The Effect of Court-Ordered Hiring Quotas on the ...jmccrary/mccrary2007.pdfThe Effect of...

The Effect of Court-Ordered Hiring Quotas on the Compositionand Quality of Police

By JUSTIN MCCRARY*

Arguably the most aggressive affirmative action program ever implemented in theUnited States was a series of court-ordered racial hiring quotas imposed onmunicipal police departments. My best estimate of the effect of court-orderedaffirmative action on work-force composition is a 14-percentage-point gain in thefraction African American among newly hired officers. Evidence on police perfor-mance is mixed. Despite substantial black-white test score differences on policedepartment entrance examinations, city crime rates appear unaffected by litigation.However, litigation lowers slightly both arrests per crime and the fraction blackamong serious arrestees. (JEL H76, J15, J78, K31)

Arguably the most aggressive affirmative ac-tion program ever implemented in the UnitedStates was a series of court-ordered racial hiringquotas imposed on municipal police depart-ments. These quotas arose out of a wave of classaction employment discrimination lawsuits filedin the federal district courts beginning in 1969.Court-ordered affirmative action in this sectorhas been both aggressive and persistent: Bostonand Cambridge, Massachusetts, remain to thisday subject to hiring quotas first imposed in1973, and Philadelphia, Pennsylvania, andMontgomery, Alabama, labored under similar

affirmative action remedies into the 1990s.1 Bythe standards of current affirmative action pro-posals, these measures are remarkably interven-tionist. In this paper, I address two key issues.First, did these affirmative action policies suc-ceed in raising the fraction of police officerswho were African American, or did they merelyratify preexisting trends? Second, what effectdid court-ordered changes in hiring policieshave on stated police department objectives, inparticular crime reduction?

Evaluating the magnitude of these impacts ischallenging. First, suitable data—in particular,historical information on black employmentshare and information on the pattern of litiga-tion—are not publicly available. I use a newpanel dataset on 314 large American cities from1960 to the present. To measure employment ofAfrican American police, I combine confiden-tial information from the Equal EmploymentOpportunity Commission (EEOC) with pub-lished data from historical sources. To measurethe onset of litigation against departments inthis sample, I use published court decisions.Information on black employment share andlitigation is combined with information on citydemographics from the Census Bureau and on

* Ford School of Public Policy and Department of Eco-nomics, University of Michigan, 735 S. State, Ann Arbor, MI48109 (e-mail: [email protected]). I thank three anony-mous referees for thoughtful reports and useful suggestions.For detailed comments on earlier drafts, I thank David Card,Ken Chay, John DiNardo, Guido Imbens, Jonathan Leonard,Heather Royer, and Emmanuel Saez. For comments that im-proved the paper, I thank Joe Altonji, Liz Cascio, David Lee,Nicole Maestas, Jesse Rothstein, Eric Verhoogen, Till vonWachter, and seminar participants at UC Berkeley and NBERLabor Studies. I also thank Patrick Ronald Edwards, ClariceBryce, Kevin Hudson, and Betty Turner of the Research andTechnical Information Branch of the EEOC for their role inrecovering much of the historical data used in this project.Adam Kingsley of the City of Chicago Department of Lawprovided data on the Chicago Police Department; JoanneVanatta of the FBI Criminal Justice Information Services Di-vision, data on the pre-1975 UCR; and Neldra Zeigler of theNYPD, data on entrance exam scores. For research assistance,I thank Stephanie Watt, Jeff Butler, Andrea Cann, AmyHawkins, Katie Ikard, Alma Vega, and Shayesteh Zarrabi. Anyerrors are my own.

1 Castro v. Beecher, 365 F. Supp. 655, 660–662 (D.Mass. 1973), and personal communication with Toni Wolf-man; Freeman v. City of Philadelphia, 751 F. Supp. 509(E.D. Penn. 1990); and U.S. v. City of Montgomery, 957 F.Supp. 1241 (M.D. Ala. 1997).

318

police staffing, arrests, and crimes from theFederal Bureau of Investigation (FBI).

The second evaluation challenge regardsselection—litigated departments are not nec-essarily directly comparable with unlitigateddepartments. Both private litigants and the De-partment of Justice (DOJ) targeted those em-ployers with the largest number of potentialblack jobs at stake—big departments with dis-parities between departmental black employ-ment share and the city fraction AfricanAmerican. To circumvent this selection prob-lem, I take advantage of the staggered timing oflitigation against police departments and focuson event study estimates of litigation’s impact,as in Louis S. Jacobson, Robert J. LaLonde, andDaniel G. Sullivan (1993). Administrative de-lays in the processing of complaints by theEEOC, as well as capacity constraints facing theEmployment Section of the Civil Rights Di-vision of the DOJ in the early years of en-forcement, led to substantial and plausiblyexogenous variation in the timing of litigationagainst police departments.2

A third evaluation challenge is that unliti-gated departments may have responded to thegeneral phenomenon of litigation by increasingblack employment share, confounding the directeffect of litigation with the effect of the threat oflitigation. I address this question empirically bycomparing the evolution of work-place demo-graphics in unlitigated departments before andafter the litigation of other departments in thesame federal district.

The empirical analysis points to several im-portant conclusions. First, despite substantialinitial differences, by 1999 litigated and unliti-gated cities employed black workers at similarrates, conditional on city demographics. Sec-ond, initial differences, per se, are not importantenough to account for the gains accruing to

litigated cities. Third, event study analysesindicate that the convergence in employmentpatterns between litigated and unlitigated de-partments occurred entirely in the years fol-lowing litigation. My best estimate of the25-year gain in black employment share is onthe order of 10 percentage points. Using first-order Markov approximations outlined in Sec-tion II, I estimate that this corresponds to a14-percentage-point increase in the hiring frac-tion African American following litigation.Fourth, there is little evidence of litigationthreat effects. Unlitigated departments in fed-eral districts with litigated departments are nomore likely to hire African Americans afterlitigation than they were before. Fifth and fi-nally, there is mixed evidence of differences inpolice performance between litigated and unliti-gated departments, but the bulk of the evidencesuggests little to no effect. City crime rates,arrest rates, and the racial composition of arrest-ees all appear to be at best modestly related tolitigation. Court-ordered affirmative action inmunicipal police departments may thus be anexample of an affirmative action program with asubstantial impact on work-force compositionbut a generally minor impact on productivity.

These findings relate primarily to two litera-tures. The first of these is concerned with theimpact of federal government labor market in-terventions on black economic progress (Rich-ard B. Freeman 1973; Orley Ashenfelter andJames J. Heckman 1976; Charles Brown 1984;Jonathan S. Leonard 1990; John J. Donohue andHeckman 1991). An important topic for thisliterature has been assessing the impact of thefederal contractor program, which obliges firmsthat do business with the federal government toengage in affirmative action (e.g., Leonard1984b). The literature’s consensus is that thefederal contractor program has had somewhatmodest effects on black economic outcomes(James P. Smith and Finis Welch 1989; Leonard1990). A few articles have sought to estimatethe impact of court-ordered affirmative actionon black economic outcomes (e.g., Andrea H.Beller 1978), but as noted by Donohue andHeckman (1991), no consensus has emerged onthe evidence, and interpretation is difficult dueto endogeneity problems. Phyllis A. Wallace(1976) gives a detailed analysis of the impact ofcourt-ordered affirmative action for AT&T.Using industry-level data on class action em-

2 For example, in 1977 the National Association of Gov-ernment Employees (NAGE) filed charges with the EEOCalleging discrimination by San Antonio against MexicanAmericans. The EEOC referred the case to the DOJ in 1980.The DOJ acknowledged in 1989 that it had lost the paper-work for the case, and the trial did not proceed until 1989(NAGE v. City Public Service Board of San Antonio, 40 F.3d 698, 702). For introductory material on the variety ofdelays encountered by plaintiffs seeking to file an employ-ment discrimination case, see for example Barbara Linde-mann Schlei and Paul Grossman (1976), David L. Rose(1989), and Frank J. Landy (2005).

319VOL. 97 NO. 1 MCCRARY: COURT-ORDERED HIRING QUOTAS

ployment discrimination litigation, black em-ployment, and productivity, Leonard (1984a)estimates small productivity impacts of court-ordered affirmative action.

The second literature to which this papercontributes is the economics of crime, partic-ularly the subliterature focused on police per-formance. The role of race in policing is along-standing subject of general interest inthe American urban context (William Kephart1957; National Advisory Commission on CivilDisorders 1968; W. Marvin Dulaney 1996). Re-cently, the topic has attracted the attention ofeconomists (e.g., John Knowles, Nicola Persico,and Petra Todd 2001; Kate L. Antonovics andBrian Knight 2004). John R. Lott (2000) pre-sents an analysis related to that here, focusingon the impact of affirmative action on city crimerates. Donohue and Steven D. Levitt (2001) takea broader view and estimate the general impactof police department racial composition on theracial composition of arrestees using panel data.

The remainder of the paper is organized asfollows. Section I describes the aspect of policehiring procedures that were the subject of liti-gation and discusses the legal rationale for ju-dicial intervention into hiring practices. InSection II, a unique administrative dataset isused to examine the racial composition of newhires for Chicago, Illinois, before and after lit-igation, and Markov approximations are used toconvert estimated impacts on black employ-ment share into impacts on black hiring share.Sections III and IV present evidence on theimpact of litigation on black employment shareand police performance, respectively, whileSection V concludes. Appendix I describes thedata used, and Appendix II provides details onthe Markov approximations used.

I. Background

For much of the twentieth century, municipalpolice departments have been required by stateand local civil service regulations to hire in rankorder by police department entrance examina-tion.3 Although there are other aspects to police

hiring, such as a criminal record check, it isgenerally agreed that the primary stumblingblock to hiring is performance on the entranceexamination. Thus, police department selectionmethods are essentially the employment equiv-alent of the William G. Bowen and Derek Bok(1998, 31–42) model of race-neutral collegeadmissions.

Many police department entrance exams, es-pecially in the prelitigation years, were aptitudetests akin to the verbal SAT. Detroit adminis-tered a three-hour I.Q. test (the “Otis”) to ap-plicants in the 1960s and into the 1970s.4 Overthe same period, the District of Columbia useda civil service examination designed for posi-tions in the federal bureaucracy. This test com-prised 80 questions on vocabulary, readingcomprehension, and analogies. These questionsclearly measure aptitude, but are not related inany obvious way to police work.5 For example,two questions are:

“[13.] The purpose of trademarks is to(A) show that a tax has been paid (B)distinguish the brand of goods manufac-tured (C) show that a patent has beengranted (D) indicate that goods are un-adulterated (E) distinguish home fromforeign products.

[14.] CRISP means most nearly (A)broken (B) frosty (C) brittle (D) burnt (E)dry.”

The use of aptitude tests in police hiring isongoing, largely because civil service regula-tions require that some sort of test be used, andbecause departments and judges agree that qual-ity police work requires some degree of apti-tude. For example, the Memphis PoliceDepartment continues to use an I.Q. test to

3 Rank order hiring is mitigated to a certain extent by theso-called “Rule of Two” or the “Rule of Three,” and by therequirement that those with sufficiently high scores passadditional hurdles, such as a background investigation orphysical examination. Myrdal (1944, 539, fn. b) notes the

prevalence of civil service systems in the North and Southalready by the 1940s, although he does not mention entranceexaminations specifically. George Greisinger, Jeffrey S.Slovak, and Joseph J. Molkup (1979, 26) note that “[b]y theearly 20th century civil service systems based on the meritprinciple were established in many state and local govern-ments. Since then, they have grown in numbers at a veryrapid pace, so that by the contemporary era they havebecome almost ubiquitous.”

4 Baker v. City of Detroit, 483 F. Supp. 930, 948–952(E.D. Mich., 1979).

5 Davis v. Washington, 512 F. 2d 956, 975 (D.C. Cir.,1975). The entire test is reproduced in the Appendix to themajority decision.

320 THE AMERICAN ECONOMIC REVIEW MARCH 2007

screen its applicants.6 Generally, police depart-ments being litigated were not able to demon-strate statistically a relationship betweenperformance on the job and entrance examina-tion scores. In a particularly careful study of theNew York City Police Department entrance ex-amination, Bernard Cohen and Jan M. Chaiken(1972, xiv) conclude that “the entrance exami-nation for patrolmen does not appear to predictany aspect of job performance measured in thisstudy, other than the ability to pass later civilservice examinations for promotion.”

African American applicants, historically aswell as today, do not perform as well as whiteapplicants on police department entrance exami-nations.7 For example, in the Detroit, Michigan,exams of 1967 to 1971, the African Americanpass rate was 44.3 percent, and the white pass ratewas 80.7 percent. The Memphis, Tennessee, testsadministered from 1981 to 1989 had a similarimpact on black applicants. The pass rate forwhites was a high 96.7 percent, but that for Afri-can Americans was 69.2 percent.

This disparity in black-white performancecontinued into “second-generation” police de-partment entrance examinations that made clearattempts to improve the bearing of the questionson police work. For example, approximately 20to 25 percent of the questions on the 1970 NewYork City Police Department (NYCPD) en-trance examination asked applicants to supplythe appropriate behavioral response to a hypo-thetical situation supposed to typify the day-to-day experiences of a police officer.8 Yet thisexam excluded African Americans at almost thesame rate as the Memphis exam: 81.9 percent ofwhites passed the 1970 exam, while 54.5 per-cent of African Americans did.9

Despite the best attempts of police depart-ments to design tests that would satisfy the newlegal regime in which they found themselves,the 1970s federal judiciary frequently foundthat use of these exams in police hiring wasdiscriminatory, sometimes even after depart-ments had spent many years attempting to de-vise a valid test. In reaching these findings, thecourts relied on the notion of disparate impact,a legal theory developed by jurists in the mid- tolate-1960s (Schlei and Grossman 1976). Thecentral tenet of disparate impact theory is thatan employment practice with no apparent racialmotivation may nonetheless be interpreted astentative evidence of discrimination if the em-ployment practice disproportionately harms agroup protected under civil rights law, such asAfrican Americans or women. If a protectedclass group member may demonstrate that anemployment practice leads to a disparate impactfor his or her group, then the employer isobliged to demonstrate that the selection mech-anism is predictive of job performance. TheSupreme Court sanctioned this theory in 1971in Griggs v. Duke Power Company: “Thetouchstone is business necessity. If an employ-ment practice which operates to exclude Ne-groes cannot be shown to be related to jobperformance, the practice is prohibited.”10

Disparate impact theory was largely devel-oped in cases against private sector defendantsalleging violations of Title VII of the 1964 CivilRights Act (CRA) and the equal protectionclause of the Fourteenth Amendment. Althoughcoverage of Title VII would not be extended topublic employers until the 1972 amendments,disparate impact theory arguments were put tothe courts between 1969 and 1971 alleging vi-olations of the Fourteenth Amendment and theReconstruction Civil Rights Acts of 1866 and1871 (Michael Reiss 1977). The courts werereceptive to these arguments, and in many casesrequired police departments to hire according toquotas by race, foreshadowing the remedies thatwould result from Title VII litigation broughtafter 1972. That the Reconstruction Civil Rights

6 Ashton v. City of Memphis, 49 F. Supp. 2d 1051, 1072(W.D. Tenn., 1999).

7 Compare with the general evidence on the black-whitetest score gap in Christopher Jencks and Meredith Phillips(1998). To my knowledge, William Kephart (1957, 35) isthe first to relate black underrepresentation on police forcesto low average test scores. Speaking of Philadelphia, henotes “under-representation seems to stem not from dis-criminatory personnel practices, but from the failure of largenumbers of Negroes to qualify on the civil service exami-nations.”

