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A Meta-Analysis of Procedures to Change Implicit Measures


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Using a novel technique known as network meta-analysis, we synthesized evidence from 492 studies (87,418 participants) to investigate the effectiveness of procedures in changing implicit measures, which we define as response biases on implicit tasks. We also evaluated these procedures’ effects on explicit and behavioral measures. We found that implicit measures can be changed, but effects are often relatively weak (|ds| < .30). Most studies focused on producing short-term changes with brief, single-session manipulations. Procedures that associate sets of concepts, invoke goals or motivations, or tax mental resources changed implicit measures the most, whereas procedures that induced threat, affirmation, or specific moods/emotions changed implicit measures the least. Bias tests suggested that implicit effects could be inflated relative to their true population values. Procedures changed explicit measures less consistently and to a smaller degree than implicit measures and generally produced trivial changes in behavior. Finally, changes in implicit measures did not mediate changes in explicit measures or behavior. Our findings suggest that changes in implicit measures are possible, but those changes do not necessarily translate into changes in explicit measures or behavior.
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A Meta-Analysis of Change in Implicit Bias
July 1, 2017
Patrick S. Forscher*1, Calvin K. Lai*2, Jordan R. Axt3, Charles R. Ebersole3, Michelle Herman4,
Patricia G. Devine5, and Brian A. Nosek3,6
1Dept. of Psychological Science, University of Arkansas, 2Dept. of Psychological & Brain
Sciences, Washington University in Saint Louis, 3Dept. of Psychology, University of Virginia,
4Dept. of Psychology, University of North Carolina at Chapel Hill, 5Dept. of Psychology,
University of Wisconsin Madison, 5Center for Open Science, Charlottesville, VA.
*Authors contributed equally to this manuscript. Order was determined by coin flip.
Author notes:
Conceived research: Forscher & Lai, Devine, Nosek; Designed research: Forscher & Lai;
Coordinated data collection: Lai; Coded articles: Forscher & Lai, Axt, Ebersole, Herman;
Analyzed data: Forscher; Wrote paper: Forscher & Lai; Revised paper: all authors.
We thank Katie Lancaster, Diana Abrego, Amy Bisker, Isabelle Gigante, Julie Lee, Lauren
Loffredo, Ryan Massopust, Margot Mellon, Kelci Straka, and Nicole Sather for their assistance
with the early phases of article coding. We also thank Mike W.-L. Cheung and Ian White for
their assistance and advice about the analyses presented in this paper.
Address correspondence to Calvin K. Lai, Dept. of Psychological & Brain Sciences, Washington
University in Saint Louis, One Brookings Drive, Saint Louis, MO, 63130 (Email: and/or Patrick S. Forscher, Dept. of Psychological Science, University of
Arkansas, 216 Memorial Hall, Fayetteville, AR 72701 (Email:
Data and materials for this project can be found at
Using a technique known as network meta-analysis that is new to psychological science, we
synthesized evidence from 494 studies (80,356 participants) to investigate the effectiveness of
different procedures to change implicit bias, and their effects on explicit bias and behavior. We
found that implicit bias can be changed, but the effects are often weak (|ds| < .30). Procedures
that associate sets of concepts, invoke goals or motivations, or tax mental resources changed
implicit bias the most, whereas procedures that induced threat, affirmation, or specific
moods/emotions changed implicit bias the least. Most procedures were brief and were tested
within a single experimental session, and funnel plot analyses suggested that the effects could be
inflated relative to their true population values. Many procedures changed explicit bias, but to a
smaller degree than they changed implicit bias. We found no evidence of change in
behavior. Finally, changes in implicit bias did not mediate changes in explicit bias or behavior.
Our findings suggest that changes in measured implicit bias are possible, but those changes do
not necessarily translate into changes in explicit bias or behavior. We discuss potential
interpretations of these findings, including the possibility that current manipulations change non-
associative aspects of implicit measures and the possibility that the automatic
retrieved associations do not influence explicit biases or behavior.
