Police stops to reduce crime: A systematic review and meta-analysis

Types of studies

For studies to be considered eligible for this review the evaluation was required to include a treatment group that received a pedestrian stops intervention and a separate comparison group that did not receive a pedestrian stops intervention. Here, the treatment group could be comprised of either geographic areas or individuals, and eligible treatments could include proactive policing interventions, natural variation in the use of pedestrian stops across areas, or natural variation in the prevalence of police stops across individuals. In other words, we included comparisons of areas and individuals that differed naturally in their exposure to police stops, regardless of whether these differences were the result of any planned policing intervention. Eligible comparison conditions could include any group of areas or people that were not exposed to a pedestrian stops intervention or were exposed to a lower dosage of the intervention. For geographic studies, comparison conditions generally involved standard police practices, and for individual-level studies comparison conditions were generally comprised of individuals who had not directly experienced police stops. Studies were included regardless of their publication status.

Both randomized and quasi-experimental research designs were considered eligible for inclusion (Campbell & Stanley, 1966; Cook & Campbell, 1979; Shadish et al., 2002). This inclusion threshold was adapted from the inclusion criterion in the Global Policing Database (GPD) protocol (Higginson et al., 2015, pp. 47–48), which was the primary search source for this review. From the GPD, we included the following types of designs:

Randomized controlled trials (RCTs)

Thus, this review includes weaker quasi-experimental studies with “unmatched” control groups; for example, studies that compared a target area or group to the remainder of a jurisdiction or population. Accordingly, any evaluation of pedestrian stops that included a comparison group or area that did not receive the intervention was considered eligible so long as it met our other inclusion criteria. However, we distinguish between matched and unmatched designs in a subsequent moderator analysis (Section 5.4).

Types of participants

Given our interest in examining the impacts of pedestrian stops on crime, the community, and the individuals subject to these stops, this review includes the following populations:

Law enforcement officers (including any particular race, ethnicity, gender)

Types of interventions

Studies that evaluated interventions in which police-initiated pedestrian stops of individuals or groups of individuals (for the purpose of questioning, investigation, and/or frisking and searching) were carried out as a major component of a policing intervention were considered eligible for this review. As previously noted, the term “intervention” included natural variation in general policing approaches throughout a jurisdiction and/or natural variation in exposure to police stops among samples of individuals. That is, any comparison of people or places with differential exposure to pedestrian stops was considered an intervention for the purposes of this review. It is important to note here that our focus was on pedestrian stops, and as such, we excluded studies that were solely or primarily focused on traffic stops. More specifically, our interest was in isolating interventions consistent with the concept of SQF, which is traditionally associated with pedestrian stops (see Jones-Brown et al., 2010; Lachman et al., 2012). However, we did include studies in which both pedestrian and traffic stops were used, given the often-overlapping nature of these forms of policing, and so long as pedestrian stops remained a major component of the intervention.

We did not attempt to distinguish between the individual motivations behind pedestrian stops or determine whether stops were used reactively or proactively (i.e., whether stops were in response to observed criminal behavior), but rather focused on the intent of the program in which pedestrian stops were a component. This review was not limited to interventions targeting specific types of crime or disorder (e.g., weapon and drug-related crime), or any specific type of overarching policing tactic (e.g., hot spots policing, crackdowns, directed patrol, etc.). However, we did exclude studies employing pedestrian stops in a minor capacity relative to other policing tactics (as the effects of the stop component would be difficult to isolate from the other components of the policing intervention).

Types of outcome measures

This review included the following outcome measures. All outcomes were considered primary, and eligible studies were required to report at least one of these measures for inclusion:

Crime and disorder (including displacement)

Crime/disorder and displacement outcomes were considered eligible if measured using official data (e.g., incident and arrest data, calls for service, crime rates), unofficial crime data (e.g., crime reported by civilians, self-report delinquency via questionnaires or surveys), and systematic social observations of crime. All types of crime and/or disorder were included in this review (e.g., property, drug, violent crime).

We anticipated that incidents of violence in police-citizen encounters would be measured through police use-of-force reports (Weisburd et al., 2021). We planned to be as discrete as possible, including capturing use-of-force that results from suspect resistance and varying levels of force when possible. We also note that this outcome is not necessarily a measure of unjustified use-of force, and thus distinguished this outcome from officer misbehavior. We anticipated that officer misbehavior would be measured through formal citizen complaints or community surveys reporting on police abuse or violence.

We included studies where fear of crime and attitudes towards police were measured using questionnaires or surveys at the community-level or taken from individuals who directly experienced police stops, as well as those who did not.

For mental and physical health issues, we included studies that measured these outcomes via self-reports taken from individuals with direct police stop experience or via official data (e.g., injury data from hospitals), and we included data measured at both the individual- and community-levels of analysis. For the purposes of this review, mental health issues were defined as symptoms or diagnoses related to an established mental health condition or a “clinically significant behavioral or psychological syndrome or pattern that occurs in an individual” (Stein et al., 2010, p. 1760), such as anxiety, post-traumatic stress disorder (PTSD), suicidality, depression, etc. Physical health issues concerned any characteristic or condition that could directly impact or have implications for physical functioning, such as self-reported physical health, sleep problems, and/or functional limitations (see e.g., Baćak & Apel, 2020; Testa et al., 2021).

Duration of follow-up

Eligible studies were not restricted to any particular follow-up period. At the geographic level, stop interventions are likely to produce short-term deterrent effects (Sherman, 1990; Weisburd et al., 2016), though the impacts on individuals directly experiencing stops may be long term (see Dennison & Finkeldey, 2021; Wiley et al., 2013). In the protocol for this review (Weisburd et al., 2021), we planned to synthesize studies by length of follow-up period (<6 months, 6–12 months, >1 year). However, this approach needed to be adapted due to the nature of included studies and is described in the results section.

Types of settings

No restrictions were placed on geographic region, racial, ethnic, or demographic makeup, or written language. We used Google Translate to conduct title and abstract screening for any non-English language studies, as well as for the main text of any non-English language articles that required full-text review.

Electronic searches

Our systematic search strategies were led by the GPD research team at the University of Queensland (Elizabeth Eggins and Lorraine Mazerolle) and Queensland University of Technology (Angela Higginson). The GPD is a web-based and searchable database designed to capture all published and unpublished experimental and quasi-experimental evaluations of policing interventions conducted since 1950 (http://www.gpd.uq.edu.au). There are no restrictions on the type of policing technique, the type of outcome measure, or the language of the research (Higginson et al., 2015). The GPD is compiled using systematic search and screening techniques, which are reported in Higginson et al. (2015) and summarized in Supporting Information: Appendices A and B. Broadly, the GPD search protocol includes an extensive range of search locations to ensure that both published and unpublished research is captured across criminology and allied disciplines.