8 Guardian’s Association of the New York City PoliceDepartment v. Civil Service Commission of the City of NewYork, 431 F. Supp. 526, 543 (S.D. New York, 1977).

9 The Rand Corporation, in summarizing its study of the1968 and 1970 NYCPD entrance examinations, concluded

that it was “confident that the patterns observed for [the1970 exam] are not unique to that exam but are most likelytypical of the patterns for all recent civil service patrolmen’sexams.” Quoted in 431 F. Supp. 526, 540.

10 401 U.S. 424, 431 (1971).


Acts lay dormant for nearly a century before thecourts began to enforce them underscores theidea that the federal judiciary may have playedat least as important a role as Congress in thefederal antidiscrimination effort. Historiansstudying the evolution of civil rights policyassign the courts a critical role, focusing on thecourts’ expansive interpretation of the 1964CRA (e.g., Hugh Davis Graham 1990).

Cases alleging discrimination in police de-partments could be brought either by privatelitigants or, after 1972, by the DOJ. DOJinvolvement was important not only becauseof the high caliber of the government attor-neys, but also because it placed in jeopardythe revenue sharing funds distributed to po-lice departments by the federal government.11

Nonetheless, while the DOJ was undoubtedlyan active player in the litigation, private liti-gants brought fully 80 percent of the classaction suits studied here. A common pattern isfor the local black police union to have broughtsuit on behalf of members and potential mem-bers. Unlike the education cases studied byJonathan Guryan (2004) and Sarah Reber(2003), the National Association for the Ad-vancement of Colored People (NAACP) andother national civil rights organizations wereessentially uninvolved in litigation against po-lice departments.12

Following a judicial determination that a po-lice department entrance examination dispar-ately impacted African Americans, there wastypically a one- to three-year lag before anyquota would be imposed. During this period, thejudge would order the city to devise a test thateither did not exhibit disparate impact or wasjob-related. If hiring was to proceed in the in-terim, temporary hiring quotas were sometimesput in place until the new exam was adminis-

tered. If the department proved unable to devisea test that satisfied the court, the court oftenimposed an ongoing quota.13,14

II. Litigation and the Integration of the ChicagoPolice Department

Before turning to the main empirical analysis,I first consider the case of Chicago, Illinois. Thehiring and promotion practices of the ChicagoPolice Department (CPD) have been subjectedto litigation continuously from 1970 to 2000,and the remedies from this litigation includeaggressive hiring quotas and the withholding ofsome $100 million in revenue sharing funds.15 Idemonstrate the impact of litigation on CPDhiring patterns using a unique administrativedataset provided to me by the City of Chicago.The dataset contains records on the race andhiring and termination dates of a large sample ofpolice officers dating to the early 1960s.16

These data are superior to those collected by theEEOC, because they can be used to calculatethe fraction African American among new hiresfor many years prior and subsequent to litiga-tion. In contrast, EEOC data contain only infor-mation on the overall black employment share.

The CPD was first required to justify its em-ployment practices to a federal district courtjudge in 1970, after the Afro-American Pa-trolmen’s League initiated suit. At that time,Chicago employed a substantial number ofblack officers, especially relative to other major

11 Crime Control Act of 1976, §122(c)(2)(E), 90 Stat.2418 (1976). Based on my reading of police departmentcases, I believe this penalty, while used as a threat inconjunction with the Syracuse litigation, was used onlyagainst the Chicago Police Department.

12 The NAACP participated in the Boston hiring litiga-tion, the Pittsburgh, Pennsylvania, hiring litigation, and theDetroit promotion litigation; brought a series of suits againstsmaller departments (several municipalities in New Jersey,including Harrison; East Haven, Connecticut; Corinth, Mis-sissippi; and Evergreen, Alabama); and was the lead orga-nization behind the Alabama state troopers case (NAACP v.Allen, 340 F. Supp. 703 (M.D. Ala., 1972)).

13 Ongoing quotas either expired by their terms (e.g., ajudge might require that 50 percent of new hires be AfricanAmerican until 40 percent of the force was African Amer-ican) or remained in operation until judicially withdrawn.

14 The departments under study lost approximately 80percent of the cases brought against them from 1969 to1980, and interim or ongoing quotas were imposed in over90 percent of the cases they lost in these same years. Casesbrought in the 1980s and 1990s were less numerous, tar-geted small police departments, and were less likely toresult in affirmative action requirements. Police depart-ments litigated after 1980 won approximately 65 percent ofthe cases brought against them, and only 43 percent of thecases departments lost resulted in a hiring quota. Thesefigures are measured with a high degree of noise due todifficulties with unpublished decisions (see Appendix I),which motivates the paper’s focus on the reduced formeffect of litigation.

15 See, for example, the discussion of the litigation inU.S. v. City of Chicago, 411 F. Supp. 218, 225–245 (N.D.Ill. 1976).

16 See Appendix I for details.


cities.17 Figure 1 gives the black employmentand black hiring share in the CPD from 1960 to1997. The black employment share in the 1960sand early 1970s was roughly 18 percent. Forcomparison, 23 percent of Chicago residents in1960 were African Americans, and 33 percentwere African Americans in 1970. The DOJjoined the suit against the CPD in 1973, and in1974 an interim hiring quota on behalf of Afri-can Americans was imposed, followed by anongoing hiring quota in 1976. Figure 1 demon-strates that there was substantial compliancewith the court’s orders. In the years 1971 to1973, the hiring share was roughly 10 percent.By 1975 it had climbed to 40 percent, andthroughout the 1975–1990 period, the hiringshare averaged 32 percent. Although the demo-graphic composition of new hires to the CPDresponded dramatically to the hiring quota, thedemographic composition of the police forcechanged only slowly, because of low quit rates.Using these data, I estimate an annual quit rateof 3.6 percent, which is within the range of theavailable estimates for other police departmentsin varying time periods.18 Considering the lowpolice department quit rates, we should not ex-pect court orders to lead to dramatic changes inblack employment share. Instead, we wouldexpect these to lead to a trend break in blackemployment share after the filing date oflitigation.

For cities other than Chicago, high-qualitydata on black hiring share are not available.However, I have collected data on black em-ployment share for a large sample of policedepartments. If quit rates are stable over time, asthey appear to be for police departments, it ispossible to approximate the gain in the hiringshare African American using data on the gainin the black employment share; I next describea simple methodology for doing so. Appendix IIdevelops the approximation

(1) Ft ! !Ft ! k " "1 # !#f!,

where Ft is the black employment share in pe-riod t, f! is the average hiring fraction AfricanAmerican during the period t ! k to t, and ! is

a convex factor to be defined. The approxima-tion is an identity if the quit rates for black andall officers are equal, and if hiring rates, thehiring fraction African American, and quit ratesare constant over the period t ! k to t. Thoseconditions imply that ! $ ((1 ! q!)/(1 % $!))k,where q! denotes the quit rate, and $! denotes theyear-over-year police force growth rate.19 Sup-pose the approximation is valid and contem-plate a restated version of (1):

(2) f! # Ft ! k !1

1 # !"Ft # Ft ! k #.

A simple way to think of (2) is as follows.Suppose that in period t ! k a police departmentis in a steady state, such that the hiring fractionAfrican American is equal to the overall policedepartment black employment share (i.e.,ft!k $ Ft!k, where ft!k is the hiring fractionAfrican American in period t ! k). Litigationoccurs, and an affirmative action program isimposed on the police department, resulting inan increase in the hiring share African Ameri-can. After k periods, the police departmentblack employment share is observed to haveincreased by Ft ! Ft!k. Then, with an estimateof the quit rate q! and the year-over-year growthrate $! , we compute ! $ ((1 ! q!)/(1 % $!))k andinflate the gain Ft ! Ft!k by the factor 1/(1 !!); the approximation in (2) justifies an inter-pretation of this quantity as the gain in thehiring share African American over the initialhiring share African American (i.e., f! ! ft!k).

To make these ideas concrete, consider Fig-ure 1, where it is clear that the average hiringfraction African American from 1974 to 1997far exceeded the historical hiring fraction Afri-can American. Using the 0.088 gain in the blackemployment share from 1974 to 1997, we canuse the approximation in (2) to estimate the gainin the hiring fraction African American. Using a3.6-percent quit rate and the observed annualgrowth rate of the police force of 0.06 percent,the estimated gain in the hiring fraction AfricanAmerican is 0.088/(1 ! ((1 ! 0.036)/(1 %0.0006))1997!1974) ! 0.153. Unlike the dataanalyzed in the main body of the paper, the

17 The CPD employed substantial numbers of black of-ficers even as of 1940 (Arthur Raper 1940).

18 See Appendix II. Quit rates appear to vary somewherebetween 3 and 5 percent.

19 As discussed in Appendix II, the approximation re-mains accurate if quit rates and hiring rates are small andsatisfy a law of large numbers and if black quit rates areapproximately equal to overall quit rates.


FIGURE 1. THE CHICAGO EXPERIENCE


administrative data from Chicago allow us tocalculate the hiring share African American di-rectly. Thus, we may assess the quality of theapproximation by simply calculating the hiringshare African American over the period 1974 to1997 and comparing it to the prediction basedon the approximation in (2). The actual gain inthe hiring share African American in these datais 0.161, which is roughly comparable to theprediction of 0.153 given above.

There is some discrepancy, however. Theprediction based on the approximation in (2)will be understated (overstated) if the quit rate isoverstated (understated). For example, a quitrate of 3.3 percent rationalizes the predictionand the actual, and a quit rate of 4 percent leadsto a prediction of 0.144, which is too small. Asshown in Appendix II, the prediction will alsobe understated if the black quit rate exceeds theoverall quit rate. This is an important consider-ation. There is a large body of evidence indi-cating that in departments subject to federalcourt oversight on account of litigation, whiteofficers harassed black officers with the appar-ent goal of inducing a high black quit rate.20 Ifthe black quit rate exceeds the overall quit rate,then the true gain in the black hiring share is atleast as large as implied by (2). On the otherhand, it is possible that the black quit rate is lessthan the overall quit rate, given the clear incen-tives created by public sector wage schedulesand the private sector black-white wage gap.21

On balance, the approximation probably yieldspredictions that are in the right ballpark, butcare should be exercised in interpretation.

Did the federal court’s aggressive interven-tion into CPD hiring practices affect police per-

formance measures? Panel B of Figure 1 showsthe size of the work force (solid line, solidsquares), the scope of crime in Chicago (solidline, open triangles), and two measures of ar-rests per crime (dotted lines). The figure showsthat police per capita has remained nearly con-stant over the entire period. Crime per capitadoes appear to increase slightly in the same yearas the quota imposition. It is also apparent,however, that crime is a volatile series—theincrease does not appear unusual, compared toother year-over-year changes in the series. Ar-rests per crime are measured by (a) the numberof index crimes cleared, normalized by thenumber of crimes (solid squares), and (b) thenumber of index crime arrests, normalized bythe number of crimes (open triangles). The firstof these measures is on the same data file as thenumber of crimes. The second of these mea-sures is available in a greater number of years,but is taken from two separate data files andhence is presumably measured with more errorthan the first. The two series are both rathernoisy, and it is not immediately clear whetherthere are any productivity effects.

Panel C of Figure 1 gives the fraction AfricanAmerican for arrests for all index crime arrestsand for all arrests. The city fraction black isprovided for comparison. These series are noisyas well and fail to reveal any clear patternaround either the litigation filing date or the dateof quota imposition.

Perhaps the strongest conclusion implied bythe police performance measures in panels Band C is that detecting productivity effects willrequire a statistically powerful approach, suchas that pursued below. The focus on a largenumber of cities should help to eliminate muchof the noise in the available performance mea-sures through averaging, enabling us to detectthe productivity effects of affirmative action.

III. Litigation and the Composition of Police

In this section of the paper, I first considercomparisons between litigated and unlitigateddepartments over time. Second, I consider esti-mators that take advantage of the timing oflitigation. Third, I discuss threats to the internalvalidity of the estimates presented in the secondsubsection. Finally, I present a direct test oflitigation threat effects (cf. Sherwin Rosen1969), or the hypothesized tendency of unliti-

20 For example, “in a welcoming speech given to at leastone academy class, a Captain reminded the cadets that whilethe Division of Police was forced to accept blacks andfemales, they did not have to keep them” (Police Officersfor Equal Rights v. City of Columbus, 644 F. Supp. 393, 401(S.D. Ohio, 1985)). For further examples, see for instanceU.S. v. City of Buffalo, 457 F. Supp. 612, 632 (W.D. NewYork, 1978); Ways v. City of Lincoln, 871 F. 2d 750, 753(8th Cir., 1989); Busby v. City of Orlando, 931 F. 2d 764,781 (11th Cir., 1991); and Phillips v. Heydt, 197 F. Supp. 2d207 (E.D. Pa., 2002).

21 See William J. Carrington, Kristin McCue, andBrooks Pierce (1996) and Joseph Altonji and RebeccaBlank (1999). An analogous context is blacks in the mili-tary, where in 1978 the black quit rate was lower than theoverall quit rate; see Baker v. City of Detroit, 483 F. Supp.930, fn. 58 (D.C. Mich., 1979).


gated departments to integrate in order to avoidlitigation.

A. Contrasting the Litigated and theUnlitigated

Litigated cities are far from a representativesample of the 314 cities under study.22 Table 1presents means and standard deviations of keyvariables by litigation status for two samples: the“full sample” (all 314 cities) and the “long sam-ple” (120 cities with information on black em-ployment share dating to 1960). For cities in thefull sample, estimates on black employment shareare not necessarily available before 1969. All sta-tistics in the table, and throughout the paper, areweighted by 1970 city population unless other-wise noted.