Keywords: meta-analysis, implicit bias, intervention, social cognition
A Meta-Analysis of Change in Implicit Bias
What we intend to do often conflicts with what we actually do. We may plan to diet but
find ourselves reaching for a chocolate bar over an apple. Or, we might try to quit smoking but
find the temptation of cigarettes too difficult to resist. We can even value racial equality but
choose to hire a White job candidate over a similarly qualified Black job candidate (Bertrand &
Mullainathan, 2004). These gaps between what we intend and what we actually do characterize
many societal problems, such as intergroup discrimination (Devine, 1989), depression (Beevers,
2005; Haeffel et al., 2007), and addiction (Wiers et al., 2010).
The prevalence of unwanted behaviors across many areas of human life suggests that
mental processes outside of one’s conscious awareness or control influence behavior (Smith &
DeCoster, 2000). Based on this reasoning, researchers have developed dual-process theories that
distinguish between automatic mental processes which are relatively fast, efficient, and
unintentional, and deliberate mental processes which are relatively slow, controlled, and
intentional. By this logic, the same underlying mental construct can be retrieved either
automatically or deliberately. For example, the association between the concepts “Flowers” and
“Good” can be retrieved automatically, as when a person spots a vase of flowers and feels good,
or deliberately, as when a person is asked to think about how much they like flowers.
Dual process theories posit that deliberate processes are more influential on behavior
when people have sufficient motivation, awareness, and the ability to reflect before acting,
whereas automatic processes are more influential when motivation, awareness, or the ability to
reflect are compromised (Devine, 1989; Fazio & Olson, 2014; cf. Greenwald et al., 2009). Dual
process theories also predict that dissociations between intentions and behavior are most likely to
occur when the output of automatic and deliberate processes are opposed. Given opposing
automatic and deliberate processes, lack of motivation, awareness, or the ability to reflect can
cause people to act against their intentions.
Dual process theories are attractive on both theoretical and practical grounds.
Theoretically, they provide a parsimonious approach for explaining dissociations between
intentions and behavior and between mental phenomena more broadly. Dual process theories are
used to account for such wide-ranging phenomena as attention (Schneider & Shiffrin, 1977;
Shiffrin & Schneider, 1977), reasoning (Evans, 1989; Sloman, 1996; Stanovich & West, 2000),
decision-making (Barbey & Sloman, 2007; Kahneman, 2011), memory (Jacoby & Dallas, 1981;
Roediger, 1990), attitudes (Wilson, Lindsey, & Schooler, 2000), stereotypes and prejudice
(Devine, 1989), the self (Schnabel & Asendorpf, 2010), motivation (Chartrand & Bargh, 2002),
and emotion regulation (Mauss, Bunge, & Gross, 2007). Practically, dual-process theories
suggest a solution to problems caused by unintentionally biased behavior: change the automatic
processes and changes in behavior will follow (Lai, Hoffman, & Nosek, 2013; Forscher &
Devine, 2014).
Implicit and explicit measures of mental associations between concepts have been a
particular interest for dual process theorists.
Implicit measures assess associations through a
In the present article, we describe implicit and explicit measures as assessing an association that is retrieved
automatically or deliberately. We are theoretically uncommitted to whether implicit and explicit measures assess a
common representation or categorically different representations, and whether the measures are assessing stored
behavior that does not require deliberate retrieval of the target association (e.g., the speed of
sorting words into different categories relevant to the association). In contrast, explicit measures
assess the target association through a behavior that does require deliberate retrieval (e.g.,
answers to a questionnaire). On an implicit measure, comparisons between behavior that results
from pairings between one set of concepts relative to the resulting behavior from a different
pairing is termed implicit bias; similar comparisons on explicit measures are termed explicit bias.
For example, differences in the time to identify the word “flower” when it is preceded by the
words “good” vs. “bad” can serve as an indicator of implicit bias, whereas differences in the
ratings from ratings of the degree to which flowers are good and bad can serve as an indicator of
explicit bias.
Implicit and explicit biases are assumed to indicate the presence of automatically or
deliberately retrieved associations, respectively. However, like all psychological measures,
implicit and explicit measures are not process-pure. Implicit and explicit measures are both prone
to measurement error, and implicit and explicit biases can be influenced by many processes other
than automatically and deliberately retrieved associations (e.g., task-switching ability and
impulse inhibition for implicit measures, social desirability and acquiescence bias for explicit
measures; Calanchini et al., 2013; Conrey et al., 2005; Cronbach, 1946; Blanton et al., 2006;
Crowne & Marlowe, 1960).
