EFFECT OF SUSPECT RACE ON OFFICERS’ ARREST DECISIONS^*

Abstract

Many respondents to opinion surveys say that the citizen's race influences how police officers treat the public, yet recent expert social‐science panels have declared that research findings are too contradictory to form a conclusion on whether American police are biased against racial minorities. We perform a meta‐analysis of quantitative research that estimates the effect of race on the police decision to arrest. Screening nearly 4,500 potential sources, we analyze the results based on 27 independent data sets that generated 40 research reports (both published and unpublished) that permitted an estimate of the effect size of the suspect's race on the probability of arrest. The meta‐analysis shows with strong consistency that minority suspects are more likely to be arrested than White suspects. Depending on the method of estimation, the effect size of race varied between 1.32 and 1.52. Converting the race effect size to probabilities shows that compared with the average probability in these studies of a White being arrested (.20), the average probability for a non‐White was calculated at .26. The significant race effect persists when taking into account the studies’ variations in research methods and the nature of explanatory models used in the studies. Implications for future research are presented.

Making an arrest is a relatively rare event in the daily work of the average police officer (Bittner, 1970; Black, 1980; Brown, 1981; Klinger, 1996), but it is one of the most consequential ways that the State restricts the liberty of the public. Are American police influenced by a suspect's race when deciding whether to make an arrest? Significant portions of the public are inclined to believe that police discretion is influenced by race. Public opinion surveys have shown that three fourths of the general public regard racial profiling by police as a problem, and that low ratings of police fairness are especially concentrated among Blacks, with only slightly more than one third indicating that police in their community treat all races fairly (Gallagher et al., 2001: 59–72). Even three in ten White respondents declined to rate the police in their community as fair to all races (Gallagher et al., 2001: 60). But when blue‐ribbon academic panels convened in recent years to review the research‐based evidence, they judged the findings to be so mixed that they have been unable to draw a definitive conclusion. Examining research on a range of police practices that included arrest, the National Research Council's Committee to Review Research on Police Policy and Practices concluded, “the evidence is mixed, ranging from findings that indicate bias against racial minorities, findings of bias in favor of racial minorities, and findings of no race effect” (Skogan and Frydl, 2004: 122–3). A few years later, an American Sociological Association report produced by a working group of 45 social scientists found conflicting results within the existing research on racial bias in criminal justice processing and was unable to draw firm conclusions (Rosich, 2007: 22). Both expert groups called for continued research to improve understanding of whether, and under what circumstances, police behave in a racially biased manner.

There is obvious tension between a significant public belief that policing is influenced by the citizen's race and the received academic wisdom that the evidence is mixed. During the last 50 years, a body of quantitative research on police practices, and especially the decision to arrest, has emerged; yet expert reviews of that literature have led to results that are deemed inconclusive, requiring more and better research. Our purpose is to submit that body of research to a rigorous meta‐analysis that will allow a more conclusive interpretation, one that points the way toward a better understanding of whether, when, and why race may influence police arrest practices.

Although our analytic method removes us from the streets where police officers practice their occupation, we begin with a consideration of the event‐by‐event, suspect‐by‐suspect world where the arrest decision is made. We then move to a brief discussion of the quantitative research literature assessing the effects of race on arrest before presenting our own meta‐analytic assessment of the extant literature. Our study produces a clearer picture than prior academic analyses have suggested. Focusing on a comparison of the treatment of Black and White suspects, we find a strong and strikingly consistent pattern of race effects. In most studies that satisfy our criteria for consideration, the suspect's race does increase the probability of arrest, taking into account other factors that have been shown to influence arrest as well. This pattern of results is robust across a wide range of assumptions. We submit the data on the studies to analyses that might account for the variation that we do observe in the scope of race effects, and we offer suggestions for improving future research.

ANALYZING THE DECISION TO ARREST

Although police detectives define success almost solely in terms of making arrests, most arrests in America are made by the ordinary patrol officer in the course of his or her everyday work on the streets, and the bulk of these arrests are made without the use of a warrant, essentially a legal mandate that at least in theory eliminates the discretion of the officer. Therefore, it is impossible to observe on a case‐by‐case basis the true scope of influence the suspect's race may exert on the arrest decision. To the extent that race is a conscious factor, nowadays we have many social and legal disincentives for American police to manifest obvious indications (e.g., uttering a racial epithet) that race influences their decisions: civil lawsuits and penalties, internal discipline, and bad publicity. Similarly, they are unlikely to reveal any such motivation in the official documents they complete or even in confidential interviews. That is not to say that such events seldom occur¹1 See Kennedy (1997: 113–25) for several contemporary examples of where police have exhibited strong indicators that racial prejudice influenced their actions toward Blacks.
but only that their absence is no reliable indicator of a lack of an effect of race on arrest. Race may not even be a conscious factor in decision making, but it could still be a powerful one.

The recent, highly publicized arrest of Harvard Professor Henry Louis Gates, Jr. for disorderly conduct is a good example of the difficulty of determining the influence of race on an individual case basis (Cambridge Review Committee, 2010). Professor Gates, a Black man, was questioned by police when a neighbor phoned in a report of a possible break‐in. In fact, Professor Gates and a friend had been forcing open a stuck door in Professor Gates's own home. The police report indicated that in the course of the questioning process, the professor acted inappropriately toward an officer who had requested identification from the professor and had asked him to step outside, and after warning him, the officer arrested him for disorderly conduct. The professor claimed that he was treated inappropriately and that it was because of his race. The difficulty with establishing the veracity of this claim is that we have no obvious indicator that race played a role in this situation, such as a racial epithet. Would the officers have treated a White man in a similar fashion? The officer involved claims he would have. As extensive social‐psychological research has shown, race may have affected the officer's decision in subtle ways of which he was unaware, but that hardly makes it easier to discern whether that was so in this case. This case illustrates the difficulties in determining the existence of racism in individual cases. However, if we could compare several similar situations, some with Black suspects and some with White suspects, we could make an evidence‐based judgment about whether the department shows a pattern of arresting Blacks more frequently than Whites under similar circumstances. That is in fact what many social‐science studies have tried to do, producing an array of effects that social‐science expert panels have found perplexing. We take the next step and synthesize this array of findings with a meta‐analysis.

Many studies observe what most of the public seems to believe—that minorities are arrested at a higher rate than Whites—but demonstrating this difference does not establish the extent to which the suspect's race is responsible for the observed differences. Researchers have appropriately argued that many other factors may influence the arrest decision, and unless their effects are taken into account, we cannot say with confidence just how influential is the suspect's race.

FACTORS THAT INFLUENCE THE ARREST DECISION

Researchers interested in assaying the effects of race on police decision making often attempt to isolate the effects of race alone by controlling for legal factors that justify an arrest and other legally irrelevant (extralegal) considerations that might influence the decision (Skogan and Frydl, 2004: 115). Legal considerations are those set forth by law that define the circumstances under which an arrest is allowable or required (Black, 1980) and “strategic factors that bear upon the case's prospects in subsequent legal proceedings” (Mastrofski, Worden, and Snipes, 1995: 541). Among legal considerations are the strength of the inculpatory evidence (does it meet the requirements of probable cause?), the availability of a cooperating complainant (willing to testify in court), the seriousness of the offense (more serious offenses presumably being worthy of more severe punishment and less likely to be dismissed by the prosecutor), the criminal record of the suspect (the longer the record, the greater the need for the consequences that arrest can produce), and mandatory arrest policies for particular offenses (e.g., domestic violence). Extralegal considerations are those features of the situation that are prohibited or not explicitly authorized by law as relevant to the arrest decision. The personal characteristics of the suspect and victim (e.g., race, sex, age, religion, wealth, and other indicators of social status) fall into this category, as do certain behaviors, such as showing a “bad attitude” or disrespect to the officer, or failure to cooperate (in ways that are not themselves legal violations). They also may include certain conditions (evidenced by relationships, behavior, or appearances) that may justify concerns about the need to exert some control, even if arrest is not justified: intoxication, heightened emotional state, and incoherent or irrational behavior. Another extralegal consideration is the degree of intimacy or closeness between antagonists: the closer the relationship (acquaintance or partner), the lower the inclination to arrest, presumably because of the greater availability of “sublegal” forms of social control available to parties in closer relationships (Black, 1971: 1108).²2 The passage of mandatory arrest legislation for domestic violence in the last decade or so altered the legal decision calculus for police. Police enjoy the legal discretion to arrest or not for most misdemeanor offenses, but mandatory arrest laws eliminate that discretion and require arrest in domestic violence situations where probable cause requirements are satisfied.

