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INTERPERSONAL RELATIONS AND GROUP PROCESSES
A Meta-Analytic Test of Intergroup Contact Theory
Thomas F. Pettigrew
University of California, Santa Cruz Linda R. Tropp
Boston College
The present article presents a meta-analytic test of intergroup contact theory. With 713 independent samples
from 515 studies, the meta-analysis finds that intergroup contact typically reduces intergroup prejudice.
Multiple tests indicate that this finding appears not to result from either participant selection or publication
biases, and the more rigorous studies yield larger mean effects. These contact effects typically generalize to
the entire outgroup, and they emerge across a broad range of outgroup targets and contact settings. Similar
patterns also emerge for samples with racial or ethnic targets and samples with other targets. This result
suggests that contact theory, devised originally for racial and ethnic encounters, can be extended to other
groups. A global indicator of Allport’s optimal contact conditions demonstrates that contact under these
conditions typically leads to even greater reduction in prejudice. Closer examination demonstrates that these
conditions are best conceptualized as an interrelated bundle rather than as independent factors. Further, the
meta-analytic findings indicate that these conditions are not essential for prejudice reduction. Hence, future
work should focus on negative factors that prevent intergroup contact from diminishing prejudice as well as
the development of a more comprehensive theory of intergroup contact.
Keywords: intergroup prejudice, intergroup contact, meta-analysis
For decades, researchers and practitioners have speculated about
the potential for intergroup contact to reduce intergroup prejudice.
Some writers thought contact between the races under conditions
of equality would only breed “suspicion, fear, resentment, distur-
bance, and at times open conflict” (Baker, 1934, p. 120). Others
proposed that interracial experiences could lead to “mutual under-
standing and regard” (Lett, 1945, p. 35) and that when groups “are
isolated from one another, prejudice and conflict grow like a
disease” (Brameld, 1946, p. 245; see also Watson, 1946).
Early studies of intergroup contact provided preliminary tests of
these proposals and revealed encouraging trends. After the U.S.
Merchant Marine began desegregating, Brophy (1946) found that
the more voyages the White seamen took with Blacks, the more
positive their racial attitudes became. Likewise, White police
officers who worked with Black colleagues later objected less to
having Blacks join their police districts, teaming with a Black
partner, and taking orders from Black officers (Kephart, 1957).
As studies of intergroup contact grew in number, the Social Science
Research Council asked Robin Williams, Jr., a Cornell University
sociologist, to review research on group relations. Williams’s (1947)
monograph, The Reduction of Intergroup Tensions, offers 102 testable
“propositions” on intergroup relations that include an initial formula-
tion of intergroup contact theory. In particular, he noted that inter-
group contact would maximally reduce prejudice when the two
Thomas F. Pettigrew, Department of Psychology, University of Califor-
nia, Santa Cruz; Linda R. Tropp, Department of Psychology, Boston
College.
A preliminary report of this research, which included the first 203
studies collected, appeared in Pettigrew and Tropp (2000). The National
Science Foundation supported this research (SBR-9709519), with Thomas
F. Pettigrew and Stephen Wright serving as coinvestigators. Though listed
alphabetically, the co-authors shared equally in the preparation of this
manuscript and in their work on this 8-year project. An earlier version of
this paper won the Gordon W. Allport Intergroup Research Prize awarded
by the Society for the Psychological Study of Social Issues in 2003.
We thank Stephen Wright and the following dedicated research assistants at
the University of California, Santa Cruz, and Boston College for their invalu-
able assistance: Rebecca Boice, Geoffrey Burcaw, Susan Burton, Darcy Ca-
bral, Robert Chang, Daniel Cheron, Vanessa Lee, Kimberly Lincoln, Peter
Moore, Danielle Murray, Neal Nakano, Rajinder Samra, Michael Sarette,
Christine Schmitt, Amanda Stout, and Gina Vittori. We are grateful to the
library staffs of the University of California, Santa Cruz, and Boston College
for their help with tracking down hundreds of relevant journal articles in a wide
assortment of specialized journals. We thank Makiko Deguchi, Greg Kim,
Adele Kohanyi, Daphne Malinsky, and Mark Pettigrew for their help in
translating research articles. We also thank Sue Duval, Blair Johnson, David
Kenny, and Jack Vevea for their statistical advice and assistance and Jack
Dovidio, Samuel Gaertner, Miles Hewstone, and Brian Mullen for their
comments on earlier versions of this article. In addition, we wish to express our
deep appreciation for the many researchers who dug into their files to find the
detailed data needed to compute effect sizes.
Correspondence concerning this article should be addressed to Thomas
F. Pettigrew, Department of Psychology, Social Sciences II, University of
California, Santa Cruz, California 95064 or to Linda R. Tropp, Department
of Psychology, McGuinn Hall, Boston College, Chestnut Hill, Massachu-
setts 02467. E-mail: pettigr@ucsc.edu or tropp@bc.edu
Journal of Personality and Social Psychology, 2006, Vol. 90, No. 5, 751–783
Copyright 2006 by the American Psychological Association 0022-3514/06/$12.00 DOI: 10.1037/0022-3514.90.5.751
751
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groups share similar status, interests, and tasks and when the situation
fosters personal, intimate intergroup contact.
Researchers then began to test the theory more rigorously. Field
studies of public housing provided the strongest evidence and
marked the introduction of large-scale field research into North
American social psychology. In a notable example of this work,
Deutsch and Collins (1951) interviewed White housewives across
different public housing projects with a design that Campbell and
Stanley (1963) later labeled “quasi-experimental.” Two housing
projects in Newark assigned Black and White residents to separate
buildings. Two comparable housing projects in New York City
desegregated residents by making apartment assignments irrespec-
tive of race or personal preference. The authors found that White
women in the desegregated projects had far more optimal contact
with their Black neighbors. Moreover, they held their Black neigh-
bors in higher esteem and expressed greater support for interracial
housing. Further research extended this work, showing that equal-
status interracial contact in public housing related to more positive
feelings and intergroup attitudes for both Blacks and Whites (Wil-
ner, Walkley, & Cook, 1952; Works, 1961).
Armed with Williams’s initial effort and the rich findings of the
housing studies, Allport (1954) introduced the most influential
statement of intergroup contact theory in The Nature of Prejudice.
His formulation of intergroup contact theory maintained that con-
tact between groups under optimal conditions could effectively
reduce intergroup prejudice. In particular, Allport held that re-
duced prejudice will result when four features of the contact
situation are present: equal status between the groups in the situ-
ation; common goals; intergroup cooperation; and the support of
authorities, law, or custom.
Allport’s formulation of intergroup contact theory has inspired
extensive research over the past half century (Pettigrew, 1998; Petti-
grew & Tropp, 2000). These investigations range across a variety of
groups, situations, and societies. Going beyond a focus on racial and
ethnic groups, investigators have tested the theory with participants of
varying ages and with target groups as diverse as elderly, physically
disabled, and mentally ill participants. Contact studies also have used
a wide variety of research methods and procedures, including archival
research (e.g., Fine, 1979), field studies (e.g., Deutsch & Collins,
1951), laboratory experiments (e.g., Cook, 1969, 1978), and surveys
(e.g., Pettigrew, 1997; Sigelman & Welch, 1993). In addition to
spanning many disciplines, contact theory has been usefully applied to
a host of pressing social issues ranging from the racial desegregation
of schools (Pettigrew, 1971) and the resolution of ethnopolitical
conflicts (Chirot & Seligman, 2001) to explaining regional differences
in prejudice (Wagner, van Dick, Pettigrew, & Christ, 2003) and the
educational mainstreaming of physically and mentally disabled chil-
dren (Harper & Wacker, 1985; Naor & Milgram, 1980).
Past Reviews of the Intergroup Contact Literature
Past reviews of this vast literature have often reached conflicting
conclusions regarding the likely effects of intergroup contact.
Numerous reviews show general support for contact theory, sug-
gesting that intergroup contact typically reduces intergroup preju-
dice (Cook, 1984; Harrington & Miller, 1992; Jackson, 1993;
Patchen, 1999; Pettigrew, 1971, 1986, 1998). However, other
reviews reach more mixed conclusions. Amir (1969, 1976) con-
ceded that contact under optimal conditions tends to reduce prej-
udice among participants, but he stressed that these reductions in
prejudice may not generalize to entire outgroups. Moreover, Amir
(1976) noted that contact under unfavorable conditions “may in-
crease prejudice and intergroup tension” (p. 308). Likewise,
Forbes (1997), a political scientist, concluded that intergroup con-
tact often lowers prejudice at the individual level of analysis but
fails to do so at the group level of analysis. Hence, he argued that
contact can cure individual prejudice but not group conflict.
1
Stephan (1987) acknowledged that intergroup contact has the
potential to reduce prejudice, but he emphasized the complexity
involved in the link between intergroup contact and prejudice. For
example, characteristics of the contact setting, the groups under
study, and the individuals involved may all contribute to enhancing
or inhibiting contact’s effects (see also Patchen, 1999; Pettigrew,
1998; Riordan, 1978).
Additional reviews have been more critical regarding the poten-
tial for contact to promote positive intergroup outcomes. Ford
(1986) examined 53 papers (from six journals) on contact. He
found support for the contact hypothesis to be, at best, “premature”
and that the research presented in these papers was “grossly
insufficient in representing the various settings of daily life” (Ford,
1986, p. 256). McClendon (1974) suggested that “contact research
has been rather unsophisticated and lacking in rigor” (p. 47) and
concluded that this body of work “would not lead [one] to expect
a widespread reduction in prejudice” (p. 52).
Such conflicting views regarding the effects of contact have led
some social psychologists to discard contact theory. Indeed, as
Hopkins, Reicher, and Levine (1997) asserted, some believe that
“the initial hopes of contact theorists have failed to materialize” (p.
306). However, three major shortcomings of these past reviews
may account for their divergent conclusions.
Incomplete Samples of Relevant Papers
Whereas there have been literally dozens of partial reviews of
the contact literature, we are not aware of any review of this vast
literature that attempts to encompass the entire relevant research
base. Instead, past reviews have typically been restricted to a
particular set of groups, such as racial or ethnic groups (e.g.,
Patchen, 1999), or a particular contact setting, such as interracial
housing (e.g., Cagle, 1973) or schools (e.g., Carithers, 1970).
Further examination also reveals that these reviews covered a
mean of less than 60 research articles each, compared with the
hundreds of studies that comprise the contact research literature.
Thus, past reviews offer only limited views regarding the effects of
intergroup contact.
Absence of Strict Inclusion Rules
With no inclusion rules, these previous reviews used sharply
contrasting definitions of intergroup contact. For example, some
reviews included studies that used intergroup proximity, rather
than established contact, as the independent variable. This proce-
dure may contribute considerable error to the analysis and obscure
the test of contact’s influence on prejudice.
1
Many social psychologists would take issue with Forbes’s distinction.
If reductions in prejudice generalize broadly from contact, the group level
of analysis is necessarily involved (Brown & Hewstone, 2005).
752 PETTIGREW AND TROPP
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Nonquantitative Assessments of Contact Effects
Moreover, none of the previous reviews used fully quantitative
assessments of contact effects. Instead, authors of past reviews
have tended to offer subjective judgments of the contact–prejudice
relationship that are based on their own readings of a subset of the
research literature. Although this approach can be useful, selection
biases and differing interpretations of the literature limit the ability
to reach definitive conclusions about contact’s effects. Thus, quan-
titative approaches to research synthesis are preferred, as they
provide a means for examining replicable patterns of effects across
the full accumulation of relevant studies (Johnson & Eagly, 2000;
Rosenthal, 1991).
Given these limitations of past reviews and the diverse nature of
contact research, the evaluation of this literature requires a meta-
analytic approach. Yet, to our knowledge, no investigators have
conducted such an analysis of this vast and rich research literature.
Thus, a central goal of the present research was to assess the
overall effect between intergroup contact and prejudice on the
basis of the population of empirical studies that constitute the
research literature of the 20th century. With a quantitative means
of analyzing a far greater number of relevant studies chosen by
strict inclusion rules, we aim to determine more conclusively than
past reviews the overall relationship between intergroup contact
and prejudice.
The present article reports on such an effort, utilizing 515
individual studies with 713 independent samples and 1,383 non-
independent tests. Combined, 250,089 individuals from 38 nations
participated in the research. Along with including more than 300
additional studies, this work extends an earlier preliminary analy-
sis, presented in Pettigrew and Tropp (2000), in several important
theoretical and empirical directions.
Testing and Reinterpreting Allport’s Optimal Conditions
Whereas intergroup contact theory has traditionally held that
Allport’s optimal conditions are essential, we propose that All-
port’s conditions facilitate contact’s reduction of intergroup prej-
udice. Social psychology has shown repeatedly that greater expo-
sure to targets can, in and of itself, significantly enhance liking for
those targets (Bornstein, 1989; Harmon-Jones & Allen, 2001; Lee,
2001; Zajonc, 1968; see also Homans, 1950). Moreover, studies
with social targets have shown that the enhanced liking that results
from exposure can generalize to greater liking for other related, yet
previously unknown, social targets (Rhodes, Halberstadt, & Braj-
kovich, 2001). Applying this work to intergroup contact research,
the mere exposure perspective suggests that, all things being equal,
greater contact and familiarity with members of other groups
should enhance liking for those groups. Thus, in the present
analysis, we test whether intergroup contact is associated with less
prejudice even when Allport’s conditions are not established in the
contact situation, as well as whether these conditions significantly
enhance the degree to which contact promotes positive intergroup
outcomes.
Extending our earlier, preliminary analysis (Pettigrew & Tropp,
2000), we examine these issues in three ways. Initially, we use a
global indicator of Allport’s conditions: structured programs de-
signed to achieve optimal conditions. We test whether including
this indicator in the contact situation is necessary to produce
positive intergroup outcomes and whether it typically enhances the
positive effects of contact. To check for the consistency of these
effects, we then compare the results for our full sample with those
subsets of cases that either do or do not involve racial and ethnic
contact. In addition, for the subset of 134 samples that feature a
structured situation boasting many of Allport’s proposed condi-
tions, we rate each condition separately and examine the average
effect sizes associated with each condition.
Ruling Out Alternative Explanations for
Contact–Prejudice Effects
The present analysis also includes additional tests that allow us
to test more effectively four alternative explanations for contact–
prejudice effects.
Participant Selection and the Causal Sequence Problem
A potential participant selection bias could limit the interpreta-
tion of many studies of intergroup contact (Pettigrew, 1998).
Instead of optimal contact reducing prejudice, the opposite causal
sequence could be at work. Prejudiced people may avoid, and
tolerant people may seek, contact with outgroups.
Statistical methods borrowed from econometrics allow research-
ers to compare roughly the reciprocal paths (contact lowers prej-
udice vs. prejudice decreases contact) with cross-sectional data. As
shown directly in other research (e.g., Herek & Capitanio, 1996),
these methods reveal that prejudiced people do indeed avoid
intergroup contact. But the path from contact to reduced prejudice
is generally much stronger (Butler & Wilson, 1978; Pettigrew,
1997; Powers & Ellison, 1995; Van Dick et al., 2004). Longitu-
dinal studies also have revealed that optimal contact reduces
prejudice over time (e.g., Eller & Abrams, 2003, 2004; Levin, van
Laar, & Sidanius, 2003), even when researchers have eliminated
the possibility of participant selection (e.g., Sherif, 1966). Thus,
various methods suggest that, although both sequences operate, the
more important effect is that of intergroup contact reducing
prejudice.
2
In the present analysis, we respond to this concern by concen-
trating on intergroup situations that severely limit choice (see Link
& Cullen, 1986). By eliminating the possibility of initial attitudes
leading to differential contact, such research provides a clearer
indication of the causal relationship between intergroup contact
and prejudice. We make use of this method in our analyses by
coding samples for the extent to which participants could choose to
engage in the contact. Of course, experiments limit choice through
randomization of subjects to condition. But our choice rating is not
simply a surrogate variable for experimental designs. Almost half
of our quasi-experimental samples, and even 31 samples with
weaker designs, allowed no participant choice.
The File Drawer: Publication Bias Problem
Another major potential threat to the interpretation of our results
pertains to the file drawer problem that besets all literature reviews
(Begg, 1994; Rosenthal, 1991). Published studies may form a
2
See Irish (1952) and Wilson (1996) for other methods that reach the
same conclusion.
753
META-ANALYTIC TEST OF INTERGROUP CONTACT THEORY
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biased subset of the relevant studies actually conducted, as the
statistical significance of a study’s results may influence the prob-
ability of it being submitted and published. Indeed, investigators
have demonstrated this bias in both the social science and medical
research literatures (Coursol & Wagner, 1986; Dickersin, 1997;
Dickersin, Min, & Meinert, 1992; Easterbrook, Berlin, Gopalan, &
Mathews, 1991; Glass, McCaw, & Smith, 1981; Lipsey & Wilson,
1993; Rotton, Foos, Van Meek, & Levitt, 1995; Shadish, Doherty,
& Montgomery, 1989; Smith, 1980; Sommer, 1987). Researchers
may be reluctant to send in studies with modest or countertheory
findings. And journals may publish studies with large effects and
reject studies with small or no effects. Thus, reviews may system-
atically overestimate effect sizes, as they rely heavily on published
work.
Estimating publication bias is a difficult task, but numerous
investigators have directed considerable attention to the problem in
recent years. The many tests for bias are based on particular
assumptions and consequently have their unique strengths and
shortcomings (Sutton, Song, Gilbody, & Abrams, 2000). In the
present research, we investigated this potentially serious problem
from multiple directions by using a variety of tests and thereby
extend our analysis beyond our initial findings (Pettigrew &
Tropp, 2000).
First, following Rosenthal (1991), we calculated a fail-safe
index. Though often criticized, this technique is one of the most
widely used methods for crudely gauging publication bias (Sutton,
Song, et al., 2000). It reveals how many missing studies that
average no relationship between contact and prejudice (Z⫽.00)
would be required to raise the significance levels above the .05 or
.01 level of confidence. But this focus is the index’s basic weak-
ness. It assumes that the missing studies will average to no effect.
Thus, the fail-safe index underestimates publication bias to the
extent that the average of the missing studies runs counter to the
hypothesis being tested.
Other rough, initial tests involve the relationship between sam-
ple size and effect size. We can test for the possibility of publi-
cation bias in several ways. Two preliminary methods are simply
to correlate sample sizes with effect sizes and to develop a funnel
graph consisting of a scatter diagram with the two variables (Light
& Pillemer, 1984). A nonsignificant correlation and a symmetrical
funnel graph each suggest minimal publication bias.
The funnel graph in turn relates to two additional methods of
testing for publication bias. The “trim-and-fill” technique detects
potentially missing studies by adjusting for funnel plot asymmetry
(Duval & Tweedie, 2000a, 2000b; Sutton, Duval, Tweedie,
Abrams, & Jones, 2000). The general linear model approach of
Vevea and Hedges (1995) focuses on the absence of small studies.