Implicit and explicit biases are correlated, but the extent to which they correlate varies
(Cameron, Brown-Iannuzzi, & Payne, 2012; Greenwald et al., 2009; Hofmann et al., 2005;
Nosek & Hansen, 2008). These correlations range from very low (r = .07; e.g., attitudes toward
approaching vs. avoiding) to very high (r = .70; e.g., attitudes toward Democrats vs Republicans;
Nosek & Hansen, 2008). Half of the variation in implicit-explicit relations can be accounted for
with four aspects of the social and mental context: the social sensitivity of the target concepts,
the extent to which people have thought about the concepts, the degree to which the concepts in
the implicit measures are diametrically opposed (e.g., pro-choice vs. pro-life) or not (e.g., dog vs.
furniture), and the degree to which people view their opinions about the concepts to be distinct
from others (Nosek, 2005; 2007). The predictability of the relation between implicit and explicit
bias measures suggest underlying processes that are causally related and/or influenced by third
When automatic and deliberate processes are not aligned discrepancies between
intentions and behavior may arise, such as intending to be unbiased in selection of candidates for
an honor society but showing racial discrimination anyway (Axt, Ebersole, & Nosek, 2016).
Consistent with dual process theories, some evidence suggests that implicit biases are more
strongly correlated with behavior in socially sensitive issues (Greenwald et al., 2009; cf. Oswald
et al., 2013), whereas explicit biases are relatively strongly correlated with behavior when the
situation demands a more deliberate response (Devine, 1989; Fazio & Olson, 2014; cf.
Greenwald et al., 2009). Alternatively, when automatic and deliberate processes are aligned,
these processes mutually reinforce each other to guide behavior. Consistent with this claim,
representations or active constructions (Greenwald & Nosek, 2008). Likewise, we use “association” with a theory-
uncommitted view (Greenwald et al., 2005). We do not assert a commitment to a particular understanding of what
the underlying constructs or processes are (e.g., associative or propositional; Gawronski & Bodenhausen, 2006).
Various accounts of the underlying constructs / processes can be adapted to accommodate the changes in implicit
bias observed in the present meta-analysis.
behavior is most consistent with both implicit and explicit biases when implicit and explicit
biases are more strongly correlated (Greenwald et al., 2009).
Implicit bias change
Of course, correlation is not causation, so understanding the causal importance of
automatically retrieved associations first requires procedures that can change observed levels of
implicit bias. At first, the prospect of changing implicit bias through randomized experiments
was dim. Approaches such as cognitive dissonance reduction and persuasive appeals were
successful changing self-reported attitudes but often had limited impact on implicit bias (for
reviews, see Cooper, 2007; Gawronski & Strack, 2012; Petty & Cacioppo, 1986). The apparent
rigidity of automatic processes led the social psychologist John Bargh to portray them as a
“cognitive monster” (Bargh, 1999) that is deep-rooted, immune to social pressure, and resistant
to the influences of deliberate processes.
Yet this understanding changed with the discovery that brief experiences can change
implicit bias without affecting explicit bias (Blair, Ma, & Lenton, 2001; Dasgupta & Greenwald,
2001; Kawakami, Dovidio, Moll, Hermsen, & Russin, 2000). Over the past sixteen years, the
accumulated evidence suggests that implicit biases can be changed, but doing so often relies on
mechanisms that are ineffective for shifting explicit biases (for reviews, see Blair, 2002;
Dasgupta, 2009; Gawronski & Bodenhausen, 2011; Gawronski & Sritharan, 2010; Lai et al.,
2013; Lenton et al., 2009; Sritharan & Gawronski, 2010). For example, the mere presence of a
Black experimenter changed implicit bias without affecting explicit bias (Sinclair, Lowery,
Hardin, & Colangelo, 2005). More recently, some studies suggest that approaches that affect
explicit bias can also affect implicit bias, such as intergroup contact, social threat, and cognitive
balance (Bradley et al., 2012; Shook & Fazio, 2008; Smith, De Houwer, & Nosek, 2012).
Further, some strategies highlight the process-impurity of implicit measures by changing aspects
of performance in implicit measures that are unrelated to underlying associative processes (e.g.,
instruction to fake on an implicit measure; Kim, 2003; Fiedler & Bluemke, 2005).