Most studies attempting to discern the effects of the suspect's race on the probability of arrest, especially those based on field observations and department records, have taken into account at least some legal and extralegal considerations. Presumably, the more of these other factors that are included as controls in the analysis, the greater the confidence that any race effects are not mistaken for these other influences, and that any masking effects are revealed (Black, 1980: 108). Prior research has shown fairly consistently that the following variables significantly increase the likelihood of an arrest: evidence strength, severity of the offense, request by the victim to make an arrest, and the suspect's negative demeanor. Researchers have found that minorities are more likely to show disrespect toward the police; they are more likely to be suspected of serious offenses; and they are more likely to ask the police to arrest the suspect (Skogan and Frydl, 2004: 115–28). If researchers fail to account for the effects of these influences, then what might otherwise appear as racial bias could be a result of one or more of these variables. Whether these independent variables also are subject to police choices born of racial bias is a matter of some debate not fully resolved (Anderson, 1990, 1999; Reisig et al., 2004), but it is standard practice to attempt to control for them when attempting to isolate the effects of race.

Although the above legal and extralegal variables are with fair consistency the most powerful predictors of the police arrest decision, they do not exhaust its possible influences. The suspect's sex, social class, and mental health have been examined, but the studies are relatively rare and the findings are mixed as to their impact, not to mention their relevance to the effects of race (Skogan and Frydl, 2004: 120–8). So too have some studies explored the impact of officers’ personal characteristics and attitudes, but these have generally not proven to be powerful or consistent predictors of arrest, including the race of the officer (Skogan and Frydl, 2004: 128–52); however, see Donohue and Levitt (2001) for evidence of an effect of officer race.

Furthermore, in recent years, a debate has emerged about the extent to which researchers studying police arrest practices have accurately distinguished legal from extralegal influences (Skogan and Frydl, 2004: 118). Klinger (1994, 1996) argues that many studies failed to identify illegal acts committed by suspects in the course of the encounter, either missing them entirely or treating them as a part of some putative extralegal variable, such as demeanor (e.g., physically resisting or acting violently toward the police officer). Some have responded that reanalyses of the data that correct at least some of these problems have not altered conclusions about race effects (Lundman, 1996: 319), whereas others have argued that this is a problem only if the researcher's purpose is to observe whether the arrest can be legally justified post hoc (Worden, Shepard, and Mastrofski, 1996: 327). Nonetheless, it is conceivable that either model misspecification or measurement errors of this sort could affect the estimation of race effects, which is a concern that meta‐analysis should take into account.

THE INFLUENCE OF RESEARCH CHOICES

Aside from controlling for the effects of other influences, several methodological features of a study might influence the nature and extent of the observed race effect. A possible source of variation in results is how the arrests were observed. One approach is to use participants at the scene as informants. Police agencies require officers to document certain situations where arrest is a possible outcome (e.g., during pedestrian or vehicle stops or contacts with juveniles), so these documents may be used. Surveys of victims or the general public may also be used, where the respondent's account of what transpired during a police contact may be gathered. Yet another approach is for researchers to train observers to accompany police and note what transpired. One might expect that official police documents would render the weakest race effects, inasmuch as there are strong disincentives in most contemporary agencies to showing racial bias, especially at a time when police are being scrutinized for racial profiling. However, research relying on victim surveys might yield stronger race effects because of patterns in the way that citizens infer or attribute police motives to racism, minorities being more inclined to attribute negative experiences with the criminal justice system to their race than Whites (Hagan and Albonetti, 1982; Henderson et al., 1997; Hurwitz and Peffley, 2005). It is not obvious how field observation by disinterested third‐party researchers who guarantee the confidentiality of the police officer's identity would affect the strength of race effects in the study. Because accuracy and objectivity are the goals of selecting and training field researchers, and observation is their sole function in the field, the accuracy and objectivity of observations should be much stronger, but officers may react to the observer's presence, altering what they do. We have some reason to think that the presence of an observer causes officers to be less passive and more legalistic and, hence, less likely to show a race effect (Mastrofski and Parks, 1990; Mastrofski, Parks, and McCluskey, 2010; Spano, 2007). It also seems that observers (by their personal characteristics and behavior) can influence patterns of police behavior (Spano, 2007). Unfortunately, researchers have not explored how the presence or actions of an observer affect the relationship between race and arrest, and presumably this could vary depending on the specifics of who conducted observations and how they conducted themselves. Given the frequency that field researchers report observing police misbehavior and abusive practices, it seems likely that the presence of an observer is not a major deterrent to police behaving in ways that are proscribed culturally or legally (Gould and Mastrofski, 2004; Mastrofski, Parks, and McCluskey, 2010; Mastrofski et al., 1998; Reiss, 1968, 1971; Terrill and Mastrofski, 2004).

Another factor that could affect the strength of race effects is the nature of the offense under consideration. One would expect that (at least since the 1960s) police discretion that is the least legally constrained or subject to the least oversight (by the courts, for example) would be that which demonstrates the strongest race effects. On the one hand, a study that sampled misdemeanors or other minor offenses should show stronger race effects than one focusing on more serious crimes. The latter typically receive far more scrutiny than the former. On the other hand, where police are charged with enforcing a mandatory arrest law (such as with misdemeanor domestic violence cases in many jurisdictions in the last two decades), then race effects should be lower.

Other theoretically and methodologically relevant factors could affect the strength of effects found, but those discussed earlier are those we could assess in the extant data. We will discuss other possible factors in our discussion of future research possibilities in the concluding section of this article.

METHOD

Meta‐analysis was used to synthesize the extant evidence of the relationship between race and likelihood of an arrest for two main reasons. First, it provided us with a credible method of examining the distribution of effects across studies that focused on the magnitude and direction of the effect rather than on the statistical significance. The latter is problematic when examining conflicting results across studies (for a discussion of this, see Hedges and Olkin, 1980). Second, it provided statistical methods for exploring the relationship between study features, such as whether suspect demeanor was incorporated into the model, and the observed effect. This allowed for the exploration of the influence on results of theoretically important substantive, and methodological features of studies.

SELECTION CRITERIA

We developed explicit criteria for establishing which studies would be included and excluded from the meta‐analysis. The goal was to create a clear demarcation of the boundaries for the review. Applying the criteria provided in the subsequent discussion yielded a final sample of 40 documents and 23 research projects that produced 27 independent data sets usable for meta‐analysis.

Research Design

To be included, studies must have examined the relationship between a citizen's race/ethnicity and the likelihood of arrest. This required the following design features: 1) that the design used microlevel data—data collected at the encounter or suspect level; 2) that arrest versus a less severe alternative to arrest at the time of the incident was used as a dependent variable; 3) that citizen race was an independent variable in at least one analysis; and 4) that the study only included cases where the citizen was actually present at the time of the police/citizen encounter or the study controlled for the ability to locate a suspect. We defined arrest as taking a person into custody for the purpose of charging him/her with a criminal offense, which would exclude stops in which the most serious possible consequence was a traffic summons. This is consistent with Terrill, Paoline, and Manning (2003) but is admittedly conservative, at least by the standards of United States v. Mendenhall (1980), in which the U.S. Supreme Court provided a broader and more subjective definition: “only if, in view of all the circumstances surrounding the incident, a reasonable person would have believed that he is not free to leave.” In fact, police departments vary in how they operationalize arrest (Linn, 2005: 10). The definition we selected fits most closely with popular conceptions of an arrest and is consistent with the way most empirical studies have defined it.