It assumes that random effects are distributed normally and that the
survival probability of a given study can be described by a stop
function around such critical probability points as .05 and .01. It
should be noted, however, that such funnel graph methods tend to
overestimate publication bias (Sterne & Egger, 2000).
Finally, we also tested directly whether this particular literature
suffers from the file drawer problem. We compared the effect sizes
between intergroup contact and prejudice from published sources
(journals and books) and unpublished sources (graduate disserta-
tions, conference papers, and other unpublished manuscripts). This
method also makes a critical assumption, namely, that the unpub-
lished studies that we uncovered constitute a random sample of
unpublished research on the topic. For this and other reasons, the
power of this direct approach, as Begg (1994) noted, is “directly
proportional to the assiduousness of the search” (p. 405). Thus, we
expended great effort in obtaining as many unpublished manu-
scripts as possible. We uncovered 88 unpublished contact studies,
70% of which are graduate dissertations.
The Generalization of Effects Problem
A third issue concerns the generalization of contact effects—an
issue not fully addressed by Allport (1954; see Pettigrew, 1998).
Critics generally concede that intergroup contact often leads to
improved attitudes among the participants. But the critical question
is whether these altered attitudes generalize beyond the immediate
situation to new situations, to the entire outgroup, or even to
outgroups not involved in the contact (Pettigrew, 1997, 1998).
Such generalization is crucial to the useful application of contact
theory. If the changes wrought by contact are limited to the
particular situation and the immediate outgroup participants, the
practical value of the theory is obviously severely restricted.
Hence, we examine whether each test of the link between contact
and prejudice involves some generalization beyond the immediate
contact situation and participants.
Rigor of Research Studies
A final test of validity involves the relationship between indices
of research rigor and the magnitude of the contact–prejudice effect
sizes. If less rigorous research was largely responsible for the
average effect size between contact and prejudice, we would
hesitate to accept it as established. But if the more rigorous studies
produce stronger contact effects, it would lend credibility to the
results. Meta-analysts have checked on this issue with a variety of
generally accepted indices of rigor. We used five rated variables:
type of study, type of contact measure, type of control group,
quality of the contact measure, and quality of the prejudice
measure.
Study and Participant Characteristics as Moderators of
Contact–Prejudice Effects
In addition to examining variables of theoretical and method-
ological interest, we also identify and analyze other possible
sources of variability in the contact–prejudice relationship. With
our extensive set of contact studies, we consider a range of study
and participant characteristics that may moderate the relationship
between contact and prejudice. In addition to the aforementioned
indicators of research rigor, we examine contact–prejudice effects
in relation to the date of publication, the study setting, and the
geographical area in which the research was conducted. We also
inspect contact–prejudice effects in relation to participant charac-
teristics such as age, gender, and the types of groups involved in
the contact.
Method
Inclusion Criteria
We define intergroup contact as actual face-to-face interaction between
members of clearly defined groups. From this definition flow several
inclusion criteria.
754 PETTIGREW AND TROPP
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Criterion 1. Because our focus is on the relationship between inter-
group contact and prejudice, we consider only those empirical studies in
which intergroup contact acts as the independent variable and intergroup
prejudice as the dependent variable. Eligible studies include both experi-
mental studies that test for the effects of contact on prejudice and corre-
lational studies that use contact as a correlate or predictor of prejudice.
Criterion 2. Only research that involves contact between members of
discrete groups is included. This rule ensures that we examine intergroup
outcomes of contact rather than interpersonal outcomes.
Criterion 3. The research must report on some degree of direct inter-
group interaction.For inclusion, the intergroup interaction must be ob-
served directly, reported by participants, or occur in focused, long-term
situations where direct contact is unavoidable (e.g., small classrooms).
This third rule eliminates a variety of studies that are often cited in
previous summaries of contact research. In particular, it excludes research
that uses rough proximity or group proportions to infer intergroup inter-
action. As Festinger and Kelley (1951) made clear a half century ago,
proximity is a necessary but not sufficient condition for social contact. One
cannot assume contact from the opportunity for contact, such as living in
an intergroup neighborhood with no report of actual interaction (e.g.,
Hamilton & Bishop, 1976; Hood & Morris, 2000). Our rare exceptions
carefully demonstrated that the intergroup proximity correlated highly with
actual contact, as it did in Deutsch and Collins’s (1951) famous interracial
housing study.
This rule also omits investigations that attempt to gauge contact with
indirect measures such as information about an outgroup (e.g., Taft, 1959).
We also excluded studies that asked about attitudes toward contact, unless
the researchers directly linked such indicators to prior intergroup experi-
ence (e.g., Ford, 1941). In addition, this rule eliminates research that
categorizes participants into groups that do not directly interact, as is the
case in many minimal group studies (e.g., Otten, Mummendey, & Blanz,
1996; Tajfel, Billig, Bundy, & Flament, 1971).
This inclusion rule is important and differs from many prior reviews of
this literature. The extensive research by Catlin (1977) on the impact of
interracial dormitories at the University of Michigan illustrates the rule’s
operation. Catlin found only small relationships between interracial living
and prejudice, but we did not enter these aggregate results into our files.
However, Catlin also checked on the racial attitudes of White students who
reported on whether they had Black acquaintances. We used these results
because cross-racial “acquaintance” directly specifies face-to-face contact.
Criterion 4. The prejudice dependent variables must be collected on
individuals rather than simply as a total aggregate outcome. Thus, studies
concerning the relationships between contact and prejudice were included
only if they used individuals as the unit of analysis such that prejudice
scores could be examined in relation to individuals’ contact experiences.
Locating Relevant Studies
To locate studies that meet our inclusion rules, we used a wide variety
of search procedures. First, we conducted computer searches of the psy-
chological (PsychLIT and PsycINFO), sociological (SocAbs and Socio-
File), political science (GOV), education (ERIC), dissertation (UMI Dis-
sertation Abstracts), and general research periodical (Current Contents)
abstracts published through December 2000. These searches used 54 dif-
ferent search terms ranging from single words (e.g., contact,interracial)to
combined terms (e.g., age ⫹intergroup contact,disabled ⫹contact).
Across the various databases, we conducted three types of searches: by title
words, by keyword, and by subject. Following the “descendancy approach”
described by Johnson and Eagly (2000), we used the Social Sciences
Citation Index to check on later citations of seminal contact studies.
To reach the “invisible college” of intergroup contact researchers, we
wrote personal letters to researchers who published relevant research and
sent for pertinent unpublished conference papers. Reference lists from
located studies and previous reviews proved a rich source. We also repeat-
edly requested relevant materials through e-mail networks of social psy-
chologists in Australia, Europe, and North America. These methods
yielded 526 papers (reporting 515 studies), written between 1940 and the
end of 2000, that meet our inclusion criteria. These studies yield 713
independent samples and 1,383 individual tests. Most of the studies com-
prise journal articles published during the past 3 decades (median year of
publication ⫽1986). Slightly more than half of the samples (51%) focused
on racial or ethnic target groups. In addition to conducting analyses for the
full set of samples, we conducted analyses with this subset exclusively as
well as with the remaining subset that used nonracial and nonethnic targets.
Whereas 38 different countries contribute data, the United States provides
71% of the studies. Survey and field research constitute 71% of the studies,
quasi-experiments 24%, and true experiments 5%. The research typically
used college students or adult participants of both sexes who reported on
their intergroup contact.
Several prototypical studies predominate. The principal prototype is a
questionnaire or survey study. This research uses retrospective reports of
personal contact with the outgroup. A quite different prototype uses ex-
periments that involve an intergroup contact intervention and checks to see
whether the treatment influences the participants’ prejudice. A final pro-
totype uses various quasi-experimental designs. These studies mirror the
experimental research, but they lack randomization of participants to
condition in between-groups designs. These three basic prototypes shaped
the research moderators and other techniques that we use in the
meta-analysis.
Computation and Analysis of Effect Sizes
Whereas most past meta-analytic studies in social psychology have used
fixed effects models (Johnson & Eagly, 2000), the nature of the contact
research literature makes a random effects model more appropriate for our
analysis.
3
This model holds that part of the differences in effects across
studies is essentially random and involves unidentifiable sources (Hedges,
1994; Hedges & Olkin, 1985; Lipsey & Wilson, 2001; Mosteller & Colditz,
1996; Raudenbush, 1994; Rosenthal, 1995). As Cook et al. (1992) con-
cluded, this approach is “particularly attractive when considering (1) stud-
ies that are quite heterogeneous, (2) treatments that are ill-specified, and/or
(3) effects that are complex and multidetermined” (p. 310). Because all
three of these conditions hold for much of the intergroup contact literature,
we used a random effects model. An additional advantage of using the
random effects approach is that it allows our findings to be generalized to
other contact studies beyond those used in our analysis. This choice is a
conservative procedure that markedly reduces the probability levels
obtained.
We report Pearson’s ras our indicator of effect size throughout our
analysis. If the studies do not report this measure, we derived it from other
statistics by using the conversion formulas provided by Johnson (1993). A
negative mean effect size indicates that greater intergroup contact is
associated with lower prejudice.
If researchers reported a relationship as nonsignificant, we conserva-
tively assigned a value of .00 for the effect size. Rosenthal (1995) has
questioned this procedure as too conservative and likely to yield mislead-
ingly low effect size estimates. He has recommended that meta-analysts
conduct principal analyses both with and without these studies—a proce-
dure that we follow in our summary analyses, although only 17 (2.4%) of
our samples are involved. We also follow the suggestion of Johnson and
Eagly (2000) and omit these samples when we fit our moderator models to
the effect sizes. The small number of samples involved means that they
affect only slightly the total effect size.
3
Although a fixed effects approach was used in our preliminary analyses
(Pettigrew & Tropp, 2000), we have now revised our analytic strategy to
use a random effects model.
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We used two primary units of analysis: independent samples and indi-
vidual tests. The use of independent samples is helpful because they are
more numerous than are studies and allow detailed comparisons. Tests are
especially numerous and allow us to compare effect sizes for even more
detailed factors. But multiple tests reported for a single sample violate
assumptions of independence, and we have an average of almost two tests
per sample. Thus, we used tests as our unit of analysis for just one potential
moderator (type of generalization) that can be measured at this level only.
For each category of effect sizes, we calculated the mean effect size,
weighted for sample size. Thus, the larger and more reliable samples
contribute proportionately more to the mean. The homogeneity of each set
of effect sizes was examined by calculating the homogeneity statistic Q
that has an approximate chi-square distribution with k⫺1 degrees of
freedom, where kis the number of effect sizes (Hedges & Olkin, 1985).
Weighting by sample size, however, posed a problem. Five especially
large studies constitute only 1% of our study file but 28% of the total
number of participants. To keep these few studies from having such
enormous influence on the results, we capped their study sizes at 5,000,
sample sizes at 3,000, and tests at 2,000 participants. Whereas these caps
are arbitrary, only seven samples and 17 tests are involved. As Table 1
shows, omitting the studies that report only “nonsignificant” effects and
applying these sample size caps results in only trivial differences of the
average effect size across studies, samples, and tests for both fixed effects
models and random effects models.
Ratings for Studies and Samples
We rated and recorded 16 separate variables at their appropriate levels of
analysis. Tables 2–5 and 11–12 provide the particular categories used for
the ratings of each of these variables, and the Appendix supplies the ratings
for each sample.
Ratings of study characteristics include the date and source of publica-
tion and whether it used a within- or between-subjects design. In addition,
we rated research quality in several ways. We established ratings for the
type of study (e.g., survey, quasi-experiment, or experiment). We also rated
the type of control group used in studies with between-subjects designs
(e.g., no, some, or considerable earlier contact with the outgroup). We
found that many of these control groups actually had prior contact with the
target group; such “leakage” obviously renders these groups as less ade-
quate controls. Another indicator of research rigor checked on the type of
contact measure used (e.g., whether the contact was assumed from long-
term situations in which contact was unavoidable, reported by the partic-
ipants, or directly observed by the researchers). The quality of the measures
for contact and prejudice was rated according to whether they consisted of
either a single item, a multi-item scale with unreported or low reliability
(
␣
⬍.70), a multi-item scale with high reliability (
␣
ⱖ.70), an experi-
mental manipulation (for contact indicators only), or other forms.
The ratings of participant characteristics included age, sex, and geo-
graphical area of the study and the kind of target group involved (e.g.,
racial or ethnic, elderly, mentally ill). Additional ratings focused on the
contact situation, including the setting of the contact (e.g., educational,
residential, laboratory) and whether participants had any choice in partic-
ipating in the contact. Another rating concerned the type of generalization
involved (e.g., to outgroup members within the situation, to the whole
outgroup, across situations, or to other outgroups).
Two independent judges achieved kappas above .80 for all ratings of
these variables (after we collapsed error-prone adjacent rating categories).
Thus, if a four-category variable had a disproportionately large number of
Table 1
Summary of Effect Sizes for Contact and Prejudice
Level of analysis r95% CL ZkN
Studies
All studies
Fixed ⫺.225 ⫺.23/⫺.22 ⫺113.96*** 515 250,089
Random
a
⫺.205 ⫺.22/⫺.19 ⫺27.12*** 515 250,089
With data corrections
b
Fixed ⫺.209 ⫺.21/⫺.20 ⫺94.92*** 500 202,742
Random
a
⫺.210 ⫺.22/⫺.20 ⫺28.93*** 500 202,742
Samples
All samples
Fixed ⫺.225 ⫺.23/⫺.22 ⫺114.15*** 713 250,089
Random
a
⫺.210 ⫺.22/⫺.20 ⫺31.22*** 713 250,089
With data corrections
b
Fixed ⫺.210 ⫺.21/⫺.21 ⫺94.96*** 696 199,830
Random
a
⫺.215 ⫺.23/⫺.20 ⫺32.24*** 696 199,830
Tests
All tests
Fixed ⫺.218 ⫺.22/⫺.22 ⫺154.96*** 1,383 494,912
Random
a
⫺.214 ⫺.22/⫺.20 ⫺39.83*** 1,383 494,912
With data corrections
b
Fixed ⫺.204 ⫺.21/⫺.20 ⫺127.15*** 1,365 381,723
Random
a
⫺.217 ⫺.23/⫺.21 ⫺38.31*** 1,365 381,723
Note. These analyses were conducted with Fisher’s z-transformed rvalues. Mean effects and confidence limits
listed in this table have been transformed back to the r-metric from the z-transformed estimates obtained in these
analyses. r⫽correlation coefficient representing the mean effect size; 95% CL ⫽the 95% confidence limits of
r;Z⫽ztest for the mean effect sizes; p⫽probability of ztest; k⫽number of samples associated with the mean
effect size; N⫽total number of participants.
a
Random effects variance components (based on Fisher’s z-transformed rvalues) ranged from .019 to .024 for
studies and samples and from .030 to .036 for tests.
b
Data corrections involved capping especially large numbers of participants (5,000 for studies, 3,000 for
samples, 2,000 for tests) and excluding 15 nonsignificant studies from the analysis.
*** p⬍.001.
756 PETTIGREW AND TROPP
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errors at Categories 2 and 3, we combined Categories 2 and 3 to form a
three-category rating. The median kappa for all ratings was .86. All
discrepancies between the raters were resolved through further discussion.
We also conducted ratings to examine whether the contact situation
approached the optimal context specified by Allport’s key conditions. We
began by attempting to rate each of Allport’s four conditions individually
for each study. However, this procedure proved impossible given the lack
of information about situational characteristics provided by the vast ma-
jority of our 515 studies. Reliable ratings were largely unattainable for all
but a subset of the studies that directly addressed the characteristics of the
contact.
Consequently, we conducted comparisons by using a global measure of
Allport’s contentions. This procedure actually offers a more direct test of
the original theory, as Allport advanced his four conditions as a necessary
package for positive contact effects rather than as a listing of variables that
must be considered individually. In particular, we rated for all samples
whether the contact situations involved structured programs designed to
approximate Allport’s optimal conditions.
4
Next, for the 134 samples with contact in the context of structured
programs, we attempted to conduct more fine-grained ratings for each of
Allport’s conditions. Though these research studies often implemented the
conditions together, we used “yes” and “no” ratings to discern whether the
program clearly and explicitly (a) focused participants on common goals,
(b) emphasized a cooperative environment, (c) presented the groups with
equal status, and (d) demonstrated authority sanction for the contact.
Ratings of these variables by two independent judges yielded kappas
between .76 and .97, with a median kappa of .84.
Results
Examining the Overall Pattern of Effects: Does
Intergroup Contact Reduce Prejudice?
Table 1 reveals the inverse association between intergroup con-
tact and prejudice for all studies, samples, and tests for both fixed
effects analyses and random effects analyses. The mean estimates
for the contact–prejudice effect size are consistent across units of
analysis, data corrections, and types of analysis. With random
effects analysis, the 515 studies, 713 samples, and 1,383 tests yield
mean rs that range from ⫺.205 to ⫺.214. Our data corrections of
eliminating the studies, samples, and tests that did not provide
precise effect sizes and capping the largest studies, samples, and
tests made little difference. It is these files—with the 17 “nonsig-
nificant” samples removed and the largest samples and tests
capped—that we use in the following analyses. The fixed effects
analyses and random effects analyses show similar mean effect sizes,
although, as expected, the Zs of the random effects analyses are
sharply reduced. We use the random effects model for all subsequent
analyses. In sum, the initial answer to our query is that intergroup
contact generally relates negatively and significantly to prejudice.
5
Though in most empirical contexts, psychologists would con-
sider this effect size to be “small” to “medium” in magnitude
(Cohen, 1988), we should emphasize several points. First, given
the large number of samples, the effect is highly significant (p⬍
.0001). Second, 94% of the samples show an inverse relationship
between contact and prejudice. A scatter plot of the effect sizes by
sample size reveals that the effects center around an average rof
approximately ⫺.21, which corresponds closely to the overall
mean effect size (see Figure 1). Finally, we later note markedly higher
mean effect sizes for subsets of samples from rigorous studies.
At the same time, these effect sizes are highly heterogeneous
across the samples (Q
w
(695) ⫽4,990.44, p⬍.0001). Indeed, even
when we remove the results of one fifth of the samples that are the
largest outliers, highly significant heterogeneity remains. Such
vast heterogeneity is, of course, precisely what intergroup contact
theory predicts. These studies are highly diverse as to research
methods, participants, situations, and targets, all of which are
potential moderators of the link between contact and prejudice. As
with most meta-analyses, the ultimate thrust of our analysis is not
so much the gross effect sizes but more so the moderating vari-
ables that suggest the conditions under which intergroup contact
reduces prejudice. Before turning to this task, however, we first
test for four threats to validity that provide alternative explanations
for the findings shown in Table 1.