To capture eligible studies, we used the following terms related to pedestrian stops to search the GPD corpus of full-text documents that have been screened as reporting on a quantitative impact evaluation of a policing intervention. Search terms were limited to the title and abstract fields and included studies published between January 1970 and December 2019. This timeframe was chosen based on evidence that police departments began using pedestrian stops as elements of proactive policing interventions toward the end of the 20th Century (White & Fradella, 2016):

stop*

To extend the timeframe of the GPD search, we conducted an additional search for studies published between January 2020 and December 2021. This search included the same parameters and keywords as those used in the GPD search and utilized the following databases (see Supporting Information: Appendix C):

Criminal Justice Abstracts (EBSCO)

Searching other resources

We used several additional strategies to supplement the approaches described above. First, we searched additional databases from Japan, Korea, the Middle East, and Europe by consulting subject guides through the Duke University Library. Specifically, we searched the following databases using keywords related to policing and pedestrian stops consistent with those described in our main search strategies:

CiNii Articles

Second, and similar to recent reviews using the GPD (Hinkle et al., 2020; Lum et al., 2020; Mazerolle et al., 2020), we performed hand searches of published volumes of leading journals in criminology from 2019 to 2021 to identify any studies that had yet to be indexed in electronic databases. Third, we conducted forward citation searches using Google Scholar and reference harvesting of prior reviews on related topics (Braga et al., 2019; Koper & Mayo-Wilson, 2012). Finally, after completing all searches, we e-mailed our list of eligible studies to the lead authors of these articles to identify any research that the above searches may have missed.

Selection of studies

All search results were first screened on title and abstract content to determine potential relevance to pedestrian stops. As an initial step, two screeners (Petersen and Fay) reviewed the same subset of 25 titles/abstracts to establish inter-rater reliability. Afterwards, the remaining results were double screened by both authors. All abstracts were reviewed using Abstrackr, which is a free online tool designed for abstract screening in systematic reviews (Wallace et al., 2012). We then retrieved a full-text copy of all results marked as potentially relevant during title/abstract review. These results were also double screened by both reviewers. Any discrepancies in eligibility determinations or studies identified as “on the fence” were discussed among the entire research team before reaching consensus.

Data extraction and management

Eligible studies were double coded by authors KP and SF using the coding sheet in Appendix D. Our coding protocol captured various items related to: a.

Reference information (title, authors, publication etc.)

The research team met frequently to discuss coding items and any discrepancies in coding were discussed among all review authors before coming to a final coding decision. EpiData Software (https://www.epidata.dk/index.htm) was used to digitize coding forms and facilitate data entry.

Assessment of risk of bias in included studies

Six items adapted from the Cochrane randomized and non-randomized risk of bias tools (Sterne et al., 2016; Sterne et al., 2019) were used to assess the potential for bias across all studies included in our meta-analysis.

Nonequivalence between groups (item B) was coded “probably yes” or “yes” if there was evidence of important baseline differences between groups that were not controlled for statistically. Otherwise, this item was coded as “probably no.” The appropriateness of the statistical analysis (item C) was coded as “probably yes” for quasi-experimental studies using multiple regression or ANCOVA models, and “yes” for quasi-experimental studies using strong statistical matching procedures (e.g., propensity score matching). Quasi-experimental studies that did not control for confounding factors were rated as “probably no” or “no” for this measure. For experimental studies, the appropriateness of the analysis was coded as “yes” so long as a statistical significance test was used that did not appear to violate any necessary distributional assumptions (e.g., normality, independence). Implementation failures and data missingness (items D and E) were coded as “no” if there was high program fidelity and no evidence of missing data. Similarly, this measure was coded as “probably no” if there was no evidence that implementation issues or data missingness favored one group over the other. Finally, the ability of researchers to establish temporal ordering (item F) was coded as “no” or “probably no” for cross-sectional studies (i.e., cross-sectional surveys), and “probably yes” for longitudinal studies. Only longitudinal studies that could definitively separate the intervention and the outcome in time were coded as “yes” on this measure.

At the study-level, place-based quasi-experiments reporting evidence of uncontrolled baseline differences between groups were rated as “high risk” of bias. Quasi-experimental studies that reported either no evidence of baseline differences between groups or that statistically controlled for baseline differences were rated as “some concerns”. Only place-based studies using random assignment were rated as “low risk” of bias, so long as the authors did not report evidence of significant issues with the assignment process, analysis, or program implementation.

For person-based studies, any study coded as “No” or “Probably no” on our temporal ordering measure was rated as “high risk” of bias (i.e., cross-sectional studies). Studies coded as either “Yes” or “Probably yes” on our temporal ordering measure were rated as “some concerns,” so long as these studies used analytic methods that controlled for possible confounding variables (i.e., longitudinal studies using multiple regression analyses). Only longitudinal studies using strong statistical matching techniques (e.g., propensity score matching) with clear separation of treatment and outcome measures across time were rated as “low risk” of bias for person-based studies.

Measures of treatment effect

The protocol for this review outlines the anticipated approach for effect size calculations based on the expected nature of the outcome measurements (Weisburd et al., 2021). This section provides a precise outline of our effect size calculations based on the studies included in the review.

Measures of treatment effect varied considerably across outcome groupings. For eligible place-based studies, effect sizes were calculated using logged relative incident rate ratios (RIRR). These studies predominately reported count data for treatment and control groups during pre- and post-intervention periods (or during post-intervention periods alone). Given that Cohen's d effect sizes are sensitive to the way in which counts are divided across time and space, Wilson (2022) suggests the use of the RIRR for place-based studies. The RIRR is a difference-in-difference effect size that can be expressed using the following equation:

ln ( RIRR ) = ln ( x 11 / t 11 ) ( x 00 / t 00 ) ( x 01 / t 01 ) ( x 10 / t 10 ) , $\ln (\text{RIRR})=\ln \left[\frac{{(x}_{11}/t_{11})(x_{00}/t_{00})}{{(x}_{01}/t_{01})(x_{10}/t_{10})}\right],$

v ln ⁡ ( RIRR ) = 1 x 11 + 1 x 10 + 1 x 01 + 1 x 00 . $v_{\ln {\rm{}}({RIRR})}=\frac{1}{x_{11}}+\frac{1}{x_{10}}+\frac{1}{x_{01}}+\frac{1}{x_{00}}.$

However, given that overdispersion is common in count data (see MacDonald & Lattimore, 2010), an adjustment to the variance is often necessary. Wilson (2022) recommends the following correction for over-dispersion based on the quasi-Poisson model:

Φ = 1 Σ n k − 4 Σ s k 2 ( n k − 1 ) X ¯ k , ${\rm{\unicode{x00424}}}=\left(\frac{1}{{\Sigma }_{n_k}-4}\right)\Sigma \frac{s_k^2(n_k-1)}{{\bar{X}}_k},$

X ˉ k ${\mathop{X}\limits^{̅}}_k$

S k $S_k$

n k $n_k$

Φ ${\rm{\unicode{x00424}}}$

Φ ${\rm{\unicode{x00424}}}$

Φ ${\rm{\unicode{x00424}}}$

For most eligible studies of crime and displacement, we were able to calculate an RIRR using reported means or counts. Several studies, however, required alternate methods to obtain an effect size. Two studies reported regression coefficients from count-based models (MacDonald et al., 2016; McCandless et al., 2016), allowing us to use the logged incident rate ratio and standard error reported directly in the regression model. These regression coefficients also provided estimates that were adjusted for various confounding factors or forms of non-independence that were possible within the data. One study used a linear probability model to assess the mean difference in probability of a crime occurring for treatment areas/times compared to control areas/times (Weisburd et al., 2016). Here, we used the regression coefficient and the intercept of the regression model to construct a risk ratio. Given that risk ratios can be considered censored counts (see Wilson, 2022), we synthesized this effect size with studies reporting count data. Finally, one study required the use of a digitizing software to obtain numeric data from a line graph comparing treatment and control areas (Murray, 2014). To accomplish this, we used Engauge Digitizer, which has been recommended and used in recent meta-analyses (see No et al., 2018; Tantry et al., 2021).

Mental and physical health outcomes were most frequently reported as dichotomous measures, often using some form of logistic regression. As such, we synthesized these studies using logged odds ratios (ORs). We note here that risk ratios may have been preferable given their ease of interpretation (Weisburd et al., 2022), but we did not often have the requisite data to convert reported ORs into risk ratios. In most cases, we coded ORs directly from logistic regression models and calculated the standard error of the logged OR using the reported 95% confidence interval (CI) (Dennison & Finkeldey, 2021; Hirschtick, 2017; Hirschtick et al., 2020; Jackson, Testa, Vaughn, & Semenza, 2020; Jackson et al., 2021; Lewis & Wu, 2021; Sundaresh et al., 2020; Testa et al., 2021).

5

This calculation involves dividing the 95% confidence interval by the z-value associated with 95% of a two-tailed standard normal distribution as follows:

S E = CI Upper − CI Lower 3.92 . $SE=\frac{{{CI}}_{\mathrm{Upper}}-{{CI}}_{\mathrm{Lower}}}{3.92}.$

Individual attitudes toward the police and self-reported crime/delinquency were generally operationalized as scaled or continuous measurements. We synthesized these studies using Hedges' g effect sizes, which represents the standardized mean difference between groups (Hedges, 1981). In many cases, g values were calculated from standardized or unstandardized linear regression coefficients (Baćak & Apel, 2021; Rosenbaum et al., 2005; Slocum et al., 2016; Swaner & Brisman, 2014; Wheelock et al., 2019), or path coefficients from structural equation models (Lee et al., 2017; Murray et al., 2021). Other studies reported means and standard deviations (Wiley & Esbensen, 2016; Wiley et al., 2013), t-tests (Tyler et al., 2014), or ordinal frequency distributions from which g values could be calculated (Friedman et al., 2004). A small subset of studies examining attitudes toward the police reported ORs or dichotomous frequencies/proportions (Harris & Jones, 2020; Singer, 2013). For these studies, we calculated logged ORs and converted them to Hedges' g estimates. Once again, this conversion was done using the Cox logit method, which divides the logged OR by 1.65 and the variance of the logged OR by 1.65² (see Sánchez-Meca et al., 2003; Wilson, 2017).

All effect sizes were calculated using functions manually built in R statistical software (R Core Team, 2022) based on equations listed in Lum et al. (2020) and Wilson (2017). When applicable, effect sizes were cross-checked against results from David Wilson's effect size calculator (https://www.campbellcollaboration.org/escalc/html/EffectSizeCalculator-Home.php).

Unit of analysis issues

The unit of analysis for this review was the research study, defined here as each unique or statistically independent sample from which outcomes were drawn. In our main analyses, each study/sample was included only once per outcome grouping. However, we did encounter situations in which a single study reported multiple outcomes from within the same outcome grouping, or where multiple studies reported similar outcomes taken from the same sample of subjects. In these situations, we employed a selection rule to maintain statistical independence between effect sizes included in the same meta-analytic model. For studies of crime and displacement, we were able to calculate an aggregate effect size for all studies included in the meta-analysis. Given that these effect sizes utilized all available information, no further selection rule was required. For studies measuring other outcomes, we first attempted to select or calculate the most general/aggregate effect size possible. This led to the selection of general measures such as self-reported mental or physical health over more specific measures such as sleep problems or functional limitations (Baćak & Apel, 2020; Testa et al., 2021). Where such a selection was not clearly possible, we prioritized the most valid effect size as determined by our risk of bias ratings. For example, a number of studies analyzed similar outcomes taken from the same longitudinal cohort surveys (see e.g., Geller, 2017; Slocum et al., 2016; Turney, 2021; Wiley et al., 2013; Wiley & Esbensen, 2016). In these situations, we selected the effect size determined by coders as being the best causal estimate, or the estimate that did the best job of establishing the elements of causality. In general, this criterion prioritized the selection of well-matched or adjusted estimates over unmatched or unadjusted estimates.

At times, however, our selection of effect sizes was subjective or arbitrary. To ensure that these selections did not bias the results of our review, we conducted sensitivity analyses that incorporated all calculated effect sizes for each study/sample. These analyses were conducted using robust variance estimation (RVE), which is a method capable of analyzing statistically dependent data structures in meta-analysis (see Tanner-Smith et al., 2016). In the RVE model, the weight of each effect size is no longer directly related to its variance. Assuming a correlated data structure, the effect size weights in RVE models become the product of the average effect size within each grouping unit and the number of effect sizes nested within that grouping unit (see Tanner-Smith et al., 2016). Thus, the weight of each effect size within a study or sample will display an inverse relationship with the number of effect sizes nested within that study or sample. Additionally, all effect sizes within a grouping unit will receive the same weight. This method avoids potential issues associated with the over-representation of a sample or study due to the inclusion of multiple effect sizes. For our analyses, we assumed a correlated data structure and clustered standard errors by each unique sample (for a similar approach see Wilson et al., 2021).

Dealing with missing data

When studies that were otherwise eligible did not report the necessary data to calculate an effect size, we attempted to contact study authors. Ultimately, we were unable to calculate an effect size for only one eligible study that otherwise would have been included in a meta-analytic model (Alderden et al., 2011). We review the narrative results of this study and all other eligible studies not included in our meta-analysis in subsequent sections.