The table indicates that although only 30percent of all cities are ever litigated, residentsof litigated cities comprise nearly 58 percent ofthe 60 million residents in 1960, and 50 percentof the 75 million residents in 1999. While gen-erally much of the federal antidiscriminationeffort was focused on the South, that pattern isnot true of the cases studied here. Among liti-gated cities, 23 percent of the population livesin the South, and 11 percent in the Deep South;among unlitigated cities, these statistics are 33and 13 percent, respectively. Figure 2 is a mapof the contiguous United States, with unlitigatedcities represented as circles in the top panel andlitigated cities represented as stars in the bottompanel. It is clear from the map that litigation wasnot confined to any particular region.

In substantive terms, the most important dif-ference between litigated and unlitigated citiesregards the city fraction African American.23

Throughout the sample period, 1960 to 1999,

litigated cities had larger African Americanpopulations than did unlitigated cities. In 1960,12 percent of the residents of unlitigated citieswere African Americans, but 18 percent of theresidents of litigated cities were. This 6-pointdifference grew to a 10-point difference in 1970and an 11-point difference in 1980 before sta-bilizing.

Police department black employment sharedid not initially keep up with these sharp gains.In 1970, litigated departments employed only 7percent black officers. Between 1970 and 1980,black employment and population shares in-creased by equal amounts, and between 1980and 1990, and again between 1990 and 1999,black employment share grew by more than thecity fraction African American. Consequently,from 1970 to 1999, the difference betweenblack employment and population shares, or therepresentation gap, in litigated departments con-verged from !0.17 to !0.09. In contrast, therepresentation gap among unlitigated depart-ments remained roughly constant at !0.10 in1970 and 1980, and !0.09 in 1990 and 1999.

To economize on space, the estimates in Ta-ble 1 are given only at ten-year intervals. For allyears for which estimates are available, Figure 3gives the time series graph of the representationgap separately for litigated and unlitigated de-partments. The top panel gives estimates for thefull sample, beginning with 1969. Several as-pects of the graph are of note. First, unlitigateddepartments experience almost no convergenceuntil around 1985. From 1985 to 1993 there isconvergence of about 0.015, followed by aslight widening in the mid- to late-1990s. Sec-ond, starting some time near 1977, litigateddepartments’ representation gap converges tothat of unlitigated departments. The conver-gence is very nearly linear in time startingaround 1980.

Taking the numbers in Table 1 and Figure 3 atface value, a simple difference-in-differencesestimate of the long-run impact of litigation onthe representation gap is about 0.07. This esti-mate could understate or overstate the impact oflitigation. For example, the estimate may be toosmall if there are important threat effects tolitigation, since then part of unlitigated depart-ments’ convergence in representation gap wouldreflect the effect of litigation. The estimatemay also be too small if there is heterogeneityin the timing of litigation, since late-litigated

22 See Appendix I for details on the selection of cities forstudy.

23 Litigated departments are more likely to have experi-enced a riot. Of the cities analyzed here, 300 (90 litigatedcities) were also analyzed by Seymour Spilerman (1970). Iestimate that experiencing a riot in any of the years 1961 to1968 increases the probability of litigation by roughly 40percentage points (separate regressions for each year) anddecreases the year of litigation by 3 years. Unlike theestimates on the impact of litigation below, these correla-tions reflect differences in city size; for example, controllingadditionally for the log of city population leads to insignif-icant results for all but 2 of the 16 coefficients described. Inthese regressions, the 2 significant coefficients suggest thata riot in 1962 or 1965 delayed litigation by just over 4 years.


TABLE 1—MEANS AND STANDARD DEVIATIONS OF KEY VARIABLES BY LITIGATION STATUS

Year

Full sample Long sample

All(n $ 314)

Litigated(n $ 92)

Unlitigated(n $ 222) Difference

All(n $ 120)

Litigated(n $ 43)

Unlitigated(n $ 77) Difference

A. City characteristicsFraction South1 NA 0.28 0.23 0.33 !0.10 0.36 0.28 0.52 !0.24

[0.45] [0.42] [0.47] (0.05) [0.48] [0.45] [0.50] (0.09)Fraction Deep NA 0.12 0.11 0.13 !0.02 0.15 0.12 0.20 !0.09

South2 [0.32] [0.31] [0.33] (0.04) [0.35] [0.32] [0.40] (0.07)City population3 in

hundred1960 1.9 3.8 1.1 2.7 2.5 4.9 1.2 3.7

[5.3] [9.2] [1.5] (0.6) [7.9] [12.5] [2.2] (1.5)thousands 1999 2.4 4.1 1.7 2.4 3.2 5.2 2.1 3.2

[5.5] [9.6] [1.8] (0.7) [7.9] [12.5] [2.3] (1.5)Fraction African

American1960 0.16 0.18 0.12 0.07 0.19 0.19 0.17 0.02

[0.11] [0.10] [0.12] (0.01) [0.11] [0.09] [0.14] (0.02)1970 0.20 0.24 0.14 0.10 0.23 0.26 0.18 0.07

[0.13] [0.11] [0.14] (0.01) [0.13] [0.11] [0.16] (0.02)1980 0.24 0.29 0.18 0.11 0.28 0.31 0.23 0.08

[0.17] [0.14] [0.18] (0.02) [0.17] [0.13] [0.21] (0.03)1990 0.26 0.31 0.20 0.11 0.30 0.33 0.26 0.07

[0.18] [0.15] [0.20] (0.02) [0.18] [0.13] [0.24] (0.03)1999 0.28 0.32 0.22 0.11 0.31 0.33 0.28 0.05

[0.19] [0.16] [0.21] (0.02) [0.19] [0.14] [0.26] (0.04)

B. Police departmentcharacteristics

Log sworn police per100,000population

1960 5.2 5.3 5.0 0.35 5.3 5.4 5.0 0.38[0.4] [0.4] [0.3] (0.04) [0.4] [0.4] [0.4] (0.07)

1999 5.6 5.8 5.4 0.46 5.8 5.9 5.5 0.48[0.4] [0.4] [0.3] (0.04) [0.4] [0.4] [0.4] (0.07)

African Americanemployment

1960 NA NA NA NA 0.05 0.05 0.03 0.02[0.04] [0.04] [0.03] (0.01)

share 1970 0.06 0.07 0.05 0.02 0.07 0.07 0.06 0.02[0.05] [0.05] [0.06] (0.01) [0.05] [0.05] [0.05] (0.01)

1980 0.10 0.12 0.08 0.04 0.12 0.12 0.11 0.02[0.08] [0.06] [0.09] (0.01) [0.09] [0.07] [0.12] (0.02)

1990 0.15 0.18 0.11 0.07 0.17 0.19 0.15 0.03[0.12] [0.09] [0.13] (0.01) [0.12] [0.10] [0.16] (0.02)

1999 0.18 0.23 0.13 0.10 0.21 0.23 0.17 0.06[0.14] [0.12] [0.15] (0.02) [0.15] [0.11] [0.19] (0.03)

C. City crime rateLog UCR index

crimes per100,000population

1960 7.9 7.8 7.9 !0.13 7.9 7.8 8.0 !0.21[0.4] [0.4] [0.5] (0.05) [0.4] [0.3] [0.5] (0.07)

1970 8.7 8.8 8.7 0.05 8.8 8.8 8.7 0.09[0.3] [0.3] [0.4] (0.04) [0.3] [0.2] [0.4] (0.06)

1980 9.1 9.1 9.1 0.00 9.2 9.2 9.2 0.01[0.3] [0.3] [0.3] (0.03) [0.3] [0.2] [0.3] (0.05)

1990 9.3 9.3 9.2 0.05 9.3 9.3 9.3 0.01[0.3] [0.3] [0.3] (0.04) [0.3] [0.3] [0.3] (0.06)

1999 8.9 8.8 9.0 !0.11 8.8 8.7 9.0 !0.26[0.5] [0.5] [0.5] (0.05) [0.5] [0.5] [0.6] (0.10)

Notes: Standard deviations in brackets; standard errors in parentheses. Unless otherwise noted, all statistics are weighted by1970 city population.

1 South as defined by the Census Bureau.2 Deep South is defined as Alabama, Mississippi, Louisiana, Arkansas, Tennessee, Georgia, South Carolina, North

Carolina, and Virginia.3 Equally weighted.


departments do not have as many years as early-litigated departments to experience gains inblack employment. These two considerationsare addressed empirically in Sections IIID andIIIB, respectively.

On the other hand, a difference-in-differencesestimate may be too large. First, convergence inthe representation gap may simply reflect pre-existing trends. Second, litigation may be asso-ciated with broader social trends which wouldhave led to integration, even were litigationnever to have occurred—the “social change”hypothesis of Donohue and Heckman (1991,1605). I next discuss these two hypotheses insomewhat more detail.

Direct evidence regarding the preexistingtrends hypothesis may be obtained from thelong sample of cities, for which information onblack employment share predates 1969. Infor-mation on these departments is included in thefinal three columns of Table 1. The estimates inTable 1 suggest that black employment share in

1960 was neither zero, nor yet as high as itwould be in 1970. Interestingly, the 1960 to1970 increase in black employment share islarger for unlitigated cities than for litigatedcities, despite the fact that the black populationshare in unlitigated cities rose only marginallyfrom 0.17 to 0.18, while that in litigated citiesrose from 0.19 to 0.26.

The bottom panel of Figure 3 presents thetime series plot of the representation gap fordepartments in the long sample. The figure speaksagainst a preexisting trends hypothesis—the rep-resentation gap worsened substantially in litigateddepartments between 1960 and 1970. During thedecade of litigation, 1970 to 1980, the representa-tion gap slowed its negative slide. By the end ofthe decade, the gap was closing. Unlitigated de-partments, in contrast, appear to have exhibited aslowly improving representation gap from 1960 to1999, with some acceleration near 1985. In short,the figure is not consistent with an important rolefor preexisting trends. Indeed, the evidence is

FIGURE 2. MAP OF CITIES BY LITIGATION STATUS


consistent with the proposition that litigation re-versed preexisting trends, a proposition strength-ened by the evidence from event study estimatesshown below.

To be more specific regarding the type ofmechanism underlying a social change hypoth-esis, suppose that the 1970s saw both a decadeof class action lawsuits against municipal policedepartments and the beginning of a new, na-tional hiring regime in which the fraction Afri-

can American among new hires was only a littlebelow the city fraction African American.24 In

24 An alternative version of the social change hypothesisasserts that a case is more likely to be filed when there isgeneral political pressure to integrate the police department.Two considerations suggest that this is not an importantthreat to validity. First, the estimates below are strengthenedrather than weakened when unrestricted state-by-yearcontrols are included. Since social change is likely to be

A. Full Sample

-0.20

-0.18

-0.16

-0.14

-0.12

-0.10

-0.08

1960 1965 1970 1975 1980 1985 1990 1995Year

Rep

rese

ntat

ion

Gap

Litigated (n=92) Unlitigated (n=222)

B. Long Sample

-0.20

-0.18

-0.16

-0.14

-0.12

-0.10

-0.08

1960 1965 1970 1975 1980 1985 1990 1995Year

Rep

rese

ntat

ion

Gap

Litigated (n=43) Unlitigated (n=77)

FIGURE 3. REPRESENTATION GAP BY LITIGATION STATUS

Note: Figure gives time series of the difference between police department black employmentshare and city fraction African American (“representation gap”), separately by litigationstatus, for two samples. See text for details.


such a state of the world, it would mechanicallybe true that cities with low representation gapswould experience the greatest gains. This con-cern is addressed empirically in Section IIIC,below, using propensity score reweighting tech-niques (Paul R. Rosenbaum and Donald B. Ru-bin 1983).

The prelitigation estimates in Table 1 and inFigure 3 suggest that litigation was targeted atbig cities in which the police department blackemployment share did not initially rise as quicklyas the city fraction African American. Economi-cally, a pattern of targeted enforcement is notablefor two reasons. First, it suggests that it mayhave been possible for a department to forestalla class action employment discrimination suitby hiring more black officers. This does notestablish that threat effects contributed to theobserved gains in black employment share inunlitigated cities. It does mean, however, thatsuch a story is not entirely implausible. Second,targeted enforcement is notable because previ-ous research has failed to find evidence of tar-geting in the federal contractor program.Leonard (1985, 372) characterizes the compli-ance review program as a “random enforcementprocess,” consistent with the earlier conclusionsof Heckman and Kenneth Wolpin (1976).25

B. The Timing of Litigation

Having considered comparisons between lit-igated and unlitigated departments, I now turnto an examination of the timing of litigation.This identification strategy is feasible only tothe extent that different departments are liti-gated at different times. Figure 4, which givesthe histogram of litigation filing dates of the

cases under study, demonstrates that there isquite a bit of heterogeneity in terms of thetiming of the cases brought against police de-partments.

Importantly, while the cross-sectional differ-ences between litigated and unlitigated cities inconfounders are often quite substantial, the dif-ferences among litigated cities litigated at dif-ferent times are more minor. Table 2 givesweighted means and standard deviations of keyvariables for five different ranges of filing dates.Regional composition varies by the timing oflitigation. However, key confounders such ascity fraction African American are quite com-parable across at least the first three filing dateranges.26

The estimates I present next correspond toleast squares estimates of %j in the regressionmodel

(3) Yi,t & 'i " (r"i#,t " "j $ a

b

%j Di,tj " ei,t ,

where Yi,t denotes the representation gap in de-partment i at time t and Di,t

j are leads and lags oflitigation filing dates, defined as

(4) Di,tj & #Di1(t ) *i " a) for j & a

Di1(t & *i " j) for a + j + bDi1(t , *i " b) for j & b

,

where Di is an indicator for whether the depart-ment was ever the defendant in a class actionemployment discrimination lawsuit allegingdiscrimination against African Americans inhiring, *i gives the filing date for litigated de-partments, and 1(A) is one if A is true but isotherwise zero.27 Because not all parameters areidentified as written, normalize %0 $ 0. Thesequence %j then admits the interpretation of the

similar for two cities in the same state, this pattern speaksagainst this specific version of a social change hypothe-sis. Second, the cases studied here only rarely involvecivil rights groups (which would be expected to beheavily involved if litigation merely reflected a broadersocial movement).

25 In comparing the enforcement process of the CRA andthe federal contractor program, it is economically interest-ing to note that judicial enforcement of the CRA is highlydecentralized, with the decision to litigate largely in thehands of individuals who feel they have been discriminatedagainst. When the CRA was initially passed, civil rightsadvocates took a dim view of decentralized enforcement,preferring an Equal Employment Opportunity Commissionwith cease-and-desist authority (Rose 1989, 1133–34).

26 The fourth filing date range is also somewhat close tothe others in terms of many characteristics, but the fifthfiling date range is more similar to the unlitigated cities thanto any of the litigated cities. In a weighted regression,however, the contrasts will be focused between the first fourfiling date ranges because of their much greater size.