Inspired by social problems characterized by unintentional or unwanted behavior, many
studies aim to change implicit bias with the goal of changing behavior. Many of these studies
occur in domains, such as race relations or addiction, where automatic and deliberate
associations are often thought to be at odds and where deliberate processes are either resistant to
change or theorized to have a limited influence on behavior (e.g., Wiers et al, 2010; Mann &
Kawakami, 2012). If interventions on deliberate processes are of limited utility, perhaps
approaches that change automatically retrieved associations will be more effective.
Despite the proliferation of many approaches to changing implicit bias, little is known
about their relative effectiveness (Lai et al., 2013; 2014; 2016). At the same time, there is also
little understanding about what approaches are consistently effective across a wide range of
phenomena, and what kinds of approaches are inconsistently effective and are contextually
dependent on the population, study methodology, or topic of study. Advances in these areas of
knowledge would inform a basic understanding of the mental mechanisms that are most
influential on implicit biases and a practical understanding of what interventions would be most
effective for changing implicit biases.
Overview of present research
We conducted a meta-analytic review to understand the relative effectiveness of different
procedures to change implicit bias and whether the changes in implicit bias generalize to changes
in explicit bias and behavior. The diversity in research goals means that research on implicit bias
change spans many disciplines, theoretical perspectives, and methodological approaches. Study
designs range from two-condition single-session laboratory experiments (e.g., Rudman & Lee,
2002) to multiple-condition longitudinal studies (Sportel, de Hullu, de Jong, & Nauta, 2013).
They also differ in what kinds of manipulations are used, from minimal manipulations that prime
a concept in memory (Dasgupta & Greenwald, 2001) to intensive long-term interventions that
unfold over several weeks (O’Brien et al., 2010). The studies are also diverse in their dependent
measures, ranging from popular measures such as the Implicit Association Test (IAT;
Greenwald, McGhee, & Schwartz, 1998; Nosek, Greenwald, & Banaji, 2007) to less popular
measures such as the Implicit Relational Assessment Procedure (IRAP; Barnes-Holmes, Murphy,
Barnes-Holmes, & Stewart, 2010; Hussey et al., 2015).
This research diversity poses two unique analytic issues for meta-analysis. First,
different studies often compare different sets of procedures. The diversity in procedures is a
challenge for conventional meta-analytic methods that synthesize two-group studies because
conventional methods assume all studies use a common comparison. Second, studies in this
literature sometimes compare the effects of three or more procedures within the same design.
Conventional meta-analytic methods assume that each effect size is independent and thus cannot
accommodate these non-independent comparisons.
We used a technique from the medical sciences called multivariate network meta-analysis
to address these issues (Lu & Ades, 2004; Caldwell, Ades, & Higgins, 2005; Salanti, 2012).
Compared to conventional meta-analytic methods, network meta-analysis synthesizes
information from many procedures simultaneously to better addresses research literatures where
there are many studies that compare distinct procedures (Lumley, 2002). A multivariate
implementation of network meta-analysis addresses the problem of single studies making
multiple comparisons by modeling the non-independence between multiple comparisons
extracted from the same study (White et al., 2012; Mavridis & Salanti, 2012). Multivariate
network meta-analysis therefore allows us to use all information from studies comparing many
procedures to change implicit bias, rather than having to simplify the information available when
a study has more than one possible contrast (e.g., via averaging, dummy-codes, or data
Our meta-analysis of procedures for changing implicit bias was guided by 5 central
questions: 1. What approaches to changing implicit bias are most influential? We developed a
taxonomy of procedures to change implicit bias and compared the effectiveness of
procedures within that taxonomy.
2. Are the sample, methodology, or topic of a study associated with the magnitude
of implicit bias change? We assessed whether any of these characteristics were
associated with the degree of implicit bias change.
3. How do changes in implicit bias correspond with changes in explicit bias? We
compared the relative size of explicit bias change to implicit bias change. We also
examined whether implicit bias change mediated explicit bias change.
4. How do changes in implicit bias correspond with changes in behavior? We
compared the relative size of behavioral change to implicit bias change. We also
examined whether implicit bias change mediated behavioral change.