Assessment of heterogeneity

We assessed heterogeneity in effect sizes estimates using the Q statistic, I ² values, and τ ² values. Here, the Q statistic represents the statistical significance of the between-study variance (i.e., whether there is more variance than would be expected from sampling error alone), the I ² value represents the percentage of total variance attributable to variance between studies, and the τ ² value represents the magnitude of the random-effects variance component (see Borenstein et al., 2010; Higgins & Thompson, 2002). Additionally, we explored between-study heterogeneity using various moderator analyses (see Section 4.3.10).

Assessment of reporting biases

Three methods were used to assess the potential for reporting bias. First, we conducted moderator analyses comparing the mean effect sizes for published and unpublished studies. Second, we generated funnel plots with trim-and-fill analyses to identify any asymmetries in effect size estimates across standard error values and to impute missing values if needed (Duval & Tweedie, 2000). Finally, we conducted Egger's regression tests to assess the linear relationship between standard error and effect size magnitude (Egger et al., 1997).

Data synthesis

Data synthesis for this review involved standard inverse-variance weighted meta-analysis. A separate model was estimated for each unique outcome construct and all outcomes were analyzed using random effects models. The random effects variance component (τ ²) for each model was derived using restricted maximum likelihood estimation. These primary analyses were conducted in R statistical software using the metafor package (Viechtbauer, 2010). Sensitivity models incorporating all calculated effect sizes were estimated using the robu() function found in the robumeta package in R statistical software (Fisher & Tipton, 2015).

Subgroup analysis and investigation of heterogeneity

Per the protocol for this review (Weisburd et al., 2021), we investigated heterogeneity across effect size estimates using a variety of additional moderator analyses. Due to the characteristics of our eligible studies and the data that was frequently reported, the moderators used for each outcome grouping differ from those listed in the protocol. For place-based studies these moderators included:

Research design (“matched” vs. “unmatched” designs)

For studies assessing mental health outcomes, these moderators included:

Research design (“adjusted” vs. “unadjusted” estimates)

For studies assessing individual attitudes toward the police, these moderators included:

Research design (“adjusted” vs. “unadjusted” estimates)

We did not employ moderator analyses for physical health outcomes or self-reported crime/delinquency, given the small number of studies included in these models.

Sensitivity analysis

In addition to the RVE models previously described (see Section 4.3.5), several sensitivity analyses were conducted. One study measuring attitudes toward the police produced a large effect size that was an apparent outlier in the forest plot for this outcome (Singer, 2013). As such, we re-estimated this model excluding this effect size from the analysis. Additionally, several studies reported measures of police stops that compared only individuals who experienced unfair, false, or dissatisfying stops to those without direct stop experience (Baćak & Apel, 2021; Baćak & Nowotny, 2020; Dennison & Finkeldey, 2021; Lee et al., 2017; Testa et al., 2021). Given the potential for the qualitative nature of the stop experience to be an important moderating factor (see Harris & Jones, 2020; Mazerolle et al., 2013; Slocum et al., 2016), we re-estimated all applicable models while excluding these studies from the analysis.

Results of the search

As seen in Figure 1, our systematic search strategies yielded a total of 1,940 results published between 1970 and 2021. Of these, 964 were provided by the GPD, 960 were identified by our secondary search strategies, and 16 were recommended by subject matter experts.

OPEN IN VIEWER

Figure 1

PRISMA flowchart for search results

Description of included studies

The vast majority of included studies were conducted in the United States, though a handful of studies took place in Europe. Non-US studies generally occurred in the United Kingdom (five of seven non-US studies), and two studies involved respondents from multiple European countries including the United Kingdom (Baćak & Apel, 2020; Baćak & Apel, 2021). Nearly three-quarters of our eligible studies used individuals as the unit of analysis rather than geographic areas. The most common outcomes included crime and disorder, mental health, and attitudes toward the police. While over three-fourths of our eligible studies were published in peer-reviewed journals, the methodological rigor of these studies was relatively weak overall, with the majority being classified as unmatched quasi-experimental designs. Finally, it is important to note here that our search did not yield 40 statistically independent studies. Instead, four survey samples were associated with 15 separate studies, yielding a total of 29 unique samples.

Of the 10 eligible studies measuring crime and disorder outcomes, nine were included in our meta-analysis (see Table 2).

Several other studies examined the impact of pedestrian stops on crime and disorder through exploitation of natural variation in the use of pedestrian stops by police forces across time and space (MacDonald et al., 2016; McCandless et al., 2016; Murray, 2014; Weisburd et al., 2016). Two studies evaluated the use of pedestrian stops at targeted areas in New York City during the early 21st Century (i.e., Operation Impact). MacDonald et al. (2016) compared monthly crime counts for census block groups within impact zones to monthly crime counts for census block groups in other areas of the city, and Weisburd et al. (2016) evaluated the probability of a crime occurring for areas/weeks in which a pedestrian stop occurred to areas/weeks in which a stop did not occur. McCandless et al. (2016) evaluated the impact of Operation BLUNT (a stop and search initiative used to combat knife crime in London) by comparing monthly crime counts for boroughs that were more heavily targeted by the initiative to those that received less attention. Murray (2014) charted levels of violent crime for two police forces in Scotland both before and after diverging trends in stop patterns began to emerge between the two. Across nearly all geographic studies of crime and disorder, researchers reported aggregate crime outcomes or aggregate violent/gun crime outcomes. Follow-up durations were generally 1 year or less, though two studies provided multiple years of follow-up data (McCandless et al., 2016; Murray, 2014). In almost all cases, the outcome evaluation occurred while the intervention was still active, and given the relatively small variance in follow-up durations, we do not conduct separate analyses of results based on follow-up length.