27 This specification is similar in spirit to that used byJacobson, Lalonde, and Sullivan (1993). For departmentsnot having judicial interventions, the filing dates are irrele-vant so define them to be zero. It is understood that a & 0.


representation gap difference from filing date toj periods thereafter.28 I refer to the parametersequence 'i as “city effects” and to (r(i),t as“region-by-year effects.” The empirical workuses “regions” of the four census regions, the

nine census divisions, and U.S. states, and alsoconsiders the restriction that the region-by-yeareffects are cross-sectionally constant ((r(i),t $(t). Both the city effects and the region-by-yeareffects are nuisance parameters and are to beestimated by fixed effects.

It is important to note that, moving from leftto right in the event study graph, the sample ofcities driving the identification of %j is generallysubject to change. For example, only early-litigated cities can drive the estimated impactsof 20 years after litigation, since late-litigatedcities will not yet have been observed 20 yearsafter they were litigated. For this reason, I as-

28 This is a different normalization than that employedby Jacobson, Lalonde, and Sullivan (1993). Because theiroutcome variable (earnings) was available far before thefirst treatment date, the omitted category was earnings fromlong before the treatment. This strategy is not feasible here;the first treatment date (1969) is also the first year for whichdata on African American employment share in police de-partments are available for the full sample.

A. Unweighted

0

2

4

6

8

10

12

14

16

1969 1974 1979 1984 1989 1994 1999

Year

Num

ber o

f Citi

es L

itiga

ted

B. Weighted by 1970 City Population

0

1

2

3

4

5

6

7

8

9

10

1969 1974 1979 1984 1989 1994 1999

Year

Pop

ulat

ion

(in

Mill

ions

) Liti

gate

d

FIGURE 4. HISTOGRAMS OF LITIGATION FILING DATES


sign more weight to prelitigation estimates ob-tained from the long sample—for many cities,the first period of information on black employ-ment share is 1969, which coincides with theonset of litigation.

These composition bias effects may be com-pounded by irregular observation of the out-come variable, coupled with heterogeneoustreatment effects. An example will serve to il-lustrate. Because data on police department

TABLE 2—MEANS AND STANDARD DEVIATIONS OF KEY VARIABLES BY LITIGATION TIMING

Year

Litigated1969–71(n $ 19)




Litigated1981–2000(n $ 20)

A. City characteristicsFraction South NA 0.07 0.24 0.50 0.15 0.23Fraction Deep South NA 0.03 0.10 0.25 0.12 0.06

City population in hundred thousands 1960 4.4 8.5 3.1 2.7 0.9[8.8] [18.1] [2.4] [5.6] [0.5]

1999 4.0 8.5 3.7 3.4 1.2[7.0] [18.8] [3.6] [8.4] [0.5]

Fraction African American 1960 0.20 0.19 0.21 0.15 0.08[0.09] [0.09] [0.12] [0.08] [0.10]

1970 0.27 0.27 0.23 0.19 0.12[0.11] [0.11] [0.11] [0.07] [0.13]

1980 0.32 0.32 0.29 0.20 0.15[0.13] [0.13] [0.13] [0.09] [0.16]

1990 0.33 0.35 0.32 0.20 0.16[0.12] [0.13] [0.15] [0.11] [0.17]

1999 0.33 0.36 0.36 0.21 0.19[0.12] [0.14] [0.18] [0.14] [0.18]

B. Police department characteristicsLog sworn police per 100,000 population 1960 5.6 5.5 5.1 5.1 4.9

[0.2] [0.4] [0.3] [0.2] [0.4]1999 6.0 6.0 5.5 5.6 5.4

[0.3] [0.3] [0.2] [0.2] [0.4]African American employment share 1960 0.081 0.041 0.041 NA NA

[0.05] [0.01] [0.04]1970 0.12 0.06 0.05 0.04 0.04

[0.07] [0.03] [0.03] [0.02] [0.05]1980 0.16 0.12 0.10 0.09 0.05

[0.06] [0.06] [0.05] [0.03] [0.05]1990 0.21 0.19 0.19 0.15 0.08

[0.07] [0.10] [0.10] [0.05] [0.08]1999 0.26 0.25 0.24 0.16 0.09

[0.09] [0.11] [0.15] [0.06] [0.08]

C. City crime rateLog UCR index crimes per 100,000 population 1960 7.8 7.8 7.8 8.1 7.8

[0.3] [0.2] [0.2] [0.5] [0.5]1970 8.6 8.9 8.7 8.8 8.6

[0.4] [0.2] [0.2] [0.2] [0.5]1980 9.0 9.2 9.1 9.2 9.1

[0.3] [0.1] [0.3] [0.2] [0.5]1990 9.3 9.3 9.3 9.2 9.2

[0.4] [0.2] [0.4] [0.2] [0.5]1999 9.0 8.7 9.1 8.8 8.8

[0.3] [0.5] [0.3] [0.3] [0.6]

Notes: Standard deviations in brackets. Estimates presented are based on the full sample only, unless otherwise noted.1 Estimates for 1969–1971, 1972–1973, and 1974–1976 taken from the 11, 9, and 8 respective cities in the long sample

with litigation dates in the given categories. Estimates for other litigation date ranges omitted because long sample cities donot appear to be representative.


black employment share are available only atperiodic intervals29 a city such as Oakland, Cal-ifornia, which is litigated in 1969, is observed atlitigation lags 0, 4, 5, 6, 8, and so on. A citysuch as Chicago, which is litigated in 1970, isinstead observed at litigation lags !1, 3, 4, 5, 7,and so on.30 In other words, in the absence of acorrective procedure, litigation effects will beestimated over partially nonoverlapping sub-samples. Continuing the example, if Chicagoand Oakland exhibit different gains in represen-tation gap following litigation, then the eventstudy graph will oscillate about the averageeffect of the two.

A natural method to correct for the composi-tion bias is to interpolate linearly between ob-servation years, taking care to correct thestandard errors for both the induced serial cor-relation and degrees of freedom. This procedureseems particularly plausible in the present con-text, because of the low quit rate of policeofficers (see equation (1)). Practically, the pro-cedure amounts to using clustered standard er-rors at the level of city, inflated manually by adegrees-of-freedom correction to reflect thatmany observations are imputed.

The top panel of Figure 5 gives estimates offour specifications of equation (3) based on thefull sample. The thick solid line gives estimatesfrom a year effects specification, the thin dashedline gives estimates from a region-by-year ef-fects specification, the thick line with circlesgives estimates from a division-by-year speci-fication, and the dashed line with triangles givesestimates from a state-by-year specification. Al-though the four specifications give estimatesthat are rather different in their magnitude, thedirection of the estimated effects is quite simi-lar. In the first decade after litigation, blackemployment share begins to converge towardthe city fraction African American. In the sec-ond and third decades, the improvement be-comes marked.

The convex shape of the event study graph isexpected for two reasons. First, a cursory read-ing of the decisions in these cases indicates that

judges were more inclined to intervene aggres-sively into police department hiring practices inthe early years of the litigation. Litigation ef-fects at the longest lags reflect primarily theexperience of the earliest litigated. Second,there is heterogeneity in how long after thefiling date the judge would wait before impos-ing an affirmative action remedy. Some depart-ments would almost immediately be required tohire according to a quota regime, whereas otherdepartments would be given some time to de-vise a new test.

The prelitigation estimates for the full sampleare based on less reliable information than thosefor the long sample. Estimates for the longsample are given in the bottom panel of Figure5. The estimates for the long sample stronglysuggest that litigation was not preceded by rep-resentation gap convergence. In the decadeprior to litigation, the representation gap ap-pears to have been constant, or perhaps evengrowing. The postlitigation estimates are notidentical to those of the top panel, but are sim-ilar in magnitude. An important difference be-tween the estimates in the top and bottom panelsis that the four specifications in the long samplegive estimates that are more widely varyingthan those in the full sample. For example,while the region-by-year effects models aresimilar in the long and full samples, the state-by-year effects models are much larger in thelong sample. Conversely, the year effects mod-els are much smaller in the long sample than inthe full.

Because of the near linearity of the estimatesequences graphed in Figure 5, it is natural topool the individual estimates to estimate thepostlitigation and prelitigation slopes. The toppanel of Table 3 presents a variety of estimatesof the postlitigation slope for the full sample.Following the pattern of the specifications inFigure 5, Model 1 includes year effects only,Model 2 region-by-year effects, Model 3 division-by-year effects, and Model 4 state-by-year ef-fects. The first four columns are the estimatesfor all 314 cities in the full sample. For thesecities, the estimated slope is in the range 0.07 to0.12, with a standard error of about 0.02.31

29 For example, black employment share for cities in thefull sample is observed only in 1969, 1973, 1974, 1975,1977, 1980, and so on.

30 The litigation lags listed assume use only of the fullsample dataset. Estimates for the 1960s are also available forboth Oakland and Chicago, as both are in the long sample.

31 As noted above, the reported standard errors here andthroughout the paper are “clustered” at the level of the cityand inflated by a degrees of freedom correction. More


Columns 5 to 8 exclude all unlitigated citiesfrom the estimation. The litigation effects forthese models, then, are based purely off of thetiming of the litigation among the litigated. This

has some appeal: one might view with somecaution estimates that rely on using the unliti-gated as a model of the counterfactual evolutionof the representation gap among the litigated,

specifically, they are the square root of the diagonals of thematrix (nT/¥i$1

n Ti)(¥i$1n X'iXiwi)

!1(¥i$1n X'ieie'iXiwi)(¥i$1

n

X'iXiwi)!1, where T is the number of possible time-series

observations, Ti is the number of time-series observationsfor city i with (unimputed) information on black employ-ment share, wi is 1970 city population, normalized to sum to1, Xi is the T ( K matrix of time-series observations for city

i, and ei is the T-vector of fitted residuals for city i. Becausethere are a moderate to large number of cities in all speci-fications in Table 3, conventional t-ratio tests using thesestandard errors will exhibit approximately correct size re-gardless of the form of the heteroskedasticity and serialcorrelation within each city, provided that the residualsacross cities are independent. (The only potential exception

FIGURE 5. EVENT STUDY ESTIMATES OF THE IMPACT OF LITIGATION ON THE REPRESENTATION GAP


had they in fact never been litigated. Neverthe-less, caution is warranted in interpreting theseestimates. Identification leans on a and b, theendpoints of the event study graph, which areusually thought of as nuisance parameters. Tosee the role played by a and b in identification,suppose that we were to estimate the pre- andpostlitigation slopes in one step, by regressing

Yi,t on city effects, year effects, and on the pre-and postlitigation trends Wi,t

1 $ (t ! *i)Di1(a &t ) *i) % aDi1(t ) a) and Wi,t

2 $ (t !*i)Di1(*i & t ) b) % bDi1(t ) b). As a3 !*and b 3 *, Wi,t

1 % Wi,t2 3 (t ! *i)Di, which is

linearly dependent on city and year effects in asample with Di $ 1 for each city. That is, themodel is unidentified. Alternatively, a researcherthinking not of the event study graph but rather ofa trend-break model might have defined the re-gressors as Wi,t

1 $ (t ! *i)Di1(t & *i) and Wi,t2 $

(t ! *i)Di1(t ) *i). This model is similarly un-identified: Wi,t

1 % Wi,t2 $ (t ! *i)Di.

With these caveats in mind, it is interesting to

to this is the estimates in columns 21 to 24, which are basedon only the 43 litigated cities in the long sample. For theseestimates, t-ratio tests of nominal 5-percent size likely haveactual size of 10 percent.)

TABLE 3—PARAMETRIC ESTIMATES OF THE IMPACT OF LITIGATION ON THE REPRESENTATION GAP

A. Full sample estimatesAll 314 cities 92 litigated cities only

Model 1 Model 2 Model 3 Model 4 Model 1 Model 2 Model 3 Model 4

(1) (2) (3) (4) (5) (6) (7) (8)25 " Postlitigation trend 0.060 0.096 0.097 0.121 0.057 0.107 0.107 0.154

(0.031) (0.022) (0.024) (0.018) (0.066) (0.046) (0.045) (0.032)

255 cities identifying Model 4 Reweighting the unlitigated



(0.033) (0.026) (0.027) (0.018) (0.032) (0.028) (0.032) (0.022)

B. Long sample estimatesAll 120 cities 43 litigated cities only



(0.046) (0.042) (0.047) (0.025) (0.062) (0.052) (0.054) (0.035)25 " Post-pretrend difference 0.123 0.179 0.175 0.283 0.041 0.162 0.158 0.278

(0.059) (0.061) (0.060) (0.045) (0.091) (0.055) (0.056) (0.040)

86 cities identifying Model 4 Reweighting the unlitigated



(0.071) (0.056) (0.057) (0.025) (0.046) (0.041) (0.046) (0.032)25 " Post-pretrend difference 0.172 0.199 0.189 0.283 0.134 0.183 0.173 0.289

(0.107) (0.070) (0.068) (0.034) (0.069) (0.067) (0.063) (0.041)

Notes: Standard errors, clustered at the level of the city and adjusted for degrees of freedom, presented in parentheses. PanelA presents estimates of the annual gain (times 25) in representation gap in the years following litigation for four choices ofspecification, three subsets of the full sample, and two different weighting schemes. The four specifications correspond tothose from Figure 5: year effects only, region-by-year effects, division-by-year effects, and state-by-year effects. Estimatesin columns 13 to 16 are weighted by a factor that approximately equalizes in distribution the 1969 representation gap forlitigated and unlitigated cities (see text for details). Panel B is organized identically, but is based on the 120 cities in the longsample. Panel B additionally reports the difference in postlitigation and prelitigation annual gains in representation gap.


note that the estimates for the 92 litigated citiesare somewhat larger than the estimates that in-clude all 314 cities. Estimates using all 314cities can differ from those using the 92 litigatedcities only due to different estimated year ef-fects (or region-by-year effects, etc.). It is ap-parent that the year effects implicit in theestimates for the 92 litigated cities exhibitsomewhat less of an upward trend than do theyear effects from estimates for all 314 cities.

A pattern common to the estimates from boththe full and the long samples is that the richerthe set of geographical controls, the larger arethe estimated effects. For example, the state-by-year effects specification (Model 4) suggeststhat the impact of litigation is at least twice thatsuggested by the year effects specification(Model 1). This pattern is particularly pro-nounced for the long sample estimates in thebottom panel. This pattern strengthens the plau-sibility of the hypothesis that litigation is play-ing a causal role in black employment sharegains; if litigation merely reflected omitted fac-tors which were correlated with black employ-ment share gains, then we would expectinclusion of richer geographic controls to makethe effects smaller rather than larger.32

The bottom panel of Table 3 reports postliti-gation trend estimates for subsets of cities in thelong sample. These are generally similar tothose in the top panel. The estimated impact oflitigation is altered only slightly when we re-strict our attention to litigated cities and whenwe restrict our attention to cities contributing toidentification of Model 4.