Tests for Threats to Validity
The causal sequence problem: Examining choice to engage in
contact. The negative link between contact and prejudice may
largely reflect the avoidance of contact by prejudiced people. If
this is so, the effect sizes for those studies that provided partici-
pants with choice as to whether to engage in the intergroup contact
4
As a secondary, indirect indicator of Allport’s conditions, we recorded
whether cross-group friendship served as the measure of contact. Friend-
ship typically involves cooperation and common goals as well as repeated
equal-status contact over an extended period and across varied settings
(Pettigrew, 1997). Many researchers have pointed to the role intimacy can
play in reducing prejudice (Amir, 1976; Patchen, 1999; Williams, 1947),
such that close, cross-group relationships may be especially likely to
promote positive intergroup outcomes. Thus, together with a focus on
Allport’s optimal conditions for contact, we also examined the effects of
cross-group friendships.
5
With a more stringent criterion for examining contact effects, we
conducted supplementary analyses that excluded the 39 cases in which
some degree of intergroup contact was assumed. Mean effect sizes for the
remaining cases were ⫺.209 for studies (⫺.214 with data corrections) and
⫺.221 for samples (⫺.220 with data corrections).
Figure 1. Scatter plot of mean contact–prejudice effect sizes (r)in
relation to sample size.
757
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should reveal larger effect sizes than do those that provided no
such choice. In other words, only the studies with choice risk
having a participant selection bias. Table 2 provides the results
relevant to this issue.
Note that the no-choice samples provide a significantly larger
mean effect size (mean r⫽⫺.280) than do those samples in which
participants had some choice (mean r⫽⫺.190), Q
B
(1) ⫽20.58,
p⬍.0001, or full choice (mean r⫽–.218), Q
B
(1) ⫽8.98, p⬍.01.
The fact that the no-choice studies were, in general, of higher
quality magnifies this difference between these three types of
studies. The basic correlation between choice and effect size, r⫽
⫺.086, p⬍.05, becomes nonsignificant, r⫽.005, p⫽.89, when
we partial out four indicators of research quality.
6
But the key
finding is that the studies that allow the participant selection bias
to operate do not typically yield the larger effect sizes that would
be predicted by participant selection bias.
The file drawer problem: The application of multiple tests.
First, we apply Rosenthal’s (1991) fail-safe index. According to
our uncorrected effect size estimate for all samples based on the
random effects model (see Table 1), it would require more than
1,200 missing samples that average no effect to erase the signifi-
cance of the intergroup contact and prejudice association at the 5%
level of confidence. This figure is considerably larger than the 713
samples uncovered by our intensive 6-year search. Next, we check
on publication bias by determining that the relationship between
sample sizes and effect sizes is not significant for either the
original set of 713 samples, r⫽⫺.02, p⫽.67, or the 696 samples
included in our analysis, r⫽.04, p⫽.33. Large samples provide
more reliable results, and this lack of a relationship between
sample size and effect size is a crude indicator of limited publi-
cation bias.
Figure 1 provides a scatter diagram using the two variables. The
graph roughly resembles a funnel, as is suggested by Light and
Pillemer (1984). Most important, the funnel is not sharply skewed,
and the mean effect remains approximately the same regardless of
sample size. Hence, the mean (r⫽⫺.216), median (r⫽⫺.205),
and mode (r⫽⫺.210) of the distribution of samples are similar.
The more symmetrical the funnel, the more it suggests that pub-
lication bias is not a major problem with this dataset.
Duval and Tweedie’s (2000a, 2000b) “trim-and-fill” method
was used to adjust for missing studies by focusing on funnel plot
asymmetry. With Zas the effect size and with the random effects
model, Duval used her technique to estimate that about 72 (10.3%)
samples were missing. When she filled in for these missing data,
the effect size estimate increased to a Zof ⫺.245, with 95%
confidence limits of ⫺.258 to ⫺.231. This result suggests a mean
effect that is comparable to those reported in Table 1.
Contradicting these results in part is an analysis that uses Vevea
and Hedges’s (1995) general linear model approach. Vevea kindly
conducted this analysis for us and found that the sample file was
missing numerous small studies with small effects. After adjust-
ment for these cases, his method did not find a significant overall
relationship between contact and prejudice (Z⫽⫺.02, ns). How-
ever, for those 118 samples with between-groups designs and
strong controls, the adjusted effect size did reach statistical signif-
icance (mean Z⫽⫺.109, one-tailed, p⬍.02).
Finally, as a direct test for publication bias, we compare (in
Table 2) the negative mean effect sizes between intergroup contact
and prejudice from published sources (journals and books) and
unpublished sources (dissertations, conference papers, and other
unpublished manuscripts). Note that the unpublished work has a
6
The four rated variables for research quality included ratings of study
type, quality of the contact and prejudice measures, and the quality of the
control groups, as detailed later in the text.
Table 2
Testing Threats to Validity for Contact–Prejudice Effect Sizes
Variable r95% CL ZkNQ
B
Participant choice (samples)
No choice ⫺.280 ⫺.31/⫺.25 ⫺16.13*** 116 15,133
Some choice ⫺.190 ⫺.21/⫺.17 ⫺18.45*** 279 95,267
Full choice ⫺.218 ⫺.24/⫺.20 ⫺21.51*** 301 89,430
Between-classes effect 21.52***
Publication source (samples)
Published ⫺.211 ⫺.23/⫺.20 ⫺28.38*** 577 162,085
Unpublished ⫺.237 ⫺.27/⫺.21 ⫺14.51*** 119 37,745
Between-classes effect 2.17
Type of generalization (tests)
Within situation ⫺.231 ⫺.26/⫺.20 ⫺13.03*** 152 31,554
Across situations ⫺.244 ⫺.33/⫺.15 ⫺5.20*** 17 7,553
Whole outgroup ⫺.213 ⫺.22/⫺.20 ⫺36.08*** 1,164 333,608
To other outgroups
a
⫺.190 ⫺.28/⫺.10 ⫺3.89*** 18 3,396
Between-classes effect 1.61
Note. These analyses were conducted with Fisher’s z-transformed rvalues. Mean effects and confidence limits
listed in this table have been transformed back to the r-metric from the z-transformed estimates obtained in these
analyses. Random effects variance components (based on Fisher’s z-transformed rvalues) ranged from .022 to
.023 for analyses based on samples and was .032 for the analysis based on tests. As in Table 1, r⫽correlation
coefficient representing the mean effect size; 95% CL ⫽the 95% confidence limits of r,Z⫽ztest for the mean
effect sizes; p⫽probability of ztest; k⫽number of samples associated with the mean effect size; N⫽total
number of participants; Q
B
⫽between-classes test of homogeneity.
a
Homogeneity can be obtained with less than 20% of the cases trimmed.
*** p⬍.001.
758 PETTIGREW AND TROPP
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slightly larger mean effect size between contact and prejudice
(mean r⫽⫺.237) than does published work (mean r⫽⫺.211)
although this difference is not significant, Q
B
(1) ⫽2.17, p⫽.14.
Thus, all but one of our indicators suggest that a file drawer
publication bias does not pose a major threat to the results of Table
1. However, the one notable exception—the results of Vevea and
Hedges’s (1995) test—lends caution in interpreting the following
findings. But even this test uncovers a significant relationship
between intergroup contact and diminished prejudice in studies
that use between-groups designs with strong controls.
The generalization of effects problem. Do contact effects ex-
tend beyond the immediate situation? The summary results shown
in Table 2 provide an affirmative answer. A total of 152 tests
examined effects within the contact situation and focused exclu-
sively on outgroup members directly involved in the contact. As
shown in Table 2, their average effects correspond closely with the
mean effects of our full analysis (mean r⫽⫺.231).
Most of the tests, however, concerned generalized effects of
contact on prejudice toward the entire outgroup. These 1,164 tests
provide an average effect that is not significantly weaker than the
effects obtained for individual outgroup members within the con-
tact situation (mean r⫽⫺.213), Q
B
(1) ⫽.94, p⫽.33. In addition,
only 17 of the tests, drawn from nine samples, checked on con-
tact’s effects on prejudice across situations (but see Gathing, 1991;
Nesdale & Todd, 1998, 2000). These few tests rendered consid-
erable generalization (mean r⫽⫺.244). Finally, 18 additional
tests checked on contact effects on prejudice toward outgroups not
involved in the contact. This rarely considered form of generali-
zation also operates (mean r⫽⫺.190).
7
Taken together, these
results suggest a far wider generalization net of contact effects than
is commonly thought.
Research rigor: Examining multiple tests. An additional test
of validity involves the relationship between indices of research
rigor and the magnitude of the contact–prejudice effect sizes.
Results from five rated variables reveal that greater research rigor
is routinely associated with larger effect sizes. Put differently, the
less rigorous studies sharply reduce the overall relationships ob-
served between contact and prejudice.
Study type. One measure of research rigor involves the type of
study. Table 3 shows that samples tested with true experiments
(mean r⫽⫺.336) yield significantly larger effects than do those
tested with either quasi-experiments (mean r⫽⫺.237), Q
B
(1) ⫽
6.72, p⬍.01, or surveys and field studies (mean r⫽⫺.204),
Q
B
(1) ⫽15.99, p⬍.001. Note that contact’s effects on prejudice
in experiments (r⫽⫺.336) approach what Cohen (1988) de-
scribed as a “large” effect size for psychological data (d⫽⫺.713).
In addition to demonstrating differences in effect sizes associated
with research rigor, this result is relevant to the causal sequence
problem discussed previously. True experiments, with their random
assignment of participants to condition, remove the possibility of a
selection bias operating in those who participate in intergroup contact.
Quality of control groups used. Another indicator of research
rigor concerns the quality of control groups used in the research
with between-subjects designs. Table 3 shows that for the samples
with between-subjects designs, the less contact the control group
had with the target outgroup prior to the study, the larger the mean
effect sizes. Thus, the samples with control groups that had no
7
We excluded 14 other tests from one study that attained even larger
effects because it used “intergroup friends” as its contact measure (Petti-
grew, 1997).
Table 3
Type of Study, Control Group, and Contact Measure as Moderators for Contact–Prejudice Effect
Sizes
Variable r95% CL ZkNQ
B
Type of study (samples)
Surveys and field studies ⫺.204 ⫺.22/⫺.19 ⫺26.53*** 492 180,386
Quasi-experiments
a
⫺.237 ⫺.27/⫺.21 ⫺15.64*** 168 16,497
Experiments
a
⫺.336 ⫺.40/⫺.27 ⫺9.94*** 36 2,947
Between-classes effect 18.51***
Type of control group (samples)
Within design ⫺.221 ⫺.24/⫺.20 ⫺23.58*** 365 116,091
No contact control ⫺.244 ⫺.27/⫺.21 ⫺15.60*** 119 33,817
Some contact control
a
⫺.209 ⫺.24/⫺.18 ⫺14.69*** 156 35,155
Extensive contact control
a
⫺.138 ⫺.18/⫺.09 ⫺5.96*** 56 14,767
Between-classes effect 15.78***
Type of contact measure (samples)
Observed contact
a
⫺.246 ⫺.27/⫺.22 ⫺19.50*** 249 25,247
Self-reported contact ⫺.210 ⫺.23/⫺.19 ⫺25.29*** 408 162,292
Assumed contact ⫺.132 ⫺.18/⫺.08 ⫺4.75*** 39 12,291
Between-classes effect 16.44***
Note. These analyses were conducted with Fisher’s z-transformed rvalues. Mean effects and confidence limits
listed in this table have been transformed back to the r-metric from the z-transformed estimates obtained in these
analyses. Random effects variance components (based on Fisher’s z-transformed rvalues) were .022 for each
analysis. r⫽correlation coefficient representing the mean effect size; 95% CL ⫽the 95% confidence limits of
r, Z ⫽ztest for the mean effect sizes; p⫽probability of ztest; k⫽number of samples associated with the mean
effect size; N⫽total number of participants; Q
B
⫽between-classes test of homogeneity.
a
Homogeneity can be obtained with less than 20% of the cases trimmed.
*** p⬍.001.
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prior outgroup contact (mean r⫽⫺.244) had a higher mean effect
than did samples with controls that had either some prior outgroup
contact (mean r⫽⫺.209), Q
B
(1) ⫽2.77, p⫽.09, or extensive
prior outgroup contact (mean r⫽⫺.138), Q
B
(1) ⫽10.71, p⫽
.001. In addition, samples with within-subject designs had an
average effect size (mean r⫽⫺.221) that did not differ signifi-
cantly from that of all between-subjects samples combined (mean
r⫽⫺.217), Q
B
(1) ⫽0.07, p⫽.79.
Type of contact measure. Table 3 shows differences in mean
effects between samples with contrasting contact measures. Sam-
ples with directly observed contact yield the highest mean effect
(mean r⫽⫺.246). Significantly smaller effects were obtained
from samples that used self-report measures of contact (mean r⫽
⫺.210), Q
B
(1) ⫽6.39, p⫽.01, or assumed contact from a close,
ongoing situation in which some degree of contact was unavoid-
able (mean r⫽⫺.132), Q
B
(1) ⫽11.82, p⬍.001.
8
Quality of contact and prejudice measures. The quality of the
contact and prejudice indicators is highly influential. Multiple-item
measures with low or unreported reliabilities render weaker effects
than do other measures. This finding is important because, as
shown in Table 4, contact researchers have often used these
measures. Moreover, for contact indicators, the samples tested
with reliable multiple-item measures or experimentally manipu-
lated contact (mean r⫽⫺.296) provide significantly larger effect
sizes than do those with other measures combined (mean r⫽
⫺.189), Q
B
(1) ⫽53.22, p⬍.0001. For prejudice indicators, the
samples tested with unreliable multiple-item measures provide
smaller effects (mean r⫽⫺.190) than does each of the other types
of measures: single items (mean r⫽⫺.233), Q
B
(1) ⫽2.89, p⬍
.09, reliable multi-item scales (mean r⫽⫺.246), Q
B
(1) ⫽16.38,
p⬍.0001, and other reliable measures of the dependent variables
(mostly high interrater reliability; mean r⫽⫺.293), Q
B
(1) ⫽6.60,
p⬍.01. Note also in Table 4 that the quality of the contact
measures is more closely related to the effect sizes than is the
quality of the prejudice measures.
Evaluating the Role of Allport’s Conditions
Having addressed the major threats to validity, we can proceed with
an investigation of more specific questions relevant to our research
goals. Of particular interest are tests of whether Allport’s stated
conditions contribute to positive contact outcomes and whether such
conditions are necessary for positive outcomes to occur.
Global test: Structured optimal contact. Our global predictor
involves the issue of whether the contact consisted of a structured
program that the researchers designed to establish Allport’s opti-
mal conditions in the contact situation. Table 5 shows that the 134
samples with optimal contact conditions yield significantly greater
reductions of prejudice (mean r⫽⫺.287) than do the other
samples (mean r⫽⫺.204), Q
B
(1) ⫽20.19, p⬍.0001.
9
Is this result largely a function of Allport’s optimal conditions,
or does it merely reflect other aspects of this subset of contact
research? We addressed this question by conducting a regression
analysis that includes as predictors the structured program test of
Allport’s conditions and our strongest methodological moderators:
the type of study, the quality of the contact and prejudice measures,
8
It should be noted that ratings for type of contact measure are strongly
associated with ratings for the type of study, r⫽.66, p⬍.001.
9
In addition, a less direct test of Allport’s conditions involves tests for
intergroup friendship. Only 4 of the 134 samples that experienced optimal
structured contact used friends as the measure of contact. Yet, paralleling
the findings for optimally structured contact, the 154 tests that used
intergroup friendship as the measure of contact (mean r⫽⫺.246) showed
a significantly stronger effect than did the remaining 1,211 tests (mean r⫽
⫺.212), Q
B
(1) ⫽4.42, p⬍.05.
Table 4
Quality of Contact and Prejudice Indicators as Moderators for Contact–Prejudice Effect Sizes
Variable r95% CL ZkNQ
B
Quality of contact measure (samples)
Single item ⫺.195 ⫺.22/⫺.17 ⫺14.95*** 151 64,927
Multiple items (
␣
⬍.70) ⫺.195 ⫺.22/⫺.17 ⫺16.31*** 182 72,187
Multiple items (
␣
ⱖ.70) ⫺.298 ⫺.33/⫺.26 ⫺14.59*** 60 22,289
Experimental manipulation ⫺.295 ⫺.33/⫺.26 ⫺17.08*** 129 10,168
Other ⫺.175 ⫺.20/⫺.15 ⫺12.64*** 174 30,259
Between-classes effect 54.94***
Quality of prejudice measure (samples)
Single item
a
⫺.233 ⫺.28/⫺.18 ⫺8.83*** 44 11,508
Multiple items (
␣
⬍.70) ⫺.190 ⫺.21/⫺.17 ⫺21.05*** 384 110,407
Multiple items (
␣
ⱖ.70) ⫺.246 ⫺.27/⫺.22 ⫺22.13*** 241 76,469
Other
a
⫺.293 ⫺.37/⫺.22 ⫺7.23*** 27 1,446
Between-classes effect 20.86***
Note. These analyses were conducted with Fisher’s z-transformed rvalues. Mean effects and confidence limits
listed in this table have been transformed back to the r-metric from the z-transformed estimates obtained in these
analyses. Random effects variance components (based on Fisher’s z-transformed rvalues) ranged from .020 to
.022 for each analysis. r⫽correlation coefficient representing the mean effect size; 95% CL ⫽the 95%
confidence limits of r,Z⫽ztest for the mean effect sizes; p⫽probability of ztest; k⫽number of samples
associated with the mean effect size; N⫽total number of participants; Q
B
⫽between-classes test of
homogeneity.
a
Homogeneity can be obtained with less than 20% of the cases trimmed.
*** p⬍.001.
760 PETTIGREW AND TROPP
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and the adequacy of the control group.
10
Table 6 reveals significant
relationships between ratings on the structured program variable and
the methodological moderators. Samples with structured programs
tended to use more rigorous procedures, more reliable measures, and
better controls. An inverse variance weighted regression analysis was
then conducted with SPSS macros, developed by Wilson (2002),
which provide the appropriate parameters and probability values for
meta-analytic data (see also Lipsey & Wilson, 2001).
Table 7 displays the regression results. Ratings of the quality of the
contact and prejudice measures and the adequacy of the control
groups all relate significantly to the magnitude of the contact–
prejudice effect sizes. To further demonstrate the combined impor-
tance of these three methodological predictors, we formed a subset of
77 samples that boasted the most rigorous category for each of these
variables. The mean effect for this rigorous subset (r⫽⫺.323)
proved far stronger than did that of the remaining, less rigorous
samples (r⫽⫺.202), Q
B
(1) ⫽35.96, p⬍.0001. Thus, when
properly tested with rigorous measures and research procedures, stud-
ies of contact–prejudice relationships typically yield larger effects.