Treatment conditions in individual-level studies were operationalized in numerous ways, though all included some comparison of individuals with direct stop experience to those without direct stop experience. Studies deriving from the Fragile Families and Child Wellbeing survey (FFCWS) measured treatment by asking youth whether they had ever been stopped by police “while on the street, at school, in a car, or some other place” (Jackson, Testa, & Vaughn, 2020, p. 753), and youth in the National Evaluation of the Gang Resistance Education and Training program (GREAT) were asked how many times in the past 6 months they had been stopped by the police for questioning (though this variable was generally dichotomized). In the FFCWS, this measure was often taken during the year 15 wave (i.e., when respondents were roughly 15 years old), and the GREAT survey administered this item during the second/third waves of data collection, when the youth were generally 12 years of age or older (see Wiley & Esbensen, 2016). Adults in the National Longitudinal Study of Adolescent to Adult Health survey (Add Health) were asked about police stop experience at two time points. During wave III (when respondents were 18–26 years old), they were asked whether they had ever been stopped or detained by police (excluding minor traffic violations), and at wave V (when respondents were 34–43 years old) they were asked if they had ever been “unfairly stopped, searched, or questioned by police” (Dennison & Finkeldey, 2021, p. 263). Studies using the Add Health data varied in the measure of police stops that they used, with Testa et al. (2021) using the wave V measure, Baćak and Nowotny using the wave III measure, and Dennison and Finkeldey (2021) providing estimates from both measures. Respondents in the European Social Survey (ESS) were asked whether police in their country had approached them, stopped them, or made contact with them for any reason during the past two years (Baćak & Apel, 2020, 2021). The ESS was cross-sectional, and respondents were, on average, in their late 40s. Other measures of treatment included simply asked respondents whether and how many times they had been stopped by police (e.g., during their lifetime or the past 12 months, see Hirschtick et al., 2020; Lewis & Wu, 2021; Singer, 2013), whether they had ever been “falsely stopped” (Lee et al., 2017, p. 101) by police, whether they had ever been “stopped and searched by a police officer” (Murray et al., 2021, p. 268), or whether they had been subject to police-initiated/involuntary contact (Rosenbaum et al., 2005; Wheelock et al., 2019).

Ten individual-level studies measured mental health outcomes. These outcomes commonly included anxiety (Geller, 2017; Geller et al., 2014), depression (Baćak & Nowotny, 2020; Hirschtick et al., 2020; Turney, 2021), suicidality (Dennison & Finkeldey, 2021; Jackson et al., 2021) and PTSD symptoms (Geller, 2017; Hirschtick et al., 2020; Lewis & Wu, 2021). All such studies used self-reported questionnaire or interview surveys, often incorporating items from validated medical instruments. Similar procedures were used across the five studies measuring physical health outcomes, which included self-reported poor health (Baćak & Apel, 2020; McFarland et al., 2019) and sleep problems (Jackson, Testa, Vaughn, & Semenza, 2020; Testa et al., 2021). Attitudes toward the police and self-reported crime/delinquency were also measured using self-report surveys and interviews. Common outcomes for attitudes toward the police included scaled or ordinal measures of police legitimacy (Baćak & Apel, 2021; Murray et al., 2021; Tyler et al., 2014), respect (Friedman et al., 2004; Harris & Jones, 2020; Singer, 2013), trust (Friedman et al., 2004; Murray et al., 2021; Singer, 2013), satisfaction (Wheelock et al., 2019), and overall negative attitudes (Rosenbaum et al., 2005; Swaner & Brisman, 2014). For the six studies measuring self-reported crime/delinquency, these measures were operationalized as composite counts or scales that included multiple forms of adolescent or adult criminality (Slocum et al., 2016; Wiley & Esbensen, 2016; Wiley et al., 2013), drug use (Dennison & Finkeldey, 2021), or general non-compliance with the law (Murray et al., 2021). Mental/physical health outcomes and attitudes toward the police were generally measured as current or lifetime outcomes, while studies on self-reported crime/delinquency measured behavior taking place within the prior 6–12 months.

As previously mentioned, there was considerable overlap in the surveys/samples used across person-based studies. Seven studies analyzed respondents from the FFCWS (Geller, 2017; Harris & Jones, 2020; Hofer et al., 2020; Jackson, Testa, & Vaughn, 2020; Jackson, Testa, Vaughn, & Semenza, 2020; McFarland et al., 2019; Turney, 2021), three studies analyzed respondents from the Add Health survey (Baćak & Nowotny, 2020; Dennison & Finkeldey, 2021; Testa et al., 2021), three studies analyzed respondents from the GREAT survey (Slocum et al., 2016; Wiley & Esbensen, 2016; Wiley et al., 2013), and two studies analyzed respondents from the ESS (Baćak & Apel, 2020, 2021). The FFCWS, Add Health, and GREAT surveys are all longitudinal cohort surveys administered in the United States, while the ESS is a cross-sectional survey of 26 European countries. Though the survey waves and total sample sizes analyzed across these studies differed, there is still considerable overlap between them. At times, studies using the same sample analyzed conceptually distinct outcomes, such as attitudes toward police (Harris & Jones, 2020) and mental health (Geller, 2017). However, at other times these outcomes were conceptually similar. For example, both Geller (2017) and Turney (2021) used the FFCWS to measure mental health outcomes (anxiety and depressive symptoms, respectively). In these situations, only one study was selected per model (see Section 4.3.5), and accordingly, our main analyses do not generally include the total number of studies for each outcome grouping reported in Table 1. For mental health outcomes, two samples were associated with four studies, resulting in a total of eight unique samples. For physical health outcomes, one sample was associated with two studies, resulting in a total of four unique samples. For self-reported crime/delinquency, one sample was associated with three studies, resulting in a total of four unique samples. In addition, of the 14 studies that reported outcomes for youth samples, seven of these studies used the FFCWS survey and three used the GREAT survey, resulting in only six unique samples.

Finally, four studies met our inclusion criteria but were too conceptually dissimilar from the studies described above to include in our meta-analysis. Two studies used self-report surveys from the FFCWS to measure respondents' degree of legal cynicism (Hofer et al., 2020; Jackson, Testa, & Vaughn, 2020). Here, legal cynicism involved attitudes toward multiple aspects of the legal and criminal justice systems, rather than toward the police alone. Thus, while we considered legal cynicism to be an important outcome, we did not synthesize it with studies measuring attitudes toward the police. One study measured community members perceived sense of safety, comparing individuals who had been stopped by police in the past 6 months to those who had not (Kochel & Nouri, 2021). We considered this outcome analogous to fear of crime (defined as eligible in the protocol for this review), but we did not have enough conceptually similar outcomes to conduct a meta-analysis. Additionally, one study measured civic engagement using 311 calls to the police by comparing precincts above and below the mean stop rate per capita (Lerman & Weaver, 2014). While 311 calls are not a measure of crime, they may represent a measure of citizen engagement with the legal system. However, the unit of analysis in this study was geographic and we lacked comparable outcomes from our other geographic studies. We review the results of the studies not included in our meta-analysis in Section 5.5. Additionally, narrative summaries of all eligible studies can be seen in Supporting Information: Appendix E.

Excluded studies

A number of studies published between 1970 and 2021 warranted further discussion during our screening processes but were ultimately determined to be ineligible. These studies were generally deemed ineligible based on measures of treatment that were either too broad (see Bradford, 2017; DeVylder, Frey, et al., 2017; DeVylder, Oh, et al., 2017; Kennedy et al., 2015; Lehrer & Lepage, 2020; McFarland et al., 2018; Rosenfeld et al., 2014; Sargeant et al., 2021; Villaveces et al., 2000) or too specific (Bryant et al., 2015; Ostrom & Whitaker, 1973). For example, we excluded studies that compared individuals who were searched by police to those who were not searched by police (rather than a more general measure of police stops), interventions solely or primarily involving traffic stops or citations, or interventions incorporating larger legislative, enforcement, or community-based efforts.