Because of the greater confidence in the pre-litigation estimates for the long sample, the bot-tom panel also presents estimates of thepostlitigation trend less the prelitigation trend.In all but one case (column 21), these trend-break estimates are larger than the simplepostlitigation trend, reflecting the negative esti-mated prelitigation trends for cities in the longsample.33

C. Social Change

In Section IIIA, above, I discussed the pos-sibility that initial differences in the representa-tion gap could contribute mechanically to gainsin black employment share. To address thispossibility, I assign weights to the unlitigated,where the weights are chosen so that the re-weighted distribution of the 1969 representationgap for the unlitigated is similar to the distribu-tion for the litigated.34 The weighting functionthat achieves this balance is the ratio of theconditional to the unconditional probability oflitigation. Such reweighting schemes are com-monly used to generate counterfactual distribu-tions (John DiNardo, Nicole Fortin, andThomas Lemieux 1996) and in the programevaluation literature (e.g., Heckman et al.1998).35

Columns 13 to 16 of Table 3 give reweightedestimates of the postlitigation slope for the fourspecifications considered above. To estimate theconditional probability of litigation, I use a pro-bit model with a third-degree polynomial in the1969 representation gap; for the unconditionalprobability, I use the sample average.

The estimates from this reweighting schemesuggest that the 25-year gain in black employmentshare may be slightly smaller than previously

32 Comparisons across these specifications could in prin-ciple be invalid, since the observations identifying Model 4are a subset of the observations identifying Models 1, 2, and3. However, the estimates in columns 9 through 12 indicatethat the effects are similar when the estimates are estimatedover the same subsamples.

33 It is unclear whether the postlitigation trend is more orless appropriate than the trend-break model. For example,

the postlitigation trend would be more appropriate if thenegative prelitigation trend would have abated soon afterthe filing date of litigation. However, the postlitigation trendwould be too conservative, and the trend-break modelwould be more appropriate, if the negative prelitigationtrend would have continued in the absence of litigation.

34 One could also reweight the data to mimic the initialdistribution of the representation gap for the unlitigated orfor the average department. In this paper, I focus on ad-dressing the counterfactual evolution of the representationgap in litigated cities, had they never been litigated. From apolicy perspective, this is the right treatment effect to beestimated, since future affirmative action policies of thistype would target departments with representation gapssimilar to those of the litigated.

35 The literature’s motivation for reweighting is typicallyimplicit rather than explicit. Here is a short proof thatreweighting balances potential confounders in distribution:let X denote covariates to be balanced, D an indicator, g"an arbitrary bounded, continuous function, and assume p +E[D$X] ! (0, 1) and - + E[D] ! (0, 1). Note thatE[g(X)(1 ! D)(p/1 ! p)] $ E[g(X)p] and E[g(X)D] $E[g(X)p], implying E[g(X)$D $ 1] $ E[g(X)w$D $ 0],where w + (p/1 ! p)/(-/1 ! -). The implication followsfrom the converse to the Helly-Bray theorem (James Da-vidson 1994, Theorem 22.8).


estimated. For example, the difference betweenModel 2 in column 2 (usual weights) and Model2 in column 14 (reweighting the unlitigated toachieve balance) is about 0.023; that betweenthe estimates for Model 4 is about 0.008. Asimilar reweighting exercise is performed incolumns 29 to 32 for the long sample. Theseestimates suggest that the degree of overstate-ment in the original estimates is between 0.003and 0.012. Unreported event study estimates ofthe impact of litigation on the representationgap, weighting by the same factor, are visuallyquite similar to those presented in Figure 5.

D. Threat Effects

Testing a litigation threat effects hypothesisrequires that we specify how beliefs regardingthreats are formed. A natural approach in thisapplication is to consider whether unlitigatedcities respond to the litigation of other cities inthe same federal district.

To test this idea, I consider the unlitigated citiesin the full and long samples, matching each un-litigated city with a litigated city in the samefederal district.36 For cases where a single matchis available, I assign to the unlitigated city thelitigation date of the litigated city. In situationswith multiple matches, I assign to the unlitigatedcity the minimum of the available dates, since thatwould correspond to the first date as of which anunlitigated city would have been alerted to thepossibility of litigation in the district.37

This matching procedure generates a sampleof unlitigated cities in the full and long sampleswith neighbor-litigation dates. Some cities arelocated in a state or substate area with no liti-gated city (e.g., the cities in Rhode Island).These cities play the role of the unthreatened inthis analysis and are analogous to the unlitigatedin the analysis of the preceding subsections.

Figure 6 presents the event study of the im-pact of neighbor-litigation on the representation

gap. The results are surprisingly inconsistentwith a threat effects hypothesis. The postlitiga-tion estimates for the full sample unlitigatedcities, given in the top panel, never exceed 0.01.Among unlitigated cities in the long sample,given in the bottom panel of Figure 6, thereappears to be very little prelitigation trend.Postlitigation, the estimated effects for the longsample are negative rather than the expectedpositive for both Model 3 and Model 4.

E. Robustness

Because the dependent variable in the estima-tion above is the simple difference between blackemployment share and city fraction AfricanAmerican, the estimates presented are potentiallydriven by changes in city demographics, whichpresumably do not respond to litigation. The mostdirect way to address this concern is to reestimateequation (3) with city fraction African Americanreplacing the representation gap. In results notreported, such estimates are quite small in magni-tude (generally below 1 percentage point) andslightly positive in the postlitigation period. For allmodels, reestimating equation (3) with police de-partment black employment share as the depen-dent variable and including city fraction AfricanAmerican as a control results in a coefficient closeto one for city fraction African American. Therobustness of the results to the manner in whichwe control for city fraction African Americanmeans that the estimates of the impact of litigationreported in this paper apply equally to the repre-sentation gap and to police department black em-ployment share.

While litigation is unrelated to city fractionAfrican American, litigation is related to blackand white flight. Reestimating equation (3) withthe log of city population replacing the repre-sentation gap indicates that litigation is associ-ated with roughly a 10-percent decline in citypopulation over 25 years (results not reported).

IV. Litigation and Crime

The judges intervening in police departmenthiring practices seem to have had a clear goal ofinducing police departments to hire more blackofficers. It is not inconceivable, however, thatan unintended consequence of the effort wasmore crime. As noted in Section I, above, police

36 Some federal districts (e.g., the Northern, Middle, andSouthern Districts of Alabama) were consolidated into onestate area due to a small number of cities.

37 Note that if cities respond to the national trend oflitigation by integrating, then estimation of threat effectswill require that we impose assumptions on the secularblack employment share time path in the absence of litiga-tion. I do not consider such assumptions here and so discussthis type of threat effect no further.


department entrance examinations exhibit size-able black-white test score gaps. It is fairly clearthat police department entrance examinationstest aptitude, at least to some extent. If theseexams successfully isolate aspects of aptitudethat are relevant to the job of police officer, thenthe natural expectation is that hiring quotas withbite would lead to a downgrading in the qualityof a police force, as departments are required tohire individuals whose low test scores wouldotherwise have prevented their selection.

If, however, these exams select applicants on

the basis of aspects of aptitude that are irrelevantto police performance, then court-ordered hiringquotas would be of little consequence, except tothe extent that more black officers would be hiredas a result. It has long been argued that AfricanAmericans are more effective crime fighters thanother Americans, at least conditional on entranceexam score (e.g., National Advisory Commissionon Civil Disorders 1968, chap. 11; National Ad-visory Commission on Criminal Justice Standardsand Goals 1973, 330–33; Scott H. Decker andRussell L. Smith 1980; Donohue and Levitt

FIGURE 6. A DIRECT TEST OF THE LITIGATION THREAT EFFECT HYPOTHESIS


2001). It is possible that this effect could be strongenough to offset any aptitude differences betweenapplicant groups. Moreover, in Section IVB, Isimulate the effect of quota hiring on the test scoredistribution of new hires, as compared with thetraditional mechanism of rank-order hiring, disre-garding race. Quantitatively, quota hiring affectsentrance exam scores of new cadets only slightly.This suggests that aptitude differences are likely tobe small, and that net productivity effects willreflect primarily the crime-fighting ability of themarginally hired African American officer relativeto that of the marginally hired individual absent aquota hiring regime.

Litigation might also afford the productivity ofincumbent officers through a morale effect. Mo-rale and productivity effects would be expected tomanifest themselves at different time horizons.Shortly after litigation, nearly all officers are stillincumbents, due to the low police quit rate. Thus,productivity effects should be small and moraleeffects should predominate. Many years after lit-igation, much of the work force will have beenreplaced with officers hired under the affirmativeaction regime, and productivity gains or lossesshould manifest themselves more strongly. Atthe same time, it is plausible that morale effectsdissipate over long time horizons, so that thelong-run effect is dominated by productivity con-siderations. As emphasized above, however, netproductivity reflects both the skill content of po-lice department entrance exams and the crime-fighting ability of black officers relative to that ofother officers, so the sign of any long-run effect oflitigation on police performance is theoreticallyambiguous.

Even if litigation does not affect crime, it couldaffect intermediate aspects of police performance,such as the racial composition of arrests. Thisissue has been studied by Donohue and Levitt(2001), who conclude that the hiring of black(white) officers increases the number of white(black) arrestees, but leaves unchanged the num-ber of black (white) arrestees. Since litigation re-sults in an increase in black officers at the expenseof white officers, their results imply that litigationshould decrease the number of black arrests andincrease the number of white arrests, for a de-crease in the fraction black of arrestees. The evidencepresented below is consistent with this prediction,but the magnitude of the effect is modest.

The effect of court-ordered affirmative actionon crime has also been studied by Lott (2000).

Lott considers only affirmative action requiredby DOJ consent decrees still in place as of 1987,when public-use data on police departmentblack employment share become available.Lott’s estimates imply that affirmative actionincreases crime. Lott emphasizes a specificmechanism, arguing that affirmative action overthis period involves reducing standards for ap-plicants generally. This argument is difficult toreconcile with the simulation of Section IVB.Moreover, that mechanism is less plausible inthe historical context studied here, where affir-mative action typically meant hiring in rankorder of test score, stratified by race—in whichcase no reduction of standards for nonblackapplicants was required.38

The 19 departments still subject to consentdecrees as of 1987 are a selected sample, in twodifferent ways, of departments placed under af-firmative action obligations. First, they do notinclude those departments litigated by privateactors. Second, they do not include those de-partments which by 1987 had already compliedwith any court-ordered affirmative action.These considerations suggest that crime rates inthese cities may have as much to do with in-flexible management as they do with changes inwork-force demographics. My own measure ofaffirmative action is whether a department wasever subject to litigation alleging hiring dis-crimination against African Americans. It incor-porates litigation brought by both the DOJ andprivate actors and does not reflect compliancewith affirmative action mandates.

A. Descriptive Statistics and EstimationResults

I begin with a consideration of simple de-scriptive statistics on crime rates by litigationstatus and litigation timing. For both the full andlong samples, panel C of Table 1 gives the logcrime rate for litigated and unlitigated cities atten-year intervals beginning in 1960. For the

38 If entrance examinations were previously job relatedand were diluted of their content in order to eliminatedisparate impact, then these considerations again becomeimportant. While there are undoubtedly examples of testdilution, my reading of the history is that the additionalpressure to establish a fair and impartial process for derivingtest questions related to job performance on net made theexaminations more job related rather than less.


full sample, it appears that crime rates in liti-gated and unlitigated cities differed by less than10 percent until the 1990s, when crime rates felldramatically in the litigated cities. Among citiesin the long sample, the unlitigated had highercrime than the litigated in 1960. Beginning in1970, however, the crime rates in litigated andunlitigated cities have a close correspondence.

Panel C of Table 2 gives the log crime rate forfive categories of litigation date ranges at ten-yearintervals beginning in 1960. Cities litigated in the1977–1980 period have a 1960 crime rate that is30 percent higher than the estimates for the otherfour litigation date ranges. Between 1960 and1970, however, the crime rate in cities that werelitigated between 1969 and 1974 and in the 1980ssoared relative to that in cities litigated in the1977–1980 period. Between 1970 and 1999, thecrime rates in the five city groups appear to moveroughly in parallel.

Panel A of Figure 7 gives log crime rates bylitigation status for 1960 to 1999 (cf. Figure 1,panel B). As suggested by the ten-year intervaldata in Table 1, there are no discernible differ-ences between litigated and unlitigated cities onaverage following the onset of litigation. Whatdifferences do exist are concentrated in the yearsbefore litigation: during the 1960s, the crime ratein litigated cities grew rapidly relative to that ofunlitigated cities. Already by 1970, however, thecrime rates had equalized. From 1970 to 1994,crime rates in the two sets of cities were virtuallyidentical. Only with the late 1990s drop in crimedo any differences in crime rates emerge. Thecrime rate differences at the beginning and end ofthe sample appear to reflect state-by-year specificpatterns, and are largely absorbed in the state-by-year controls in the event study analysis below.

At the bottom of panel A are log policing ratesby litigation status. While litigated departmentsemploy more officers per capita than do unliti-gated departments, there is no discernible trenddifferential in this measure over time. The eventstudy analysis below corroborates this impression.

Panel A of Figure 7 also gives, by litigationstatus, two additional police performance mea-sures: index arrests per index crime, and the frac-tion of index crimes cleared.39 In principle, bothmeasures proxy a single phenomenon—the rate at

which officers are engaging in the apprehension ofindividuals in a manner coordinated with solvingindex crimes known to police (as opposed to mak-ing many prostitution arrests, for example). Asnoted in Section II, however, the first proxy istaken from two different survey forms, whereasthe second proxy is based on information from asingle form. This suggests that clearance rates aremeasured with less error than arrest rates.

There is remarkable similarity between liti-gated and unlitigated departments in terms ofarrest rates and clearance rates. While arrestrates exhibit a differential litigated-unlitigatedtrend prior to the era of litigation, this is notconfirmed by the data on clearance rates. In-deed, clearance rates corroborate the essentialimpression conveyed by crime rates: litigatedand unlitigated departments delivered roughlysimilar police performance before, during, andafter litigation. The event study estimates belowsuggest, however, that these broad similaritiesmay potentially mask some modest effect sizes.

Panel B of Figure 7 gives the fraction AfricanAmerican among index crime arrestees, separatelyby litigation status. Litigated departments havealways arrested substantially more African Amer-icans than unlitigated departments. There is someconvergence in the arrest fraction black beginningin the 1990s, but the magnitude is small.

