comparable units of analysis with less “statistical noise,” where the effect of BWCs (or any intervention) can be more accurately estimated.

Using this approach, I tested the effect of BWCs on street segments in Denver, CO, over a period of 6 months. Street segments in one police district out of six was assigned BWCs, while all other street segments in other districts served as comparison sites without BWCs. Officers were asked to conduct patrols across the city, as they normally would, and to respond to calls for service. The target areas were established on the basis of street segments methodology (Weisburd, Groff, & Yang, 2012) and were then stratified according to “heat” level, that is, the number of incidents in the year prior to the study. The stratification process created homogenous street segments (see Ariel & Farrington, 2014), ranging from 1 to 20 incidents per year in the lower stratum, to 100 or more crime incidents per year in the upper bound stratum, mirroring variations in other characteristics of street segments as well (residential, night time economy, etc). Results were then measured based on changes in “crime density” in the treatment, versus the control district segments—or the number of 911 incidents per 100 meters.

The article begins with a narrative review of the literature on BWCs, followed by an exploration of the possible effect this technology may have on crime reporting, more broadly. The case for using street segments as the unit of analysis is then laid out, with an emphasis on the stability and stronger tests that can potentially be used in the study of BWCs (and beyond), when using these small-size, yet prevalent units. A description of the methods used in this experiment are depicted next, explaining the treatment and control conditions, the stratification procedure, the outcome measures, and the statistical analyses used to estimate the causal link between police patrols with BWCs on crime reporting. After presenting the results of these analyses, the article concludes with a discussion of the findings and the limitations of the approach.

Why Would Body-Worn Cameras Have an Effect on Crime Reporting?

The proliferation of BWCs in police operations is continuously increasing worldwide. BWCs allow the police to record, both in audio and video, interactions between the police officers and witnesses, victims, and offenders. While CCTV and police dashboard cameras have been widely available for some time now, BWCs allow officers to collect and store evidence from the officer’s perspective. Their expansion has recently been portrayed dramatically, with massive media hype and a premier endorsement at the Presidential Taskforce on Crime, as a device that can aide in restoring the seemingly lost legitimacy of the police (wh.gov/community-policing).

A recent review of the available evidence conducted by Lum et al. (2015) has shown that there are currently 12 existing empirical studies of BWCs and about 30 ongoing research projects (see also review by White, 2014). While there were attempts to implement BWCs in policing nearly a decade ago (Goodall, 2007; Harris, 2010), evidence on their effectiveness has only surfaced in the last couple of years (see Lum et al., 2015). Five of the studies employed randomized controlled trials (Ariel et al., 2016a, 2016b; Ariel et al., 2014; Grossmith et al., 2015; Jennings et al., 2015; Owens, Mann, & Mckenna, 2014), and others have used less robust designs. For example, the most recent studies in Orlando, FL, where the unit of analysis was the individual officer (Jennings et al., 2015), volunteers versus non-volunteers (Ready & Young, 2015), or some version of cluster random assignment (Grossmith et al., 2015), have all measured various consequences of the use of BWCs in police routine operations. Lesser designs, without random allocation of units into treatment and control conditions (e.g., Ariel, 2016; Ellis, Jenkins, & Smith, 2015), have produced mixed results about the effectiveness of BWCs, ranging from supportive evidence, to null, and even backfiring effects.

The Rialto experiment (Ariel et al., 2014) was the first randomized controlled trial that looked at the effectiveness of BWCs, and specifically focused on use of force and complaints. Rialto Police Department, a small jurisdiction in California with just over 50 frontline officers, compared nearly 500 police shifts during which all police–public encounters were equally assigned to either treatment or control conditions. During treatment shifts, Rialto officers were asked to videotape all their encounters with members of the public and to store evidence on a secured cloud. In control shifts, the officers were tasked never to carry on them and use the devices. Outcomes were then measured, in terms of officially recorded use of force incidents and complaints lodged against Rialto police officers. Following this 12-month experiment, Ariel et al. (2014) reported a relative reduction of roughly 50% in the total number of incidents of use of force compared with control conditions, and about a 90% reduction in citizens’ complaints, compared with the 12 months prior to the experiment.

Ready and Young (2015) conducted an experiment with the Mesa, Arizona Police Department. The study analyzed nearly 3,700 field reports completed by 100 sworn patrol officers. Assignment of the officers into treatment and control groups have resulted in several important findings: first, officers that did not wear body worn cameras were more likely to conduct stop and search and were also more likely to make an arrest. This means that wearing BWCs may cause officers to be more cautious and risk-averse than control conditions. At the same time, treatment officers were more likely to give citations and initiate encounters. This suggests that BWCs may cause officers to be more proactive with this technology, however, without increasing their use of invasive strategies that “may threaten the legitimacy of the organization” (Ready & Young, 2015, p. 445).

Finally, Jennings et al. (2015) have also observed the effect of BWCs on policing but focused particularly on response to resistance incidents. In their controlled experiment, they randomly assigned 46 (of 89) officers to wear BWCs, with the remaining 43 officers assigned to a no-BWC condition. The study has shown that BWCs reduced these types of incidents and serious external complaints. The prevalence of response-to-resistance incidents and the prevalence and frequency of serious external complaints were significantly less for officers randomly assigned to wear BWCs (p. 480).