Finally, several studies published after our 2021 deadline that would have otherwise met our eligibility criteria were recommended by subject matter experts. While we excluded these studies from our meta-analysis and main results, we discuss the general findings of these studies and their implications for the results of our review in Section 5.5.

Crime and displacement

Figures 2 and 3 display effect sizes from nine eligible studies of crime/disorder and four studies of spatial displacement following pedestrian stop interventions. All such studies were place-based and utilized official data sources (e.g., incident reports or calls for service). Effect sizes to the left of the reference line indicate reductions in crime/disorder for treatment areas relative to control areas, and thus are considered effects favorable to treatment. The size of the point estimates in the forest plots represent the weight that each study received in the analysis, which is inversely related to the variance of the effect size. The combined sample size for crime and displacement outcomes was 20,876 and 8,220 geographic areas, respectively.

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Figure 2

Crime effects for place-based studies

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Figure 3

Displacement effects for place-based studies

As seen in Figure 2, pedestrian stops interventions were associated with a statistically significant reduction in crime of 13% (p < 0.001) for treatment areas relative to control areas. CIs for this outcome suggest a crime reduction effect ranging from 9% to 16%. There is also a notable lack of heterogeneity in these effect sizes. All effect sizes tend to favor treatment with overlapping CIs, and between-study heterogeneity was not statistically significant, as indicated by the Q statistic.

Figure 3 displays effect sizes for studies measuring spatial displacement. Here, we followed the approach used by Telep et al. (2014) in comparing treatment catchment or buffer areas to control areas when catchment areas were not drawn around the control areas themselves. Results indicate a statistically significant diffusion of crime control benefits. Specifically, police stop interventions were associated with a 7% (p < 0.001) decrease in crime for treatment displacement areas relative to control areas, with CIs ranging from a 4% decrease in crime to a 9% decrease in crime. There was also a lack of significant or excess heterogeneity in this model, as indicated by the Q and τ² statistics. It is important to note, however, that these results seem to be driven by one study receiving a large amount of weight in the analysis (MacDonald et al., 2016). In fact, three out of the four effect sizes favor displacement rather than diffusion. Given this, and the small number of studies, we urge caution in the interpretation of these findings.

Mental and physical health

Pedestrian stops may be a stressful and traumatizing experience that has negative effects on subjects' mental and physical functioning. Figures 4 and 5 display effect sizes from eight studies measuring mental health issues and four studies measuring physical health issues. Here, effect sizes to the right of the reference line indicate increases in the odds of a mental health issue for treatment groups relative to control groups, and these effects are considered favorable to control groups. Sundaresh et al. (2020) was included in both mental and physical health models given that their outcome (life evaluation) incorporated measures of both mental and physical health. The effect size for this study was also reverse coded so that effects favorable to control moved in the same direction across all studies. The combined sample size for mental and physical health outcomes was 71,810 and 64,898, respectively.

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Figure 4

Mental health issues for person-based studies

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Figure 5

Physical health issues for person-based studies

The eight effect sizes shown in Figure 4 suggest that individuals stopped by police were associated with a statistically significant 46% (p < 0.001) increase in the odds of a mental health issue, with CIs ranging from a 24% increase to a 72% increase. All effect sizes favored control groups, though there was significant heterogeneity in effect sizes estimates, as roughly 78% of the total variance could be attributed to between-study variance.

As seen in Figure 5, the four studies measuring physical health outcomes provided similar results. Overall, there was a statistically significant 36% (p < 0.001) increase in the odds of a physical health issue for treatment groups relative to control groups, and the CI for this outcome suggests that likely effects range from a 14-62% increase. All four studies showed significant effects favoring control, though there remains statistically significant between-study heterogeneity. Despite the strong and significant backfire effects indicated by these mental and physical health analyses, it is important to reiterate the inherent difficulties and potential biases involved in measuring these outcomes. Causal interpretations should be made cautiously.

Attitudes toward the police

Individuals subjected to pedestrian stops, particularly those that are perceived as false or unfair, may harbor resentment and negative future attitudes toward the police. Our nine eligible studies measuring attitudes toward the police are displayed in Figure 6. Hedges' g effect sizes were used for these outcomes given their often scaled or continuous nature. Thus, effect sizes to the left of the reference line indicate worsening attitudes toward the police and are defined as effects favorable to control. Several effect sizes were reverse coded to ensure that negative values corresponded to worsening attitudes for all studies (Rosenbaum et al., 2005; Swaner & Brisman, 2014). The combined sample size for this outcome was 41,423.

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Figure 6

Attitudes toward the police for person-based studies

Results from Figure 6 indicate that pedestrians stops were associated with a statistically significant small to moderate decrease in attitudes favorable to the police (g = −0.38, 95% CI: −0.59, −0.17, p < 0.001). The classification of this effect size as small to moderate is based on the conventions suggested by Cohen (1992), however, outside of laboratory settings this effect may be considered rather large (Lipsey et al., 2012). Using the binomial effect size display to convert this effect into a percentage point difference suggests an 18.6% differential between control and treatment groups.

11

This conversion can be expressed as the following (see Lipsey & Wilson, 2001):

g g 2 + 4 $\frac{g}{\sqrt{g^2+4}}$

.

Self-reported crime/delinquency

If pedestrian stops result in the imposition of a formal label that leads to the exclusion of individuals from conventional bonds and activities, then we may also expect to see a backfire effect in terms of specific deterrence. Results from the four eligible studies comparing self-reported crime/delinquency for individuals stopped by police to individuals not stopped by police are shown in Figure 7. Here, effects to the right of the no reference line indicate increases in self-reported crime/delinquency for treatment groups relative to control groups, and thus are defined as effects favorable to control. The combined sample size for this outcome was 11,402.

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Figure 7

Self-reported crime/delinquency for person-based studies

Results from this analysis continue to suggest deleterious individual-level effects of pedestrian stops. Specifically, there was a statistically significant increase in self-reported crime/delinquency for treatment groups relative to control groups (g = 0.30, 95% CI: 0.12, 0.48, p < 0.001). Using the binomial effect size display to convert this effect into a percentage point difference suggests an approximate 15% differential between control and treatment groups. All four effect sizes reported here favored control, though there remains a statistically significant amount of between-study heterogeneity.

Violence in police-citizen encounters

We did not locate any eligible studies providing measures of violence in police-citizen encounters.