Geographic Location

We restricted our search to studies that collected data in the United States. The nature of this relationship is likely to vary across countries, and the focus of this review is the nature of this relationship within the United States.

Statistical Data

To be included, a study had to report the results on the relationship between race and arrest in a way that permitted the computation of an effect size and its associated standard error. The effect size index for this meta‐analysis was the odds ratio, with analyses performed on the logged odds ratio (see subsequent discussion for more information on the coding and analysis of effect sizes). Effect sizes were coded directly from logistic regression models or converted from probit regression models and some ordinary least‐squares (OLS) regression models. Although a few publications were excluded because of insufficient information to enable the computation of an effect size and standard error, most identified data sets are represented. A few minor data sets (e.g., a traffic stop study in Savannah, GA) were excluded because no available manuscript provided sufficient statistical information to compute an effect size of the race and arrest relationship.

Timeframe

We did not limit the review to studies based on data collected after a specific date. We had several reasons for this decision. First, we wanted to examine the full spectrum of evidence addressing this research question that also met our design criteria. These studies are difficult and time consuming to conduct, and we therefore anticipated that the total number of available studies would be modest. Second, we were interested in exploring whether any observed relationship between race and likelihood of arrest had changed over time. We began with the expectation that by the 1960s, the Civil Rights Movement had set in motion a series of legal and social changes that might reduce the effects of race on police decision making, and that over time we would see a decline in the strength of any observed relationship between race and the probability of arrest (Skogan and Frydl, 2004: 283). The studies meeting the inclusion criteria ranged from 1966 to 2004, which is a span of nearly four decades.

Publication Status

We did not exclude studies based on publication status. That is, both published and unpublished studies were eligible for inclusion. This has become standard practice within meta‐analysis and helps guard against publication‐selection bias or the tendency of the published literature to be biased in favor of results that are statistically significant (see Gerber and Malhotra, 2008; Lipsey and Wilson, 2001a; Rothstein, Sutton, and Borenstein, 2005).

SEARCH STRATEGY

Our search strategy attempted to identify all studies meeting these criteria. It is possible that we missed at least one publication or manuscript, but we are confident that this approach identified all major data sets that examined this relationship. We searched electronic databases; examined the bibliographies of relevant articles, books, and reviews; reviewed American Society of Criminology Annual Conference agendas from 2000 through 2007; and browsed recent relevant journals. The databases searched were as follows: Criminal Justice Abstracts, Criminal Justice Periodical Index, Dissertation Abstracts International, National Criminal Justice Reference Service (NCJRS), National Technical Information Service (NTIS), ProQuest Research Library, ProQuest Social Science Journals, PsycINFO, Public Affairs Information Service, Sociological Abstracts, Social Science Citation Index, Social Services Abstracts, and Worldwide Political Sciences Abstracts. The search terms used included race, racial, ethnicity, discriminate, discriminatory, discriminated, bias, biased, disparity, disparate, disparities, minority, African American, or Black in combination with arrest not cardiac, arrest and decision, police and (encounter, discretion, or decision), officer and (encounter, discretion, or decision), or juvenile and referral. We also searched for police stop data because of an abundance of racial profiling studies conducted in recent years.

The electronic search produced more than 4,200 hits, including duplicates. A relatively small number of additional documents resulted from the other types of searches. From nearly 4,500 potential sources, we selected 601 documents for retrieval that seemed from their title or abstract to meet our eligibility criteria. Of those documents, we retrieved 566. Thirteen of the 35 documents that could not be retrieved seemed to be alternative versions of documents that were retrieved. Furthermore, another of the 35 documents was determined to be preliminary thoughts for a paper and not an actual manuscript. Based on a review of the full documents by the first author with ongoing communication with the second author, 40 documents met the eligibility criteria. These 40 documents are based on 23 unique data sets.

STUDY CODING AND EFFECT SIZE COMPUTATION

We developed a coding protocol designed to capture various pieces of information about the study, including the data collection method, sampling strategy, sample size, level of analysis (suspect/encounter/other), geographic locations and years of the data collection, crime type, suspect age and sex of the samples, the data source, document type, type of statistical analyses applied, independent variables included, and the effect sizes for race on arrest, among other things. We created a data structure that allowed us to handle the complex hierarchical nature of the data. Most studies reported multiple analyses of the race/arrest relationship, and multiple publications or manuscripts reported many of the data sets.

The effect size index used in this meta‐analysis was the odds ratio. The odds ratio is ideal for relationships between two binary or dichotomous variables (see Fleiss, 1994; Fleiss and Berlin, 2009; Lipsey and Wilson, 2001a), such as arrest (yes/no) and race (minority/nonminority or Black/White, etc.). The regression coefficient for race from studies that reported the results from logistic regression models is a logged odds ratio, and the antilogarithm is the odds ratio. As such, the effect size from logistic regression models was coded directly from these results. Furthermore, logistic regression models were the most common form of analysis across studies. A handful of studies reported probit regression models. The unstandardized regression coefficient for race from a probit model reflects the predicted difference in the likelihood of arrest on a normal distribution, rather than a logistic distribution, as it is in a logistic regression model. These probit regression coefficients were transformed into an approximate logged odds ratio through multiplication by π/. This provides a good approximation between the normal and logistic distributions (see Hasselblad and Hedges, 1995). The standard error was transformed by first converting it to a variance, then multiplying it by π²/3, and then taking the square root. Computing an odds‐ratio effect size and related standard error from the results from OLS regression models (or related statistical methods) was more difficult. The unstandardized regression coefficient for race from these models represents the predicted difference in the proportion arrested versus not arrested. Combining this with descriptive statistics on the proportion of the overall sample arrested, it was possible through simple algebra to reconstruct a 2 × 2 contingency table representing the arrest by race relationship, adjusted for the variables represented in the model. The odds ratio and associated standard error were then computed from these values. Although this method of computing the effect size is less precise than the results from a logistic regression model, using this approximation allowed us to include these studies in the meta‐analysis. This only affected two data sets in the final analyses. Although these OLS models produced somewhat smaller effect sizes, sensitivity analyses showed that the results were roughly the same whether these studies were included or excluded.

Effect sizes were coded for each reported analysis with one exception. We did not code effect sizes from a regression model that included both a main and an interaction effect involving race unless centered versions of the relevant variables were used. The main effects in models with an interaction term are not interpretable in unbalanced designs without centering. We coded the direction of all effects such that positive effects (odds ratios higher than 1 or positive logged odds ratios) indicated that Blacks or minorities had a greater odds of arrest and a negative effect (odds ratios less than 1 or negative logged odds ratios) indicated that Blacks or minorities had a lower odds of arrest.

To ensure reliability of coding, all studies were double‐coded and differences between the two coders were resolved by the first author with consultation from the second author. We also assessed the reliability of the coded items to identify potentially problematic items. Overall, inter‐rater reliabilities were good: 59 of 66 substantive coding items (i.e., those not related to tracking identifiers, etc.) had reliabilities greater than 80 percent, with 42 items with reliabilities greater than 90 percent. Only two variables had reliabilities less than 70 percent. These were the number of independent variables in the model and the variable related to the method of data collection. The former variable suffered from an unclear decision rule regarding how to count dummy coded variables. Recall, however, that all differences between coders were resolved.