Notably, the existing research focused primarily on the cooling off effect of BWCs in police–public encounters (see Ariel, 2016). “Functions of the [BWC] are to record evidence of activities and behaviors relevant to a crime, deter violence or negative behavior against an officer, and improve the accountability of police officers and reduce the number of complaints against officers” (National Institute of Justice, 2012, p. 1). The mechanism that is assumed to causally link BWCs to these outcomes in police daily operations revolves around two complementary theories: self-awareness and deterrence theories (see Ariel, 2013; Ariel et al., 2014; White, 2014). First, several lines of research suggest that people alter their behavior once made aware that they are being observed (Chartrand & Bargh, 1999; Dzieweczynski, Eklund, & Rowland, 2006; Jones & Nisbett, 1971). A rich body of evidence on perceived social surveillance—self-awareness (Wicklund, 1975) and socially desirable responding (Paulhus, 1988)—proposes that people adhere to social norms and change their conduct because of their cognizance that someone else is watching (Munger & Shelby, 1989). Knowing, with sufficient certainty, that our behavior is being observed or judged, affects various social cognitive processes: We experience public self-awareness (Duval & Wicklund, 1972; Gervais & Norenzayan, 2012) and feel the need to cooperate with rules (Barclay, 2004; Milinski, Semmann, & Krambeck, 2002; Wedekind & Braithwaite, 2002).

In criminology, these cues are more broadly explored under deterrence theory (the second theory linked to the present study). An extensive body of recent rigorous research, across several categories of criminal behavior, has shown that when certainty of apprehension for wrongdoing is “high,” socially and morally unacceptable acts are dramatically less likely to occur (Nagin, 2013a; Pratt, Cullen, Blevins, Daigle, & Madensen, 2006; Von Hirsch, Bottoms, Burney, & Wikstrom, 1999). Particularly, in terms of crime and disorder, when the consequences of apprehension can be bleak (imprisonment, fines, etc.), people simply do not want to get caught. In this framework, getting caught doing something morally or socially wrong is often registered as behavior that can potentially lead to negative consequences, which is an outcome that rational individuals tend to avoid (Klepper & Nagin, 2006; Nagin, 2013a). Studies have, nevertheless, uncovered a propensity to avoid negative outcomes, and findings generally agree that individuals react compliantly to even the slightest cues indicating that somebody may be watching (see Bateson, Nettle, & Roberts, 2006; Burnham & Johnson, 2005; Fehr & Schneider, 2010; Haley & Fessler, 2005).

It is important to note that this mechanism is true for both the offender and the police officer, as both actors are assumed to be rational calculators. Offenders are deterred by physical cues around them that indicate the probability of getting caught breaking the law, while the power-holders are equally deterred by ecological signals that motivate them to comply with regulations, rules, and norms. As such, a BWC can be viewed as an external contingency and will likely deter people against noncompliance (criminal, administrative, or both). Tilley (1993, pp. 3–5) rightly pointed out that the cameras may “fire a number of mechanisms,” but that one prominent preventative mechanism of a cameras is that it “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.” Much like live observers, mirrors, or pictures of eyes, cameras can not only make us continuously conscious of the fact that we are being watched but also drive us into compliance. When we become aware that a video camera is recording our actions, we become aware that unacceptable behaviors are likely to be captured on film, and the perceived certainly of punishment is at its highest. “Getting-away” with rule breaking is, consequently, far less conceivable if one is being videotaped and one is cognizant that the behavior is, in fact, videotaped (Drover & Ariel, 2015). Cameras can, therefore, be viewed as “credible threats” (Jervis, 1989, p. 3): Because the certainty of apprehension for negative behavior is more forcefully acknowledged when the BWCs are on, it follows that we can directly exert deterrence when the certainty of getting caught for noncompliance is greatly intensified (Ariel et al., 2014).

Can BWC’s Affect the Reporting of Crime?

Despite the existing findings about the impact of BWCS on the quality of police-public encounters, BWC studies left many stones unturned. In particular, the body of work did not test the effects of BWCs on police legitimacy, criminal justice outcomes, or other facets. The use of BWCs may also have repercussions for the ways in which officers view themselves and their professional role (Jennings, Fridell, & Lynch, 2014) or the extent to which they feel micromanaged in an era of digital surveillance (Wain & Ariel, 2014). In the present study, however, we look at another outcome of interest which has been overlooked: the effect of BWCs on reported crime more broadly. Namely, does BWCs impact reporting of crime and disorder?

The potential effect of BWCs on crime reporting patterns is not straightforward. The mechanism deserves more attention that previously alluded to (e.g., Ellis et al., 2015). We must acknowledge two rival hypotheses: that using BWCs will reduce crime through deterrence, and that using BWCs in police operations will increase the reporting of crime. On the one hand, deterrence theory requires that BWCs must be perceived as effective tools, increasing sanction threats by the virtue of bringing offenders to justice more efficiently. If this is the case, then BWCs should have a suppressive effect on crime. On the other hand, wearing BWCs may change how victims and witnesses of crime perceive the utility, accountability, and overall legitimacy of the police. Victims and witnesses might then think that the police are mandated to act, as they are more accountable and, therefore, are more likely to report crime and disorder to the police. As a result, BWCs would cause “more” reported crimes. These two views are elaborated on, more fully, below.