Nonetheless, the structured program indicator of Allport’s condi-
tions remains a significant predictor of contact–prejudice effects (

⫽
⫺.099, p⬍.03) even when entered with these methodological mod-
erators. As such, this multivariate model provides a stronger test for
Allport’s theory of intergroup contact than do the univariate compar-
isons for structured programs. Still, mean comparisons reported in
Table 5 indicate that the inverse relationship between contact and
prejudice persists—though not as strongly—even when the contact
situation is not structured to match Allport’s conditions.
Specific tests of individual conditions. We conducted a series
of tests with ratings of individual contact conditions for the 134
samples with structured programs. These cases were rated as
having authority sanction, an unsurprising finding that was virtu-
ally assured by the implementation of programs designed to pro-
mote Allport’s conditions.
As a first step, we conducted mean comparisons between sam-
ples that were rated as with or without each of the three remaining
conditions (i.e., common goals, cooperation, and equal status).
These tests showed no significant differences in mean contact–
prejudice effects for samples rated with and without common
goals, Q
B
(1) ⫽1.89, p⫽.17, cooperation, Q
B
(1) ⫽0.03, p⫽.86,
or equal status, Q
B
(1) ⫽0.70, p⫽.40. We also compared samples
that included all four of Allport’s conditions with those that did not
include all four conditions, and we found no significant differences
in mean contact–prejudice effects, Q
B
(1) ⫽1.48, p⫽.22. Addi-
tional analyses indicated that ratings of common goals, coopera-
tion, and equal status were highly correlated with each other (rs
ranging from .51 to .63, p⬍.001), with 72% of the samples rated
as having at least three of Allport’s four optimal conditions. We
then conducted inverse weighted regression analyses (see Lipsey
& Wilson, 2001; Wilson, 2002) to test common goals, cooperation,
and equal status as predictors for contact–prejudice effect sizes.
The models revealed no significant effects for these three condi-
tions when either entered simultaneously as predictors (

s ranging
from .02 to .18, p⬎.15) or when entered separately alongside our
methodological moderators (

s ranging from .05 to .06, p⬎.50).
Given that none of the three conditions emerged as a significant,
independent predictor, additional analyses were conducted to examine
whether authority sanction might play a special role in predicting the
contact–prejudice effect sizes. For this analysis, samples rated as
having only authority sanction (k⫽31) were compared with samples
rated as having two or more of Allport’s conditions (k⫽103) as well
as with the remaining samples in our analysis (k⫽564). Results show
that the mean effect for samples with only authority sanction (mean
r⫽⫺.286) did not differ significantly from the mean effect for
samples with two or more of Allport’s conditions (mean r⫽⫺.290),
Q
B
(1) ⫽0.01, p⫽.93, whereas both of these groups showed
significantly stronger effects than did the remaining samples in our
analysis (mean r⫽⫺.204), Q
B
(1) ⫽6.10, p⬍.05, and Q
B
(1) ⫽16.18,
p⬍.001.
Subset Analyses for Racial or Ethnic Samples and Other
Samples
To check for consistency in general patterns of effects, we
conducted additional analyses examining contact–prejudice rela-
10
For the regression analyses, ratings of the quality of the contact and
prejudice measures were dichotomized such that ratings would indicate
either high reliability (e.g., multi-item scale with high reliability, experi-
mental manipulation, high interrater reliability) or low reliability (e.g.,
single-item measure, multi-item measure with low or unknown reliability).
Ratings of the control measure were trichotomized: (a) the control group
had no prior contact or the sample used a within-subject design, (b) the
control group had some prior contact, or (c) the control group had extensive
prior contact with the outgroup.
Table 5
Structured Programs as a Moderator for Contact–Prejudice Effect Sizes
Variable r95% CL ZkNQ
B
Structured programs (samples)
Program
a
⫺.287 ⫺.32/⫺.25 ⫺16.09*** 134 10,400
No program ⫺.204 ⫺.22/⫺.19 ⫺28.11*** 562 189,430
Between-classes effect 20.19***
Note. These analyses were conducted with Fisher’s z-transformed rvalues. Mean effects and confidence limits
listed in this table have been transformed back to the r-metric from the z-transformed estimates obtained in these
analyses. The random effects variance components (based on Fisher’s z-transformed rvalues) was .022 for this
analysis. r⫽correlation coefficient representing the mean effect size; 95% CL ⫽the 95% confidence limits of
r, Z ⫽ztest for the mean effect sizes; p⫽probability of ztest; k⫽number of samples associated with the mean
effect size; N⫽total number of participants; Q
B
⫽between-classes test of homogeneity.
a
Homogeneity can be obtained with less than 20% of the cases trimmed.
*** p⬍.001.
761
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tionships across two subsets of cases. As approximately half of the
samples in our analysis (51%) involved contact between racial and
ethnic groups, we analyze these cases and the remaining cases as
two separate subsets. Contact theory was originally developed to
address racial and ethnic prejudices, but recent decades have
witnessed a massive use of the theory for a range of different target
groups. Is this expansion of contact theory justified? And do these
nonracial and nonethnic samples yield meta-analytic patterns that
are similar to those for racial and ethnic samples?
Comparisons across the racial and ethnic subsets and the nonracial
and nonethnic subsets yield virtually identical mean estimates of
contact–prejudice effect sizes (mean r⫽⫺.218 and ⫺.220, respec-
tively), Q
B
(1) ⫽0.027, p⫽.87. Table 8 presents results for each
subset in relation to our four strongest methodological moderators.
Higher quality of the contact and prejudice measures tend to show
larger average effect sizes for samples in both subsets. At the same
time, study type and type of control group proved especially important
for the nonracial and nonethnic samples, whereas quality of the
prejudice measures proved particularly important for the racial and
ethnic samples. Overall, however, the patterns of results observed for
these subsets largely reflect those obtained in the full analysis.
We then examined contact–prejudice effects for each subset in
relation to the global indicator of Allport’s conditions (see Table
9). Structured programs developed in line with Allport’s condi-
tions enhanced contact–prejudice effects for both subsets of cases,
though the effects tended to be stronger among the nonracial and
nonethnic samples, Q
B
(1) ⫽19.67, p⬍.001, than among the
racial and ethnic samples, Q
B
(1) ⫽2.62, p⫽.11. At the same
time, no significant differences in mean contact–prejudice effects
emerged between structured program samples with racial and ethnic
targets and nonracial and nonethnic targets, Q
B
(1) ⫽1.23, p⫽.27.
Paralleling our analysis of the full sample, regression analyses
then examined the structured program variable and four method-
ological moderators as predictors for contact–prejudice effects in
each subset (see Table 10). These analyses reveal some variability
in the degree to which the different methodological indicators
predict the contact–prejudice effects. In addition, the structured
program variable testing Allport’s contentions consistently
emerges as a marginally significant predictor of contact–prejudice
effects for both the racial and ethnic samples,

⫽⫺.112, p⫽
.069, and the remaining samples,

⫽⫺.105, p⫽.094.
Overall, then, results from both subsets closely resemble the
findings from the full analysis. Moreover, although there are some
slight differences associated with methodological factors, the pre-
ponderance of the evidence indicates similar patterns of effects
across the two subsets of samples.
Supplementary Analyses of Participant and Study
Moderators
A final set of analyses examines several additional participant
and study variables as potential moderators for contact–prejudice
effects.
11
Target group. Extending our analysis of the intergroup con-
texts under study, Table 11 presents mean effect sizes for the many
types of target groups studied in the contact literature. We consis-
tently find significant relationships between intergroup contact
11
Comparisons of samples with and without Allport’s conditions were
not conducted in relation to these variables because they would have
involved tests with extremely small numbers of cases.
Table 6
Correlation Matrix and Descriptive Statistics of Predictor Variables
Predictor variable 1 2 3 4 5
1. Type of study (3) —
2. IV quality (2) .539*** —
3. DV quality (2) .016 .219*** —
4. Type of control (3) .058 ⫺.009 ⫺.106** —
5. Program (2) .570*** .390*** .102** .095* —
M1.34 1.27 1.39 1.39 1.19
SD .57 .45 .49 .63 .40
Note. Numbers in parentheses represent the number of levels for each variable. For type of study, 1 ⫽survey
or field study, 2 ⫽quasi-experiment, 3 ⫽experiment; for independent variable (IV) and dependent variable
(DV) quality, 1 ⫽other, 2 ⫽reliable indicator; for type of control, 1 ⫽within-subjects design or between-
subjects design with no prior contact, 2 ⫽some prior contact, 3 ⫽considerable prior contact; for program, 1 ⫽
no structured program, 2 ⫽structured program.
*p⬍.05. ** p⬍.01. *** p⬍.001.
Table 7
Summary of Inverse Variance Weighted Regression Model
Predicting Contact–Prejudice Effect Sizes
Predictor variable BSE

Zp
Model
summary
Type of study .001 .017 .002 .035 .972
IV quality ⫺.088 .018 ⫺.206 ⫺4.775 .000
DV quality ⫺.031 .014 ⫺.084 ⫺2.231 .026
Type of control .034 .010 .121 3.303 .001
Program ⫺.053 .024 ⫺.099 ⫺2.219 .027
R
2
.10***
Q
Model
77.29***
k696
Note. This analysis was conducted with Fisher’s z-transformed rvalues.
The random effects variance component for this analysis (based on Fisher’s
z-transformed rvalues) was .020. B⫽raw regression coefficient; SE ⫽
standard error for the regression coefficient;

⫽standardized regression
coefficient; Z⫽ztest for the regression coefficient; p⫽probability of ztest;
R
2
⫽proportion of variance accounted for; Q
Model
⫽test of whether the
regression model explains a significant portion of variability across effect sizes
(see Wilson, 2002); k⫽number of samples included in the analysis.
*** p⬍.001.
762 PETTIGREW AND TROPP
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andprejudice across contexts, though the magnitudes of the
contact–prejudice effect sizes vary in relation to different target
groups. The largest effects emerge for samples involving contact
between heterosexuals and gay men and lesbians (mean r⫽
⫺.271). These effects are significantly larger than are those for the
other samples combined (mean r⫽⫺.211), Q
B
(1) ⫽5.34, p⫽
.02. Research focused on contact with the physically disabled
(mean r⫽⫺.243) also provides a larger-than-average effect size.
The most studied target groups, racial and ethnic groups (mean r⫽
⫺.214), and research on contact with the mentally disabled (mean
r⫽⫺.202) yield average effects. But research with other target
groups generally produces smaller effects. In particular, samples
concerning contact with the mentally ill and the elderly combined
(mean r⫽⫺.183) render significantly lower mean effects than do
the other target groups combined (mean r⫽⫺.221), Q
B
(1) ⫽
4.51, p⫽.03.
Table 8
Indicators of Research Rigor as Moderators for Contact–Prejudice Effect Sizes Among Racial and Ethnic Samples and Nonracial and
Nonethnic Samples
Variable
Racial and ethnic samples Nonracial and nonethnic samples
r95% CL ZkQ
B
r95% CL ZkQ
B
Type of study
Surveys and field studies ⫺.215 ⫺.23/⫺.20 ⫺22.05*** 299 ⫺.186 ⫺.21/⫺.16 ⫺15.26*** 193
Quasi-experiments ⫺.211 ⫺.26/⫺.16 ⫺8.25*** 54 ⫺.251 ⫺.29/⫺.22 ⫺13.49*** 114
Experiments ⫺.221 ⫺.34/⫺.09 ⫺3.37*** 9 ⫺.377 ⫺.44/⫺.31 ⫺9.67*** 27
Between-classes effect 0.03 27.89***
Quality of contact measure
Single item ⫺.210 ⫺.25/⫺.17 ⫺10.98*** 65 ⫺.184 ⫺.22/⫺.15 ⫺10.40*** 86
Multiple items (
␣
⬍.70) ⫺.201 ⫺.23/⫺.17 ⫺14.34*** 128 ⫺.181 ⫺.22/⫺.14 ⫺8.29*** 54
Multiple items (
␣
ⱖ.70) ⫺.323 ⫺.36/⫺.28 ⫺14.00*** 44 ⫺.226 ⫺.30/⫺.15 ⫺5.76*** 16
Experimental manipulation ⫺.236 ⫺.30/⫺.17 ⫺6.77*** 32 ⫺.314 ⫺.35/⫺.28 ⫺15.24*** 97
Other ⫺.170 ⫺.20/⫺.14 ⫺9.52*** 93 ⫺.181 ⫺.22/⫺.14 ⫺8.52*** 81
Between-classes effect 31.85*** 34.98***
Quality of prejudice measure
Single item ⫺.235 ⫺.29/⫺.18 ⫺8.24*** 34 ⫺.225 ⫺.34/⫺.11 ⫺3.63*** 10
Multiple items (
␣
⬍.70) ⫺.182 ⫺.20/⫺.16 ⫺15.77*** 210 ⫺.200 ⫺.23/⫺.17 ⫺14.09*** 174
Multiple items (
␣
ⱖ.70) ⫺.259 ⫺.29/⫺.23 ⫺16.37*** 105 ⫺.235 ⫺.26/⫺.21 ⫺15.03*** 136
Other ⫺.344 ⫺.44/⫺.24 ⫺6.31*** 13 ⫺.235 ⫺.35/⫺.12 ⫺3.91*** 14
Between-classes effect 23.73*** 2.97
Type of control group
Within design ⫺.228 ⫺.25/⫺.21 ⫺19.59*** 217 ⫺.209 ⫺.24/⫺.18 ⫺13.68*** 148
No contact control ⫺.166 ⫺.22/⫺.11 ⫺6.25*** 39 ⫺.284 ⫺.32/⫺.25 ⫺14.96*** 80
Some contact control ⫺.220 ⫺.26/⫺.18 ⫺11.16*** 73 ⫺.197 ⫺.23/⫺.16 ⫺9.86*** 83
Extensive contact control ⫺.179 ⫺.24/⫺.12 ⫺5.99*** 33 ⫺.081 ⫺.15/⫺.01 ⫺2.28* 23
Between-classes effect 6.56 29.93***
Note. These analyses were conducted with Fisher’s z-transformed rvalues. Mean effects and confidence limits listed in this table have been transformed
back to the r-metric from the z-transformed estimates obtained in these analyses. Random effects variance components (based on Fisher’s z-transformed
rvalues) ranged from .019 to .024. r⫽correlation coefficient representing the mean effect size; 95% CL ⫽the 95% confidence limits of r,Z⫽ztest
for the mean effect sizes; p⫽probability of ztest; k⫽number of samples associated with the mean effect size; Q
B
⫽between-classes test of
homogeneity.
*p⬍.05. *** p⬍.001.
Table 9
Structured Programs as a Moderator for Contact–Prejudice Effect Sizes Among Racial and Ethnic Samples and Nonracial and
Nonethnic Samples
Variable
Racial and ethnic samples Nonracial and nonethnic samples
r95% CL Zk Q
B
r95% CL ZkQ
B
Program ⫺.262 ⫺.32/⫺.20 ⫺8.30*** 40 ⫺.299 ⫺.34/⫺.26 ⫺13.80*** 94
No program ⫺.210 ⫺.23/⫺.19 ⫺22.37*** 322 ⫺.194 ⫺.22/⫺.17 ⫺17.21*** 240
Between-classes effect Q
B
(1) ⫽2.62 19.67***
Note. These analyses were conducted with Fisher’s z-transformed rvalues. Mean effects and confidence limits listed in this table have been transformed
back to the r-metric from the z-transformed estimates obtained in these analyses. Random effects variance components for these analyses (based on Fisher’s
z-transformed rvalues) were .022. r⫽correlation coefficient representing the mean effect size; 95% CL ⫽the 95% confidence limits of r, Z ⫽ztest for
the mean effect sizes; p⫽probability of ztest; k⫽number of samples associated with the mean effect size; Q
B
⫽between-classes test of homogeneity.
*** p⬍.001.
763
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Age. Table 11 also shows that the effects obtained with chil-
dren (mean r⫽⫺.239) and college students (mean r⫽⫺.231) do
not significantly differ from those obtained with adolescents (mean
r⫽⫺.208), Q
B
(1) ⫽1.20 and 1.37, respectively, p⬎.20. At the
same time, effects for children are marginally stronger, Q
B
(1) ⫽
3.59, p⫽.06, and effects for college students are significantly
stronger, Q
B
(1) ⫽5.49, p⬍.05, than are those obtained for adults
(mean r⫽⫺.197). That college students yield significantly stron-
ger average effects than do adults is consistent with Sears’s (1986)
contentions that college students are generally more open to
change than are older adults.
Sex. Participants’ sex proves to be a minor factor in interpreting
contact–prejudice effects (see Table 11). The difference between
all-male and all-female samples is not significant, Q
B
(1) ⫽0.70, p⫽.40.
Table 10
Summary of Inverse Variance Weighted Regression Model Predicting Contact–Prejudice Effect Sizes Among Racial and Ethnic
Samples and Nonracial and Nonethnic Samples
Predictor variable
Racial and ethnic samples Nonracial and nonethnic samples
BSE

ZpStatistic BSE

ZpModel summary
Type of study .062 .027 .147 2.29 .022 ⫺.036 .022 ⫺.112 ⫺1.61 .108
IV quality ⫺.095 .025 ⫺.216 ⫺3.79 .000 ⫺.068 .027 ⫺.162 ⫺2.53 .011
DV quality ⫺.059 .020 ⫺.161 ⫺2.93 .003 ⫺.023 .020 ⫺.059 ⫺1.14 .256
Type of control ⫺.003 .014 ⫺.010 ⫺.18 .857 .064 .015 .213 4.16 .000
Program ⫺.073 .040 ⫺.112 ⫺1.82 .069 ⫺.049 .029 ⫺.105 ⫺1.68 .094
R
2
.10*** .15***
Q
Model
40.45*** 59.74***
k362 334
Note. These analyses were conducted with Fisher’s z-transformed rvalues. Random effects variance components (based on Fisher’s z-transformed r
values) ranged from .019 to .020. B⫽raw regression coefficient; SE ⫽standard error for the regression coefficient;

⫽standardized regression coefficient;
Z⫽ztest for the regression coefficient; p⫽probability of ztest; R
2
⫽proportion of variance accounted for; Q
Model
⫽test of whether the regression model
explains a significant portion of variability across effect sizes (see Wilson, 2002); k⫽number of samples included in the analysis; IV ⫽independent
variable; DV ⫽dependent variable.