5. Is there evidence that the size of reported effects is biased? We examined whether
reported effect sizes are likely to be larger than the true effect sizes (e.g., due to
publication bias or p-hacking; Rosenthal, 1979; Simmons, Nelson, & Simonsohn,
Inclusion criteria
Valid meta-analysis requires careful consideration of which studies are relevant to the
research question and which studies are not. We set the following inclusion criteria:
(1) The study is a between-subjects experiment. We excluded studies that used
correlational or quasi-experimental designs (e.g., Rudman, Ashmore, & Gary, 2001) and
manipulations that were exclusively within-subjects (e.g., Wheeler & Fiske, 2005). We
also excluded studies that experimentally manipulated the stimuli or categories in an
implicit measure (e.g., by manipulating whether pictures of animals and plants in an
animal/plant pleasant/unpleasant IAT are positively or negatively valenced; Govan &
Williams, 2004) because the conditions assessed categorically different associations
rather than changing a particular set of associations.
(2) The study includes an implicit measure that is administered after the onset of the
experimental manipulation. Implicit measures were defined as measures of associations
between concepts that do not require the participant to actively bring to mind the target
association. This definition included measures that are both widely used (e.g., the IAT;
Greenwald, et al., 1998; Nosek et al., 2007) and less widely used (e.g., Stereotypic
Explanatory Bias, Sekaquaptewa et al., 2003). Measures for which the manipulation
began during task instructions or practice trials (e.g., Foroni & Mayr, 2005) and for
which the manipulation extended into the measure (e.g., Huntsinger et al., 2010) were
also considered eligible.
(3) The implicit measure assesses a pre-existing association. We defined a “pre-existing
association” as an association that either should theoretically be present, or has been
empirically demonstrated as present, within the target population before the study began.
For example, most non-Black people implicitly associate Black people with bad and
White people with good more easily than the reverse (Nosek, Smyth, et al., 2007).
In making these decisions, we assumed that people tend to associate positive attributes with both themselves and
with their own groups, and that people tend to possess associations that are commonly present in their culture (e.g.,
Black people with the attribute “musical”). When we could not make a clear determination, we sought data
collected from the target population and/or examined whether a pre-existing association was present in a control
condition for the study in question.
Based on the nature of the pre-existing association, we defined pairings that strengthen
(e.g., Black-bad and White-good) and weaken (e.g., Black-good and White-bad) the
measured association. We excluded studies that formed a new association (e.g., about
fictitious people or social groups, McConnell, Rydell, Strain, & Mackie, 2008) and
studies of ambivalent or unelaborated associations (e.g., Petty et al., 2006) based on this
(4) The study is reported in English. We excluded studies that were not written in
Article retrieval
Our article retrieval procedure was conducted in three phases between September 2012
and July 2015 and again between August 2016 and October 2016. In the first phase (September
2012 to June 2014; August 2016), we retrieved articles that potentially matched our inclusion
criteria. We searched PsycINFO and Web of Science using the following search terms: (names
of implicit constructs, measures, and acronyms, e.g., implicit self-esteem*, affect misattribution
procedure, GNAT) AND (malleab* OR chang* OR influenc* OR moderat* OR reduc* OR
increas* OR shift* OR alter*) AND (1995 TO 2015). We created the list of eligible implicit
measures and acronyms by compiling lists from published reviews of implicit measurement
(Nosek, et al., 2011; Gawronski & Payne, 2010), and from discussions among the lead authors
(for the full list, see We supplemented these results with direct requests
for relevant studies through email and the Society for Personality and Social Psychology listserv,
and an additional 115 articles from an unpublished meta-analysis of the malleability of implicit
intergroup bias. Our search procedure resulted in approximately 5,238 articles that potentially
matched our inclusion criteria.
In the second phase (September 2012 to October 2014; August 2016 to October 2016),
trained coders inspected each article and eliminated articles that did not contain a study matching
our inclusion criteria. This thinned our database to 418 articles, 594 studies, and 692
independent samples.
Finally, for any studies that did not report sufficient data to calculate effect sizes and
variance components, we sent emails to the corresponding authors requesting the required
statistics (November 2014 to July 2015; October 2016). If the authors did not respond, we sent
two follow-up reminder emails. If the data required to calculate effect sizes on the implicit
measure could not be retrieved for a study, we eliminated that study from the meta-analysis.