STATISTICAL APPROACH

This meta‐analysis used the inverse‐variance weight method of meta‐analysis (see Fleiss and Berlin, 2009; Hedges and Olkin, 1985; Lipsey and Wilson, 2001a; Shadish and Haddock, 1994). This approach provides greater weight to effect sizes from larger studies, although the actual weight is a function of the standard error of the effect. Thus, more precise estimates are provided great weight in determining the mean effect size. The analyses were performed on the logged odds ratios, but the final results were converted back into odds ratios for ease of interpretation. We assumed a random‐effects model a priori. That is, we assumed that the true underlying population race/arrest effect estimated by the studies varied because of genuine study differences. In addition to examining the overall mean effects, we directly explored variability in effects across studies through moderator analyses. Both analog‐to‐the‐analysis‐of‐variance (ANOVA) and meta‐analytic regression methods were used (see Lipsey and Wilson, 2001a). All analyses were performed using Stata macros (StataCorp, College Station, TX) written by David B. Wilson, available at http://mason.gmu.edu/~dwilsonb/ma.html.

An important statistical issue in meta‐analysis is handling the statistical dependencies of multiple effect sizes generated from a single sample. The typical study in this area reported the results from multiple statistical models. Because these multiple effect sizes are based on the same data set, they are statistically dependent and cannot be treated as independent estimates of the relationship between race and arrest. To complicate matters even more, multiple publications report on the results based on a common data set. We restricted any given analysis of effect sizes to a single effect size per data set unless the effect sizes were based on completely independent subsets of the data. For example, Wordes and Bynum (1995) reported all analyses separately for juvenile felonies, juvenile misdemeanors, and juvenile status offenses. Because these represent independent data sets, one effect size from each was allowed in any given analysis. Thus, the data include 23 studies with 27 independent effect sizes for any given analysis.

To ensure that our results were not being overly influenced by the specific effect size selected from a given data set, we ran several analyses with different selection rules. These analyses included calculating the average effect size within each data set, selecting the smallest effect size within each data set, selecting the largest effect size within each data set, and selecting the effect size that met explicit criteria that we believe represent the best effect size for that data set. The selection criteria for the best effect size within a data set gave preference to 1) the effect sizes based on a logistic regression model rather than on an OLS or probit regression model; 2) the standard error that was reported directly and not imputed from other information, such as sample size; 3) the effect sizes that were based on the full sample rather than on a subset or the effect size with the largest sample size; 4) the models where the operationalization of the dependent variable was clearly arrest versus no arrest rather than on some other less severe alternative sanction (e.g., Crawford, 2000; Patnoe, 1990); 5) the race variable that represented Black versus White rather on than minority versus nonminority or White versus non‐White; 6) the statistical model that included demeanor as an independent variable; 7) the statistical model that included officer characteristics; and 8) the effect size that was based on a model with the largest number of independent variables. If multiple effect sizes remained after applying these selection criteria, the median effect size was chosen. This only occurred for Lundman (1996).

RESULTS

The search strategy resulted in the identification of 40 documents, 23 unique data sets, and 27 independent effects. Although we did not limit the dates of publication or of data collection, the earliest eligible study was published in 1977 and most studies were written or published in the 1980s through the 2000s. More than half (22 of 40) were published in 2000 through 2007. Three data sets represent data collected in the 1960s or 1970s. Two data sets began data collection in 1966 and 1968 (Black and Reiss's collection in Boston, Washington, and Chicago [Friedrich, 1977] and the 1958 Philadelphia birth cohort [Sealock and Simpson, 1998], respectively). The Midwest City study (Lundman, 1994, 1996) began data collection in 1970, and the police services study (Smith and Klein, 1984; Smith, Visher, and Davidson, 1984) began data collection in 1977. The limited number of eligible pre‐1980 studies limits our ability to examine changes in the relationship between race and arrest occurring during or immediately after the Civil Rights Movement.³3 Early studies, published in the 1960s to 1970s, tended to use descriptive statistics rather than regression‐based or multivariate models, and therefore, as many as ten studies published in the 1960s and 1970s could not be included in our sample.

Thirty‐five percent of these data sets draw on observations of police by observers as they conduct business, and an additional 35 percent rely on police recording their experiences when they stop a motorist or pedestrian, which often are logged to allow assessments about racial profiling. The remaining studies include documentation from routine police records: incident reports or referrals of juveniles (26 percent), and interviews or surveys of citizens who have been involved in police encounters as either a victim or a suspect (4 percent). Table 1 displays the characteristics of the 23 data sets included in our synthesis.

Table 1. Descriptive Information on the 23 Data Sets Included in This Meta‐Analysis

Data Set	Collection Dates	Location	Studies	Full Sample	Source	Suspect Age
Albert Reiss Police—Citizen Encounters	1966	Boston, MA; Washington, DC; Chicago, IL	Friederich (1977)	3,955	Observation	Both
1958 Philadelphia Birth Cohort	1968–1975	Philadelphia, PA	Sealock and Simpson (1968)	27,160	Police contact data	Juvenile
Sykes and Clark Midwest City Police–Citizen Encounters	1970–1971	Midwest City	Lundman (1994 and 1996)	2,000	Observation	Both
Police Services Study (PSS)	1977	St. Louis, MO; Rochester, NY; Tampa and St. Petersburg, FL	Engel, Sobol, and Worden (2000); Smith (1984, 1986, and 1987); Smith and Klein (1984); Smith and Visher (1981); Smith, Visher, and Davidson (1984);Visher (1983); Worden and Shepard (1996)	5,688	Observation	Both
Pima County Police Referrals	1984	Pima County, AZ	Patnoe (1990)	6,126	Police referrals	Juvenile
Metro Dade Police Department Dispute Study	1985–1986	Metro Dade County, FL	Klinger (1996)	245	Observation	Both
Role of Alcohol Use in Breaches of Peace and Crime	1986–1987	Chicago, IL	Freeman (1992)	2,365	Observation	Both
Richmond Bureau of Police Police–Citizen Encounters	1992	Richmond, VA	Mastrofski, Worden, and Snipes (1995)	1,630	Observation	Both
Incident Data Police Agencies in Los Angeles County	1995–1998	Los Angeles County, CA	Viehe (2003)	1,040	Incident reports	Both
Project on Policing Neighborhoods (POPN)	1996–1997	Indianapolis, IN St. Petersburg, FL	Engel (2000); Myers (2002); Spano (2002 and 2003)	7,443	Observation	Both
Cincinnati Police Department Community Policing Study	1997–1998	Cincinnati, OH	Brown and Frank (2005 and 2006); Novak (1999); Novak et al. (2002); Ratansi (2005)	2,671	Observation	Both
Police Records in Nine Michigan Jurisdictions	1990	9 Michigan Jurisdictions	Wordes and Bynum (1995)	2,845	Police records	Juvenile
Domestic Violence Incidents	1997–1998	City in Michigan	Robinson and Chandek (2000)	471	Supplemental incident data	Both
Midwest City Noise Complaint Incidents	1998–1999	Midwest City	Crawford (2000)	594	Incident data	Both
BJS Police‐Public Contact Survey NCVS Supplement	1999	Nationwide (U.S.)	Engel and Calnon (2004)	80,543	Citizen survey	Both
Domestic Violence Incidents	2000–2001	Niagara Falls, NY	Gibbs (2003)	1,401	Incident data	Both
Miami Dade County Police Stop Study	2001	Miami Dade County, FL	Alpert Group (2004); Smith, Makarios, and Alpert (2006)	86,232	Police contact data	Both
Wichita Stop Study	2001	Wichita, KS	Withrow (2004)	37,454	Police contact data	Both
Las Vegas Stop Study	2002	Las Vegas, NV	Doran (2007)	167,432	Police contact data	Both
Eugene Police Department Vehicle Stop Study	2002–2003	Eugene, OR	Gumbhir (2005)	36,011	Police contact data	Both
Pennsylvania State Police Stop Study	2002–2003	Pennsylvania	Engel et al. (2004)	327,120	Police contact data	Both
Pennsylvania State Police Stop Study	2003–2004	Pennsylvania	Engel et al. (2005)	315,705	Police contact data	Both
Los Angeles Stop Study	2003–2004	Los Angeles, CA	Alpert et al. (2006)	814,492	Police contact data	Both

We coded 146 effect sizes across the 23 data sets and 40 documents. Twenty‐six of these effect sizes were based on a race variable that contrasted a non–African American minority group with Caucasians. These were not used in the analyses that follow. Fifty‐four effect sizes were based on race defined as White/Black, 34 as White/non‐White, 29 as non‐Black/Black, and 3 as Nonminority/Minority. Across all 23 samples, the percentage of non‐Black minorities was low. Consequently, this sample of studies compares mostly African Americans to White Americans. Among the independent set of effect sizes used in Table 2, 19 were based on race defined as White/Black, 5 as White/non‐White, 2 as non‐Black/Black, and 1 as Nonminority/Minority.