Testing the Effect Using Street Segments as the Unit of Analysis

Whichever the direction of the anticipated outcome—fewer crimes or more reported crimes—we must demand that the hypothesis could be falsifiable (Popper, 1954). This is not easy, theoretically and methodologically, because the link between using BWCs and crime, or crime reporting, is difficult to observe directly. To measure the general deterrence effect of BWCs on offenders, one would require access to a sample of potential offenders and then ascertain whether BWCs had altered their risk perceptions and, ultimately, demotivated them from committing crime. Similarly, a survey of victims or witnesses would be required, in order to look at their preferences and decision-making processes and whether BWCs affected their willingness to come forward. The difficulty is that one would require individuals who did not call the police as well, in order to avoid the selection bias problem. For both samples, however, one would require comparable groups that were not exposed to the intervention (i.e., BWCs)—and these are challenging to locate. Control settings are even more difficult to create when the unit of analysis is the individual officer because the distribution of victims or witnesses is generally exogenous to the individual officer and cannot be controlled for. Instead, the causal link between the use of BWCs and variation in crime can be achieved when the unit of analysis is the place, and more specifically street segments (see Weisburd et al., 2012). There are theoretical as well as practical advantages to using the street segment as the unit of analysis.

If BWCs have a deterrent effect on crime, then the effect must be directly observed. However, measuring general deterrence is very difficult, as one may need access to large stratified samples or entire populations. Beyond measurement, and more precisely in the context of a proper test, it is virtually impossible to split the “general” population into treatment and control conditions, and to observe the causal estimate of the general deterrence condition, under controlled settings (Gibbs, 1975). A general deterrence effect, where the entire population is affected by some condition, cannot rule out alternative explanations, as such a design lacks a counterfactual comparison group. A general deterrence effect of BWCs must assume that the general population is aware of the ways in which the treatment (BWCs) is administered and to what extent, a finding which we cannot empirically test. Likewise, crude before-after analyses with no control conditions—that is, some measure of overall crime before the use of BWCs and then again in the follow-up period—is characterized by spuriousness (Lewis, 1973), and internal validity becomes highly suspect. Instead, the concept of non-specific deterrence can best be explained as the “spatiotemporal bounded” deterrence effect of BWCs—or what Sherman et al. (2014) and Ariel et al. (2015) refer to as the “local deterrence” effect of police presence. The local deterrence effect stipulates that rational offenders are likely to calculate the costs associated with committing certain street crimes, in certain places, that are more likely to result in apprehension. Within these confined places—such as hotspots or unique addresses—non-specific deterrence can be directly measured, as the assumption that non-involved individuals are aware of the intervention is not only stronger but falsifiable: the intervention is precise, definable, and its non-specific-deterrence effect, or local deterrence effect, can be estimated within confounded and discernable settings.

Thus, while BWCs may exert a general deterrence effect on crime (i.e., on offenders) or might change the reporting behavior of victims and witnesses through enhanced legitimacy, the causal effect on the overall population would be difficult, if not impossible, to measure. However, within the confinement of certain places, the test stands some chance. This means that spatiotemporally bounded places, which are exposed to police patrols by officers wearing BWCs, would be affected, resulting in invariably different crime counts to similar places that are not exposed to police patrols equipped with BWCs.

The Denver BWC Study

The hypothesis that wearing BWCs in routine police operations would affect crime or crime reporting in hotspots of crime and disorder was tested in Denver. All response police officers in one district—which happened to be the busiest in terms of crime, night life, and human traffic—were assigned BWCs, while the other districts were not given BWCs at all. Officers were tasked to patrol the streets “as they normally would,” in both treatment and comparison hotspots, while the observable difference between the two arms was the BWCs. “Crime density,” or the number of crimes reported by members of the public to the police, within 100 meters of street segments, before deploying the BWCs were measured, and then again during the 6 months of the experiment, across all hotspots in the city (n = 27,003 street segments) was used as an outcome measure.

Methods and Data

Outcomes

Descriptive Statistics

Table 1 presents pretreatment and posttreatment raw figures on the key features. As shown, the data are broken down into the six geographic districts, with District 6 serving as the target area, while the other districts served as comparison areas. The number of incidents at baseline ranged from 19,811 to 36,790, with the treatment area situated in the upper bound of this range. There were overall 188,137 incidents, scattered around 27,003 street segments in the entire city (about seven reported incidents per street segment). On the other hand, there were significantly fewer street segments in the treatment area (n = 1,327), making up less than 5% of all street segments in the city, while street segment lengths were generally shorter as in the comparison areas. The mean number of incidents per street segment was substantially larger than any other comparison site (M = 26.56; SD = 58.46), or the overall mean across all districts (M = 6.97; SD = 23.15). The same pattern emerged for mean crime density, or number of incidents per 100 meters (M = 7.64; SD = 22.35 and M = 1.98; SD = 9.38), respectively.

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Table 1.

Pre and Post Raw Figures.