After eliminations, our final sample represented 80,356 participants and included 343 articles,
494 studies, and 573 independent samples.
Article coding
This number reflects the number of articles from searches of PsycINFO and Web of Science. Web of Science
yielded 4,979 articles and PsycINFO yielded 4,161 articles, most of which were also in Web of Science. Articles
retrieved through email requests were not tracked systematically, meaning that the actual number of potential
articles is somewhat higher.
Coders underwent extensive training to reliably apply the coding scheme. We adopted an
iterative process to maximize reliability and validity of the coding scheme (Lipsey & Wilson,
2001). When coders encountered an ambiguity, they added the ambiguity to the agenda for a
weekly coding meeting. During these meetings, we discussed each ambiguity until we reached a
consensus for resolution. Some ambiguities revealed issues with the coding scheme. In these
cases, we revised the coding scheme and rolled out any required coding changes to all other
studies. We have made our coding scheme, data, and analysis scripts publicly available
( Anyone who is interested can delve into these materials to assess how
the results change with different coding decisions.
We tested the reliability of our coding scheme by choosing a random sample of 50 fully
coded articles and assigning each coder 10 articles to double-code. The random sample was
stratified by topic to ensure that each coder received articles that varied in topic and coding
difficulty. Where appropriate, Cohen’s κ calculated using these data is shown in the descriptions
Experimental procedures (κ = .71). Each experimental procedure was categorized into
one of fourteen categories. We developed these categories based on preliminary searches of the
literature and prior reviews of malleability and change in implicit bias (e.g., Blair, 2002;
Dasgupta, 2009; Gawronski & Bodenhausen, 2011; Gawronski & Sritharan, 2010; Lai et al.,
2013; Lenton et al., 2009; Sritharan & Gawronski, 2010) with the goal of capturing the breadth
of approaches that researchers have employed. Two of the fourteen categories (physiological
deprivation and satiation) were excluded from the final dataset because there were not enough
procedures that fit the description (four and two procedures respectively across four papers).
Researchers often disagree about the likelihood and mechanism by which a manipulation
might change implicit bias. To address this issue and maximize agreement between coders, our
coding scheme prioritized procedural elements of the study conditions over theoretical
expectations regarding the impact of these procedural elements. For example, conditions from
two studies that both give participants instructions to show no bias on an IAT would be placed
same category, regardless of whether the authors of the studies differ in their predictions as to
whether this condition would produce change in IAT scores (e.g., Kim, 2003; Fiedler &
Bluemke, 2005). If a given experimental condition fit into multiple coding categories or did not
find into a category clearly, that condition was excluded from the meta-analysis. As shown in
Table 1, our final coding scheme included twelve categories:
(1) Strengthen associations directly (k = 128) / Weaken associations directly (k = 155).
Some efforts to change implicit biases create experiences that directly affirm or counter
one’s own biases (e.g., Blair et al., 2001; Dasgupta & Greenwald, 2001). These two
categories involve creating pairings of the concepts used in the implicit measure that
either strengthen or weaken the measured implicit bias. For example, exposing people to
pictures of admired Black people and despised White people in a study assessing
associations between Black people/White people and good/bad would go in the “weaken
associations directly” category. In contrast, exposing people to admired White people
and disliked Black people would go in the “strengthen associations directly” category
(Dasgupta & Greenwald, 2001).
Table 1. Taxonomy of experimental procedures.
(2) Strengthen associations indirectly (k = 86) / Weaken associations indirectly (k = 154). A
related approach to the first category is creating experiences that bring to mind an idea or
mindset that will indirectly affirm or counter one’s biases (Blair, 2002). These categories
were similar to the “strengthen / weaken associations directly” categories except that the
concepts used to create the pairings are not the ones used in the implicit measure, but
instead are assumed to lead to their mental activation through some intermediate idea or
mindset. For example, taking the perspective of a Black person is theorized to create
overlap between a person’s self-concept and Black people (Galinsky & Moskowitz, 2000;
Todd et al., 2011). As most people evaluate themselves positively (Taylor & Brown,
1988), linking Black people to the self creates an indirect link between Black people and
positivity that changes implicit racial attitudes. Other examples include taking an abstract
construals to associate a temptation with negativity (Fujita & Han, 2009) and changing
approach/avoid tendencies to change implicit attitudes toward math versus arts
(Kawakami, Steele, Cifa, Phills, & Dovidio, 2008).