*** p⬍.001.
Table 11
Participant Predictors of Contact–Prejudice Effect Sizes Across Samples
Variable r95% CL ZkNQ
B
Target groups
Sexual orientation ⫺.271 ⫺.32/⫺.22 ⫺10.49*** 42 12,059
Physically disabled ⫺.243 ⫺.28/⫺.21 ⫺12.91*** 93 15,584
Race, ethnicity ⫺.214 ⫺.23/⫺.20 ⫺23.62*** 362 133,249
Mentally disabled
a
⫺.207 ⫺.26/⫺.15 ⫺7.16*** 40 6,116
Mentally ill
a
⫺.184 ⫺.23/⫺.14 ⫺8.41*** 66 17,218
Elderly ⫺.181 ⫺.23/⫺.13 ⫺6.73*** 54 6,424
Other
a
⫺.192 ⫺.25/⫺.13 ⫺6.27*** 39 9,180
Between-classes effect 11.95
Age of participants
Children (1–12 years) ⫺.239 ⫺.28/⫺.20 ⫺11.30*** 82 10,207
Adolescents ⫺.208 ⫺.24/⫺.18 ⫺12.68*** 114 45,602
College students ⫺.231 ⫺.25/⫺.21 ⫺20.50*** 262 46,553
Adults ⫺.197 ⫺.22/⫺.18 ⫺17.81*** 238 97,468
Between-classes effect 6.68
Sex of participants
Females
a
⫺.214 ⫺.26/⫺.17 ⫺9.06*** 63 13,183
Males
a
⫺.185 ⫺.23/⫺.14 ⫺7.56*** 59 15,598
Both or undetermined ⫺.218 ⫺.23/⫺.20 ⫺29.58*** 574 171,049
Between-classes effect 1.83
Note. These analyses were conducted with Fisher’s z-transformed rvalues. Mean effects and confidence limits
listed in this table have been transformed back to the r-metric from the z-transformed estimates obtained in these
analyses. Random effects variance components (based on Fisher’s z-transformed rvalues) were 0.23 for each
analysis. r⫽correlation coefficient representing the mean effect size; 95% CL ⫽the 95% confidence limits of
r;Z⫽ztest for the mean effect sizes; p⫽probability of ztest; k⫽number of samples associated with the mean
effect size; N⫽total number of participants. Q
B
⫽between-classes test of homogeneity.
a
Homogeneity can be obtained with less than 20% of the cases trimmed.
*** p⬍.001.
764 PETTIGREW AND TROPP
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Geographic area. With 72% of our samples conducted in the
United States, it is important to determine whether there are
significant differences in effect sizes in contact research conducted
elsewhere. A general test across the six geographical areas re-
vealed no significant differences in effects, Q
B
(5) ⫽1.88, p⫽.87
(see Table 12). And a focused test shows that there is virtually no
difference in effect sizes between U.S. (mean r⫽⫺.215) and
non–U.S. samples (mean r⫽⫺.217), Q
B
(1) ⫽.01, p⫽.90.
Contact setting. Various research settings relate significantly
to the size of the effects (see Table 12). Although there likely are
differences in intensity and duration of contact among these set-
tings, their discrepant mean effects are suggestive. The smallest
mean effect results from intergroup contact through tourism and
travel. Though based on only 13 samples from nine studies, this
tourism effect size (mean r⫽⫺.113) is significantly smaller than
is that of the other samples combined (mean r⫽⫺.217), Q
B
(1) ⫽
3.84, p⬍.05. By contrast, the largest mean effects emerge from
contact that occurs in recreational and laboratory settings. The 48
samples studied in these settings provide a mean effect (mean r⫽
⫺.287) that is significantly larger than that of the other settings
combined (mean r⫽⫺.211), Q
B
(1) ⫽6.86, p⬍.01.
Date of study. Though early samples studied prior to 1960
uncovered slightly larger average effects (mean r⫽⫺.228), the
dominant trend is for recent research to reveal greater mean effects
than does earlier work. Thus, the 415 samples tested after 1979
yield a significantly larger average effect (mean r⫽⫺.236) than
do the 281 samples tested prior to 1980 (mean r⫽⫺.184),
Q
B
(1) ⫽15.59, p⬍.0001. It is tempting to speculate how major
events, such as American racial conflict in the 1960s, might have
shaped this difference. However, the difference across the two
time periods is explained largely by the increased rigor of modern
research. Relative to earlier work, contact research since 1979 has
used more rigorous measures and procedures, as indicated by the
quality of the contact measure,
2
(1) ⫽13.70, p⬍.001, the
quality of the prejudice measure,
2
(1) ⫽52.62, p⬍.001, and the
quality of the controls used in the research,
2
(2) ⫽12.14, p⬍.01.
When these indicators of research rigor are controlled, the differ-
ence in effect sizes between the early and late intergroup contact
samples is sharply reduced but remains statistically significant,

⫽⫺.08, p⬍.05.
Discussion
These meta-analytic findings shed important light on long-standing
debates in the contact literature concerning the central questions of
whether contact reduces prejudice and the role that Allport’s condi-
tions play in promoting positive intergroup outcomes.
Table 12
Study Predictors of Contact–Prejudice Effect Sizes Across Samples
Variable r95% CL ZkNQ
B
Geographic area of research
United States ⫺.215 ⫺.23/⫺.20 ⫺26.81*** 501 133,598
Europe ⫺.217 ⫺.25/⫺.18 ⫺10.96*** 80 36,799
Israel
a
⫺.196 ⫺.26/⫺.13 ⫺5.42*** 24 6,808
Canada ⫺.232 ⫺.30/⫺.16 ⫺6.19*** 21 4,732
Australia and New Zealand
a
⫺.259 ⫺.34/⫺.18 ⫺6.11*** 16 3,704
Africa, Asia, Latin America ⫺.205 ⫺.25/⫺.16 ⫺8.45*** 54 14,189
Between-classes effect 1.88
Research setting
Laboratory
a
⫺.273 ⫺.35/⫺.19 ⫺6.25*** 22 1,754
Recreational
a
⫺.299 ⫺.37/⫺.23 ⫺7.60*** 26 2,168
Work, organizational ⫺.224 ⫺.27/⫺.18 ⫺10.20*** 73 16,608
Educational ⫺.213 ⫺.24/⫺.19 ⫺16.72*** 209 52,980
Residential
a
⫺.202 ⫺.25/⫺.16 ⫺8.48*** 57 8,778
Tourism, travel ⫺.113 ⫺.22/⫺.01 ⫺2.08* 13 2,211
Mixed and other ⫺.213 ⫺.23/⫺.19 ⫺21.82*** 296 115,331
Between-classes effect 11.14
Date of publication
Prior to 1960 ⫺.228 ⫺.27/⫺.19 ⫺10.12*** 57 19,667
1960–1969
a
⫺.176 ⫺.21/⫺.14 ⫺9.18*** 83 16,350
1970–1979 ⫺.169 ⫺.20/⫺.14 ⫺11.24*** 141 44,297
1980–1989 ⫺.233 ⫺.26/⫺.21 ⫺16.81*** 165 37,217
1990–2000 ⫺.238 ⫺.26/⫺.22 ⫺21.82*** 250 82,299
Between-classes effect 21.15***
Note. These analyses were conducted with Fisher’s z-transformed rvalues. Mean effects and confidence limits
listed in this table have been transformed back to the r-metric from the z-transformed estimates obtained in these
analyses. Random effects variance components (based on Fisher’s z-transformed rvalues) ranged from .022 to
.023 for each analysis. r⫽correlation coefficient representing the mean effect size; 95% CL ⫽the 95%
confidence limits of r,Z⫽ztest for the mean effect sizes; p⫽probability of ztest; k⫽number of samples
associated with the mean effect size; N⫽total number of participants; Q
B
⫽between-classes test of
homogeneity.
a
Homogeneity can be obtained with less than 20% of the cases trimmed.
*p⬍.05. *** p⬍.001.
765
META-ANALYTIC TEST OF INTERGROUP CONTACT THEORY
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Does Intergroup Contact Reduce Prejudice?
The meta-analytic results clearly indicate that intergroup contact
typically reduces intergroup prejudice. Synthesizing effects from
696 samples, the meta-analysis reveals that greater intergroup
contact is generally associated with lower levels of prejudice
(mean r⫽⫺.215). Moreover, the mean effect rises sharply for
experiments and other rigorously conducted studies. In addition,
94% of the samples in our analysis show an inverse relationship
between intergroup contact and prejudice.
Additional findings suggest that these relationships between
contact and prejudice are not artifacts of either participant selec-
tion or publication bias. Consistent with past research, the partic-
ularly strong effects observed for experimental studies confirm
that contact can cause meaningful reductions in prejudice. More-
over, the investigations that allowed no choice for their partici-
pants to avoid the intergroup contact yield a slightly larger mean
effect size in reducing prejudice than do studies that allowed
choice. In addition, of the six tests we conducted to test for
publication bias, all but one indicate that this bias is not a serious
threat to the validity of our results, and the one exception still
revealed a significant contact–prejudice effect among the most
rigorous research studies.
Results from our analysis also show that intergroup contact
effects typically generalize beyond participants in the immediate
contact situation. Indeed, the generalization of contact’s effects
appears to be far broader than what many past commentators have
thought. Not only do attitudes toward the immediate participants
usually become more favorable, but so do attitudes toward the
entire outgroup, outgroup members in other situations, and even
outgroups not involved in the contact. This result enhances the
potential of intergroup contact to be a practical, applied means of
improving intergroup relations.
The findings also reveal that intergroup contact may be useful
for reducing prejudice in a variety of intergroup situations and
contexts. The patterns of contact–prejudice effects observed for
racial and ethnic samples closely resemble those observed for the
remaining samples in our analysis. Moreover, although we observe
variability in the magnitude of contact–prejudice effects across
different intergroup contexts, the relationships between contact
and prejudice remain significant across samples involving differ-
ent target groups, age groups, geographical areas, and contact
settings. These results support the recent extension of intergroup
contact theory to a variety of intergroup contexts, beyond its
original focus on racial and ethnic groups. In sum, our meta-
analytic results provide substantial evidence that intergroup con-
tact can contribute meaningfully to reductions in prejudice across
a broad range of groups and contexts.
What Role Do Allport’s Conditions Play in Helping
Contact to Reduce Prejudice?
Results from the meta-analysis also offer important insights
regarding the role of Allport’s conditions in reducing prejudice
through intergroup contact. Consistent with much of the intergroup
contact literature (see Allport, 1954; Pettigrew, 1998), those sam-
ples that experienced carefully structured contact situations de-
signed to meet Allport’s optimal conditions achieved a markedly
higher mean effect size than did other samples. Moreover, a
multivariate model shows that structured contact predicted stron-
ger contact–prejudice effects, beyond that explained by multiple
indices of research rigor. This trend emerged for racial and ethnic
samples as well as for the remaining samples in our analysis.
Taken together, these results show that establishing Allport’s op-
timal conditions in the contact situation generally enhances the
positive effects of intergroup contact.
At the same time, Allport’s conditions are not essential for
intergroup contact to achieve positive outcomes. In particular, we
found that samples with no claim to these key conditions still show
significant relationships between contact and prejudice. Thus, All-
port’s conditions should not be regarded as necessary for produc-
ing positive contact outcomes, as researchers have often assumed
in the past. Rather, they act as facilitating conditions that enhance
the tendency for positive contact outcomes to emerge.
Moreover, further examination of Allport’s conditions suggests
that institutional support may be an especially important condition
for facilitating positive contact effects. Although the present anal-
ysis offers a relatively crude test, samples with structured pro-
grams showed significantly stronger contact–prejudice effects than
the remaining samples, irrespective of whether they were rated as
having conditions beyond authority support. At the same time, it is
important to note that our ratings of authority support were con-
ducted in the context of structured programs designed to approx-
imate optimal conditions for positive intergroup contact. Hence,
although authority support appears to play an important role, this
condition should not be conceived of or implemented in isolation.
Institutional support for contact under conditions of competition or
unequal status can often enhance animosity between groups,
thereby diminishing the potential for achieving positive outcomes
from contact (see Sherif, 1966). Thus, consistent with Allport’s
original contentions, we believe that optimal conditions for contact
are best conceptualized as functioning together to facilitate posi-
tive intergroup outcomes rather than as entirely separate factors.
Moving Toward a Reformulation of Intergroup Contact
Theory
Combined with other recent empirical advances, these meta-
analytic findings suggest new ways of thinking about the likely
effects of intergroup contact. We posit that the process underlying
contact’s ability to reduce prejudice involves the tendency for
familiarity to breed liking. Emphasized by Homans (1950) and
demonstrated experimentally by Zajonc (1968), this phenomenon
leads to the prediction that intergroup contact will induce liking
under a wide range of conditions. Research has consistently found
evidence for the relationship between exposure and liking with a
range of targets (e.g., Bornstein, 1989; Harmon-Jones & Allen,
2001; Lee, 2001) and across varied research settings (e.g., More-
land & Zajonc, 1977; Zajonc & Rajecki, 1969). Moreover, recent
work has demonstrated that the increases in liking that derive from
exposure can generalize to greater liking for related, yet unknown,
targets (Rhodes et al., 2001); this is comparable to the generaliza-
tion of contact’s effects to unknown outgroup members.
These mere exposure findings also help to explain why Allport’s
optimal conditions prove not to be essential for the positive effects
of contact to emerge. Although 94% of the 713 samples in our
analysis showed an inverse relationship between intergroup con-
tact and prejudice, only 19% of the samples involved contact
766 PETTIGREW AND TROPP
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situations structured in line with Allport’s conditions.
12
Consider
two relevant examples: Van Dyk (1990) found that rural
Afrikaans-speaking White housewives who had close contact with
their African domestic workers had more favorable attitudes to-
ward Africans in general (r⫽⫺.09). Conducted during the tense
final days of South Africa’s apartheid policy, this contact situation
sharply violates Allport’s key conditions. Likewise, Crain and
Weisman (1972) found that adult African Americans who reported
having played with Whites as children were less anti-White (r⫽
⫺.08), although they had experienced racially segregated neigh-
borhoods and elementary schools. Like these examples, many of
the meta-analysis’ studies conspicuously lack Allport’s key con-
ditions for positive contact outcomes and yet report some reduc-
tion in prejudice.
In turn, these trends beg the following question: If Allport’s
optimal conditions are not essential for achieving positive inter-
group outcomes, then what might be necessary? An answer to this
central question is forming from the confluence of several new
lines of contemporary research.
Work on the relationship between familiarity and liking sug-
gests that uncertainty reduction is an important mechanism under-
lying these relationships (e.g., Lee, 2001). Complementing this
view, emerging perspectives have pointed to the significance of
reducing intergroup anxiety to achieve reductions in prejudice
from contact (Dijker, 1987; Islam & Hewstone, 1993; Stephan &
Stephan, 1985; Stephan et al., 2002). Intergroup anxiety refers to
feelings of threat and uncertainty that people experience in inter-
group contexts. These feelings grow out of concerns about how
they should act, how they might be perceived, and whether they
will be accepted (Stephan & Stephan, 1985; see also Berger &
Calabrese, 1975; Blascovich, Mendes, Hunter, & Lickel, 2000;
Gudykunst, 1985; Mendes, Blascovich, Lickel, & Hunter, 2002).
Indeed, Stephan, Stephan, and Gudykunst (1999) have begun the task
of combining the uncertainty reduction and threat reduction theories.
A rapidly growing research literature supports this fresh per-
spective. Studies have shown repeatedly that contact can reduce
feelings of threat and anxiety about future cross-group interactions
(Blair, Park, & Bachelor, 2003; Blascovich, Mendes, Hunter,
Lickel, & Kowai-Bell, 2001; Islam & Hewstone, 1993; Paolini,
Hewstone, Cairns, & Voci, 2004; Stephan & Stephan, 1985).
Moreover, recent studies have demonstrated that intergroup anxi-
ety mediates the relationships between intergroup contact and
prejudice (e.g., Paolini et al., 2004; Stephan et al., 2002; Voci &
Hewstone, 2003). Thus, more positive contact outcomes can be
achieved to the extent that anxiety is reduced (Brown & Hewstone,
2005). Reducing negative feelings such as anxiety and threat
represents an important means by which intergroup contact dimin-
ishes prejudice.
13
Directions for Future Research
These findings, along with recent work on familiarity and liking,
suggest a new orientation for future theory and research on inter-
group contact. In particular, social psychologists must grant
greater attention to the negative factors that deter intergroup con-
tact from diminishing prejudice. When Williams (1947) and All-
port (1954) were fashioning intergroup contact theory, they as-
sumed that most contact did not reduce prejudice. Hence, they
sought to specify the positive features of those contact situations
that could maximize the potential for contact to reduce prejudice
and promote positive intergroup outcomes. Ever since, explora-
tions of contact theory have focused largely on positive factors.
But the meta-analytic data reveal that the knowledge gained from
past contact research is limited by its primary emphasis on positive
features of the contact situation. Factors that curb contact’s ability
to reduce prejudice are now the most problematic theoretically, yet
the least understood. These negative factors, ranging from inter-
group anxiety (Stephan & Stephan, 1985) to authoritarianism and
normative restraints (Pettigrew, Wagner, Stellmacher, & Christ,
2006), deserve to become a major focus of future contact research.
Such an emphasis would allow a more comprehensive understand-
ing of conditions that both enhance and inhibit the potentially
positive effects of contact.
New developments also suggest that the effects of these factors
are likely to be moderated by the degree to which group member-
ship is salient during contact. Voci and Hewstone (2003) have
shown that anxiety mediates the relationship between contact and
prejudice when group salience is high but that such mediation is
less pronounced when group salience is low.
Other studies have demonstrated that contact effects are more
likely to generalize when group membership is salient (Brown &
Hewstone, 2005). Indeed, this Hewstone and Brown (1986) con-
tention may explain why the meta-analytic results reveal such
widespread generalization. It is likely that the demands of the contact
research situation (or the need for reflection by those reporting on past
contact) led to high group salience in most of the studies.
These advances raise the possibility of the development of a
model considerably more complex and complete than Allport’s
original “contact hypothesis.” Contemporary research has exam-
ined a range of additional mediators of contact effects, including
perspective taking (Craig, Cairns, Hewstone, & Voci, 2002),
broadened views of the ingroup (e.g., Gaertner & Dovidio, 2000;
Pettigrew, 1998; Sherif, 1966), and the perceived importance of
the contact (Van Dick et al., 2004). The search for mediators has
also involved an expanded investigation of contact effects. Beyond
the influence of contact on prejudice, researchers have tested the
effects of intergroup contact on such variables as intergroup dif-
ferentiation and outgroup variability (Islam & Hewstone, 1993;
Oaker & Brown, 1986; Paolini et al., 2004), ingroup pride (London
& Linney, 1993), and a willingness to trust and forgive the out-
group (Hewstone et al., 2005).
12
It is possible that this result could reflect a selection bias involving the
intergroup situations researchers choose to study. But this type of situa-
tional selection bias appears highly unlikely. Our file contains many
studies, such as the examples just described, where the contact situation is
far less than optimal. More important, most of the studies in this meta-
analysis involve survey and questionnaire research. Here, the subjects
report on whatever intergroup contact they have had. Thus, there is limited
information regarding the contact conditions, and the researchers had no
control over the situations involved.
13
Not all contact experiences are positive, of course. Although most of
the contact studies in our analysis focused on positive contact outcomes,
some recent work has shown that negative intergroup experiences can
enhance feelings of anxiety and threat and hinder the development of
positive orientations toward the outgroup (Plant, 2004; Plant & Devine,
2003; Stephan & Stephan, 1985; Tropp, 2003).