	District 1		District 2		District 3		District 4		District 5		District 6c		Total
	Pre	Post	Pre	Post	Pre	Post	Pre	Post	Pre	Post	Pre	Post	Pre	Post
N incidents pre/post	36,790	36,418	31,665	33,346	36,504	37,667	28,119	28,883	19,811	20,892	35,248	40,076	188,137	197,282
N street segments	4,272		4,628		8,889		3,946		3,941		1,327		27,003b
Mean incidents per street segment	8.61 (28.28) a	8.52 (30.17)	6.84 (18.17)	7.21 (20.01)	4.11 (13.32)	4.24 (14.35)	7.13 (18.20)	7.32 (19.75)	5.03 (19.54)	5.30 (20.59)	26.56 (58.46)	30.20 (66.33)	6.97 (23.15)	7.31 (25.39)
Mean street segment length	421.13 (276.96)		422.66 (240.38)		426.51 (310.60)		472.17 (302.78)		475.18 (477.40)		404.80 (167.54)		437.70 (319.96)
Mean crime density (All segments)b	2.74 (12.21)	2.92 (17.41)	1.94 (6.53)	2.08 (9.46)	1.17 (6.34)	1.27 (10.39)	1.72 (6.08)	1.68 (5.18)	1.38 (9.04)	1.30 (8.05)	7.63 (22.35)	6.45 (23.50)	1.98 (9.38)	2.07 (11.75)

Note. N incidents, N street segments and segment lengths (in meters) and mean crime density (per 100 meters).

a

Figures in parentheses are standard deviations. ^bincluding segments with 0 incidents in pretreatment. ^ctarget area

Stratification and Baseline Comparability

One-way between subjects ANOVA was conducted to compare the effect of the stratification criterion on the distribution of incidents, in terms of both 911 calls for service counts as well as crime density. Data on all street segments in the city that experienced at least one incident during the baseline period were used (N = 17,726). As noted, there were six strata, with 1 to 10, 11 to 20, 21 to 30, 31 to 40, 41 to 50, and 51 or more incidents reported to the police within 6 months. The stratification procedure created strata that were significantly different from one another (Table 2), in terms of both outcome variables, F(5, 17,720) = 4157.7, p ≤ .001 and F(5, 17,720) = 1512.2, p ≤ .001, respectively, with a linear increase in the number of events reported to the police as we move from Strata 1 to 6.

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Table 2.

Justifying the Stratification Method.

		N street segments	Means per segment (SD)	F scores
	Stratum 1	13,749	3.64 (2.56) a
	Stratum 2	2,102	14.44 (2.77)
	Stratum 3	667	24.91 (2.85)
Crime incident counts	Stratum 4	383	35.15 (2.92)	4157.70***
	Stratum 5	195	45.14 (2.84)
	Stratum 6	630	109.35 (99.49)
	Total	17,726	10.61 (27.89)
	Stratum 1	13,749	1.02 (1.24)
	Stratum 2	2,102	3.62 (2.97)
	Stratum 3	667	6.67 (5.63)
Crime density (incident	Stratum 4	383	9.63 (8.79)	1512.20***
count per 100 meters)	Stratum 5	195	12.06 (10.08)
	Stratum 6	630	33.78 (49.08)
	Total	17,726	3.01 (11.44)

Note. Analyses of variance between six street segment strata of “heat”: 911 calls for service counts and crime density per 100 meters.

a

Figures in parentheses are standard deviations. ^bStratum 1 = 1–10 calls for service; Stratum 2 = 11–20 calls for service; Stratum 3 = 21–30 calls for service; Stratum 4 = 31–40 calls for service; Stratum 5 = 41–50 calls for service; Stratum 6 = 51 > calls for service, in a 6-month pretreatment period in the year preceding the experiment.

*

p ≤ .05. **p ≤ .01. *** p ≤ .001.

While we would expect that inter-strata variance to be significant, the intragroup variance (i.e., within the strata) was hypothesized to be as small and not significant. This was achieved for crime density outcomes only (no statistically significant differences emerged at the .05 level), but not for 911 calls for service. One-way ANOVA tests revealed some significant differences, particularly around the lower crime strata (up to 20 incidents per street segment in 6 months), but not in the higher crime incident strata. (F(5, 13,743) = 46.46, p ≤ .001; F(5, 2096) = 6.23, p ≤ .001; F(5, 661) = 0.841, p ≤ .521; F(5, 377) = 1.646, p ≤ .147; F(5, 189) = 0.56, p ≤ .73; F(5, 624) = 1.619, p ≤ .153, respectively.) As listed in Table 3, District 6—the target area—in general, displayed higher baseline pretreatment reported crime figures in comparison to all other districts in these cooler street segments.

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Table 3.

Pretreatment Scores Within 6 Heat Strata × 6 Geographic Districts: Analyses of Variance.