With that backdrop, I now turn to event studyestimates of the impact of litigation on policeperformance. To economize on space, I presentevent study graphs only for the more interestingresults. Panel A of Figure 8 gives event studyestimates of the impact of litigation on city crimerates. These estimates are not consistent with amajor impact of black police on crime rates, al-though the evident noise in the crime series meansit is difficult to detect small effect sizes.

Panel B of Figure 8 gives event study esti-mates for the clearance rate. While the pointestimates are generally insignificant (includingthe prelitigation estimates and the longer litiga-tion lags), there is a statistically significant dropin clearance rates in litigated departments five toseven years after litigation.40 The timing of theeffects is consistent with turmoil in the depart-ment. Quotas were typically imposed in these

39 For viewing purposes, I have added 0.10 to each of thearrest rate series.

40 For example, Model 1 estimates have t-ratios of!3.45, !2.32, and !2.29, and Model 4 estimates havet-ratios of !3.25, !3.59, and !3.24. Estimates from Model4 are significant in years 3 through 13.


cases one to three years after the filing date oflitigation, and the decline in clearances is pre-cipitous at three years after litigation. However,because affirmative action continued to affecthiring in departments throughout the study pe-riod, the timing of these effects is not consistentwith net productivity differences between affir-mative action hires and incumbents, as the ef-fects dissipate after a handful of years.

Panel C of Figure 8 gives event study esti-mates for the fraction of index crime arresteeswho are African American. This series is par-ticularly noteworthy, since the timing of theeffects is consistent with the gains in blackemployment share. As noted by Donohue andLevitt (2001), the effect of the racial composi-tion of the police on the racial composition ofarrests could reflect many factors, including

A. Aggregate Inputs and Outputs

4.90

5.40

5.90

6.40

6.90

7.40

7.90

8.40

8.90

1960 1965 1970 1975 1980 1985 1990 1995 2000

Log

Pol

ice,

Log

Cri

me

Rat

e

0

0.1

0.2

0.3

0.4

0.5

0.6

0.7

0.8

Arr

est,

Cle

aran

ce R

ate

Log Police per 100,000 Population, Unlitigated Log Police per 100,000 Population, LitigatedLog Crimes per 100,000 Population, Unlitigated Log Crimes per 100,000 Population, LitigatedArrests per Crime, Unlitigated Arrests per Crime, LitigatedClearance Rate, Unlitigated Clearance Rate, Litigated

Log Crimes

Arrests per Crime

Clearance Rate

Log Police

Note: Arrests per crime shifted by 10 percentage points for viewing purposes.

B. Racial Composition of Arrests

0.10

0.15

0.20

0.25

0.30

0.35

0.40

0.45

0.50

0.55

0.60

1960 1965 1970 1975 1980 1985 1990 1995 2000

Fra

ctio

n A

fric

an A

mer

ican

City Fraction Black, Unlitigated City Fraction Black, LitigatedFraction Black, Index Arrests, Unlitigated Fraction Black, Index Arrests, Litigated

Arrest Fraction Black

City Fraction Black

FIGURE 7. POLICE PERFORMANCE MEASURES, BY LITIGATION STATUS


FIGURE 8. EVENT STUDY ESTIMATES OF THE IMPACT OF LITIGATION ON POLICE PERFORMANCE


changes in the probabilities of false arrest (pre-sumably due to information processing) andchanges in the probabilities of true arrests (pre-sumably due to officer tastes or corruption).41

Table 4 summarizes the long-run trends in theseoutcomes, as well as for log police per 100,000population, the arrest rate, and the fraction blackamong all arrestees. Both the postlitigation trendand the break in trend at the litigation filing dataare reported. The point estimates in the table aregenerally small and insignificant. An importantexception is the estimate for the fraction blackamong index crime arrestees, which is suggestiveof effects of affirmative action on intermediateaspects of police performance.42

B. The Distribution of Entrance Exam Scoresby Race

I next present evidence on the temporal evo-lution of the distribution of entrance examina-tion scores by race for the New York CityPolice Department. These data allow direct cal-culation of the difference in the distribution oftest scores of newly hired officers under varioushiring rules. For example, it is possible to cal-culate the distribution of test scores under therank-order hiring rule traditionally used by po-lice departments, and we may compare this dis-tribution directly with the distribution of testscores which would result if an aggressive hir-ing quota were imposed. These two distribu-tions turn out to be rather similar, suggesting alimited role for the hypothesis that quotas in-crease crime by circumventing standards.

I have been able to obtain information on thedistribution of test scores by race for the 1968,1970, 1979, and 1998–1999 examinations.43

41 These are not the only effects discussed by Donohueand Levitt (2001), but the other key effects are transmittedthrough impacts on crime. The results below indicate thatthe impact of litigation on crime is modest and perhaps zero.

42 Note as well that the temporary decline in clearancerates is not captured by long-run trends. 43 See Appendix I.

TABLE 4—PARAMETRIC ESTIMATES OF THE IMPACT OF LITIGATION ON POLICE PERFORMANCE

Log police per 100,000 population Log crime per 100,000 population


(1) (2) (3) (4) (5) (6) (7) (8)25 " Postlitigation trend !0.014 0.012 0.016 0.025 !0.077 !0.088 !0.080 !0.044

(0.031) (0.027) (0.029) (0.036) (0.137) (0.062) (0.059) (0.050)25 " Post-pretrend difference !0.021 !0.016 !0.054 !0.104 !0.211 !0.078 !0.111 !0.024

(0.084) (0.063) (0.060) (0.057) (0.365) (0.153) (0.145) (0.116)

Arrest rate Clearance rate


(9) (10) (11) (12) (13) (14) (15) (16)25 " Postlitigation trend !0.072 !0.077 !0.078 !0.229 !0.044 !0.029 !0.035 !0.048

(0.059) (0.059) (0.061) (0.151) (0.041) (0.038) (0.040) (0.032)25 " Post-pretrend difference 0.114 0.039 0.012 !0.275 !0.001 0.023 0.006 0.030

(0.145) (0.097) (0.095) (0.211) (0.058) (0.054) (0.058) (0.048)

Fraction black, all arrests Fraction black, all index arrests


(17) (18) (19) (20) (21) (22) (23) (24)25 " Postlitigation trend 0.007 0.004 0.002 !0.023 !0.026 !0.033 !0.033 !0.054

(0.023) (0.020) (0.018) (0.019) (0.020) (0.020) (0.018) (0.017)25 " Post-pretrend difference 0.004 !0.004 !0.006 !0.041 0.003 !0.005 !0.004 !0.035

(0.043) (0.038) (0.038) (0.039) (0.052) (0.044) (0.044) (0.045)

Notes: Standard errors, clustered at the level of the city, presented in parentheses.


For all examinations for which I have data,Table 5 gives the fraction of white and blackapplicants with scores in each decile of theoverall test score distribution. The numbers inthe table suggest that in both the 1968 and 1970examinations, African Americans constitutedroughly 5 percent of those in the upper threedeciles and 20 percent of all applicants.

In 1972, the Guardians Association and theHispanic Society of the NYCPD mounted alegal challenge to these examinations. The courtfound that the city was in violation of Title VIIbecause the exams were insufficiently job-related; however, the case was declared mootbecause of the mid-1970s fiscal crisis, whichwas to preclude hiring in the NYCPD for aperiod of several years. When the city was againin a financial position to contemplate hiring, in1979, the Personnel Department went to greatlengths to design an exam that was job-related:

“Exam No. 8155 is a ‘second generation’selection procedure. Despite the variousflaws in construction of the test, it is clearthat some attempt was made to developthe test with recognition of at least someof the standards that courts had estab-lished in the first wave of Title VII cases.Aware that the validity of the test wouldlikely have to be demonstrated, the Cityperformed an extensive job analysis, con-sciously used concepts [from the EEOCUniform Guidelines on Employee Selec-tion Procedures] in determining the qual-ities that were being tested for, andattempted to eliminate extraneous vari-ables, such as the applicant’s prior knowl-edge, his reading level, and his ability tocomplete the test in a relatively shortamount of time.”44

44 630 F. 2d 79, 89.

TABLE 5—NEW YORK CITY POLICE DEPARTMENT ENTRANCE EXAMINATION SCORES BY RACE, 1968–1999

Decile

July 1968 examination May 1970 examination

Score range White fraction Black fraction Score range White fraction Black fraction

1 96–100 12.9 2.3 94–100 12.7 2.92 90–96 12.9 2.6 92–94 12.1 4.03 86–90 12.8 3.5 89–92 11.8 5.54 82–86 12.0 6.8 87–89 12.2 4.25 78–82 10.2 13.3 84–87 10.8 8.06 73–78 10.6 9.1 80–84 10.5 9.37 69–73 7.1 14.8 76–80 9.8 10.48 63–69 7.1 15.9 70–76 8.6 13.89 56–63 8.2 11.2 61–70 7.1 17.9

10 29–56 6.2 20.6 0–61 4.5 24.2N 2,774 725 4,511 1,002

Decile

June 1979 examination1 Pooled 1998–1999 examinations1

Score range White fraction Black fraction2 Score range White fraction Black fraction2

1 99–110 10.0 3.9 75–85 16.2 4.12 97–98 15.4 5.1 72–74 13.5 5.33 95–96 15.4 8.3 69–71 14.8 8.04 93–94 13.1 9.4 66–68 13.8 9.25 91–92 11.4 10.4 63–65 11.4 10.76 89–90 8.8 10.9 60–62 9.1 11.27 86–88 9.1 14.1 56–59 8.5 14.68 81–85 9.3 17.9 51–55 6.8 15.39 71–80 7.1 18.9 41–50 4.7 15.9

10 0–70 NA NA 0–40 1.2 5.6N 19,109 9,858 13,009 11,197

1 Because of test score aggregation, score ranges are approximate deciles.2 Black includes African American and Latinos. For the 1968 and 1970 examinations, the distribution of scores is available

separately for African Americans and Latinos. The distributions for these two groups are quite similar.


After the test was administered, however, theGuardians again challenged the test under TitleVII, because this test—although it exhibitedless disparate impact than the 1968 and 1970exams—continued to pass whites at a muchhigher rate than African Americans. For exam-ple, nonwhites constituted only 18 percent ofthose among the top three deciles, despite being34 percent of applicants.

Interestingly, the black-white test score gapon the NYCPD entrance exam does not appearto have changed much since 1979. Figure 9gives separate histograms for whites, and forAfrican Americans and Latinos combined, forthe 1979 and 1998–1999 examinations. Due to

the extremely large sample sizes, and the factthat the support of test scores is discrete, thehistogram requires no smoothing. Brief inspec-tion of the figure reveals that although there aresubstantial differences between the test scoredistributions for whites and nonwhites, there arevirtually no differences in the white test scoredistribution over time, and the nonwhite testscore distribution over time.

Using the data underlying Figure 9, it is asimple matter to simulate the impact of quotahiring on the distribution of test scores amongthe newly hired. For example, from the 1979exam, the NYCPD anticipated that all thosewith scores of at least 94 would move on to the

A. 1979 Exam

0.00

0.01

0.02

0.03

0.04

0.05

0.06

0.07

0.08

70 75 80 85 90 95 100 105

Exam Score

Fra

ctio

n of

App

lican

ts A

ttai

ning

Sco

re

Pooled African American and Latino applicants

White applicants

B. 1998-1999 Exams

0.00

0.01

0.02

0.03

0.04

0.05

30 40 50 60 70 80

Exam Score

Fra

ctio

n of

App

lican

ts A

ttai

ning

Sco

re

Pooled African American and Latino applicants

White applicants

FIGURE 9. ENTRANCE EXAM SCORE DISTRIBUTIONS BY RACE, NYCPD


next phase in the selection process. Thus, allnew hires were, in the absence of court inter-vention, to be drawn from the extreme upper tailof the test score distribution. The range ofscores would have naturally been from a low of94 to a high of 110, with an average score of96.8. In 1980, in response to the evidence re-garding the difference in the distribution of testscores by race, the district court judge orderedthat 50 percent of new hires be African Amer-ican or Latino.45 I estimate that a cohort se-lected under this aggressive quota would havehad scores ranging from 87 to 110 and an av-erage of 95.3. Thus, it appears that even with anaggressive hiring quota and a visually discern-ible difference in test score distributions, theaverage qualifications of an entering cohortwould be affected only in relatively minorways. While it is possible that one bad applespoils the bunch, the most natural model of theeffect of police officer quality on crime positsthat crime depends on the sum of officers’ testscores. If this is the right model, then even themost aggressive affirmative action measureswould not be expected to affect city crime ratesthrough effects on the distribution of aptitudeamong entering cohorts.

V. Conclusion

This paper has examined the impact of classaction employment discrimination litigation onblack employment share and police perfor-mance in 314 large municipal police depart-ments. Regarding the impact of litigation onblack employment share, the evidence points toseveral key conclusions. First, the litigation ofthe 1970s was targeted at big cities with largeand growing African American populations andlow black employment share. Second, despitesubstantial initial differences between litigatedand unlitigated cities, by 1999 litigated cities’representation gap was largely equal to that ofunlitigated cities. Third, this convergence ap-pears to have occurred almost entirely in theyears following litigation. Fourth, although un-litigated cities with large initial representation

gaps exhibit more convergence than cities withsmall gaps, this pattern is not strong enough toaccount for the gains accruing to litigated cities.Fifth, there is little evidence supporting a threateffect hypothesis. In particular, litigated citiesdo not appear to exhibit any gains in blackemployment share prior to litigation, and unliti-gated cities do not appear to integrate followingthe filing of the first class action employmentdiscrimination suit in their state.

On the whole, I interpret the evidence sum-marized in this paper as consistent with a majorrole for the federal courts in integrating policedepartments in the United States. My best esti-mate of the 25-year gain in police departmentblack employment share is 10 percentagepoints, and the effect is estimated with someprecision. Because of the low attrition rate ofpolice officers, this is consistent with a hiringfraction African American roughly 14 percent-age points above the prelitigation police depart-ment fraction black.

In contrast to the estimated impact of litigationon police department black employment share, Ifind little evidence of an impact of litigation oncrime. This may be because of a complex series ofeffects that offset one another. For example, thereis some evidence that litigation led to turmoil inthe department, temporarily reducing clearancerates, which presumably encouraged crime. How-ever, this effect on crime is not detectable, perhapsbecause African American officers are more pro-ductive crime fighters than other Americans.