767
META-ANALYTIC TEST OF INTERGROUP CONTACT THEORY
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Given the current state of the research literature, there is little
need to demonstrate further contact’s general ability to lessen
prejudice. Results from the meta-analysis conclusively show that
intergroup contact can promote reductions in intergroup prejudice.
Moreover, the meta-analytic findings reveal that contact theory
applies beyond racial and ethnic groups to embrace other types of
groups as well. As such, intergroup contact theory now stands as
a general social psychological theory and not as a theory designed
simply for the special case of racial and ethnic contact.
Still, continued advances in understanding intergroup contact
require more extensive longitudinal research. To date, findings
from longitudinal studies typically have shown the persistence of
the prejudice reduction achieved by contact (e.g., Eller & Abrams,
2003; Levin et al., 2003). But such studies are rare. In addition to
learning about the persistence of contact effects, it is necessary to
determine the effects of long-term intergroup contact. Similar to
mere exposure effects, we predict that, with continued contact, the
reduction of prejudice would asymptote at some point and provide
few further gains.
In addition, more elaborate models are needed to integrate and
account for these varied intergroup contact effects. Some such models
have begun to emerge (e.g., Brown & Hewstone, 2005; Gaertner &
Dovidio, 2000; Pettigrew, 1998), many of which use complex struc-
tural models (e.g., Eller & Abrams, 2003; Paolini et al., 2004; Van
Dick et al., 2004; Voci & Hewstone, 2003; Wagner et al., 2003). For
the future, multilevel models that consider both positive and negative
factors in the contact situation, along with individual, structural, and
normative antecedents of the contact, will greatly enhance research-
ers’ understanding of the nature of intergroup contact effects. And as
the contact literature continues to expand rapidly with rigorous meth-
ods and attention to theory, we anticipate that the future will witness
the development of such comprehensive models of intergroup contact.
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770 PETTIGREW AND TROPP
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Appendix: Ratings of Samples Included in the Meta-Analysis
Reference Sample rTest Statistic Choice Pub Type B/W Control IV IVQ DVQ Prog Target Age Sex Geo Set N
Abu-Hilal (1986) 1 ⫺.210 r⫺.210 full 2 1 W 1 1 3 3 1 1 coll b/u 6 m/o 353
Adams (1992) 1 ⫺.345 r⫺.345* full 2 1 W 1 1 2 3 1 1 coll b/u 1 m/o 42
2⫺.323 r⫺.323* full 2 1 W 1 1 2 3 1 1 coll b/u 1 m/o 26
3⫺.508 r⫺.508* full 2 1 W 1 1 2 3 1 1 coll b/u 1 m/o 51
4⫺.346 r⫺.346* full 2 1 W 1 1 2 3 1 1 coll b/u 1 m/o 67
5⫺.300 r⫺.300* full 2 1 W 1 1 2 3 1 1 coll b/u 1 m/o 58
Aday et al. (1991) 1 ⫺.311 t⫺2.29* none 1 2 B 2 2 4 3 2 2 child b/u 1 m/o 49
Aday et al. (1993) 1 ⫺.487 t⫺3.48 none 1 2 B 2 2 4 3 2 2 adol b/u 1 rec 39
Alderfer et al. (1992) 1 ⫺.105 F5.29* some 1 2 B 4 2 99 2 2 1 adult b/u 1 org 477
Aljeaid (1986) 1 ⫺.330 M/SD p ⫽.000 some 2 1 B 2 1 1 3 1 1 coll b/u 1 edu 296
Allport & Kramer (1946) 1 ⫺.154 Prop 51/66* full 1 1 B 4 1 2 2 1 1 coll b/u 1 m/o 393
Alreshoud & Koeske
(1997) 1 ⫺.290 r⫺.290 full 1 2 W 1 1 3 3 1 1 coll b/u 1 m/o 74
Altrocchi & Eisdorfer
(1961) 1 ⫺.200 Prop 82/93 some 1 2 W 1 2 99 2 1 5 coll f 1 edu 49
2⫺.181 Prop 93/100 some 1 2 W 1 2 99 2 1 5 coll f 1 edu 192
Amir & Ben-Ari (1985) 1 ⫺.088 t⫺.088 full 1 2 W 1 2 99 3 1 1 adult b/u 3 trav 483
Amir & Garti (1977) 1 ⫺.158 t⫺2.80 some 1 1 W 1 2 99 2 1 1 adol f 3 rec 78
2⫺.123 t⫺1.16 some 1 1 W 1 2 99 2 1 1 adol f 3 rec 22
Amir et al. (1978) 1 ⫺.067 t⫺2.75* some 1 1 W 1 3 99 2 1 1 adol b/u 3 edu 419
2⫹.023 t⫹1.15* some 1 1 W 1 3 99 2 1 1 adol b/u 3 edu 614
Amsel & Fichten (1988) 1 ⫺.419 t⫺4.95* full 1 1 B 2 1 1 2 1 4 coll b/u 4 m/o 117
Angermeyer &
Matshinger (1997) 1 ⫺.134 Prop 36/50* some 1 1 B 3 1 1 2 1 5 adult b/u 2 m/o 1,484
Anthony (1969) 1 ⫺.361 t⫺2.44* full 1 1 B 4 2 4 3 2 4 coll b/u 1 rec 42
Antonak (1981) 1 ⫺.150 r⫺.150* full 1 1 W 1 1 1 3 1 4 coll b/u 1 m/o 326
Antonak et al. (1989) 1 ⫺.132 p.000 full 1 1 W 1 1 2 2 1 6 adult b/u 1 m/o 557
Archie & Sherrill (1989) 1 ⫺.096 Prop 54/67* some 1 1 B 2 3 99 3 1 4 child b/u 1 edu 229
Arguc (1995) 1 ⫺.015 r⫺.015* some 2 1 W 1 1 1 1 1 1 adult m 2 m/o 96
Arikan & Uysal (1999) 1 ⫺.054 t⫺2.74* some 1 1 W 3 1 1 3 1 5 coll b/u 6 edu 630
Arkar & Eker (1992) 1 ⫺.092 p.400 none 1 1 B 3 1 1 3 1 5 adult b/u 6 org 84
Aronson & Page (1980) 1 ⫺.140 p.364* full 1 2 B 2 2 99 2 2 5 coll b/u 1 org 42
Auerbach & Levinson
(1977) 1 ⫹.519 Prop 88/38 none 1 2 B 3 3 99 2 1 2 coll b/u 1 edu 120
Bagget (1981) 1 ⫺.090 t⫺0.68* none 1 2 B 3 2 4 2 2 2 child b/u 1 edu 56
Ballard et al. (1977) 1 ⫺.339 M/SD p ⫽.051* some 1 2 B 3 2 99 4 2 6 child b/u 1 edu 33
Barnard & Benn (1987) 1 ⫺.197 F11.34 some 1 3 W 1 2 4 2 2 1 coll m 1 lab 48
Barnea & Amir (1981) 1 .000 pnssome 1 1 B 4 3 99 2 1 1 coll b/u 3 m/o 209
2 .000 pnssome 1 1 B 4 3 99 2 1 1 coll b/u 3 m/o 209
Basu & Ames (1970) 1 ⫺.484 r⫺.484* full 1 1 W 1 1 2 2 1 1 coll b/u 1 m/o 562
Beh-Pajooh (1991) 1 ⫺.341 M/SD p ⫽.000* some 1 1 B 2 1 1 2 1 6 coll b/u 2 edu 132
Bekker & Taylor (1966) 1 ⫺.258 M/SD p ⫽.01 none 1 1 B 2 3 1 2 1 2 coll b/u 1 m/o 100
Belan (1996) 1 ⫺.077 F1.75* some 2 1 B 4 1 2 3 1 5 adult b/u 1 m/o 296
Bell (1962) 1 ⫺.216 t⫺2.07* full 1 1 B 3 1 99 2 1 4 adult b/u 1 m/o 110
Benedict et al. (1988) 1 ⫺.193 r⫺.193* full 1 1 W 1 1 1 2 1 99 adult b/u 1 m/o 112
2⫺.143 r⫺.143* full 1 1 W 1 1 1 2 1 99 adult b/u 1 m/o 112
Benedict et al. (1992) 1 –.205 r⫺.205* full 1 1 W 1 1 2 2 1 99 adult b/u 1 m/o 314
Berg & Wolleat (1973) 1 ⫹.235 M/SD p ⫽.02 some 1 1 B 2 1 2 3 1 1 child b/u 1 m/o 100
Bergmann & Erb (1997) 1 ⫺.205 Prop 20/40* full 1 1 B 2 1 1 2 1 1 adult b/u 2 m/o 2,102
Bicknese (1974) 1 ⫺.195 p.25* full 1 2 W 1 2 99 2 1 1 coll b/u 2 edu 19
2⫺.108 p.52* full 1 2 W 1 2 99 2 1 1 coll b/u 2 edu 18
3⫺.173 p.25* full 1 2 W 1 2 99 2 1 1 coll b/u 2 edu 22
Biernat (1990) 1 ⫺.118 r⫺.118* full 1 1 W 1 1 1 2 1 1 coll b/u 1 res 78
2⫺.275 r⫺.275* full 1 1 W 1 1 1 2 1 1 coll b/u 1 res 90
Biernat & Crandall
(1994) 1 ⫺.349 r⫺.349* full 1 1 W 1 1 3 2 1 99 coll b/u 1 m/o 116
Borus et al. (1973) 1 ⫺.250 r⫺.250 some 1 1 W 1 1 1 3 1 1 adult m 1 m/o 1,385
Bowman (1979) 1 ⫺.201 Prop 25/44 full 1 1 B 2 1 2 1 1 3 adult b/u 5 m/o 322
Bradnum et al. (1993) 1 ⫺.163 M/SD p ⫽.006 none 1 1 B 3 3 99 2 1 1 adol b/u 6 edu 294
2⫺.221 M/SD p ⫽.000 none 1 1 B 3 3 99 2 1 1 adol b/u 6 edu 336
Brewer & Campbell
(1976) 1 ⫺.089 r⫺.089* some 1 1 W 1 1 2 2 1 1 adult b/u 6 m/o 1,500
Brigham (1993) 1 ⫺.158 r⫺.158* full 1 1 W 1 1 2 3 1 1 coll b/u 1 m/o 280
2⫺.361 r⫺.361* full 1 1 W 1 1 2 3 1 1 coll b/u 1 m/o 81
Brigham & Barkowitz
(1978) 1 ⫺.420 r⫺.420 full 1 1 W 1 1 2 2 1 1 coll b/u 1 m/o 76
(Appendix continues)
771
META-ANALYTIC TEST OF INTERGROUP CONTACT THEORY
This document is copyrighted by the American Psychological Association or one of its allied publishers.
This article is intended solely for the personal use of the individual user and is not to be disseminated broadly.
Appendix (continued)
Reference Sample rTest Statistic Choice Pub Type B/W Control IV IVQ DVQ Prog Target Age Sex Geo Set N
2⫺.130 r⫺.130 full 1 1 W 1 1 2 2 1 1 coll b/u 1 m/o 86
Brigham & Malpass
(1985) 1 ⫺.580 r⫺.580 full 1 1 W 1 1 2 3 1 1 coll b/u 1 m/o 78
Brigham & Ready
(1985) 2 ⫺.210 r⫺.210 full 1 1 W 1 1 2 3 1 1 coll b/u 1 m/o 90
Brink & Harris (1964) 1 ⫺.202 Prop 18/36 full 1 1 B 3 1 99 2 1 1 adult b/u 1 m/o 1,257
Britt et al. (1996) 1 ⫺.070 r⫺.070* full 1 1 W 1 1 2 2 1 1 coll b/u 1 m/o 131
Brockington et al.
(1993) 1 ⫺.180 r⫺.180* some 1 1 W 1 1 2 2 1 5 adult b/u 2 m/o 1,987
Brockman & D’Arcy
(1978) 1 ⫺.131 Prop 51/64 some 1 1 B 3 1 1 2 1 5 adult b/u 4 m/o 221
Brooks & Fricdrich
(1970) 1 ⫺.222 Prop 36/58 some 1 1 B 3 1 1 2 1 99 adult b/u 1 m/o 85
2⫺.143 Prop 23/36 some 1 1 B 3 1 1 2 1 99 adult b/u 1 m/o 146
Brooks et al. (1973) 1 ⫺.125 r⫺.125 full 1 1 W 1 1 1 1 1 1 coll b/u 1 m/o 54
2⫺.300 r⫺.300 full 1 1 W 1 1 1 1 1 1 coll b/u 1 m/o 56
Brophy (1945) 1 ⫺.433 Prop 28/72 none 1 1 B 4 3 99 2 1 1 adult m 1 org 447
Brown (1997) 1 ⫺.290 r⫺.290* some 2 1 W 1 1 2 3 1 1 coll b/u 1 m/o 190
Brown & Albee (1966) 1 ⫹.245 t⫹2.73* none 1 1 B 2 3 99 2 1 1 adult m 1 m/o 120
Brown et al. (1986) 1 ⫺.143 r⫺.143* full 1 1 W 1 1 1 4 1 99 adult f 2 org 29
2⫺.238 r⫺.238* full 1 1 W 1 1 1 4 1 99 adult m 2 org 16
3⫺.168 r⫺.168* full 1 1 W 1 1 1 4 1 99 adult m 2 org 30
4⫺.010 r⫺.010* full 1 1 W 1 1 1 4 1 99 adult m 2 org 39
5⫺.010 r⫺.010* full 1 1 W 1 1 1 4 1 99 adult m 2 org 33
Brown et al. (1999) 1 ⫺.450 r⫺.450 some 1 1 W 1 1 3 1 1 1 coll b/u 2 m/o 85
2⫺.230 r⫺.230 some 1 1 W 1 1 3 1 1 1 coll b/u 2 m/o 217
Brown et al.
(1999/2001) 1 ⫺.205 M/SD p ⫽.001* full 2 2 B 3 1 2 3 1 1 adult b/u 2 m/o 262
Bucich-Naylor (1978) 1 ⫺.041 M/SD p ⫽.73* none 2 2 B 4 2 4 3 2 4 child b/u 1 edu 69
Bullock (1976a/1976b/
1978) 1 ⫺.298 r⫺.298* full 1 1 W 1 1 2 2 1 1 adol b/u 1 m/o 2,076
2⫺.101 r⫺.101* full 1 1 W 1 1 2 2 1 1 adol b/u 1 m/o 1,755
Buono (1981) 1 ⫺.175 r⫺.175* full 2 2 W 1 2 99 2 1 1 adult b/u 1 res 121
2⫹.029 r⫹.029* full 2 2 W 1 2 99 2 1 1 adult b/u 1 res 50
Burgin & Walker (2000) 1 ⫺.373 Mult p⫽.000* some 2 2 B 3 1 3 2 1 1 adol f 5 rec 137
Butler & Wilson (1978) 1 ⫺.156 r⫺.156* some 1 1 W 1 1 2 3 1 1 adult b/u 1 org 1,490
2⫺.131 r⫺.131* some 1 1 W 1 1 2 3 1 1 adult b/u 1 org 3,000
Caditz (1976) 1 ⫺.131 MW p⫽.069* full 1 1 B 3 1 2 2 1 1 adult b/u 1 m/o 196
Campbell (1958) 1 ⫺.067 pp⫽.01* some 1 1 W 1 3 99 3 1 1 adol b/u 1 edu 746
Canter & Shoemaker
(1960) 1 ⫺.263 M/SD p ⫽.042* some 1 2 W 1 2 99 2 1 5 coll f 1 org 30
Carlson & Widaman
(1988) 1 ⫺.290 F70.4* full 1 1 B 2 2 99 2 1 1 coll b/u 3 trav 823
Carstensen et al. (1982) 1 ⫺.382 F4.35 none 1 2 B 3 2 4 3 2 2 child b/u 1 edu 26
Carter & Mitchell
(1956) 1 ⫺.218 t⫺2.18 some 1 1 B 3 1 1 2 1 1 adol b/u 1 m/o 124
Casey (1978) 1 ⫺.210 r⫺.210* some 1 1 W 1 1 99 2 1 4 adult b/u 1 edu 100
Caspi (1984) 1 ⫺.488 Mult p⫽.001 some 1 2 B 2 2 99 2 2 2 child b/u 1 edu 38
Catlin (1977) 1 ⫺.084 r⫺.084* some 2 1 W 1 1 1 2 1 1 coll b/u 1 edu 570
Chadwick et al. (1971) 1 ⫺.243 r⫺.243* some 1 1 W 1 1 2 2 1 1 adol b/u 1 edu 300
2⫺.155 r⫺.155* some 1 1 W 1 1 2 2 1 1 adol b/u 1 edu 35
Chang (1973) 1 ⫺.197
2
8.87 full 1 1 W 1 1 2 2 1 1 coll b/u 1 m/o 238
Chang (1998) 1 ⫺.021 r⫺.021* some 1 1 W 1 1 1 3 1 1 adult b/u 1 org 260
2⫺.113 r⫺.113* some 1 1 W 1 1 1 3 1 1 adult b/u 1 org 244
Chen et al. (1970) 1 ⫺.254 Prop 31/56 some 1 1 B 3 1 1 1 1 1 coll b/u 3 m/o 99
Chinsky & Rappaport
(1970) 1 ⫺.125 p.230 full 1 2 B 2 2 4 2 1 5 coll b/u 1 org 90
2⫺.213
2
10.8* none 1 2 W 1 2 4 2 1 99 adult b/u 1 org 119
Chou & Mak (1998) 1 ⫺.085 r⫺.085* some 1 1 W 1 1 2 2 1 5 adult b/u 6 m/o 1,273
Cleland & Cochran
(1961) 1 ⫺.023 p.750* some 1 2 W 1 2 99 2 1 6 adol b/u 1 res 98
Cle´ment et al. (1977) 1 ⫺.140 F4.68* full 1 1 B 2 2 99 1 1 1 adol b/u 4 trav 253
Clore et al. (1978) 1 ⫺.151 F2.56* none 1 2 B 3 2 4 2 2 1 child b/u 1 rec 112
Clunies-Ross &
O’Meara (1989) 1 ⫺.337 M/SD p ⫽.009* none 1 3 B 3 2 4 3 2 4 child b/u 5 rec 60
Colca et al. (1982) 1 ⫺.263 F4.75* none 1 2 B 4 2 4 2 2 1 child b/u 1 edu 64
772 PETTIGREW AND TROPP
This document is copyrighted by the American Psychological Association or one of its allied publishers.
This article is intended solely for the personal use of the individual user and is not to be disseminated broadly.
