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Evaluating the relative impact of positive and negative encounters with police: a randomized experiment

Abstract

Objectives

Examines the influence of positive, negative, and neutral police behavior during traffic stops on citizen perceptions of police.

Methods

Participants were randomly assigned to view a video clip of a simulated traffic stop in which the officer communicates with the driver in a positive (procedurally just), negative (procedurally unjust), or neutral manner. After viewing the video, participants completed a survey about their perceptions of police, including their level of trust in police, obligation to obey police orders, and willingness to cooperate with police.

Results

Observing positive interactions with police enhanced people’s self-reported willingness to cooperate with police, obligation to obey police and the law, and trust and confidence in police, whereas observing negative interactions undermined these outcomes. The effects of these interactions were much stronger for encounter-specific outcomes than for more general outcomes.

Conclusions

The results from this randomized experiment confirm that procedural justice can enhance people’s prosocial attitudes toward police, whereas procedural injustice can undermine these attitudes. While positive (procedurally just) interactions tend to have weaker effects than negative (procedurally unjust) interactions, this study finds little support for the notion that only negative experiences shape people’s views about the police.

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Fig. 1

Notes

  1. 1.

    For example, Manning (1996: 52) notes that the core technology of policing “remains people talking to people, officers trying to persuade people by various interactional strategies to comply with requests, threats, and commands….”

  2. 2.

    Note that some studies have relied on the analysis of two-wave panel data to estimate the effects of procedural justice on a variety of outcomes (e.g., Beijersbergen et al. 2015; Murphy 2005; Tyler 2006). The use of panel data typically offers stronger internal validity than correlational studies based on cross-sectional data, but weaker internal validity than studies relying on well-executed experimental or quasi-experimental designs (Worden and McLean 2016).

  3. 3.

    There is also a growing body of experimental research on the effects of procedural justice interventions outside of criminology. For instance, Wenzel (2006) randomly allocated taxpayers to receive one of three reminder letters: a standard letter (which served as the control condition), and two others containing different elements of procedural justice. The reminder letters that incorporated procedural justice principles generated greater levels of tax compliance. Several field experiments have also tested the effects of procedural justice interventions on the attitudes, intentions and behaviors of employees in organizations (e.g., Hunton and Beeler 1997; Schaubroeck et al. 1994).

  4. 4.

    Communication accommodation theory (CAT) posits that people subconsciously modify their speech patterns to match those of others with whom they are speaking. This communication accommodation, if well calibrated, can generate a number of benefits, including increased trust. However, overaccommodation can be perceived as disingenuous or artificial and can decrease trust (Lowrey et al. 2016).

  5. 5.

    Confidence in police was measured using questions on “police responsiveness to community concerns and whether police were dealing with problems that really concerned residents. There were also questions about ‘how good a job’ police were doing in preventing crime, keeping order and helping victims” (Skogan 2006: 107).

  6. 6.

    In Tyler’s (2006) process-based model of regulation, obligation to obey is treated as the principal measure of institutional legitimacy. Thus, legitimacy is said to mediate the relationship between procedural justice and outcomes like cooperation and compliance. However, recent theoretical challenges call into question the meaning and measurement of legitimacy as specified by Tyler. For instance, Tankebe (2013) has articulated a model in which legitimacy is comprised of procedural justice, distributive justice, effectiveness, and lawfulness, and obligation to obey is treated as an outcome that is influenced by legitimacy. Given that the meaning and measurement of institutional legitimacy is currently under debate, we do not incorporate legitimacy as a construct in our model. Instead we focus on the major construct used to measure it in the work of Tyler and his colleagues: obligation to obey. Obligation to obey serves as a mediator between procedural justice and outcomes like cooperation and compliance in both Tyler’s and Tankebe’s models and therefore its effects are not part of the current debate.

  7. 7.

    In addition to the three procedural justice conditions that are the focus of this study, the larger research project included additional experimental conditions that varied the demographic characteristics of the driver. These results are not reported here. The present study relies only on survey data from the 266 respondents who viewed a video featuring a teenage white male driver. Based on preliminary power analyses, we estimated that a minimum sample size of 159 would be necessary to detect a medium-sized effect (f = .25) with a power of .80 and an α level of .05 (Cohen 1992). Our achieved sample size of 266 is likely sufficient for detecting medium and large effects, but insufficient to detect small effects.

  8. 8.