Officer misbehavior

Only one eligible study provided a potential measure of officer misbehavior. The San Diego field interrogation experiment measured citizen complaints against the police both before and after the intervention, however, there were no complaints during either time period (Boydstun, 1975).

Sensitivity analyses

We conducted several robustness checks to assess the sensitivity of our results to different specifications. As previously noted, our main models included a selection of one effect size per study/sample. At times, this selection of effect sizes could be considered arbitrary, which presents concern over the potential for these selections to bias our results. Thus, we conducted sensitivity analyses using RVE that incorporated all calculated effect sizes taken from each sample and outcome grouping. These models were only estimated for mental health outcomes, attitudes toward the police, and self-reported crime/delinquency as these were the only outcomes for which difficult effect size selections were often required. For each model, standard errors were clustered by sample, resulting in eight unique clusters for mental health outcomes, nine clusters for attitudes toward the police, and four clusters for self-reported crime/delinquency.

Results from our RVE models are displayed in Table 6. For mental health issues and attitudes toward the police, RVE models continued to suggest a statistically significant effect favorable to control groups. The mean effect size for mental health studies decreased slightly (from a 46% increase in our main specification to a 37% increase in the RVE model), while the mean effect size for attitudes toward the police increased slightly (from g = −0.38 in our main specification to g = −0.40 in the RVE model). Results for self-reported crime/delinquency remained similar in magnitude (from g = 0.30 in our main specification to g = 0.26 in the RVE model), but these results were no longer significant at a 0.05 threshold. However, the degrees of freedom for this model were fewer than four, which is considered an unreliable sample size for RVE estimation (see Tanner-Smith et al., 2016).

Our main model specification for attitudes toward the police also suggested the presence of an outlier (Singer, 2013). Thus, we reanalyzed this model while excluding this study from the analysis. Results continued to indicate a statistically significant decrease in attitudes toward the police for treatment groups relative to control groups (g = −0.30, 95% CI [−0.44, −0.16]). Moreover, this effect was similar in magnitude to that of the original specification (g = −0.38, 95% CI [−0.59, −0.17]). Finally, one study measuring attitudes toward the police (Baćak & Apel, 2021), two studies measuring mental health issues (Baćak & Nowotny, 2020; Dennison & Finkeldey, 2021), and one study measuring self-reported crime/delinquency (Lee et al., 2017) used measures of police stops that were limited to unfair, false, or unsatisfactory stop experiences.

Research design

Studies with weaker methodological rigor have been shown to produce larger effect size estimates than those with stronger methodological rigor (Weisburd et al., 2001). To test the potential for methodological strength to impact our crime/disorder and mental health findings, we compared effect sizes for studies with matched versus unmatched designs. Here, “matched” does not necessarily indicate a statistical matching procedure, but rather any attempt to identify comparable control areas.

Results of these moderator analyses can be seen in Table 7. For crime and disorder outcomes, unmatched designs were associated with a 10% decrease in crime for treatment areas relative to control areas, while matched designs were associated with a 19% decrease. This difference was non-significant and both effect sizes remained statistically significant individually (as indicated by the 95% CIs). Of note, if we consider Weisburd et al. (2016) to be an unmatched design, the difference between matched and unmatched effect sizes increases in magnitude and becomes statistically significant. However, we find this distinction to be misleading as Weisburd et al. used an instrumental variable approach that is likely stronger than any of the non-statistical matching procedures used in our other studies. For mental health outcomes, unmatched studies were associated with a 49% increase in the odds of a mental health issue for treatment groups relative to control groups, while matched designs were associated with a 43% increase. Once again, this difference was non-significant and both effect sizes remained statistically significant individually, with 95% CIs greater than one.

No eligible studies for attitudes toward the police employed matching procedures. However, several studies provided only unadjusted bivariate data from which an effect size could be calculated (Friedman et al., 2004; Singer, 2013; Tyler et al., 2014). Thus, to assess risk of bias for these studies we compared effect sizes for adjusted and unadjusted estimates. Results from this analysis can be seen in Table 8. While adjusted effect sizes were notably smaller than unadjusted effect sizes, by an average of g = 0.26 (95% CI [−0.17, 0.68]), this difference was not statistically significant and both categories of studies remained significantly different from 0.

Size of geographic area

Weisburd et al. (2014) suggest that the use of pedestrian stops is often targeted at high crime microgeographic areas. If so, then the mere increase in police presence within hot spots of crime and disorder may be responsible for any observed crime reduction effect (see Braga et al., 2019). To test for this potential, we conducted a moderator analysis comparing effect sizes for studies targeting micro-geographic areas, neighborhoods/police beats, police districts/precincts, and macro-geographic areas (e.g., entire cities). Given the small number of studies within each of these categories, we treat geographic size as a continuous variable and estimate this moderator analysis as a meta-regression. Results of this analysis are shown in Table 9. On average, increases in the size of the geographic area targeted led to decreases of between 3% and 4% in effect size estimates (i.e., larger areas received smaller crime reduction benefits), however, this linear effect was not statistically significant (RIRR = 1.04, 95% CI [0.977, 1.105]). Of note, the mean effect sizes for all groups other than macro-geographic areas displayed CIs less than one, indicating statistical significance. However, we urge caution when interpreting these effects, given the small number of studies in each grouping.

Youth versus adult samples

Concern regarding the deleterious impact of pedestrian stops is particularly relevant for adolescents, as these populations may be increasingly vulnerable to stressful/traumatic experiences and the imposition of formal labels (Geller, 2017; Jackson et al., 2021; Wiley & Esbensen, 2016). For mental health outcomes and attitudes toward the police, there was sufficient variation in the samples used to compare the effects of pedestrian stops for youth and adults. The results of this analysis can be seen in Table 10.

For mental health outcomes, youth samples were associated with a 74% increase in the odds of a mental health issue for treatment groups relative to control groups, while adult samples were associated with only a 32% increase. This difference was nearly statistically significant at the 0.05 level (p = 0.0504), suggesting that police stops may have particularly salient effects on the mental health of youth. For attitudes toward the police, there was essentially no difference in mean effect sizes between youth and adult samples (g = −0.002, 95% CI [−0.45, 0.44]).

Geographic location

Per the protocol for this review, we also examined the difference in mean effect sizes by geographic location. Given that several studies used samples from multiple countries, we chose to compare studies conducted in the US and Europe. Table 11 displays the results from these analyses. For crime and disorder outcomes, US studies were associated with a statistically significant 9% larger decrease in crime relative to European studies. Individually, US studies were associated with a statistically significant 14% decrease in crime for treatment areas relative to control areas, while European studies were associated with a non-significant 5% decrease in crime. For mental health outcomes, US studies were associated with a 42% increase in the odds of a mental health issue for treatment groups relative to control groups, while European studies were associated with a 52% increase in these odds. However, this difference was not statistically significant. Finally, for attitudes toward the police, US studies were associated with a significantly smaller mean effect size compared to European studies (mean difference of g = 0.42, 95% CI [0.08, 0.76]). While this suggests that pedestrian stops in European settings may impact attitudes toward the police significantly more than in US contexts, it is important to note that the mean effect sizes for both locations suggested statistically significant negative effects. Additionally, all moderator analyses were limited by a small number of studies.