Appendix (continued)
Reference Sample rTest Statistic Choice Pub Type B/W Control IV IVQ DVQ Prog Target Age Sex Geo Set N
Cook & Wollersheim
(1976) 1 ⫺.013 Mult p⫽.87* some 1 2 B 2 3 99 2 1 6 adol b/u 1 edu 150
Cook (1969) 1 ⫺.316 Prop 65/91 none 1 3 B 2 2 4 3 2 1 coll f 1 lab 46
Cookston (1973) 1 ⫺.372 F5.10* some 2 2 B 3 2 99 2 2 1 coll b/u 1 edu 47
2⫺.272 F4.92* some 2 2 B 3 2 99 2 2 1 coll b/u 1 edu 62
Cotten-Huston & Waite
(2000) 1 ⫺.267 Mult p⫽.000* some 1 1 W 1 1 1 3 1 3 coll b/u 1 m/o 150
Couper et al. (1991) 1 ⫺.156 t⫺1.68* none 1 2 B 2 2 4 4 2 2 adol b/u 1 lab 114
Cousens & Crawford
(1988) 1⫺.309 M/SD p ⫽.000* some 1 1 B 3 1 2 3 1 5 adult b/u 5 m/o 158
Cowen et al. (1958) 1 ⫹.039 t⫹0.39 full 1 1 B 3 1 1 3 1 4 adult b/u 1 edu 101
Crain & Weisman
(1972) 1 ⫺.074 r⫺.074 full 1 1 W 1 1 1 2 1 1 adult m 1 m/o 1,715
2⫺.110 r⫺.110 full 1 1 W 1 1 1 2 1 1 adult f 1 m/o 2,043
Creech (1977) 1 ⫺.213 F18.2* full 1 2 W 1 2 4 3 1 5 coll m 1 org 95
Crull & Bruton (1979) 1 ⫺.196 M/SD p ⫽.000* full 1 1 B 2 1 1 2 1 99 coll b/u 1 m/o 1,043
D’Augelli (1989) 1 ⫺.143 r⫺.143* full 1 1 W 1 1 1 3 1 3 coll b/u 1 m/o 101
D’Augelli & Rose
(1990) 1 ⫺.200 r⫺.200* full 1 1 W 1 1 1 2 1 3 coll b/u 1 m/o 218
Davidson et al. (1983) 1 ⫺.330 r⫺.330* full 1 1 W 1 1 2 2 1 1 adult b/u 5 m/o 150
Dellmann-Jenkins et al.
(1986) 1 ⫺.188 Prop 26/44* none 1 2 B 2 2 4 2 2 2 child b/u 1 m/o 30
Dellmann-Jenkins et al.
(1991) 1 ⫺.235 Prop 85/98* some 1 2 B 3 2 4 4 2 2 child b/u 1 m/o 31
Desforges et al. (1991) 1 ⫺.150 M/SD p ⫽.21* none 1 2 W 1 2 4 2 2 5 coll b/u 1 lab 35
2⫺.291 M/SD p ⫽.01* none 1 2 W 1 2 4 2 2 5 coll b/u 1 lab 29
Deutsch & Collins
(1951) 1 ⫺.288 Prop 40/69* none 1 1 B 3 1 2 2 1 1 adult f 1 res 390
Deutsche Shell (2000) 1 ⫺.250 r⫺.250 some 1 1 W 1 1 3 3 1 1 adol b/u 2 m/o 3,000
Di Tullio (1982) 1 ⫺.873 M/SD p ⫽.000* none 2 3 B 2 2 4 3 1 6 adult m 1 org 76
Diamond & Lobitz
(1973) 1 ⫺.335 t⫺3.00* full 1 2 B 1 2 4 2 2 99 coll b/u 1 m/o 73
2⫺.447 t⫺3.46* full 1 2 W 1 2 4 2 2 99 adult m 1 m/o 12
Dijker (1987) 1 ⫺.159 r⫺.159* full 1 1 W 1 1 2 3 1 1 adult b/u 2 m/o 95
Distefano & Pryer
(1970) 1 ⫺.157 p.06* full 1 2 W 1 2 4 2 1 5 adult b/u 1 res 71
Dodson (1970) 1 ⫺.494 t⫺4.40* full 2 2 W 1 2 4 3 1 1 coll b/u 1 edu 15
2⫺.034 t⫺0.13* full 2 2 W 1 2 4 3 1 1 coll b/u 1 edu 8
Doka (1985–1986) 1 ⫺.013 Prop 51/52* full 1 2 B 4 2 4 2 1 2 adol b/u 1 rec 48
Donaldson & Martinson
(1977) 1 ⫺.253 p.05* none 1 2 B 3 2 4 3 1 4 coll b/u 1 edu 120
Dooley & Frankel
(1990) 1 ⫺.528 p.000* full 1 2 W 1 2 99 3 2 2 adol b/u 4 res 21
Drake (1957) 1 ⫺.007 Prop 33/34* none 1 1 B 3 1 1 2 1 2 coll b/u 1 m/o 397
Dubey (1979) 1 ⫹.134
2
7.72 full 1 1 B 4 1 2 2 1 99 adult b/u 6 res 428
2⫺.173
2
3.25 full 1 1 B 4 1 2 2 1 99 adult b/u 6 res 109
Duckitt (1984) 1 ⫺.201 r⫺.201* full 1 1 W 1 1 1 2 1 3 adult b/u 6 m/o 1,420
Dunbar (2000) 1 ⫺.443 r⫺.443 some 2 1 W 1 1 2 2 1 1 coll b/u 2 m/o 125
Eaton & Clore (1975) 1 ⫺.185 t⫺1.96 some 1 2 B 4 2 4 4 2 1 child b/u 1 rec 112
Eberhardt & Mayberry
(1995) 1 ⫺.120 r⫺.120* full 1 1 W 1 1 3 3 1 4 adult b/u 5 org 172
Eddy (1986) 1 ⫺.121 Prop 50/62* some 1 2 W 1 2 99 2 1 2 coll b/u 1 org 56
Eller (2000) 1 ⫺.084 r⫺.084* some 2 1 W 1 1 3 3 1 1 coll b/u 2 m/o 104
2⫺.363 r⫺.363* full 2 1 W 1 1 3 3 1 99 coll b/u 2 trav 102
3⫺.210 r⫺.210* none 2 1 W 1 1 3 3 1 99 adol b/u 2 edu 708
Eller & Abrams (1999) 1 ⫺.275 r⫺.275* some 2 1 W 1 1 3 3 1 1 coll b/u 6 m/o 67
Eller et al. (1999/2000) 1 ⫺.297 r⫺.297* some 2 1 W 1 1 2 3 1 1 coll b/u 6/1 edu 239
2⫺.300 r⫺.300* some 2 1 W 1 1 2 3 1 1 coll b/u 6/1 edu 90
Eller et al. (2000) 1 ⫺.272 r⫺.272* some 2 1 W 1 1 3 3 1 1 adult b/u 6/1 m/o 207
Ellis & Vasseur (1993) 1 ⫺.437 r⫺.437* none 1 3 W 1 1 2 2 1 3 coll b/u 1 m/o 108
Emerton & Rothman
(1978) 1 ⫹.124 t⫹1.37 full 1 1 W 1 1 2 2 1 4 coll b/u 1 edu 30
Ervin (1993) 1 ⫺.025 r⫺.025* some 2 1 W 1 1 2 1 1 1 coll b/u 1 m/o 100
2⫺.239 r⫺.239* some 2 1 W 1 1 2 1 1 1 coll b/u 1 m/o 130
Eshel & Dicker (1995) 1 ⫺.260 M/SD p ⫽.001* some 1 1 B 4 2 99 1 1 1 adol b/u 3 edu 160
Esposito & Peach
(1983) 1⫺.728 p.001 some 1 1 W 1 2 99 2 2 4 child b/u 1 edu 9
(Appendix continues)
773
META-ANALYTIC TEST OF INTERGROUP CONTACT THEORY
This document is copyrighted by the American Psychological Association or one of its allied publishers.
This article is intended solely for the personal use of the individual user and is not to be disseminated broadly.
Appendix (continued)
Reference Sample rTest Statistic Choice Pub Type B/W Control IV IVQ DVQ Prog Target Age Sex Geo Set N
Esposito & Reed (1986) 1 ⫺.490 M/SD p ⫽.000* some 1 1 B 3 2 99 4 2 4 child b/u 1 edu 92
Evans (1976) 1 ⫺.539 M/SD p ⫽.001* none 1 3 B 1 2 4 3 2 4 coll b/u 1 lab 60
Felton (1975) 1 ⫺.473 t⫺2.84 full 1 2 W 1 2 99 3 2 4 adult f 1 org 7
Fenrick & Petersen
(1984) 1 ⫺.451 Mult p⫽.000* none 1 2 B 3 2 4 2 2 99 child b/u 1 edu 63
Fichten & Amsel (1986) 1 .000 pns some 1 1 B 3 1 1 2 1 4 coll b/u 4 m/o 115
Fichten et al. (1988) 1 ⫺.206 p.05 full 1 1 B 2 1 2 1 1 4 adult b/u 4 edu 91
Fichten et al. (1989) 1 ⫺.158 t⫺1.73 full 1 1 B 2 1 1 2 1 4 coll b/u 4 m/o 125
Finchilescu (1988) 1 ⫺.335 F14.3* some 1 1 B 2 2 99 2 1 1 coll b/u 6 org 113
Florian & Kehat (1987) 1 ⫺.079 M/SD p ⫽.46 none 1 1 B 3 2 4 3 2 4 adol b/u 1 m/o 88
Floyd (1970) 1 ⫺.170 Prop 44/61 some 2 1 B 2 1 2 2 1 5 adult f 1 m/o 131
Foley (1977) 1 ⫺.070 F⫺0.070 full 1 1 W 1 3 99 2 1 1 adult m 1 m/o 40
2⫺.223 r⫺.223 some 1 1 W 1 3 99 2 1 1 adult m 1 org 30
Ford (1973) 1 ⫺.503 Prop 24/74* some 1 1 B 3 1 2 2 1 1 adult f 1 res 72
2⫺.148 Prop 43/58* none 1 1 B 3 1 2 2 1 1 adult f 1 res 73
Friedman (1975) 1 ⫺.266 M/SD p ⫽.05 none 2 2 B 2 2 4 3 2 4 child b/u 1 edu 55
Friesen (1966) 1 ⫺.250 r⫺.250 some 2 1 W 1 1 2 3 1 4 adult b/u 6 org 241
2⫺.310 r⫺.310 some 2 1 W 1 1 2 3 1 4 adult b/u 6 org 135
Furnham & Gibbs
(1984) 1 ⫺.178 F8.10* full 1 1 B 3 1 1 2 1 4 adol b/u 2 m/o 135
Furnham & Pendred
(1983) 1 .000 pns some 1 1 W 1 1 2 2 1 4 adult b/u 2 m/o 96
Furuto & Furuto (1983) 1 ⫺.232 p.01* none 1 3 B 3 2 4 2 2 1 coll b/u 1 lab 124
Gaertner et al. (1994) 1 ⫺.328 r⫺.328* some 1 1 W 1 1 2 2 1 1 adol b/u 1 edu 1,181
Gaertner et al. (1999) 1 ⫺.143 F12.11* none 1 3 B 2 2 4 2 2 99 coll b/u 1 lab 576
Gardner et al. (1969) 1 .106 O p⫽.38* full 1 1 B 2 2 99 2 1 1 adult b/u 6 m/o 68
Gardner et al. (1973) 1 ⫺.115 O p⫽.01* full 1 1 W 1 1 1 2 1 1 coll b/u 6 edu 250
Gardner et al. (1974) 1 ⫺.134 t⫺3.92* full 1 1 W 1 1 99 2 1 1 adol b/u 2 trav 211
Gelber (1993) 1 ⫺.299 M/SD p ⫽.013* none 2 3 W 1 2 4 3 2 4 coll b/u 1 lab 37
2⫺.378 M/SD p ⫽.001* none 2 3 W 1 2 4 3 2 4 coll b/u 1 lab 37
3⫺.415 M/SD p ⫽.000* none 2 3 W 1 2 4 3 2 4 coll b/u 1 lab 38
Gelfand & Ullmann
(1961) 1 ⫺.295 t⫺2.31* full 1 2 B 3 2 4 3 2 5 coll m 1 org 59
Gentry (1987) 1 ⫺.096 p.18 full 1 1 W 1 1 1 3 1 3 coll m 1 m/o 96
2⫺.191 p.006 full 1 1 W 1 1 1 3 1 3 coll f 1 m/o 105
Gerbert et al. (1991) 1 ⫺.147 p.040* some 1 1 B 4 1 1 3 1 99 adult b/u 1 m/o 1,320
Gething (1991) 1 ⫺.256 M/SD p ⫽.000 some 1 1 B 4 1 2 3 1 4 adult b/u 5 m/o 460
Glass & Meckler (1972) 1 ⫺.483 M/SD p ⫽.004 full 1 2 W 1 2 4 1 2 6 adult f 1 edu 18
Glass & Trent (1980) 1 ⫺.034 F1.74 none 1 1 W 1 1 1 2 1 2 adol b/u 1 res 388
Glassner & Owen
(1976) 1 ⫺.236 r⫺.236* full 1 1 W 1 1 1 2 1 3 coll b/u 1 edu 61
Glock et al. (1975) 1 ⫺.259 Prop 53/66 full 1 1 B 2 1 1 3 1 1 adol b/u 1 edu 750
2⫺.186 Prop 41/60 full 1 1 B 2 1 1 3 1 1 adol b/u 1 edu 608
3⫺.101 Prop 31/41 full 1 1 B 2 1 1 3 1 1 adol b/u 1 edu 1,328
Glover & Smith (1997) 1 ⫺.083 t⫺0.53 none 1 1 B 3 2 99 2 1 1 child b/u 1 edu 41
2⫺.503 t⫺2.45 none 1 1 B 3 2 99 2 1 1 child b/u 1 edu 19
Goldstein & Simpkins
(1973) 1 ⫺.471 t⫺4.12* full 1 1 W 1 2 99 3 2 99 coll b/u 1 org 15
Gordon & Hallauer
(1976) 1 ⫺.330
2
6.71* full 1 2 W 1 2 99 2 2 2 coll b/u 1 res 40
Gosse & Sheppard
(1979) 1 ⫺.244 M/SD p ⫽.000 full 1 1 B 3 1 1 2 1 4 adol b/u 4 m/o 273
2 .027 M/SD p ⫽.662 full 1 1 B 3 1 1 2 1 4 adol b/u 4 m/o 268
3⫺.477 M/SD p ⫽.000 full 1 1 B 3 1 1 2 1 4 coll b/u 4 m/o 155
Goto (2000) 1 ⫺.395 r⫺.395* some 2 1 W 1 1 2 2 1 1 adol b/u 1 m/o 511
2⫺.309 r⫺.309* some 2 1 W 1 1 2 2 1 1 adol b/u 1 m/o 135
Gottlieb & Corman
(1975) 1 ⫺.020 F0.63* some 1 1 W 1 1 1 2 1 6 adult b/u 1 m/o 394
Grack & Richman
(1996) 1 ⫺.713 F35.15 none 1 3 B 2 2 4 3 2 3 coll b/u 1 lab 34
Graffi & Minnes (1988) 1 .000 pns full 1 1 W 1 1 1 3 1 6 child b/u 4 edu 120
Grantham & Block
(1983) 1 ⫺.089 p.15* some 1 1 W 1 1 1 2 1 5 coll b/u 1 edu 289
2⫺.095 p.042 some 1 1 W 1 1 1 2 1 5 coll b/u 1 edu 229
Gray & Thompson
(1953) 1 ⫺.141 O p⫽.000 full 1 1 W 1 1 1 2 1 1 coll b/u 1 m/o 400
2⫺.447 O p⫽.000 full 1 1 W 1 1 1 2 1 1 coll b/u 1 m/o 300
774 PETTIGREW AND TROPP
This document is copyrighted by the American Psychological Association or one of its allied publishers.
This article is intended solely for the personal use of the individual user and is not to be disseminated broadly.