    Our appraisals of model fit are informed by the following considerations. For the Root Mean Square Error of Approximation (RMSEA), Browne and Cudeck (1993) conclude that values of .06 to .08 constitute acceptable fit, while values of .01 to .06 constitute “close fit.” Hu and Bentler (1999) also treat a RMSEA value of .06 as the upper threshold for close fit. For the Confirmatory Fit Index (CFI) and the Tucker–Lewis Index (TLI), Hu and Bentler (1999) suggest that values of .95 or greater indicate close fit. For the Weighted Root Mean Square Residual (WRMR), simulation evidence suggests that values below 1 are indicative of good fit (Yu 2002).

  9. 9.

    We estimated composite reliabilities using coefficient omega (Ω), which is based on the ratio of the true score variance to the total variance (McDonald 1999; Raykov 1997). Omega values for the encounter-specific outcomes were as follows: cooperation (Ω = .898), obligation (Ω = .940), and trust and confidence (Ω = .941). Omega values for the general outcomes were as follows: cooperation (Ω = .865), obligation (Ω = .838), and trust and confidence (Ω = .884).

  10. 10.

    Participants were assigned to groups based on a randomization algorithm in Qualtrics that was not susceptible to intentional or unintentional manipulation. We do not have a ready explanation for the differences in group composition. Randomization is premised on the law of large numbers and sometimes fails in small samples. The most likely possibility in this case is that the differences between groups in the number of males compared to females/intersex resulted from having a relatively small sample.

  11. 11.

    Respondents were allowed to mark more than one racial group when asked about their racial identity, and 6.7 % of the sample did so. Multiracial respondents who selected white and one or more other races were alternatively coded as either white or non-white, and regression models were run using both configurations. The coefficients and significance levels were virtually the same regardless of how these respondents were classified. The results presented here are based on the former classification (multiracial respondents who marked white as one of their racial identities were coded as white).

  12. 12.

    Since these variables were only included as covariates to account for differences between groups rather than for substantive reasons, the coefficients are not reported. Of the 18 coefficients for percent male (six outcomes × three contrasts), only two were statistically significant. In both cases, male respondents were found to have greater levels of general trust in police than female and intersex respondents.

  13. 13.

    Four models were used to generate the estimates reported in Table 3: one with encounter-specific outcomes and negative as the reference category; one with encounter-specific outcomes and neutral as the reference category; one with global outcomes and negative as the reference category; and one with global outcomes and neutral as the reference category. All four models fit the data well, with RMSEA values ranging from .051 to .052, CFI ranging from .990 to .996, TLI ranging from .986 to .994, and WRMR ranging from .525 to .685.

  14. 14.

    Our Bayesian regression analysis relies on iterative Markov chain Monte Carlo (MCMC) algorithms to “obtain an approximation to the posterior distributions of the parameters from which the estimates are obtained” (Muthén 2010: 8). The estimates in Table 4 are partially standardized regression coefficients derived from the medians of the posterior distributions. The asterisks associated with the Bayesian estimates summarize the one-tailed p values based on the posterior distributions.

  15. 15.

    Here, we use the term “proximate outcomes” to refer to phenomena that are near in time and scope to the encounter being evaluated. We use the term “distal outcomes” to refer to phenomena that are more distant in time and scope from the encounter being evaluated. The encounter-specific outcomes measured here are examples of proximate outcomes, whereas the global outcomes measured here are examples of distal outcomes. The procedural justice literature is replete with numerous other examples of proximate and distal outcomes.

  16. 16.

    An anonymous reviewer noted that, because this was a vicarious encounter, participants may have been uncertain about whether to respond to the encounter-specific items from their own personal perspective or from what they viewed as the driver’s likely perspective. Due to this uncertainty, the reviewer suggested that some participants may have answered the encounter-specific items from the perspective of the driver but the general items from their own perspective. We intended for respondents to answer the encounter-specific items from their own perspective (not from the perspective of the driver), and took steps to encourage this approach when designing the experiment and survey instrument. For instance, we carefully considered the placement of these items in the survey, as well as the survey instructions to the respondent. For example, the instructions for the encounter-specific items read: “Thinking specifically about the police officer in the video, please indicate the extent to which you agree or disagree with the following statements.” The goal here was to focus respondents on their own personal evaluation of the police officer, and not on the driver’s likely perspective. In addition, we placed the encounter-specific items immediately after the items for the manipulation check, which focused on the respondents’ assessment of the police officer’s behavior (for example: “The officer was respectful.”).

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Correspondence to Edward R. Maguire.

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Maguire, E.R., Lowrey, B.V. & Johnson, D. Evaluating the relative impact of positive and negative encounters with police: a randomized experiment. J Exp Criminol 13, 367–391 (2017). https://doi.org/10.1007/s11292-016-9276-9

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Keywords

  • Procedural justice
  • Police
  • Experiment
  • Asymmetry
  • Traffic stops