Eligible studies not included in meta-analyses

Five studies published between 1970 and 2021 were identified as eligible for inclusion in this review but were not meta-analyzed due to issues that prevented the calculation of an effect size or the lack of additional studies with conceptually similar outcome measures. Alderden et al. (2011) evaluated the implementation and efficacy of the Chicago Police Department's Deployment Operations Center process, which identified violent crime hot spots and guided leadership decisions on where to deploy officers to reduce violent crime, focusing on gang, drug, and gun crime. Specifically, the intervention employed directed patrols in which officers actively engaged citizens via street stops, traffic stops, and conducted aggressive ordinance enforcement. Fidelity checks indicated that the Chicago Police Department successfully implemented the Deployment Operations Center process as it was designed, and while results tended to favor a reduction in violent crime for DOC beats relative to non-DOC beats, the intervention was not responsible for significant reductions in violent crime.

Two eligible studies using the same longitudinal survey sample included an outcome of legal cynicism (Hofer et al., 2020; Jackson, Testa, & Vaughn, 2020). Given that this outcome was operationalized as a composite measure representing attitudes toward the legal system more broadly, we considered it too conceptually distinct to synthesize with studies measuring attitudes toward the police. Both Hofer et al. (2020) and Jackson, Testa, and Vaughn (2020) used data from the age 15 assessment of the FFCWS. Hofer et al. compared levels of legal cynicism for youth who experienced vicarious police contact (defined as having witnessed police stops in the respondents' neighborhood or school) and/or direct police contact (defined as directly experiencing a police stop) to youth who reported never having experienced any form of police contact. Youth who had experienced direct or both direct and vicarious contact with police had higher levels of legal cynicism than youth who only experienced vicarious police contact. Situational factors, such as police using harsh language or frisking the youth during an encounter with police, were associated with higher levels of legal cynicism as well. Similar findings were reported by Jackson et al., suggesting that youth subject to direct police stops develop significantly higher levels of legal cynicism than those who do not directly experience stops. While low self-control demonstrated a stronger relationship with legal cynicism in Jackson et al.'s study than stop experience itself, direct stop experience remained a significant predictor even with the inclusion of low self-control as a covariate.

Two studies, conducted by Kochel and Nouri (2021) and Lerman and Weaver (2014), investigated disadvantaged community members' perceptions of the extent and nature of police contact, and how these perceptions impacted feelings of safety and community engagement, respectively. Kochel and Nouri found that residents in the high-violence neighborhoods surveyed had the highest rate of police stop experience within the last six months, as well as more prevalent experiences with unfair police treatment. However, their analyses failed to find any significant effect of being stopped by police in the past 6 months on feelings of safety. Lerman and Weaver investigated how increased rates of stop-and-frisk activity in disadvantaged neighborhoods affected community members' civic engagement. Lerman and Weaver used nonemergency 311 calls as a proxy for engagement, comparing precincts above and below the mean stops per capita. Ultimately, Lerman and Weaver found that “high stop” precincts were associated with significantly more 311 requests, though this finding was attenuated by the proportion of stops that resulted in force.

Community surveys from place-based studies

Four place-based studies included community surveys to assess the impact of police activity on community members as a secondary outcome measure. Unfortunately, there was little overlap in the measures used and the data reported across these studies, which prevented us from calculating an appropriate effect size in many cases. Results from these surveys generally demonstrated that community members were supportive of increased police activity that included stops, especially when the intervention was effective at reducing perceived crime in their neighborhoods. For example, Alderden et al. (2011) found that residents, especially middle-class residents, who perceived a high level of disorder were more supportive of suppression-oriented policing as it had been implemented by the Chicago Police Department's Deployment Operations Center. Alderden et al. also found that many residents still preferred traditional or community-oriented policing and that higher levels of support for suppression-oriented policing were associated with stronger perceptions of police legitimacy.

McGarrell et al. (2002) similarly found that community members surveyed following the Indianapolis Police Department's directed patrol strategy indicated acceptance of the intervention, given the crime reduction outcomes that it produced. Specifically, McGarrell et al. found that support for the Indianapolis Police Department was high overall and not significantly affected by the increase in police activities, that police-community relations were not harmed as a result of the intervention, and that community members generally reported positive community-level effects after the treatment period ended. These findings align with Sherman and Rogan's (1995) findings from the Kansas City gun experiment. Target area residents surveyed both before and after the intervention reported being more satisfied with their neighborhood, less fearful of crime, and perceived lower rates of disorder and drug crime compared to residents from the control area (Sherman & Rogan, 1995; see also Shaw, 1995). Finally, Boydstun (1975) also found little evidence to suggest a negative impact of pedestrian stops on community members' attitudes toward the police. Community members in both treatment and control areas felt that field interrogations were a legitimate policing activity and there were few significant changes in resident perceptions between pre- and post-intervention surveys. However, respondents residing in areas where field interrogations were suspended did report significant increases in fear of crime that were not similarly observed for respondents in areas where field interrogations were uninterrupted.

2022 studies

Several studies published after our search cut-off date of 2021 were recommended to us by subject matter experts. While these studies are not formally included in our review, many of them would otherwise be considered eligible, and thus we considered it important to briefly review their findings. Overall, results from these studies are highly consistent with those produced by our review. Braakmann (2022) reported the results of an increase in stop activity after a 2019 murder in the United Kingdom, where Northumbria Police dramatically increased their level of stop and search operations in streets close to the site of the highly publicized murder. Braakmann (2022) used these natural variations to examine the effect of increased stop and search activity on crime, finding that property, weapon, violent, and drug crime were not significantly impacted by the increase in stop and search operations, but that there was a decline in anti-social behavior, criminal damage, and public order offenses. Turney et al. (2022) and Testa et al. (2022) analyzed survey data from the FFCWS and Pathways to Desistance studies, respectively, with both finding that personal and vicarious police contact were associated with significant decreases in respondents' future orientation. Foster et al. (2022) used the FFCWS data to study the impact of police stops on attitudes toward the police, finding that direct experience with police stops was associated with significant reductions in respect and confidence in the police. These results varied by race, however, and there was stronger evidence of deleterious effects for Black and Hispanic youth compared to White youth. Lastly, Jackson and Testa (2022) found that police contact was associated with worsening sleep behaviors among respondents from the UK millennium cohort survey.