Heat strata		District 1	District 2	District 3	District 4	District 5	District 6¥	F Scores
Stratum 1	N	2,355	2,743	3,885	2,222	2,117	427
	Density	1.25 (1.63) a	1.01 (0.97)	0.87 (1.18)	0.99 (1.13)	0.97 (1.01)	1.57 (1.84)	46.46***
	Crimes	4.06 (2.62)	3.74 (2.56)	3.17 (2.37)	3.78 (2.61)	3.42 (2.50)	5.15 (2.92)	76.22***
Stratum 2	N	400	430	390	393	230	259
	Density	3.77 (2.94)	3.84 (2.92)	3.90 (3.70)	3.12 (2.15)	3.01 (3.68)	3.93 (1.83)	6.23***
	Crimes	14.36 (2.73)	14.53 (2.88)	14.26 (2.81)	14.40 (2.70)	14.23 (2.64)	14.95 (2.72)	2.545*
Stratum 3	N	152	118	133	87	50	127
	Density	6.92 (6.54)	6.37 (3.51)	7.30 (7.31)	6.28 (6.61)	5.69 (5.73)	6.65 (2.30)	0.841
	Crimes	24.72 (2.79)	24.65 (2.68)	25.08 (2.96)	25.13 (2.80)	24.96 (2.84)	25.00 (2.99)	0.548
Stratum 4	N	61	75	70	58	24	95
	Density	12.08 (12.30)	8.81 (5.01)	8.28 (7.49)	8.88 (10.29)	11.10 (15.08)	9.78 (5.45)	1.646
	Crimes	35.82 (2.87)	34.95 (2.77)	34.90 (3.14)	35.12 (2.87)	35.33 (3.07)	35.04 (2.90)	0.861
Stratum 5	N	32	34	45	28	13	43
	Density	11.65 (6.93)	12.59 (7.78)	12.90 (13.01)	9.29 (5.04)	12.27 (24.02)	12.82 (4.56)	0.56
	Crimes	44.50 (2.45)	45.15 (2.38)	45.87 (2.97)	44.11 (2.74)	43.62 (2.66)	46.00 (3.06)	3.377**
Stratum 6	N	137	76	112	91	53	161
	Density	37.29 (55.69)	35.65 (32.97)	29.88 (43.73)	22.20 (30.03)	37.41 (65.83	37.98 (54.42)	1.619
	Crimes	102.96 (118.28)	106.34 (81.61)	96.31 (50.03)	94.46 (65.06)	125.00 (107.66)	128.52 (123.60)	2.404*

ab

Figures in parentheses are standard deviations. Target area.

*

p ≤ .05. **p ≤ .01. ***p ≤ .001.

Treatment Outcomes

As planned, repeated measures ANOVAs were then used to evaluate whether significant changes pretreatment to posttreatment were experienced in the Treatment district, compared with the five comparison districts, within each heat strata. Table 4 lists the results of the statistical analyses, including the degrees of freedom, mean squares, and F scores. As shown, significant F scores for the effect of time were found for all strata, suggesting that overall crime density scores were different in the pretreatment compared with posttreatment periods, in Strata 1 through 6, F(1, 13,743) = 64.197, p ≤ .001; F(1, 2096) = 4.071, p ≥ .05; F(1, 661) = 23.703, p ≤ .001; F(1, 377) = 8.57, p ≤ .01; F(1, 189) = 15.689, p ≤ .001; F(1, 624) = 61.303, p ≤ .001, respectively.

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Table 4.

Repeated Measures of Analysis: Crime Density Outcomes Within Six Heat Strata.

Strata × Variables		DF	Mean squares	F
Stratum 1 a	Crime density	1	883.123	64.197***
	Crime density × District	5	167.949	12.209***
	Error term	13,743	13.756
Stratum 2	Crime density	1	78.465	4.071
	Crime density × District	5	153.302	7.954***
	Error term	2,096	19.273
Stratum 3	Crime density	1	882.628	23.703***
	Crime density × District	5	99.993	2.685 *
	Error term	661	37.237
Stratum 4	Crime density	1	902.787	8.857**
	Crime density × District	5	122.177	1.199
	Error term	377	101.924
Stratum 5	Crime density	1	1387.461	15.689***
	Crime density × District	5	42.524	.481
	Error term	189	88.433
Stratum 6	Crime density	1	69878.092	61.303***
	Crime density × District	5	1457.468	1.279
	Error term	624	1139.877

Note. DF = degrees of freedom.

a

Stratum 1 = 1–10 incidents; Stratum 2 = 11–20 incidents; Stratum 3 = 21–30 incidents; Stratum 4 = 31–40 incidents; Stratum 5 = 41–50 incidents; Stratum 6 = 51 > incidents, in a 6-month pretreatment period in the year preceding the experiment.

*

p ≤ .05. **p ≤ .01. ***p ≤ .001.

Of main interest is the interaction effect between treatment group and crime density, over time. These were found to be significant for Strata 1 through 3 (up to 30 crime per 6 months), but not for Strata 4 through 6 (31 and over crimes in 6 months) (F(5, 13,743) = 12.209, p ≤ .001; F(5, 2096) = 7.954, p ≤ .001; F(5, 661) = 2.685, p ≤ .05; F(5, 377) = 1.199, p ≥ .05; F(5, 189 = .481, p ≥ .05; F(5, 624) = 1.279, p ≥ .05, respectively.) This indicates that a treatment effect at “cooler” street segments on calls for service, but no effect for “hotter” street segments.

Tukey’s HSD subgroup analyses were performed on mean crime densities in each stratum, in order to detect between which pairs of comparisons—that is, between treatment street segments and comparison street segments—the significant difference is concentrated. As shown in Table 5, virtually all comparisons are significant in Strata 1 and 2 (up to 20 incidents in 6 months) but one pairwise comparison was statistically significant between treatment area and control area Number 5 (mean difference 2.78; SE = .913, 95% CI [.168–5.85]). At the same time, one pairwise comparison in Stratum 6 (51 crimes or more in 6 months) yielded significant outcomes at the .05 level, which might be attributed to random variations between the treatment and control conditions.