Table 2. Meta‐analysis Results of Odds‐Ratio for the Effects of Race on Arrest

Analysis	Mean	95% C.I.		z	p	Q	k
		Lower	Upper
Average	1.45	1.28	1.64	5.76	.0000	57.030*	27
Smallest	1.32	1.16	1.50	4.34	.0000	43.580*	27
Largest	1.52	1.32	1.74	5.95	.0000	48.190*	27
Best	1.38	1.24	1.53	5.82	.0000	39.270*	27
Data Source					.4000	.7100
Researcher	1.39	1.09	1.75	2.68	.0074		10
Officer	1.36	1.20	1.55	4.71	.0000		16
Victim Survey	1.79	.96	3.32	1.83	.0670		1
Model type					.1430	3.8800
Logistic	1.39	1.27	1.52	7.14	.0000		23
Probit	1.63	1.13	2.37	2.58	.0098		2
OLS	1.15	.95	1.40	1.41	.1591		2
Sample Age					.7760	.0800
Juvenile	1.42	1.13	1.79	2.96	.0030		5
Mixed	1.37	1.20	1.55	4.84	.0000		22
Amount of Evidence in Model					.7100	.1370
Yes	1.35	1.15	1.58	3.77	.0002		10
No	1.41	1.20	1.65	4.28	.0000		17
Crime Type					.6400	.2200
No crime type distinction	1.43	1.21	1.69	4.25	.0000		16
Traffic related	1.32	1.10	1.59	3.02	.0025		7
Domestic	1.27	.88	1.84	1.28	.2008		3
Noise	1.78	.91	3.48	1.69	.0918		1
Crime During Encounter in Model					.9840	.0004
Yes	1.38	1.13	1.68	3.12	.0019		9
No	1.38	1.21	1.58	4.73	.0000		18
Demeanor in Model					.3500	.8900
Yes	1.49	1.22	1.82	3.93	.0001		12
No	1.33	1.17	1.52	4.29	.0000		15
Seriousness of Offense in Model					.6100	.2600
Yes	1.34	1.14	1.57	3.59	.0003		16
No	1.42	1.22	1.65	4.52	.0000		11
Suspect on Drugs or Alcohol in Model					.5600	.3400
Yes	1.49	1.12	2.00	2.69	.0071		7
No	1.36	1.21	1.53	5.10	.0000		20
Suspect Prior Record in Model					.2400	1.3600
Yes	1.52	1.25	1.84	4.19	.0000		9
No	1.32	1.16	1.50	4.17	.0000		18
Victim Requested Arrest in Model					.9480	.0040
Yes	1.37	1.09	1.72	2.68	.0074		6
No	1.38	1.22	1.57	5.01	.0000		21
Witness in Model					.9100	.0140
Yes	1.39	1.17	1.65	3.71	.0002		9
No	1.37	1.19	1.58	4.28	.0000		18
Year of Data Collection (Median Year)					.9710	.0014
1966–1975	1.33	.99	1.76	1.93	.0533		5
1976–1985	1.25	.89	1.73	1.30	.1926		3
1986–1995	1.66	1.19	2.34	2.94	.0033		5
1996–2004	1.38	1.19	1.58	4.47	.0000		14

• NOTE: All analyses based on a random‐effects model with the random effects variance component estimated via the method‐of‐moments estimator.
• ABBREVIATIONS: C. I. = confidence interval; OLS = ordinary least squares.
• *p < = .05

OVERALL RESULTS

Table 2 presents the results of the meta‐analysis of the average, smallest, largest, and best effect size within a data set. The sample size for these analyses is 27 due to two studies contributing three independent effect sizes to each aggregate analysis. Wordes and Bynum (1995) separately analyzed juvenile felony, misdemeanor, and status offenses. From the Midwest City data set, Lundman (1994) separately analyzed a subset of juvenile encounters and public drunkenness (nontraffic) encounters and Lundman (1996) analyzed drunk driving encounters. Each of the four methods of selecting one effect size per independent data set produces an overall mean effect size that was statistically significant under a random‐effects model, which is more conservative than a fixed‐effects model. The range in the mean odds ratio across selection criteria was 1.32 for the smallest effect size per data set and 1.52 for the largest effect size per data set. Using the average and best (see the Method section) effect size within each data set produced very similar results (1.45 and 1.38, respectively). The 95 percent confidence interval ranged from a low of 1.16 for the analysis using the smallest effect size per data set to a high of 1.74 for the analysis using the largest effect size per data set. These results suggest that minorities have a higher odds of arrest than nonminorities in a police/citizen encounter. The different selection models show that our results are robust to which effect size is selected from each data set.

Figures 1–4 present these data graphically. These forest plots show the observed effect size and 95 percent confidence interval for the effect selected for each data set. Examining Figure 1 shows that only 4 of the 27 odds ratios were in the negative direction with Blacks or minorities having smaller odds of arrest. We would expect a few negative effects just by chance. What is of greater interest is the pattern of results across studies. Across all four figures, we observe a clear pattern of evidence consistent with the hypothesis that minorities and Blacks have higher odds of arrest. Even when we took the most conservative effect size produced across all available analyses from each data set, we still observed a statistically significant increase in the odds of arrest for minorities and Blacks relative to Whites.

Figure 1

Forest Plot of the Average Effect Size Within Each Data Set

Figure 2

Forest Plot of the Smallest Effect Size Within Each Data Set

Figure 3

Forest Plot of the Largest Effect Size Within Each Data Set

Figure 4

Forest Plot of the Best Effect Size Within Each Data Set

By conventional standards, this is a small effect. To interpret the magnitude of the effect in meaningful terms, we converted the overall mean odds ratio of 1.38 (model based on the best effect size within each data set) into the probability of arrest for minorities and Blacks relative to Whites. This conversion is based on an assumed arrest rate of 20 percent for Whites, roughly the average across all samples. Using this value as the benchmark, an odds ratio of 1.38 is equivalent to an arrest probability of .26 for minorities and Blacks and of .20 for Whites. We believe this difference is large enough to be of practical concern.

Although the overall mean results suggest that minorities and Black suspects have a higher probability of arrest than White suspects, the results were heterogeneous across studies. The Q values shown in Table 2 are tests of effect size homogeneity, that is, variability in excess of what would be expected from sampling error alone. Across all four models, Q was significant, indicating statistically significant heterogeneity across data sets. Thus, some studies observed larger effects of race on arrest than others. The moderator analyses provided in the subsequent discussion explored potential explanations of this excess variability based on substantive and methodological study features.

MODERATOR ANALYSES

We performed two types of moderator analyses: theoretically based and methodologically based explanations of why some models may produce larger or smaller effects. These analyses are based on a single effect size per independent data set using the effect size selected as the best.