(3) Goals to strengthen bias (k = 37) / Goals to weaken bias (k = 92). Implicit biases may be
sensitive to motivations, goals, and habits (e.g., Fishbach, Friedman, & Kruglanski,
2003; Sinclair et al., 2005). Procedures in these categories gave participants goals to
respond on an implicit measure in ways that either strengthen or weaken the measured
implicit bias. These goals could be created directly, such as by instructing participants to
appear non-shy on a measure of implicit shy/non-shy self-concept (Asendorpf, Banse, &
Mucke, 2002). These goals could also created indirectly, such as by making anti-
prejudiced norms salient prior to measuring implicit bias toward Black people (Wyer,
(4) Threat (k = 72). Threat involves putting the integrity of a person’s identity at risk. Threat
plays a powerful role in shifting attention (Mogg, Bradley, De Bono, & Painter, 1997),
evaluations of one’s self (Taylor & Lobel, 1989), and evaluations of others (Stephan &
Stephan, 2000). The threats included in this category were diverse, including the threat
of confirming a negative stereotype (e.g., Frantz et al., 2004), mortality salience (e.g.,
Jong, Halberstadt, & Bluemke, 2012), and the threat of giving a speech in front of a panel
of judges (e.g., Rabbitt, 2012).
(5) Affirmation (k = 23). Affirmation involves procedures that sought to maintain the
adequacy of a person’s identity, which may buffer against acute or chronic experiences of
threat (Cohen & Sherman, 2014; Steele, 1988). Examples in this category included
procedures in which the participants were given feedback that they were competent,
moral, or unbiased (Frantz et al., 2004), and procedures where the participants were
instructed to think about a value important to a social group to which they belonged
(Peach et al., 2011).
(6) Positive affective state (k = 26) / Negative affective state (k = 27). According to an
affect-as-information account, positive affect affirms chronically accessible concepts and
negative affect rejects them (Huntsinger, Isbell, & Clore, 2014). These categories
involved procedures that induced a mood or emotion without placing the manipulation in
the “threat” or “affirmation” categories. Although manipulations that threaten or affirm a
person’s identities are likely to induce affect, we reasoned that threat and affirmation are
the primary characteristics of these conditions and take precedence.
Examples of
manipulations in these categories included both positive or negative mood inductions
(e.g., Birch et al, 2008) and inductions of specific emotions like anger, disgust, or moral
elevation (Dasgupta, DeSteno, Williams, & Huntsinger, 2009; Lai, Haidt, & Nosek,
(7) Depletion (k = 26). Depleting mental resources may lead to increased reliance on social-
cognitive biases (e.g., Bodenhausen, 1990; Gilbert & Hixon, 1991; Stangor & Duan,
1991). This category involves manipulations that reduced the amount of mental resources
We placed anger inductions into the positive affective state category as anger is more cognitively and neurally
similar to positive emotions than negative ones (Lerner & Tiedens, 2006; Harmon-Jones, 2003; Carver & Harmon-
Jones, 2009).
available to the participant during the implicit measure. Conditions in this category often
instructed people to complete a mentally effortful task, such as holding a multi-digit
number in their heads (Allen et al., 2009), prior to or during the implicit measure.
(8) Neutral (k = 429). This category involves conditions where nothing happened that was
potentially relevant to the concepts assessed by the implicit measure (e.g., control
conditions). This category did not necessarily contain conditions that a specific research
tradition would predict are ineffective. For example, on the basis of past evidence
(Dasgupta & Greenwald, 2001), some researchers might predict that exposure to images
of admired White people and disliked Black people does little to change implicit racial
attitudes because admired White people are already chronically accessible prior to the
exposure experience. Although this may be the case, exposure to liked White people
pairs White people with positivity, and thus this condition would be placed in the
“strengthen associations directly” category.