The analysis in this paper rules out one mech-anism by which litigation might have been ex-pected to affect crime. Police departments’standard practice is to hire in rank order by testscore, and judges handing down quotas typicallyallowed departments to continue to do so, butrequired that they do so separately by race. Usingdata on test score distributions in New York City,thought to be representative of those for all policedepartments, I show that in such a context, evenaggressive hiring quotas change the test scoredistribution of new hires only minimally. Thissuggests that the magnitude of any aptitude dif-ferences induced by quota hiring is small, even forlong-term quota hiring regimes. Unless AfricanAmericans fare much better on the New York CityPolice Department entrance examinations than onthe entrance examinations of other cities, theseconclusions would seem to hold for police depart-ments generally.

45 Guardians Association of the New York City PoliceDepartment v. New York City Police Department, 484 F.Supp. 785, 799 (S.D. New York, 1980). This example is forillustrative purposes only; the 50-percent hiring quota wassubsequently softened by the appeals court (630 F. 2d 79).


APPENDIX I: DATA

Sample of Cities: The 314 cities for studywere selected from among those U.S. municipal-ities with the largest police and fire departments,on the basis of the Census of Governments from1972, 1977, 1982, 1987, 1992, and 1997. Thespecific mechanism for selection was as follows.First, I merged the employment counts by func-tion of government for all municipal respondentsin the years noted above. Average employmentlevels over the period were computed. There were328 cities whose average police and fire employ-ment levels placed them in the top 400 nationallyof both categories. These cities were then soughtin the electronic files of the EEO-4 survey. Satis-factory data for 314 cities were available. Most ofthe cities unable to be matched are quite small.However, Washington, D.C., and San Franciscowere excluded from the analysis because surveyresponses from these cities were not availableuntil the 1980s.46 The resulting sample is com-prised of 314 cities in all 9 census regions, and inall but the least populated of the 48 contiguousstates.47

Black Police Officer Data: Data on policedepartment demographics are obtained primar-ily from the EEO-4 survey of the Equal Em-ployment Opportunity Commission (EEOC),conducted annually by the EEOC since 1973.48

These data are confidential, but may be madeavailable to researchers. Tabulations of thesedata have typically been published by the EEOCand are available in libraries (see, for example,Equal Employment Opportunity Commission1999). Previous researchers have been able toaccess electronic files for 1980, 1984, 1985,1987, 1989, 1990, 1991, 1993, 1995, 1997, and1999. As part of the research for this study, Itraveled to the EEOC and recovered the 1973

and 1974 surveys. Electronic files in EBCDICand packed decimal format were available, butcodebooks were not. Aided by the institutionalknowledge of Ron Edwards, I inferred a code-book for these data and constructed electronicfiles. In EEOC headquarters, I located severalnine-track reels containing the only known cop-ies of the 1982 EEO-4 survey. Unfortunately,these reels had experienced a high degree ofphysical degradation, and only half of therecords from the 1982 survey are available. Inthe Alexandria warehouse of the EEOC, I lo-cated microfilm records for 1975, 1977, and1981. A team of research assistants enteredthese data for all cities (1975 and 1977) and forthose cities missing 1980 records (1981). The1981 records are important, since large citiesare systematically missing in 1980.49 The cityidentifiers assigned by the EEOC had a smallnumber of errors for the years 1980 to 1999,which I corrected manually using name andaddress information for each city. Identifiers for1973 and 1974 also do not conform to the 1980identifiers; for these years, I created a full cross-walk for all identifiers.

Because the first EEO-4 survey was not con-ducted until 1973, further data on the number ofAfrican American officers in police depart-ments were collected from several historicalsources. The most nationally comprehensive isthe International City Manager Association(1970), which details the number of “minoritygroup employees-uniformed.” I interpret thesenumbers as the number of African Americanand Latino officers and have discounted themby the estimated 1973 fraction of African Amer-ican and Latino officers who were AfricanAmerican. The other nationally comprehensivesurvey comes from unpublished research(Raper 1940) on “Negro policemen” uponwhich Gunnar Myrdal (1944) relied.50 Raper’sresearch led to surveys of Southern police de-

46 The fire and police departments of San Francisco werelitigated in 1970 and 1973, respectively. The police depart-ment of Washington, D.C., was litigated in 1970.

47 Montana, North Dakota, Vermont, and Wyoming areall unrepresented. The 2000 population ranks of these statesamong the 48 contiguous states are 43, 46, 47, and 48,respectively.

48 Beginning in 1991, the EEOC has conducted theEEO-4 survey only once every two years. The 1972 EqualEmployment Opportunity Act granted authority to theEEOC to collect data from public employers, expanding theEEOC’s older data collection authority regarding privateemployers (conferred by the 1964 Civil Rights Act).

49 For example, neither New York nor Los Angeles isincluded in the 1980 file. The source of this problem appearsto be that electronically submitted returns were ironicallynot included in the electronic file compiled by the contractorfor the 1980 survey. Data for cities located on the samemicrofilm reel as a city with missing data were also in-cluded.

50 Comparing 1930 and 1940 Census published totals ofAfrican American police officers with Raper’s estimatessuggests that Raper identified the employers of some 90percent of the black police officers in the country.


partments spanning 1947 to 1969. Raper was alongtime writer for the Commission on Interra-cial Cooperation, which the Southern RegionalCouncil (SRC) succeeded in 1944. From 1947to 1954, the SRC continued Raper’s surveys ofthe number of “Negro uniformed policemen,detectives (plainclothes), and policewomen” forSouthern municipalities, publishing results an-nually in New South.51

Publication of these numbers ceased after1954, as the SRC focused its efforts on schooldesegregation and voter registration (Elliott M.Rudwick 1961). However, Rudwick conductedsurveys of Southern police departments in 1954,1959, and 1961 and the SRC published theresults in Rudwick (1962). Then, in 1969, theSRC attempted what was to be its final surveyof Southern police departments. The results ofthe survey were not published, but the data areavailable in recently published microfilmrecords (Southern Regional Council 2000, Reel111 (434), 289–98).

For non-Southern cities, data on the numberof “Negro police” in 1954 for a small number ofcities are published in Kephart (1954) andKephart (1957). Data on larger cities’ blackemployment share have also been published inthe reports of several presidential and guberna-torial commissions: President’s Commission onLaw Enforcement and Administration of Justice(1967), National Advisory Commission onCivil Disorders (1968), and National AdvisoryCommission on Criminal Justice Standards andGoals (1973). Finally, it appears that the U.S.Commission on Civil Rights conducted a sur-vey of employment of African American policeofficers in 230 departments in 1962 (President’sCommission on Law Enforcement and Admin-istration of Justice 1967, 167–68). However,the Commission did not publish this work, theCommission Library does not possess a copy,and the survey results are not part of the Na-tional Archives’ holdings of the Commission’spapers. I believe this is the only nationally com-prehensive survey information on the employ-ment of black police officers not included in thedata used for this study.

The historical sources consulted allowed es-timation of 1969 black employment share for all314 cities under study. Because litigation beganin 1969, this is an important aspect of the datacollection undertaken here. For a subset of 120cities, referred to in the body of the text as the“long sample,” data on black employment sharefor 1960 to 1969 are available. Data on blackemployment share were combined with data oncity fraction African American (linearly inter-polated between census years).

I also use an administrative dataset on policeofficers in the Chicago Police Department(CPD), provided to me by Adam Kingsley ofthe City of Chicago Department of Law follow-ing a records request. The dataset contains, forevery individual who has worked for the CPDsince approximately the late 1970s, a hiringdate, a termination date, race, and other infor-mation not used here. Details on the construc-tion of this dataset from CPD administrativerecords is provided in Bernard R. Siskin andDavid W. Griffin (1997). I use these data toconstruct a sample of CPD police officers for allyears from 1960 to 1997. Using the UniformCrime Reports (UCR), I estimated the samplingrate for each of these extracts. From a low of 40percent in 1960, the rate rises smoothly in time,arriving at a constant level of 95–105 percentbeginning in 1977. The sampling rate for Afri-can American officers is higher than that ofother officers for the early years (sources onblack police available for 1962, 1967, and1969). I estimate the black sampling rate inthese years to be 80, 76, and 70 percent. Theserates are to be compared to the overall rates of50, 65, and 71 percent, respectively. The down-ward trend in Figure 1 in hiring fraction AfricanAmerican pre-1970 is likely an artifact of thisphenomenon, but the 1974 spike may not beattributed to this because the sampling rateswere similar already in 1969.

Litigation Data: To learn which cities werelitigated, I read over 1,300 published decisionsin which hiring discrimination against AfricanAmericans on the part of the city police or cityfire department was alleged.52 These decisions

51 Outline of volumes used: October 1947, Vol. 2, No.10, p. 9; September 1948, Vol. 3, No. 9, p. 7; September1949, Vol. 4, No. 9, p. 9; September–October 1950, Vol. 5,Nos. 9 and 10, p. 6; September 1952, Vol. 7, No. 9, p. 6; andOctober–November 1953, Vol. 8, Nos. 10 and 11, pp. 6–7.

52 Interested researchers may obtain additional records(e.g., unpublished decisions and consent decrees) on thecases studied here by contacting the federal district court inwhich the case originated. That strategy was not pursuedhere due to cost.


were located in a multistep process. First, for all314 cities under study, a keyword search on“discrimination,” “black,” and “police”/“fire”was conducted in conjunction with the name ofthe city (e.g., “Norfolk”). Second, the resultinglist of cases was scanned and those deemedpotentially relevant were selected for skimming.In the third step, decisions determined to pertainto discrimination against either the police or firedepartment in the city were read in their entirety(preliminary research indicated that judges infire department cases frequently mention litiga-tion against the police department in the samecity). Fourth, all cases cited by each of thosedecisions as pertaining to discrimination caseswere consulted. Two pieces of evidence suggestthat this strategy led to a relatively completerecord of the litigation. First, only a handful ofcases identified in the fourth step had not al-ready been located using keyword searches.Second, the cases listed in U.S. Department ofJustice (2001) are a strict subset of the caseslocated by the first search method.

It was not possible to determine which de-partments were subject to quotas during whichtime periods. Because of unpublished decisionsand judicial choices regarding what to discuss inthe text of an opinion, information on quotas ismuch more poorly measured than whether a citywas litigated, and the date the litigation began.Litigation filing dates were determined by ref-erence to the first two digits of the Civil ActionNumber (CAN) for located cases. Because liti-gation filing dates are embedded in the CAN,the location of even one published decisionpertaining to a case results in knowledge of thefiling year.

Crime Data: Data on crime and policestaffing were obtained from the Uniform CrimeReports available from the Inter-universityConsortium for Political and Social Research(ICPSR) for 1975 to 1999. Data prior to 1975are not available from ICPSR, but are availablefrom the FBI.53

Entrance Exam Data: The 1968 and 1970data are from Chaiken and Cohen (1973). The1979 data are from Guardians Association ofthe New York City Police Department v. the

New York City Police Department, 630 F. 2d79, 103 (2nd Cir., 1980). The 1998–1999 datawere obtained from the NYCPD following arecords request.

City Demographics Data: City demograph-ics such as fraction African American and pop-ulation were taken from the population censusesfor 1960, 1970, 1980, 1990, and 2000, andlinearly interpolated between census years.Electronic files were available for all years ex-cept for 1960, where I substituted publishedtabulations.54

Riot Data: Data on riots from 1961 to 1968are taken from the Data and Program LibraryService at the University of Wisconsin.

Availability of Data: A series of electronicfiles containing all data and programs used forthis paper are available for researchers withaccess to EEOC data files. Interested research-ers should contact Ron Edwards at the EEOC.

APPENDIX II: USING QUIT RATES TO PREDICT

CHANGES IN HIRING PRACTICES

This appendix justifies the approximation in(1). Let Nt

B and Nt denote the number of blackand all officers, respectively, at time t; Ht thenumber of officers hired between t ! 1 and t; qt

B

the quit rate of black officers; and ft the hiringfraction African American. The identity

(5) NtB & Nt ! 1

B # Nt ! 1B qt ! 1

B " Ht ft

states simply that the number of black officersin period t is equal to the number of blackofficers in period t ! 1, less the number of blackofficers quitting, plus the number of black of-ficers hired. Dividing both sides by the numberof total officers implies

(6) Ft &Nt

B

Nt&

Nt ! 1B

Nt"1 # qt ! 1

B # "Ht

Ntft

&Nt ! 1

B

Nt ! 1

Nt ! 1

Nt"1 # qt ! 1

B # "Ht

Ntft

53 These files were obtained with the help of JoanneVanatta of the Programs Support Section of the FBI, RonEdwards of the EEOC, and Rick Kawin of UC Berkeley.

54 For 1970, information in the electronic file was miss-ing for East Hartford and West Hartford, Connecticut, andBrookline, Massachusetts, and published tabulations wereagain used.


&1 # qt ! 1

B

1 " $tFt ! 1 " ht ft

% .t ! 1 Ft ! 1 " ht ft ,

where .t!1 $ (1 ! qt!1B )/(1 % $t), ht is the new

hires rate and, as in the main text, Ft denotes theblack employment share in period t, and $t is theyear-over-year growth rate in the size of thework force (i.e., $t $ (Nt ! Nt!1)/Nt!1). Iter-ating on this recursion yields

(7) Ft & ,t,k Ft ! k " "j $ 0

k ! 1

,t,j ht ! j ft ! j

& ,t,k Ft ! k " h! f! "j $ 0

k ! 1

,t,j

" C-ht ! j , ft ! j . "j $ 0

k ! 1

,t,j ,

where ,t, j $ /i$1j .t! i for j ) 0 and ,t, j $ 1

for j $ 0, C[ht! j , ft! j] is the weighted covari-ance of the hiring fraction African Americanand the hiring rates over the past k periods, h! isthe weighted average of hiring rates, and f! is theweighted average of the hiring fraction AfricanAmerican, with weights proportional to ,t, j andsumming to one.

I now consider simplifying assumptions de-signed to allow something meaningful to besaid about the likely fraction African Americanamong new hires, given information solely ongains in the black employment share and anestimate of the quit rate. Two assumptionswhich are sufficient are:

A1. Quit Rates, Hiring Rates, and the HiringFraction African American are Constant: q* $q! , h* $ h! , and f* $ f!, for * ! {t ! k, t ! k %1, ... , t ! 1, t}.

A2. Black Quit Rates are Equal to Overall QuitRates: q*

B $ q* for * ! {t ! k, t ! k % 1, ... ,t ! 1, t}.

Since ht + ($t % qt!1)/(1 % $t), AssumptionsA1 and A2 imply $t + $! , leading to the identity

(8) Ft & &1 # q!1 " $!' k

Ft ! k " #1 # &1 # q!1 " $!' k( f!,

which we recognize as (1). Letting ! $ ((1 !q!)/(1 % $!))k, we have

(9) f! # Ft ! k &1

1 # !"Ft # Ft ! k #,

which we recognize as the conversion equation(2). An alternative set of sufficient assumptionsis also available, recorded here as B1 through B3:

B1. Black Quit Rates and Employment GrowthRates are Small: q*

B and $* are near zero foreach * ! {t ! k, t ! k % 1, ... , t ! 1, t}.