We first examine methodological study characteristics. Studies differed in the method of observation. Ten independent effect sizes were based on data obtained from field researchers observing police/citizen interactions; 16 were from data generated by police officers, most of which are data routinely collected as part of vehicle or pedestrian stops; some are data collected through incident reports; one data set was generated from juvenile referral records; and one was based on a victim survey. The test of the difference between these means (a Q test similar to a one‐way F) was not statistically significant (Q= .71, df= 2, p= .400). The effects are not significantly different across studies based on who collected the data. Arguably the first of these (researcher as observer) is the most credible of these research designs, and this design produced a result that was only slightly smaller than the overall result. Thus, the source of data does not seem to account for meaningful differences across studies.

Another methodological difference across the studies was the type of statistical analysis or modeling method. Most effect sizes (23 of 27) are based on the results from logistic regression models. Two of these 27 effect sizes were based on probit regression models, and two were based on OLS‐type models. The mean for the probit models was higher, and the mean for the OLS models was lower relative to the logistic models, although not by enough to account for a significant amount of variability in effect sizes (Q= 3.88, df= 2, p= .143).

Studies restricted to juveniles observed slightly higher effects, albeit not statistically significant (Q= .08, df= 1, p= .776). It is worth noting that three of the five juvenile data sets are from a single study (Wordes and Bynum, 1995), reducing the strength of any inference that might be drawn from this difference.

In addition to examining potential methodological explanations for our findings, we also examined several theoretical explanations, both legal and extralegal. Scholars have distinguished between disparity and discrimination. The logic is that disparate experiences by race when explained away by legal factors present during the encounter are not discriminatory (Skogan and Frydl, 2004: 124). Therefore, if a difference in the odds of arrest by race dissipates when accounting for mandatory arrest policies, the seriousness of the offense, amount of evidence against the suspect, or the presence of a victim supportive of arrest, we would conclude that the uncontrolled difference is not discriminatory. Rather, it demonstrates disparate legally relevant circumstances by race. Other potentially legally relevant factors include the presence of witnesses on the scene who may be able to provide eyewitness testimony; prior record of the suspect (particularly if known by the officer on the scene at the time of the encounter), as an indicator that the criminal justice system may need to take more focused action to break a pattern of behavior; the suspect being under the influence of drugs or alcohol as an indicator of his/her potential immediate threat to him/herself or others; or the observance or discovery of additional criminal acts during the course of an officer–citizen interaction (e.g., when a citizen assaults an officer).

We anticipated that the race/arrest relationship would be smaller for domestic violence crimes because of the proliferation of mandatory arrest policies for domestic violence during the last three decades. That is, since the proliferation of misdemeanor mandatory arrest laws for domestic violence that began in the 1980s, officer discretion has been substantially reduced for domestic violence cases. This should manifest itself as a smaller relationship between race and arrest when examining domestic violence cases, given the restrictions these laws place on police discretion.⁴4 Sherman (1992) reported that by 1989, 84 percent of urban police agencies had instituted preferred or mandatory arrest policies for domestic violence. By 1991, 15 states and the District of Columbia had mandatory arrest statutes for domestic violence.
Table 2 shows only limited support for this hypothesis.⁵5 Because there are only three studies of domestic violence cases, the statistical power of this moderator analysis is poor.
The mean odds ratio for the three studies that only examined domestic cases (data collected in 1995–1998, 1997–1998, and 2000–2001) was the lowest of the four categories of crime type measured (1.27) and not statistically significant. For studies limited to domestic violence incidents, we did not find strong evidence showing that race influences arrest decisions. However, among studies where we expected fewer limits on officer discretion—traffic encounters and studies that included all crime types—we did find support that race influences arrest decisions. However, a test of the difference between the mean effect size for the domestic violence studies and the other crime types was not statistically significant (Q= .22, df= 1, p= .64).

Other legal considerations showed no effects. Controlling for the seriousness of the offense did not meaningfully reduce the race/arrest relationship (Q= .26, df= 1, p= .61). Controlling for whether the victim requested an arrest also was unrelated to the size of the effect (Q= .004, df= 1, p= .95). Additionally, controlling for the presence of witnesses (Q= .014, df= 1, p= .91), the quantity of evidence at the scene (Q= .137, df= 1, p= .71), the suspect being under the influence of drugs or alcohol (Q= .34, df= 1, p= .56), and the prior record of the suspect (Q= 1.36, df= 1, p= .24) each did not significantly reduce the race/arrest relationship. Furthermore, we found no significant difference in the mean effect size of studies that controlled for the occurrence or discovery of a new criminal offense during the course of the police/citizen encounter relative to those that did not (Q= .0004, df= 1, p= .98).

Because of the failure of each of these potentially legally relevant factors to explain away the relationship between race and arrest, we also explored whether including greater numbers of legally relevant controls in a study may reduce the size of the race effect. We constructed a variable that measured the degree to which a model addressed legally relevant factors. It ranged from zero to three, with zero reflecting no legally relevant controls and three reflecting a model that controlled for seriousness of offense, amount of evidence at the scene, and whether the victim requested an arrest.⁶6 In constructing the scale, studies that included a measure of victim injury but did not also include a separate measure of the seriousness of the offense were given a point on the legal relevance scale to reflect the seriousness of the offense. We deemed it reasonable to assume that officers perceived a greater level of seriousness when the victim was injured than when he/she was not. Also, studies that controlled for the presence of witnesses, but did not also control for the amount of evidence at the scene, were given a point on the legal relevance scale to reflect amount of evidence because the presence of witnesses provides police with more evidence (witness testimony) than the absence of witnesses on scene.
These three factors were described as legally relevant by Skogan and Frydl (2004). The results of a meta‐analytic, random‐effects regression analysis showed that as the numbers of legally relevant variables in the model increased, the effect size decreased by a very small, nonsignificant amount (B=–.0326, p= .08). The difference between the high and low levels of this scale are trivial, and the race effect remains even at the high end. Controlling for legally relevant variables does not noticeably reduce or explain the relationship between suspect race and arrest. We note Klinger's (1996: 335) claim that no extant study had comprehensively controlled for the illegality of a suspect's behavior, including such behavior in the presence of the police. We accept that there is always room for improvement in the measurement of such variables, but we would also expect that if this consideration really bears on the race–arrest relationship, it would have surfaced in the variation we observed across the studies in the extent to which legal factors were taken into account. As it did not, we submit that there are solid reasons to have confidence in the validity of the race effect illuminated by the meta‐analysis.

Prior research has found that a major extralegal influence on the arrest decision is the suspect's demeanor, although there is also some evidence that the scope of this effect declines or disappears when disrespectful behavior that is illegal (e.g., physical resistance) is distinguished from that which is not (e.g., using insulting language) (Klinger, 1994). Regardless, researchers have suggested that officers making a decision to arrest may not be reacting to a suspect's race but to his or her disrespectful behavior, with Black suspects showing a greater tendency to exhibit disrespectful behaviors during encounters (Skogan and Frydl, 2004: 124). If demeanor accounts for the race/arrest relationship, then the effect size for race from models that control for demeanor should be smaller than from models that do not. However, statistical models that adjusted for demeanor produced effect sizes roughly comparable with models that did not (Q= .89, df= 1, p= .35). Studies that controlled for demeanor and studies that did not control for demeanor both showed an effect of race on arrest.

A final moderator analysis examined whether the race/arrest relationship has changed over time. We anticipated that societal and legal changes over time may reduce the inclination for police to be influenced by race in making the arrest decision. Most of these data sets were conducted only during a 1‐year (11 of 27) or 2‐year period (14 of 27), but two studies spanned more than 2 years (see Table 1). To examine the relationship between year and effect size, we used the median year of data collection. Contrary to expectation, we did not observe any decrease in effect size over time. A random‐effects, meta‐analytic regression model showed a near‐zero coefficient between mid‐year of data collection and logged odds ratio (β= .0001, p= .97). Table 2 shows the mean odds ratio for mid‐year categories (1966–1975, 1976–1985, 1986–1995, and 1996–2004) and shows no clear pattern over time. Unfortunately, this is a weak test of the race and arrest relationship given that so few studies were based on data collected before 1980.