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Table 5.

Tukey’s HSD Subgroup Analyses Comparing Mean Crime Densities—Treatment District vs. Five Comparison District Within Six Heat Strata.

				95% confidence tnterval
	Comparison districts	Mean difference (I–J)	SE	Lower bound	Upper bound
Stratum 1	District 1	1.12 *	.150	.696	1.553
	District 2	1.46 ***	.149	1.032	1.881
	District 3	1.67 ***	.146	1.256	2.087
	District 4	1.46 ***	.151	1.033	1.894
	District 5	1.62 ***	.152	1.186	2.051
Stratum 2	District 1	1.47 ***	.299	.618	2.321
	District 2	1.17 **	.294	.331	2.010
	District 3	1.30 ***	.300	.448	2.159
	District 4	1.74 ***	.300	.889	2.598
	District 5	2.41 ***	.339	1.446	3.380
Stratum 3	District 1	1.14	.657	−.737	3.020
	District 2	1.14	.699	−.861	3.134
	District 3	1.02	.678	−.920	2.956
	District 4	1.77	.761	−.404	3.945
	District 5	2.78 *	.913	.168	5.385
Stratum 4	District 1	−0.39	1.422	−4.467	3.679
	District 2	2.69	1.339	−1.144	6.526
	District 3	3.67	1.365	−.243	7.578
	District 4	2.31	1.444	−1.828	6.446
	District 5	1.57	1.980	−4.102	7.241
Stratum 5	District 1	1.99	1.761	−3.082	7.059
	District 2	1.15	1.731	−3.836	6.133
	District 3	0.074	1.609	−4.558	4.705
	District 4	2.17	1.832	−3.104	7.444
	District 5	1.47	2.387	−5.408	8.340
Stratum 6	District 1	2.71	4.710	−10.751	16.179
	District 2	5.33	5.640	−10.787	21.457
	District 3	13.63	4.986	−.627	27.880
	District 4	17.61 *	5.315	2.415	32.799
	District 5	8.45	6.417	−9.868	26.822

*

p ≤ .05. **p ≤ .01. ***p ≤ .001; I = Treatment; J = Control; Stratum = based on n of events at baseline (see Table 3 for more details).

The outcomes are displayed in Figures 1 through 6, which present the estimated marginal means of crime densities, for each stratum. Each line in the graphs represents the pre–post comparisons in terms of the interaction effect. These results, which are born out of the repeated measures ANOVA, illustrate that as the degree of “heat” increases—signified by the increasing number of crimes at baseline as we move from strata 1 to 6—the effect of BWCs becomes less apparent. While crime density scores remains relatively stagnated in comparison sites the lower strata, with little changes over time, crime density scores in the treatment area (marked by the dashed lines) increased. This pattern is noticeable for Strata 1, 2, 3, and to some extent 4 as well. On the other hand, as we move toward the hotter hotspots, particularly in street segments with 40 or more calls for service in 6 months, the overall pattern across all areas—both treatment and comparison districts—is consistent, with an overall decrease in crime densities, over time across both arms, thus illustrating the nonsignificant differences in these strata. OPEN IN VIEWER

Figures 1–6.

Estimated marginal means of crime densities: treatment vs. control conditions: Crime Strata 1: 1–10 crimes.

Discussion and Conclusions

BWCs are one of the most sought after technological solutions in policing in the world today. Yet, research evidence on their efficacy is still limited (Lum et al., 2015; White, 2014). The present study looked at one aspect: to what extent, if any at all, does using BWCs, in police operations, influence crime figures. Conceptually, BWCs can be hypothesized to reduce crime via a general deterrence message, insomuch as BWCs give the police enhanced technologies to effectively apprehend and punish offenders. Under this prism, risk sanction threats are elevated, and rational offenders will commit fewer noticeable offenses. Domestic violence, public disorder, and traffic violations stand out as likely candidate categories in which we should expect fewer repeat calls for service, but arguably more candidate categories may also be impacted. At the same time, another likely hypothesis is that the use of BWCs effects crime reporting behavior. Under this approach, victims and witnesses will report more crimes to the police as a result of the police using BWCs. Police legitimacy, stemming out of either enhanced perceptions of procedural fairness and/or increased effectiveness, may be the key mechanism that operates here, as BWCs send the public the message that reporting is dealt with professionally, fairly, and effectively.

Methodologically, answering any question about the citywide, or even statewide, effects of police policies is particularly challenging, as non-spurious relationships between independent and dependent variables are difficult to attain. Internal validity is at risk. Without proper comparison groups, under controlled conditions, the treatment effect is easily masked or becomes susceptible to rival explanations. Only true randomized experiments can comfortably assume that baseline comparability between the intervention arm of the study (whatever the intervention is) and the comparison arm, has been achieved—which is the key scientific framework for observing the causal estimate of the intervention. For this reason, assuming we can directly observe the effect of BWCs on crime is challenging. It is not falsifiable if it lacks proper counterfactual conditions.

Sadly, in policing many if not most evaluations suffer from poor evaluation designs, although tremendous leaps were made in the last 15 years or so (on rigorous evaluations in policing, see Lum, Koper, & Telep, 2011; Sherman, 2013; on methodological rigor in research, see Shadish, Cook, & Campbell 2002:1–32, Campbell & Stanley, 1966: Table 1 and associated text).