Appendix (continued)
Reference Sample rTest Statistic Choice Pub Type B/W Control IV IVQ DVQ Prog Target Age Sex Geo Set N
Green & Stoneman
(1989) 1 .000 pns some 1 1 W 1 1 1 3 1 6 adult b/u 1 m/o 117
Greenland & Brown
(1999) 1 ⫺.549 r⫺.549* some 1 1 W 1 1 3 2 1 1 coll b/u 2 m/o 236
2⫹.177 r⫹.177* some 1 1 W 1 1 3 2 1 1 coll b/u 2 m/o 40
Gregory (1997) 1 ⫺.189 r⫺.189 full 1 1 W 1 1 2 2 1 4 coll b/u 1 m/o 140
Gronberg (1982) 1 ⫺.341 t⫺3.58* none 2 2 B 2 2 99 2 2 4 child b/u 1 edu 97
2⫺.346 t⫺3.62* none 2 2 B 2 2 99 2 2 4 child b/u 1 edu 96
3⫺.336 t⫺3.57* none 2 2 B 2 2 99 2 2 4 child b/u 1 edu 100
Gruesser (1950) 1 ⫺.142 t⫺3.73* full 2 1 B 3 1 2 2 1 1 adol b/u 1 res 737
Gundlach (1950) 1 ⫺.317 Prop 12/44* some 1 1 B 3 3 99 1 1 1 adult b/u 1 org 1,418
Haddock et al. (1993) 1 ⫺.170 r⫺.170* full 1 1 W 1 1 2 2 1 3 coll b/u 4 m/o 151
Hale (1998) 1 ⫺.384 t⫺2.94 some 1 1 B 3 1 2 2 1 2 adult b/u 1 m/o 50
Hall (1969) 1 .000 pns some 2 3 B 3 2 4 2 2 6 coll b/u 1 org 264
Hall (1998) 1 ⫺.186 p.000* full 2 2 B 2 2 4 3 2 99 child b/u 1 rec 303
Hamblin (1962) 1 ⫺.230 r⫺.230 some 1 1 W 1 1 2 3 1 1 adult b/u 1 m/o 100
2⫺.170 r⫺.170 some 1 1 W 1 1 2 3 1 1 adult b/u 1 m/o 100
Hansen (1982) 1 ⫺.484 t⫺5.44 full 1 1 B 2 1 1 3 1 3 coll b/u 1 m/o 107
Harding & Hogrefe
(1952) 1 ⫺.030 Prop 55/58* full 1 1 B 2 1 1 3 1 1 adult b/u 1 org 210
Haring et al. (1958) 1 ⫺.250 t⫺.266* full 1 2 B 1 2 4 2 2 4 adult b/u 1 edu 106
Haring et al. (1987) 1 ⫺.248 p.05* full 1 3 B 2 2 4 4 2 1 adol b/u 1 m/o 59
Harlan (1942) 1 ⫺.804 M/SD p ⫽.000 full 1 1 B 1 1 1 3 1 1 coll b/u 1 m/o 502
Harper & Wacker
(1985) 1 ⫺.196 O p⫽.05 some 1 1 B 3 1 2 2 1 4 child b/u 1 edu 100
Harris & Fiedler (1988) 1 .000 pns some 1 1 W 1 1 2 2 1 2 child b/u 1 edu 157
Hastings & Graham
(1995) 1 ⫺.107 F5.97* full 1 1 W 1 1 1 2 1 6 adol b/u 2 edu 128
Hastings et al. (1998) 1 ⫺.256 F6.06* some 1 1 B 3 1 1 3 1 4 coll f 2 m/o 87
Hatanaka (1982) 1 ⫺.225 r⫺.225* none 2 2 W 1 2 99 2 2 1 adult b/u 1 lab 128
Hazzard (1983) 1 ⫺.111 r⫺.111* full 1 1 W 1 1 2 3 1 4 child b/u 1 m/o 367
He´bert et al. (2000) 1 ⫺.200 t⫺.285* some 1 1 B 3 1 1 2 1 5 adol b/u 4 m/o 284
Helmstetter et al. (1994) 1 ⫺.211 M/SD p ⫽.006* some 1 1 B 3 1 2 3 1 4 adol b/u 1 m/o 161
Herek (1988) 1 ⫺.064 r⫺.064* full 1 1 W 1 1 1 3 1 3 coll f 1 m/o 73
2⫺.048 r⫺.048* full 1 1 W 1 1 1 3 1 3 coll m 1 m/o 37
3⫺.135 r⫺.135* full 1 1 W 1 1 1 3 1 3 coll f 1 m/o 220
4⫺.124 r⫺.124* full 1 1 W 1 1 1 3 1 3 coll m 1 m/o 169
Herek (1999) 1 ⫺.389 M/SD p ⫽.000* full 2 1 B 2 1 2 3 1 3 adult f 1 m/o 652
2⫺.302 M/SD p ⫽.000* full 2 1 B 2 1 2 3 1 3 adult m 1 m/o 524
Herek & Capitanio
(1996) 1 ⫺.354 F52.3* full 1 1 B 2 1 1 3 1 3 adult b/u 1 m/o 422
Herek & Capitanio
(1997) 1 ⫺.189 M/SD p ⫽.000* full 1 1 B 2 1 1 2 1 3 adult b/u 1 m/o 594
Herek & Glunt (1993) 1 ⫺.392 F152.9 full 1 1 B 2 1 1 3 1 3 adult b/u 1 m/o 937
Herman (1970) 1 ⫺.160 Prop 37/53 full 1 1 W 1 2 99 2 1 1 coll b/u 1 m/o 56
Hicks & Spaner (1962) 1 ⫺.479 t⫺4.69* none 1 1 B 2 2 99 2 1 5 coll b/u 1 org 78
2⫺.201 Mult p⫽.01* full 1 1 B 2 2 99 2 1 5 coll b/u 1 org 330
Hill (1984) 1 ⫺.316 r⫺.316* full 1 1 W 1 1 2 2 1 1 adult b/u 2 m/o 200
Hillis (1986) 1 ⫹.075 t⫹0.77* none 2 2 B 2 2 99 2 2 4 child b/u 1 edu 117
Hillman & Stricker
(1996) 1 ⫺.280 r⫺.280 some 1 1 W 1 1 2 3 1 2 coll b/u 1 m/o 241
Hoeh & Spuck (1975) 1 ⫺.283 M/SD p ⫽.121* full 1 2 W 1 2 4 3 2 1 adol b/u 1 trav 15
Hofman & Zak (1969) 1 ⫺.208 p.046* full 1 1 W 1 2 2 2 1 1 adol b/u 6 m/o 46
Holmes et al. (1999) 1 ⫺.157 r⫺.157* some 1 1 W 1 1 3 3 1 5 adult b/u 1 m/o 83
Holtzman (1956) 1 ⫺.148
2
23.6* some 1 1 W 1 1 2 2 1 1 coll b/u 1 m/o 539
Holzberg & Gewirtz
(1963) 1 ⫺.526 t⫺4.50 full 1 2 B 2 2 4 2 2 5 coll b/u 1 org 59
Horenczyk & Bekerman
(1997) 1 ⫺.207 M/SD p ⫽.000 full 1 2 W 1 2 99 2 2 1 adol b/u 6 rec 148
2⫺.148 M/SD p ⫽.076 full 1 2 W 1 2 99 2 1 1 adol b/u 6 rec 72
Hortacsu (2000) 1 ⫺.155 r⫺.155 some 1 1 W 1 1 3 2 1 1 coll m 6 edu 47
2⫺.034 r⫺.034 some 1 1 W 1 1 3 2 1 1 coll m 6 edu 49
Hraba et al. (1996) 1 ⫺.208 r⫺.208* some 1 1 W 1 1 2 2 1 1 coll b/u 1 m/o 208
2⫺.181 r⫺.181* some 1 1 W 1 1 2 2 1 1 coll b/u 1 m/o 193
Hughey (1988) 1 ⫺.166 r⫺.166* some 2 1 W 1 1 2 3 1 4 adult b/u 1 edu 162
Hunt (1960) 1 ⫺.158 p.01 full 1 1 W 1 1 1 1 1 1 adult b/u 1 m/o 133
Hunt & Hunt (2000) 1 ⫺.186 r⫺.186* some 1 1 W 1 1 3 3 1 4 coll b/u 1 m/o 274
(Appendix continues)
775
META-ANALYTIC TEST OF INTERGROUP CONTACT THEORY
This document is copyrighted by the American Psychological Association or one of its allied publishers.
This article is intended solely for the personal use of the individual user and is not to be disseminated broadly.
Appendix (continued)
Reference Sample rTest Statistic Choice Pub Type B/W Control IV IVQ DVQ Prog Target Age Sex Geo Set N
Ibrahim (1970) 1 ⫺.176 Prop 54/71 full 1 1 B 3 1 3 3 1 1 coll b/u 1 m/o 402
Ichildov & Even-Dar
(1984) 1 ⫺.312 M/SD p ⫽.002* full 1 1 W 1 2 2 3 2 1 adol b/u 3 m/o 49
Iguchi & Johnson
(1966) 1 ⫺.222 Prop 32/55* full 1 2 B 2 2 4 3 2 5 coll b/u 1 res 98
Ijaz (1980) 1 ⫺.108 F1.92* some 2 1 B 4 1 2 2 1 1 adol b/u 4 edu 164
Ingamells et al. (1996) 1 ⫺.199 t⫺2.30 some 1 1 B 3 1 2 2 1 5 adult b/u 2 m/o 133
Irish (1952) 1 ⫺.063 p.30* some 1 1 B 4 1 99 2 1 1 adult b/u 1 res 267
Islam & Hewstone
(1993) 1 ⫺.490 r⫺.490* full 1 1 W 1 1 2 1 1 1 coll b/u 6 m/o 65
2⫺.240 r⫺.240* full 1 1 W 1 1 2 1 1 1 coll b/u 6 m/o 66
Ivester & King (1977) 1 .000 pns some 1 1 W 1 1 1 3 1 2 adol b/u 1 m/o 413
Jackman & Crane
(1986) 1 ⫺.268 Prop 38/64* full 1 1 B 3 1 2 2 1 1 adult b/u 1 m/o 1,131
Jaffe (1966/1967) 1 ⫺.115 M/SD p ⫽.21 full 1 1 B 2 1 1 2 1 6 adol b/u 1 m/o 119
James (1955) 1 ⫺.907 Prop 5/95 none 1 1 W 1 2 99 4 2 1 adol b/u 2 edu 43
James-Valutis (1993) 1 ⫺.188 r⫺.188 some 2 1 W 1 1 2 3 1 1 coll b/u 1 edu 213
Jaques et al. (1970) 1 .000 pns some 1 1 W 1 1 1 3 1 4 coll b/u 2 m/o 360
2 .000 pns some 1 1 W 1 1 1 3 1 4 coll b/u 2 m/o 307
3⫺.111 p.005 some 1 1 W 1 1 1 3 1 4 coll b/u 2 m/o 322
Jeffries & Ransford
(1969) 1 ⫺.307 Prop 16/46* full 1 1 B 2 1 2 1 1 1 adult b/u 1 m/o 99
Johannsen et al. (1964) 1 ⫺.153 p.075* full 1 2 B 3 2 99 3 1 5 coll b/u 1 org 135
Johnson & Johnson
(1981) 1 ⫺.240 t⫺1.56 none 1 3 B 2 2 4 4 2 5 child b/u 1 edu 40
Johnson & Johnson
(1985) 1 ⫺.377 t⫺1.82* none 1 3 B 3 2 4 2 2 4 child b/u 1 edu 20
Johnson & Marini
(1998) 1 ⫺.469 r⫺.469 full 1 1 W 1 1 3 3 1 1 adol b/u 1 edu 3,000
2⫺.557 r⫺.557 full 1 1 W 1 1 3 3 1 1 adol b/u 1 edu 2,648
Johnstone (1992) 1 ⫺.258 r⫺.258* full 2 1 W 1 1 3 3 1 4 coll b/u 1 m/o 185
2⫺.229 r⫺.229* full 2 1 W 1 1 3 3 1 4 coll b/u 1 m/o 189
Jones (1960) 1 ⫺.515 Prop 23/74* some 2 1 B 4 2 99 4 1 1 adult b/u 1 org 76
Jones et al. (1981) 1 ⫺.364 M/SD p ⫽.006* none 1 3 W 3 2 4 3 2 4 child b/u 1 edu 25
2⫺.537 Mult p⫽.000* none 1 3 B 3 2 4 3 2 1 child b/u 1 edu 74
Kalson (1976) 1 ⫺.414
2
5.14 full 1 1 W 1 2 99 2 2 6 adult b/u 1 rec 15
Kamal & Maruyama
(1990) 1 ⫺.320 r⫺.320 full 1 1 W 1 1 2 2 1 1 coll b/u 1 m/o 187
Kanouse-Roberts (1977) 1 ⫺.197 t⫺1.17* full 2 2 B 3 2 99 2 1 2 adol f 1 org 34
Katz & Yochanan
(1988) 1 ⫺.533 M/SD p ⫽.000* none 1 1 B 2 2 99 3 2 1 child b/u 3 edu 108
Kelly et al. (1958) 1 ⫺.286 r⫺.286* full 1 1 W 1 1 2 2 1 1 coll b/u 1 m/o 547
Kephart (1957) 1 ⫺.128 Prop 39/51* some 1 1 B 3 1 1 2 1 1 adult m 1 org 1,081
Kidwell & Booth (1977) 1 ⫺.086 p.08* full 1 1 B 4 1 1 2 1 2 adult b/u 1 edu 409
Kierscht & DuHoux
(1980) 1 ⫺.474 F40.46 none 1 2 B 2 2 4 2 1 4 child b/u 1 edu 140
Kisabeth & Richardson
(1985) 1 ⫺.175 M/SD p ⫽.277 none 1 2 B 3 2 4 2 2 4 coll b/u 1 edu 41
Kish & Hood (1974) 1 ⫺.334 p.013 none 1 2 W 1 2 99 2 1 5 coll b/u 1 org 28
2⫺.232 p.31 none 1 2 W 1 2 99 2 1 5 coll b/u 1 org 10
3⫺.228 p.05 none 1 2 W 1 2 99 2 1 5 coll b/u 1 org 37
Kishi & Meyer (1994) 1 ⫺.270 M/SD p ⫽.049* some 1 2 B 2 2 4 2 1 4 adol m 1 edu 53
2⫺.317 M/SD p ⫽.006* some 1 2 B 2 2 4 2 1 4 adol f 1 edu 74
Kleinman (1983) 1 ⫺.203 t⫺2.63* full 2 2 W 1 2 99 3 2 5 coll f 1 org 40
Knox et al. (1986) 1 ⫺.414 r⫺.414* full 1 1 W 1 1 3 2 1 2 coll b/u 4 m/o 110
Knussen & Niven
(1999) 1 ⫺.130 r⫺.130 some 1 1 W 4 1 2 2 1 99 adult b/u 2 org 174
Kobe & Mulick (1995) 1 ⫹.019 r⫹.019* full 1 1 W 1 1 2 3 1 6 coll b/u 1 m/o 37
Kocarnik & Ponzetti
(1986) 1 ⫺.163 t⫺.87* some 1 1 B 3 3 99 2 2 2 child b/u 1 edu 30
Koslin et al. (1969) 1 ⫺.339 M/SD p ⫽.000* some 1 2 B 2 2 4 2 1 1 child b/u 1 edu 64
2⫺.344 M/SD p ⫽.000 some 1 2 B 2 2 4 2 1 1 child b/u 1 Edu 65
Kosmitzki (1996) 1 ⫺.106 t⫺1.24 full 1 1 B 2 1 2 3 1 1 adult b/u 1 m/o 254
2⫺.187 t⫺1.98 full 1 1 B 2 1 2 3 1 1 adult b/u 1 m/o 137
Krajewski & Flaherty
(2000) 1 ⫺.206 M/SD p ⫽.085* some 1 1 B 3 1 1 2 1 6 adol m 1 m/o 70
2⫺.110 M/SD p ⫽.177* some 1 1 B 3 1 1 2 1 6 adol f 1 m/o 74
776 PETTIGREW AND TROPP
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Appendix (continued)
Reference Sample rTest Statistic Choice Pub Type B/W Control IV IVQ DVQ Prog Target Age Sex Geo Set N
Kuelker (1996) 1 ⫺.128 r⫺.128* some 2 1 W 1 1 2 3 1 5 adult b/u 4 m/o 489
Kulik et al. (1969) 1 ⫺.123 t⫺2.20 full 1 1 B 2 2 99 2 1 5 coll b/u 1 org 318
Kurtzweil (1995) 1 ⫺.162 r⫺.162* some 2 1 W 1 1 2 3 1 1 coll b/u 1 m/o 240
Ladd et al. (1984) 1 ⫺.544 F26.92 some 1 1 W 1 2 99 4 2 4 adol b/u 1 edu 16
Lambert et al. (1990) 1 ⫺.225 Prop 82/96* some 1 2 B 3 2 4 2 2 2 child b/u 1 edu 31
Lance (1987) 1 ⫺.450 Prop 18/61 some 1 2 B 2 1 99 2 1 3 coll b/u 1 edu 46
Lance (1992) 1 ⫺.332 Prop 35/68 none 1 1 B 2 2 99 3 1 3 coll b/u 1 edu 228
Lance (1994) 1 ⫺.294 Prop 11/35* full 1 1 B 3 1 1 3 2 3 coll b/u 1 m/o 140
Landis et al. (1985) 1 ⫺.570 M/SD p ⫽.015* none 1 3 B 4 2 4 4 2 1 coll m 1 lab 18
Larsen (1997) 1 ⫺.261 r⫺.261* some 2 1 W 1 1 2 2 1 1 adult b/u 1 m/o 11
2⫺.110 r⫺.110* some 2 1 W 1 1 2 2 1 1 adult b/u 1 m/o 6
Lazar et al. (1971) 1 ⫺.332 M/SD ⫺2.33 none 1 2 B 2 2 4 3 2 4 child b/u 1 edu 44
Leach (1990) 1 ⫺.206 Mult p⫽.041* some 2 1 B 3 1 1 2 1 4 coll b/u 1 m/o 98
Lebhart & Munz (1999) 1 ⫺.179 Prop 39/57* full 2 1 B 3 1 1 2 1 1 adult b/u 2 m/o 1,999
Leonard (1964) 1 ⫺.219 t⫺4.15 full 1 1 W 1 2 99 2 1 1 coll b/u 2 trav 85
Lepore & Brown (1997) 1 ⫺.410 r⫺.410 full 1 1 W 1 1 2 3 1 1 coll b/u 2 edu 162
Lessing et al. (1976) 1 ⫺.047 F2.35 some 1 1 W 1 1 1 2 1 1 adult f 1 edu 269
LeUnes et al. (1975) 1 ⫺.399 F32.4* full 1 2 B 2 2 4 2 1 6 coll b/u 1 res 179
Levine et al. (1969) 1 ⫺.203 Prop 45/65* some 2 1 W 1 1 1 1 1 1 adol b/u 1 m/o 419
2⫺.232 Prop 40/63* some 2 1 W 1 1 1 1 1 1 adol b/u 1 m/o 500
Levinson (1954) 1 ⫺.220 p.05 full 1 1 W 1 2 99 2 2 1 adult b/u 1 edu 28
2⫺.310 p.01 full 1 1 W 1 2 99 2 2 1 adult b/u 1 edu 28
Levinson &
Schermerhorn (1951) 1 ⫺.192 M/SD p ⫽.125 full 1 1 W 1 2 99 2 2 1 adult b/u 1 edu 32
Levy et al. (1993) 1 ⫺.199 F13.4* some 1 1 B 2 1 2 3 1 4 adult b/u 1 org 324
Lewis & Cleveland
(1966) 1 ⫺.187 p.031* some 1 2 B 3 2 99 3 2 5 coll b/u 1 org 134
Lewis & Frey (1988) 1 ⫺.439 F15.2* some 1 2 B 2 2 99 3 2 99 coll b/u 1 edu 66
Leyser & Abrams
(1983) 1 ⫺.210 M/SD p ⫽.000 some 1 2 B 3 2 99 3 2 4 coll b/u 1 edu 289
Leyser & Price (1985) 1 ⫺.111 M/SD p ⫽.39 none 1 2 B 2 2 99 2 1 4 child b/u 1 edu 60
Leyser et al. (1986) 1 ⫺.176 M/SD p ⫽.005* none 1 2 B 3 2 99 3 2 4 child b/u 1 edu 244
Li & Yu (1974) 1 ⫺.007 M/SD p ⫽.92* full 1 1 B 2 1 1 2 1 1 coll b/u 1 m/o 220
2⫹.043 M/SD p ⫽.60 full 1 1 B 2 1 1 2 1 1 coll b/u 1 m/o 145
Liebkind et al. (2000) 1 ⫺.325 r⫺.325 some 1 1 W 1 1 2 3 1 1 adult b/u 2 m/o 104
2⫺.185 r⫺.185 some 1 1 W 1 1 2 3 1 1 adult b/u 2 m/o 185
3⫺.152 r⫺.152 some 1 1 W 1 1 2 3 1 1 adult b/u 2 m/o 86
Link & Cullen (1986) 1 ⫺.266 M/SD p ⫽.001* some 1 1 B 3 1 3 3 1 5 adult b/u 1 m/o 153
2⫺.249 M/SD p ⫽.003* some 1 1 B 3 1 3 3 1 5 adult b/u 1 m/o 151
Lombardi (1963) 1 .000 pns some 1 1 B 3 1 2 3 2 1 adol b/u 1 edu 344
Lombroso et al. (1976) 1 ⫺.096 O p⫽.01 some 1 1 W 1 1 1 2 1 5 adol b/u 3 m/o 360
London & Linney
(1993) 1 ⫺.064 M/SD p ⫽.634 full 2 1 W 1 2 99 2 2 1 child b/u 1 rec 28
2⫺.141 M/SD p ⫽.362 full 2 1 W 1 2 99 2 2 1 child b/u 1 rec 21