A complication with moderator analyses is that study features often are confounded, making it difficult to interpret observed differences across studies properly (see Lipsey and Wilson, 2001b). We performed a sensitivity analysis to help ensure that meaningful moderator effects were not being masked by study feature confounding. Using only those studies for which the effect size was based on a logistic or probit regression model and excluding studies that examined domestic violence or noise complaints (k= 20), we performed a meta‐analytic regression analysis examining the relationship between the inclusion in the statistical model of the following independent variables and the effect size: suspect demeanor, seriousness of offense, and victim requested an arrest. None of the regression coefficients were statistically significant. Furthermore, the observed direction of effect was counter to expectation for suspect demeanor and victim requested an arrest. Thus, incorporating into the statistical models measures of demeanor, seriousness of offense, and whether victims requested arrest did not significantly influence the observed relationship between suspect race and the decision to arrest.

PUBLICATION‐SELECTION BIAS

Publication‐selection bias is a serious concern when conducting a meta‐analysis (Rothstein, Sutton, and Borenstein, 2005). To mitigate the possible effects of this potential bias, we explicitly sought to include unpublished studies in our meta‐analysis. Using the distribution of best effect size, we compared the results of the 11 effect sizes from unpublished documents (dissertations and government reports) with the 16 effect sizes from published documents (journal articles and book chapters). The difference showed only a slight bias toward more positive results in published manuscripts (1.44 vs. 1.23, respectively, Q= 3.26, df= 1, p= .07). A Duvall and Tweedie trim‐and‐fill analysis suggested that four small or negative results might be unobserved and produced an adjusted mean odds ratio of 1.35, slightly less than the mean for our analysis based on the smallest effect within each data set. This mean was still statistically significant under the trim‐and‐fill analysis. Given the great deal of effort it takes to collect the data used in the studies included in this meta‐analysis, it seems unlikely that many such data sets have been created that have not become part of the discoverable literature. However, it is possible that the statistical models that are reported are those that tend to produce significant results. Our analysis based on the smallest effect size within each data set provides some assurance that even if this were the case, the overall effect would still be positive and statistically significant. Publication‐selection bias may have affected the overall results, but this evidence suggests that it is likely that the magnitude of any such bias is modest and would not change the overall conclusions of this synthesis.

CONCLUSION

By focusing solely on arrest and doing so systematically and quantitatively, we help to fill the gap in knowledge reported by the National Research Council and by the American Sociological Association. From our findings, we can conclude more definitively than prior nonsystematic reviews that racial minority suspects experience a higher probability of arrest than do Whites. We report with confidence that the results are not mixed. Race matters. Our finding is consistent with what most of the American public perceives, and that finding holds over time, research site, across data collection methods, and across publication types. Furthermore, controlling for demeanor, offense severity, presence of witnesses, quantity of evidence at the scene, the occurrence or discovery of a new criminal offense during the encounter, the suspect being under the influence of drugs or alcohol, prior record of the suspect, or requests to arrest by victims does not significantly reduce the strength of the relationship between suspect race and arrest. It remains possible that unaccounted for legal aspects of the police–citizen encounter could explain the race–arrest relationship, reducing the observed effect even to zero. However, it seems unlikely that improvements in the measurement of legally relevant factors will meaningfully change the strength of the observed relationship, given the robustness of the evidence examined in this meta‐analysis to existing attempts at accounting for these factors. Thus, the most credible conclusion based on the evidence examined is that race does affect the likelihood of an arrest.

Statistically, the effect is clearly significant, but interpreting the effect size requires broader contextual considerations. On average, the chances of a minority suspect being arrested were found to be 30 percent greater than a White suspect (rising from the sample average of .20 for Whites to .26 for minorities). This finding is larger than most race effects found in a meta‐analysis of court sentencing, with the exception of non‐federal drug offenses and federal property offenses (Mitchell, 2005). Several of the overall mean effects in the court sentencing area were substantially smaller, such as an odds ratio of 1.09 for nonfederal courts’ sentencing of property offenses and 1.08 federal courts’ sentencing of drug offenses. Because of the interconnectedness of decisions made in the criminal justice system, even small racial differences that occur at many points in the criminal justice process will compound and produce profound effects further along in the system (Kempf‐Leonard, 2007). Arrest occurs at a relatively early stage in the process. Holding all other situational factors constant, the arrest risk on average is 30 percent higher for racial minorities than for Whites; thus, it would not be surprising to observe that even more modest effects during the court processing stages would still produce the level of impressive differences that are observed at the punishment end of the system.⁷7 In 2008, Black males were incarcerated in the United States at more than six times the rate of White males (3,161 per 100,000 versus 487 per 100,000, respectively [Sabol, West, and Cooper, 2009]).

The extant research does not demonstrate the causes of this racial disparity, nor does it point to a clear policy response for dealing with it. What it does establish is that where there is smoke, there is indeed fire regarding racial disparity in the arrest practices of American police. This certainly shows that future efforts to delineate the legal and ethical implications of racially differentiated policing will be based on a solid empirical foundation. And it should stimulate criminologists to develop empirical research that moves beyond just testing for race effects to research that accounts for variation in them. What follows are some suggestions to further that line of inquiry.

Even with the striking clarity of findings in our sample, we have noted substantial heterogeneity in the strength of effects across studies. Our moderator analysis did not reveal obvious substantive sources of this variation, but we speculate on some that might be incorporated into future research on the effects of suspect race on police discretion. Notable in this body of studies was the rarity with which researchers explicitly took into account the ecology of police decision making. The theoretical importance of the police environment for explaining police practices was articulated four decades ago (Reiss and Bordua, 1967), but it remains an underdeveloped aspect of empirical research on police discretion (Klinger, 2004). Following the argument that the exercise of officer discretion is not immune to external influences, we anticipate that more theoretically useful and more empirically powerful accounts of the effects of race will take four kinds of contexts into account. First is the character of the organizational environment in which individual police officers operate—the policies, structures, and cultural features that might influence the strength of the race–arrest relationship. Second is the decision context that clarifies what is at stake in the arrest decision—explicitly who or what is being served by the arrest. Third is the socioeconomic and cultural context of the police–citizen encounter, usually represented spatially as the “neighborhood” in which it occurs. Fourth is the larger context of political power or lack of power that a given minority group may have in the police jurisdiction.

By and large, studies of police arrest discretion that we reviewed paid little attention to the particulars of the organizational environment in which police officers were making the arrest decision. How actively the department attended to unequal treatment of citizens according to their race (through training and disciplinary practices, for example) would be logical starting points. Broader structural features, such as the degree of professionalism and bureaucracy, also have been hypothesized to affect race–arrest patterns (Wilson, 1968). An exceptional study in this regard explored the implications of the police department's professionalization and bureaucratization, finding no significant differences in the effects of suspect race on arrest probabilities according to type of department (Smith, 1984). Given that formal organizations exist principally to shape and control the choices and performance of their members, it seems a striking omission that so few studies seeking to assess race's impact on arrest attend to this aspect of discretion control (Klinger, 2004).