I tried to overcome the lack of random assignment into treatment and control conditions by utilizing a large number of street segments and observing the treatment effect within these places. Given the large number of units, street segments as the unit of analysis greatly enhance the statistical power of the test. With all things being equal (but cf. Weisburd et al., 2001 and more recently see Nelson, Wooditch, & Dario, 2014), larger samples are more stable. By comparison, a study comparing the effect of using BWCs in one, or even several jurisdictions, compared with another jurisdiction(s) without BWCs, will still have a relatively small number of degrees of freedom and, by implication, the statistical power of the test will be lower. Street segments, on the other hand, exist in the thousands. Indeed, the variability between the street segments can be quite extensive—for instance in terms of the “heat” of the segment, the types of problems it experiences, and so forth—but in fact, we can take advantage of this variability. A multitude of techniques can be used to reduce the “noise” between units of analysis, so that the treatment effect can be singled out more robustly: stratification, matching, and other techniques (see Ariel & Farrington, 2014)—these are all valid designs that make the use of street segments superior to larger spatiotemporal units of analysis. ²

In addition, there is a growing body of literature demonstrating that, overall, places remain predictably constant, consistent, and stable—at least the hotspots on the top of the list, in terms of incident counts. Their size changes very little over time, the frequency of calls for service is generally stagnant and their “position” in the rank-order of hotspots in the city is generally unchanged (see Weisburd et al., 2004). These stabilities are useful, because they can be utilized to assess the introduction of an intervention to some places but not others, with a stronger contention of baseline equality.

The present methodological approach gets asymptotically closer to a valid test—clearly more than a study with larger geographic units of analyses such as entire neighborhoods or communities, and certainly more than crude before-after analyses without comparison groups, designs which teach us very little about causal effects (Sherman et al., 1998). Yet to be sure, this is still not a proper randomized controlled trial. We ought to acknowledge that the risks to the internal validity of the test were not fully removed. It is also the first study of its kind, so we must wait for additional (and more rigorous) causal studies in this area of research. At the same time, the results are promising.

Overall, we find little to no evidence of the deterrence effect of BWCs on general crime patterns. Taken as a whole, the findings show no suppressive effect on crime, when observing overall crime variations. When breaking the data into heat strata, at no point can we see that crime density before-after differences—the main outcome variable in this study—are lower in the treatment sites than the comparison sites. Thus, if the estimates presented here are valid, they debunk the hypothesis that suggests BWCs can change general sanction risk perceptions.

On the other hand, when BWCs were introduced in the target street segments, they seem to overall increase people’s willingness to report crimes to the police, compared with street segments without BWCs. If these findings are valid, they provide evidence on the effect of BWCs on police legitimacy, of which one manifestation is an elevated level of cooperation with the police. Equipping officers with BWCs enhances the sense of their legitimacy, and as a consequence this promoted citizens to report more incidents reported to the police.

Legitimacy scholars have thus far provided observational evidence on the willingness to cooperate with the police. These studies defend the view that the inclination to work together with the police “against” crime is one expression of legitimacy. In particular, perceptions of procedural justice in the implementation of policies served as strong correlates of cooperation with the police (e.g., Huq, Tyler, & Schulhofer, 2011; Tyler, Schulhofer, & Huq, 2010). Tankebe (2013) analyzed data from household survey of over 5000 Londoners and his results showed that procedural justice was strongly correlated with public willingness to cooperate with the police, both among victims and non-victims of crime (see also Murphy & Barkworth, 2014). Using survey data from a random sample of 1,203 Australians, Murphy and Cherney (2012) reported similar findings about procedural justice effects on people’s willingness to cooperate with police.

Enter BWCs. These devices are assumed to cause officers to follow procedures more closely, as they elevate the risk of apprehension for not complying with guidelines. Officers become self-conscious when being equipped with BWCs, and as a consequence, they are also substantially more likely to follow rules of conduct, than officers who do not wear BWCs. Drawing from the self-awareness literature (Duval & Wicklund, 1972), individuals are likely to follow accepted mode of behavior, and in the police profession, this awareness translates into fair, respectful, and courteous conduct. These key components—public voice, neutrality in decision-making, trustworthiness, and treatment with dignity and respect—are the mechanisms of procedural justice (Gau, 2011; Tyler et al., 2007; Wolfe, 2011). The public responds to these officers’ behavioral changes and views the police as more legitimate. The immediate manifestation is an elevated willingness to cooperate with the police. This causal mechanism is depicted in Illustration 1:

However, other dimensions predicate police legitimacy as well, and these dimensions can equally be affected by knowing that police officers wear BWCs. Distributive justice (Bratton & Gertz, 2007) or lawfulness (Tankebe, 2013) have been found to matter when it comes to legitimacy. Transparency and accountability are likely to have an effect on legitimacy as well. Bottoms and Tankebe (2012) and Tankebe (2008), who view legitimacy as substantially more complex than merely being comprised of fair procedures, suggest that one critical dimension that plays part here is police effectiveness. It is, therefore, logical to speculate why citizens would view the police as more effective with BWCs—as more fully developed under Hypothesis 2 earlier—and as a consequence report more crimes to the police. This alternative interpretation is shown in Illustration 2:

This study does not provide direct evidence on neither interpretations, but we can speculate that at least one of these versions is logical. These processes would be better addressed using a citizen survey, which would have shed much light on the interpretation of the findings. However, while this study cannot pierce the walls of the “black box” of how callers to the police make decisions to call the police, it can observe that objectively higher levels of cooperation with the police were recorded. The data demonstrate behavioral changes in crime reporting patterns that took effect once officers use BWCs—which by itself is novel in the police legitimacy literature, compared with studies that focus on willingness to cooperate with the police.