B2. Hiring Rates and the Hiring Fraction Af-rican American are Uncorrelated: C[h*, f*] $ 0for * ! {t ! k, t ! k % 1, ... , t ! 1, t}.

B3. Law of Large Numbers: qt, qtB, and ht are

covariance stationary and jointly ergodic, and kis large.

Assumptions B1 and B3 imply that A1 holdsapproximately. For example, a second-orderTaylor approximation for ln(1 % x) shows that

(10) ,t,k & exp"!k0q!B " $!1# exp"12

k0V-qt ! iB .

% "q!B#2}) exp"12

k0V-$t! i. " "$!#21# " o,

where o is a general representation for anerror which is (here, to second-order) smallwhen black quit rates and employment growthrates are small, and now q! and $! denote thesimple averages of quit and employmentgrowth rates, respectively.55 Under B3, the terms1⁄2 k{V[qt!i

B ] % (q!B)2} and 1⁄2 k{V[$t!i] % ($!)2}are small if quit rates are small relative to k,leading to ,t,k 2 ((1 ! q!B)/(1 % $!))k (anotherTaylor expansion shows this is approximatelyequal to the first factor in (10)).

To assess the numerical accuracy of this ap-proximation, consider a simulation with parame-ters relevant for the context of this paper. Suppose

55 Note that since the ,t,k are bounded, under B3, thesimple and weighted averages are equal in probability.


k $ 25, qtB is distributed uniformly between 0.03

and 0.05, and $t is distributed uniformly between0.005 and 0.015. Then, ((1 ! q!B)/(1 % $!))k hasan average percentage error for ,t,k of 5.2 per-cent, with a near perfect correlation.56

Since the weights ,t, j are bounded, assump-tions B2 and B3 imply that C[ht! j , ft! j] $

p0,

and assumption B3 and Slutsky’s theorem im-ply that h! $

p($! % q!)/(1 % $!), where Ak $

pBk

means that Ak and Bk share a probability limit.This leads to

(11) Ft $p &1 # q!B

1 " $! 'k

Ft ! k

"$! " q!$! " q! B #1 # &1 # q! B

1 " $! ' k( f! " o

(cf. (1)). Letting ! $ (1 ! q!B)/(1 % $!) and / $($! % q!)/($! % q!B), we obtain

/f! # Ft ! k !1

1 # !"Ft # Ft ! k #

(cf. (2)). This implies that (1/(1 ! !))(Ft !Ft!k) will understate the regime-shift in thehiring fraction African American if q!B ) q! andwill overstate the regime-shift if q!B & q! .

In the text, I implement this approximationtechnique using a year-over-year growth rateestimate of 1 percent and a quit rate of 4 per-cent. While the year-over-year growth rate isobserved directly, the quit rate is not. However,4 percent is in line with the available evidence.The Chicago data described in Section II yieldan estimated quit rate of 3.6 percent.57 Butter-field (2001) notes that “[i]n New York City,more than 1,700 officers left the 41,000-mem-ber force last year through retirement or resig-nation, a third more than the year before”(implied quit rate estimates of 1700/41000 !0.041 and 1275/41000 ! 0.031). More histori-cally, the District Court of the Eastern Districtof Pennsylvania reports that “[a]s of September

22, 1972 there were 8,082 members of the [Phil-adelphia] Police Department. ... [D]efendantsestimate that 96 persons presently employed onthe Police Force will no longer be employed onthe Police Force as of January 1, 1973” (esti-mate of 96[365/(8 % 31 % 30 % 31)]/8082 !0.043).58

Further corroboration of this quit rate esti-mate is available from the 1991–1992 PoliceUse of Force survey (Antony M. Pate and LoriE. Fridell 1994), which reports average years ofservice among several hundred large municipalpolice departments to be 11.3. If T denotescompleted time of service, then to maintain aconstant work-force size, a department will hire1/T of its work force at each point in time, andamong those working, average time of servicewill be 30

T x(1/T) dx $ (T/2). Thus, 11.3 averageyears of service among current workers trans-lates into average completed years of service of22.6—or a quit rate of about 1/22.6 ! 0.044.This estimate is likely slightly overstated, be-cause T ) 2 ! 11.3 in a growing department,since entering cohorts must become progres-sively larger.

REFERENCES

Altonji, Joseph G., and Rebecca M. Blank. 1999.“Race and Gender in the Labor Market.” InHandbook of Labor Economics Volume 3C,ed. Orley Ashenfelter and David E. Card,3143–3259. Amsterdam; New York and Ox-ford: Elsevier Science, North-Holland.

Antonovics, Kate L., and Brian G. Knight.2004. “A New Look at Racial Profiling: Ev-idence from the Boston Police Department.”National Bureau of Economic ResearchWorking Paper 10634.

Ashenfelter, Orley, and James J. Heckman. 1976.“Measuring the Effect of an Antidiscrimina-tion Program.” In Evaluating the Labor-Market Effects of Social Programs, ed. OrleyAshenfelter and James Blum, 46-84. Prince-ton: Industrial Relations Section ResearchReport Series 120, 4684.

Beller, Andrea H. 1978. “The Economics of En-forcement of an Antidiscrimination Law: TitleVII of the Civil Rights Act of 1964.” Journal ofLaw and Economics, 21(2): 359–80.

56 On average across 10,000 replications, ((1 ! q!B)/(1 %$!))k was 0.281, while ,t,k was 0.267. The overstatement isattributable to quit rates being generally larger than employ-ment growth rates in the chosen example.

57 For the sample of officers in the force between 1979and 1997. Before 1979, it appears that the quit rate isartificially low due to the sampling scheme. 58 348 F. Supp. 1084, 1110 (E.D. Pa. 1972).


Bowen, William G., and Derek Bok. 1998. TheShape of the River: Long-Term Conse-quences of Considering Race in College andUniversity Admissions. Princeton: PrincetonUniversity Press.

Brown, Charles. 1984. “Black–White EarningsRatios since the Civil Rights Act of 1964:The Importance of Labor Market Dropouts.”Quarterly Journal of Economics, 99(1): 31–44.

Butterfield, Fox. 2001. “City Police Work Los-ing Its Appeal and Its Veterans.” New YorkTimes, July 30.

Carrington, William J., Kristin McCue, andBrooks Pierce. 1996. “Black/White WageConvergence: The Role of Public SectorWages and Employment.” Industrial and La-bor Relations Review, 49(3): 456–71.

Chaiken, Jan M., and Bernard Cohen. 1973. Po-lice Civil Service Selection Procedures inNew York City: Comparison of EthnicGroups. New York: RAND Corporation.

Cohen, Bernard, and Jan M. Chaiken. 1972.Police Background Characteristics andPerformance: Report Prepared for theNational Institute of Law Enforcementand Criminal Justice. New York: RANDCorporation.

Davidson, James. 1994. Stochastic Limit Theory:An Introduction for Econometricians. Ad-vanced Texts in Econometrics. Oxford andNew York: Oxford University Press.

Decker, Scott H., and Russell L. Smith. 1980.“Police Minority Recruitment: A Note on ItsEffectiveness in Improving Black Evalua-tions of Police.” Journal of Criminal Justice,8(6): 387–93.

DiNardo, John, Nicole M. Fortin, and ThomasLemieux. 1996. “Labor Market Institutionsand the Distribution of Wages, 1973–1992: ASemiparametric Approach.” Econometrica,64(5): 1001–44.

Donohue, John J., III, and James J. Heckman.1991. “Continuous versus Episodic Change:The Impact of Civil Rights Policy on theEconomic Status of Blacks.” Journal of Eco-nomic Literature, 29(4): 1603–43.

Donohue, John J., III, and Steven D. Levitt. 2001.“The Impact of Race on Policing and Ar-rests.” Journal of Law and Economics, 44(2):367–94.

Dulaney, W. Marvin. 1996. Black Police in Amer-ica. Bloomington: Indiana University Press.

Equal Employment Opportunity Commission.1999. Job Patterns for Minorities andWomen in State and Local Government.Washington, DC: EEOC.

Freeman, Richard B. 1973. “Changes in the La-bor Market for Black Americans, 1948–72.”Brookings Papers on Economic Activity, 1:67–120.

Graham, Hugh D. 1990. The Civil Rights Era: Ori-gins and Development of National Policy, 1960–1972. New York: Oxford University Press.

Greisinger, George, Jeffrey S. Slovak, and Jo-seph J. Molkup. 1979. Civil Service Sys-tems: Their Impact on Police Administration.Washington, DC: U.S. Government PrintingOffice.

Guryan, Jonathan. 2004. “Desegregation andBlack Dropout Rates.” American EconomicReview, 94(4): 919–43.

Heckman, James J., Hidehiko Ichimura, JeffSmith, and Petra Todd. 1998. “CharacterizingSelection Bias Using Experimental Data.”Econometrica, 66(5): 1017–98.

Heckman, James J., and Kenneth I. Wolpin.1976. “Does the Contract Compliance Pro-gram Work? An Analysis of Chicago Data.”Industrial and Labor Relations Review,29(4): 544–64.

International City Manager Association. 1970.Municipal Yearbook. Washington, DC:ICMA.

Jacobson, Louis S., Robert J. LaLonde, andDaniel G. Sullivan. 1993. “Earnings Losses ofDisplaced Workers.” American EconomicReview, 83(4): 685–709.

Jencks, Christopher, and Meredith Phillips. 1998.The Black–White Test Score Gap. Washing-ton, DC: Brookings Institution Press.

Kephart, William M. 1954. “The Integration ofNegroes into the Urban Police Force.” Jour-nal of Criminal Law, Criminology, and Po-lice Science, 45(3): 325–33.

Kephart, William M. 1957. Racial Factors andUrban Law Enforcement. Philadelphia: Uni-versity of Pennsylvania Press.

Knowles, John, Nicola Persico, and Petra Todd.2001. “Racial Bias in Motor Vehicle Search-es: Theory and Evidence.” Journal of Politi-cal Economy, 109(1): 203–29.

Landy, Frank J. 2003. “Phases of EmploymentLitigation.” In Behavioral, Quantitative, andLegal Perspectives, ed. Frank J. Landy,Chapter 1. San Francisco: Jossey-Bass.


Leonard, Jonathan S. 1984. “Antidiscriminationor Reverse Discrimination: The Impact ofChanging Demographics, Title VII and Af-firmative Action on Productivity.” Journal ofHuman Resources, 19(2): 145–74.

Leonard, Jonathan S. 1984. “The Impact of Af-firmative Action on Employment.” Journal ofLabor Economics, 2(4): 439–63.

Leonard, Jonathan S. 1985. “Affirmative Actionas Earnings Redistribution: The Targeting ofCompliance Reviews.” Journal of LaborEconomics, 3(3): 363–84.

Leonard, Jonathan S. 1990. “The Impact of Affir-mative Action Regulation and Equal Employ-ment Law on Black Employment.” Journal ofEconomic Perspectives, 4(4): 47–63.

Lott, John R., Jr. 2000. “Does a Helping HandPut Others at Risk? Affirmative Action, Po-lice Departments, and Crime.” Economic In-quiry, 38(2): 239–77.

Myrdal, Gunnar. 1944. An American Dilemma:The Negro Problem and Modern Democracy.New York: Harper and Row.

National Advisory Commission on Civil Disor-ders. 1968. Report of the National AdvisoryCommission on Civil Disorders. Washington,DC: U.S. Government Printing Office.

National Advisory Commission on Ciriminal Jus-tice Standards and Goals. 1973. Report onPolice. Washington, DC: U.S. GovernmentPrinting Office.

Pate, Anthony M., and Lorie E. Fridell. 1994.“Police Use of Force: Official Reports, Citi-zen Complaints and Legal Consequences,1991–1992.” [computer file] Washington,DC: Police Foundation.

President’s Commission on Law Enforcement andAdministration of Justice. 1967. Task ForceReport: The Police. Washington, DC: U.S.Government Printing Office.

Raper, Author. 1940. “Race and Class Pres-sures.” Unpublished.

Reber, Sarah J. 2003. “Court-Ordered Desegre-gation: Successes and Failures in IntegratingAmerican Schools since Brown.” Unpublished.

Reiss, Michael. 1977. “Requiem for an ‘Indepen-dent Remedy’: The Civil Rights Acts of 1866and 1871 as Remedies for Employment Dis-

crimination.” Southern California Law Re-view, 50: 961–1025.

Rose, David L. 1989. “Twenty-Fives YearsLater: Where Do We Stand on Equal Em-ployment Opportunity Law Enforcement?”Vanderbilt Law Review, 42: 1121– 81.

Rosen, Sherwin. 1969. “Trade Union Power,Threat Effects and the Extent of Organiza-tion.” Review of Economic Studies, 36(106):185–96.

Rosenbaum, Paul R., and Donald B. Rubin. 1983.“The Central Role of the Propensity Score inObservational Studies for Causal Effects.”Biometrika, 70(1): 41–55.

Rudwick, Elliott M. 1961. “Negro Police Em-ployment in the Urban South.” Journal ofNegro Education, 30(2): 102–08.

Rudwick, Elliott M. 1962. The Unequal Badge:Negro Policemen in the South. Atlanta:Southern Regional Council.

Schlei, Barbara L., and Paul Grossman. 1976.Employment Discrimination Law. Washing-ton, DC: Bureau of National Affairs.

Siskin, Bernard R., and David W. Griffin. 1997.Analysis of Distributions by Rank, Race andGender: City of Chicago Police Department,1987–1991. Philadelphia: Center for ForensicEconomic Studies.

Smith, James P., and Finis R. Welch. 1989.“Black Economic Progress after Myrdal.”Journal of Economic Literature, 27(2): 519–64.

Southern Regional Council. 2000. Southern Re-gional Council Papers, 1944–1968. Ann Ar-bor: University Microfilms International.

Southern Regional Council. Various years. NewSouth.

Spilerman, Seymor. 1970. “The Causes of RacialDisturbances: A Comparison of AlternativeExplanations.” American Sociological Re-view, 35(4): 627–49.

U.S. Department of Justice. 2001. “EmploymentLitigation Section Complaints Filed Involv-ing Police of Fire Department as of July 31,2001.” Unpublished.

Wallace, Phyllis A. 1976. Equal EmploymentOpportunity and the AT&T Case. Cambridge,MA: MIT Press.


The Effect of Court-Ordered Hiring Quotas on the ...jmccrary/mccrary2007.pdfThe Effect of...

Documents

Transcript of The Effect of Court-Ordered Hiring Quotas on the ...jmccrary/mccrary2007.pdfThe Effect of...