Modeling of the race–arrest linkage also will benefit from a broader consideration of what is at stake. In attempting to account for the effects of race on police arrest discretion, researchers have mostly focused on the question of which race suffers the punishment, whereas only a few have attended to the question of who benefits. We have reason to expect that, at least under some circumstances, police decisions about how to exercise their authority are driven at least as much by who benefits as who suffers (Black, 1976, 1989). For example, Smith (1987) examined a narrowly focused group of police–citizen encounters involving violence between disputants, both of whom were present. Under these circumstances, he found that, other things being equal, the estimated probability of making an arrest when the disputant dyad was non‐White was only 27 percent that of when the disputants were White,⁸8 Reported probabilities of arrest were .5850 for White disputants and .1158 for non‐White disputants (Smith, 1987: 777).
showing a propensity toward mediation rather than toward arrest for non‐White combatants. One of the strongest indicators of arrest was a preference for arrest by the perceived victim, with the probability of arrest being 65 percent greater when the victim requested formal action (Smith, 1987: 777). Alternatively, in some police–suspect encounters, no victim is present to cue a reaction from the officer or to lobby for an outcome, and in many of these cases, the victim may be unspecified and left largely to the officer to construct (e.g., traffic stops and other officer‐initiated interventions). Under these circumstances, often dealing with observed violations, suspicious circumstances, and public disorder, we might anticipate that any racial biases held by officers would be more likely to be influenced by the suspect's race. Our point is that modeling the context of how officers determine who benefits explicitly in the analysis will help to account for variation in race effects within and across studies.

A third contextual consideration is the character of the immediate spatial environment in which the arrest decision occurs. The impact of neighborhood context on police decision making is of growing interest among scholars. Klinger (1997) presented an ecological framework for explaining the “vigor” by which police exert their authority by examining the socioeconomic and crime features of the beat in which the police–citizen encounter occurs. He argued that the standards of tolerable conduct and the thresholds for police intervention are respectively lowered and raised in areas with large amounts of socioeconomic disadvantage and violent crime. A few studies have taken neighborhood‐level effects into account in predicting various forms of police discretion and have found with some consistency that disadvantaged and high‐crime areas are more likely to experience punitive, enforcement‐oriented policing, with all other things being equal (Skogan and Frydl, 2004: 189). It is possible that in our sample of studies, some variation in race effects could be attributable to variation in the character of the neighborhood samples across studies. Unfortunately, research reports did not provide sufficient detail in neighborhood sample composition to conduct more than a crude moderator analysis that showed no significant effect for studies that oversampled disadvantaged neighborhoods relative to studies that did not.

More to our point, future research should concentrate on the effects, if any, of neighborhood characteristics on the size and direction of race effects. A recent analysis of the arrest experiences of 12–18‐year‐olds found that neighborhood context factors do account for some arrest differences across racial/ethnic groups but that substantial individual differences across race/ethnic groups still persist (Kirk, 2008), with minorities generally at greater risk. Interestingly, different minority groups (Mexican vs. Black) often show consistent patterns of race effect but sometimes do not, depending on the particular neighborhood characteristic under consideration.

A fourth, and perhaps even more compelling, policy‐sensitive explanation for race effect differences could be the degree of empowerment that minorities enjoy in the communities under study. The disciplines of political science and public administration have established an extensive literature on political empowerment and representative bureaucracy that proves useful here. This research shows with fair consistency that in communities and states where racial minorities have achieved certain levels of power in elective office (e.g., having a minority‐race mayor or legislative body dominated by minorities), minority citizens tend to receive more favorable treatment from the local government (Bratton, 2002; Mladenka, 1989; Saltzstein, 1989). Where minorities have strong representation as employees in government bureaucracy, there too they are more likely to experience favorable results (Hindera, 1993; Hindera and Young, 1998; Lim, 2006; Selden, 1997). Some go even further, arguing that the effect can be disaggregated to the individual encounter level (Theobald and Haider‐Markel, 2008). They argue that when persons of the same race serve in both the officer and citizen roles, more favorable outcomes are likely—at least as perceived by the citizen. Although the evidence in terms of effects at this level is mixed when the consequences are measured in terms of police behavior, greater consistency is found when results are measured in terms of citizens’perceptions (Theobald and Haider‐Markel, 2008).

The dynamics of political empowerment and bureaucratic representation may vary (Lim, 2006). In a given police–citizen encounter, minority police officers might be expected to treat suspects of their race or ethnicity more favorably because of their ability to identify and empathize with minority citizens. But the likelihood of that dynamic may well depend on the larger organizational context in which the minority officer operates. The presence of a large number of minority officers in the department may present a very different cultural context for favorable police action than one in which minority officers comprise only a small proportion of the police employees (Sklansky, 2006). The presence of a large number of minority officers in a police department might alter the cultural pressures about acceptable practice within the organization for all officers, both minority and White, having an indirect but more pervasive effect (Sklansky, 2006). Furthermore, having politically powerful minority persons serving in executive (e.g., mayor, city manager, or police chief) and legislative positions of authority (not to mention prosecutors, judges, and defense attorneys) may signal to the police that racial disparities unfavorable to minorities are both undesired and more likely to produce negative consequences for officers who practice policing of that sort.⁹9 Using aggregate data on 125 cities, Parker, Stults, and Rice (2005) found no significant relationship between the city having a Black mayor and the arrest rates for Black or White citizens.
Finally, attempts to assess the consequences of the political empowerment of minority citizens should consider not only who holds positions of power, but what actions they have taken that might influence the nature and extent to which race enters into the calculus of street‐level decision making.¹⁰10 For example, one study found unexpectedly that White suspects in one city were more likely to experience disrespect than Black suspects (Mastrofski, Reisig, and McCluskey, 2002). The authors attributed this to the actions of a new Black police chief who had a long history in the department of vigorously opposing racist policing and from the very outset of his administration took considerable effort to convince his officers that he intended to punish relentlessly officers who practiced it. The authors speculated that this may have caused officers to reduce sharply their disrespectful behavior toward minority suspects in the community, while leaving largely unaffected past practices in the treatment of Whites.

The studies we reviewed provided no insight into the degree to which minority citizens were politically empowered in the communities or represented in police organizations studied, although there have been some ex post facto attempts to reconcile differences in race effects across studies in these terms (Lundman, 1996: 319). It would be highly valuable for future studies of race effects on policing to take these considerations into account explicitly, a practice that would facilitate cross‐study comparisons, and that we expect would go a long way toward accounting for variability in the effects of race in both cross‐sectional and longitudinal terms. Such studies also would provide more insight into the value of policies, such as affirmative action hiring, which have increased minority representation in police forces of cities throughout the United States (Sklansky, 2006). Finally, we note that we have examined only one of many discretionary choices police make, choices that are susceptible to disparate racial impact: stop and search, use of force, procedural justice, assistance to victims—to name a few. As the body of available quantitative studies on these topics grows, so also does the opportunity to use meta‐analysis to make sense of what otherwise might seem as confusing or contradictory findings.

Tammy Rinehart Kochel is an assistant professor of criminology and criminal justice at Southern Illinois University, Carbondale. Her research interests include policing reform, strategies and organization, correlates and outcomes of institutional legitimacy, and neighborhood collective efficacy. She has published in Policing, Journal of Crime and Justice, Criminal Justice Policy Review, and International Review of Victimology. Recent research projects have been sponsored by the Ministry of National Security for Trinidad and Tobago and by the U.S. Department of Justice Office of Community Oriented Policing Services.

David B. Wilson is a professor and chair of the Department of Criminology, Law and Society at George Mason University. His research interests are the effectiveness of offender rehabilitation and crime prevention efforts, program evaluation methodology, meta‐analysis, and systematic reviews. He is an associate editor of the Journal of Experimental Criminology and editor of Campbell Collaboration Systematic Reviews published by the Crime and Justice Group.

Stephen D. Mastrofski is a university professor and director of the Center for Justice Leadership and Management in the Department of Criminology, Law and Society at George Mason University. His research interests include police discretion, police organizations and their reform, and systematic field observation methods in criminology. In 2000 he received the O.W. Wilson Award from the Academy of Criminal Justice Sciences for education, research, and service on policing. In 2008 he and his coauthors received the Law and Society Association's article prize for their article on Compstat. In 2010 he was elected a Fellow of the American Society of Criminology