Next, what best explains why is the effect of BWCs on crime-reporting behavior is conditional on street segment “heat”? Why BWCs would have no impact in the hottest hot spots—where they are most needed—while the hypothesized mechanism works in street segments that need it the least? As shown in Figures 1to 6, crime densities in treatment street segments with fewer than 80 incidents per year, there is an increase over time, attributable to the use of BWCs. On the other hand, in hotspots with more than 80 incidents per year, the general trend in the treatment group parallels the trend detected in the comparison group, which is why the differences are not statistically significant. In doing so, the outcomes suggest a more complicated story about the link between BWCs and cooperation with the police than originally anticipated.

We can only speculate at this stage, but the answer would seem to revolve around the socio-ecological context of the street segment (Weisburd, 2012), as well as crime patterns within the street segments in which these measures were taken. There is no available sociodemographic database on each street segment in the city, nor an available street-level survey results of perceptions of the residents about the police more broadly. Instead, we turn to images from Google Street View and argue that there are physical attributes of the street segments that can be used as proxies to these dimensions. A set of street view images is attached, which show the epicenter of a selection of street segments (see Supplementary Materials).

Looking at the “hot hotspots” first (i.e., Fig 8 and Fig 9 in Supplementary Materials), it may in fact be unsurprising that BWCs will have no discernable effect on the decision to cooperate with the police: these are “busy” places, with primarily a nighttime economy population. These areas are predominately entertainment places for juveniles and young adults, commercial, and parks. These are areas that either offenders consciously target or places occupied by young persons who actively engage in alcohol consumption and potentially antisocial behavior. Detecting a treatment effect in an otherwise persistently “hot” street segment is difficult; even more aggressive interventions such as hotspots policing (Braga, Papachristos, & Hureau, 2014) cause significant yet weak effects on crime and disorder. Therefore, one plausible explanation for the lack of significant effect in “hot” crime hotspots is the relatively weak strength of the treatment.

On the other hand, as we move from stratum 6 (high level hotspots) to cooler street segments (stratum 1), we see that the face of the street segment dramatically changes into middle (Figure 11) and upper social class (Figure 12) residential neighborhoods. These street segments on the lower bounds of crime are primarily suburban-looking streets with single occupancy detached or semi-detached houses. Residents of these street segments may have more stable views of the police, which in turn have been improved with the introduction of BWCs. It is likely that some of the heat is generated by crime reports about the same places with similar local residents. In turn, crime-reporting behavior seems prone to being affected by the repeated interactions between callers and BWCs-wearing-police-officers. Police using BWCs sent repeated players a signal that altered their crime-reporting patterns. Whether by virtue of enhanced perceived accountability, stronger expected utility out of calling the police for problems, or as a result of fairer procedures on the part of the officers, the observed behavioral change is, therefore, more crime being reporting to the police in these places.

To be clear, these are all projected dynamics that must be explored more granularly in future research. The images presented in the Supplementary Materials are suggestive, and there was no aim to systematically assess neither the physical attributes of all street segments in our sample. They only serve as proxies to what would affect people’s perceptions about the police. In this sense, one future research avenue which seems clear is collecting “local legitimacy” and “local self-efficacy” scores, at the street segment level—which would have broader implications that just BWCs. We did not conduct surveys of residents in these street segments—or with local offenders who may, or may not, have been affected by BWCs—so the link between attitudes toward the police, crime reporting, and criminal behavior is unclear at this stage (but cf. Weisburd, Hinkle, Famega, & Ready, 2011). Therefore, the reasons given here for the increases in crime reports in lower bound street segments but not in the hotspots remain contentious.

There are at least two additional limitations to this study. First, there is a strong assumption in this theoretical analysis that people were aware of the use of BWCs. We assume that the media coverage—both locally in Denver as well as the nationwide attention—that BWCs have received, has come to the attention of the callers about crime and disorder in the target areas. We have no evidence to offer on that nor any manipulation checks. Future research should pay closer attention to this shortcoming.

Second, the study has only lasted for 6 months. This is undoubtedly a short period of time. Studies should always consider longer follow up period, particularly given the possibility of desensitization—namely that both officers and citizens are no longer affected by BWCs. This was not feasible under the present study conditions.

Despite these reservations, the current findings are informative for police practice. The rise in crime reporting in some street segments of Denver should be viewed as a sign of improved police–public relations, potentially as a result of changes of enhanced police accountability, legitimacy or perceived effectiveness—or all. Whichever the theoretical mechanism that explains the change in crime-reporting behavior, the findings can comfortably be construed as a greater confidence in the police—or else callers would not have dialed 911 at increasing rates when BWCs are used. Residents in some places seem to react positively to them by becoming willing to come forward and report crimes to the police. This is an important policy-oriented discovery.