Implicit, explicit, and behavioral measures. Measures were considered implicit if they
did not require the target association to be actively brought to mind. For example, the
Black/White good/bad IAT requires participants to categorize Black faces, White faces, positive
words, and negative words, but it does not require them to introspect about their feelings about
Black people relative to White people. Measures were considered explicit if they required the
target association to be actively brought to mind. For example, a survey item asking “How warm
do you feel toward Black people?” requires participants to actively assess their personal feelings
about Black people. Measures were considered behavioral if they involved the participant’s
actual, hypothetical, or intended behavior in relation to the target association. Behavioral
measures assessed a wide range of outcomes, such as seating distance from a Black or White
confederate (Todd et al., 2011), willingness to participate in a hypothetical beer pong game
(Goodall & Slater, 2010), intentions to drink in the future (Glock, Klapproth, & Müller, 2015;
Lindgren et al., 2015), reported chocolate consumption (Kroese, Adriaanse, Evers, & De Ridder,
2011), and intentions to vote for gay and lesbian civil rights referenda (Dasgupta & Rivera,
Explicit and behavioral measures were included only if coders judged that they assessed
the same association as the implicit measure selected from the study. For example, a
questionnaire assessing Black stereotypes would be eligible for a measure of implicit
Black/White stereotyping but not a measure of Black/White implicit attitudes. This inclusion
criterion was notably stricter than past meta-analyses that included explicit/behavioral measures
which did not narrowly tap into the same constructs (e.g., physiological or neural activity for
IATs in Greenwald et al., 2009; stereotype measures for attitude IATs in Oswald et al., 2013). As
with the implicit measures, explicit and behavioral measures were only eligible if they were
administered after the onset of the manipulation. If multiple measures in a sample met our
definition of an implicit, explicit, or behavioral measure, we selected the measure that was most
widely used in the meta-analysis (i.e., if a study included both an IAT and a Lexical Decision
Task assessing implicit self-esteem, we selected the IAT) or the measure that best matched the
implicit measure conceptually (e.g., for a relative implicit measure of stereotypes, we prioritized
relative explicit stereotyping measures over absolute stereotyping measures).
All measures were scored such that higher numbers represent greater levels of the pre-
existing bias. Implicit measures that assessed associations between two sets of concepts were
scored by creating a difference score that reflected the underlying association. For example, in a
study where researchers measured participant reaction times (RT) to categorize positively and
negatively valenced words with Black and White face primes, we created the following
difference score: (Black/good RT - Black/bad RT) - (White/good RT - White/bad RT). If a score
computed from a D score algorithm (Greenwald et al., 2003) was used, we chose that over a
reaction time difference score. If the explicit and behavioral measures were composed of
multiple parts (e.g., separate assessments of feelings of warmth toward Black people and White
people), we scored these measures to be most correspondent with the implicit measure. In a
study using the aforementioned priming measure that also contained separate feelings
thermometer ratings of Black people and White people, we created the following difference
score: White thermometer rating - Black thermometer rating.
Multiple study subsamples. If a study reported their results separately for groups with a
given individual-difference characteristic (e.g., a median split of a questionnaire measure), we
collapsed across the target individual difference. If, however, participants were recruited on the
basis of that individual difference characteristic (e.g., from the top and bottom quartile of a
scale), we treated these groups as separate subsamples for the purposes of the meta-analysis to
avoid confounding (Glass, 1977). In some cases, we analyzed groups separately even if they
were not recruited on a specific characteristic if the meaning of the measure or manipulation was
unambiguously different for different subgroups. For example, the meaning of a Bill
Clinton/George Bush good/bad IAT is likely different for Democrats and Republicans because
Democrats share a party affiliation with Bill Clinton, whereas Republicans share a party
affiliation with George Bush (Albertson, 2011). Finally, studies were split into subsamples if the
study randomly assigned participants to different implicit measures in addition to randomly
assigning them to different manipulations (e.g., by assessing the effects of reading a counter-
stereotypical vs. neutral scenario on the personalized vs. original IAT, Han et al., 2010).
Sample characteristics
Sample population (κ = .92). University student samples tend to be more compliant and
more easily socially influenced (Sears, 1986), and may be more susceptible to psychological
manipulations than non-student samples (e.g., Lai et al., 2016). Student and non-student samples
may also differ because of issues related to the publication process (e.g., reviewers may be less
critical of small effects if the study does not use an undergraduate convenience sample). To
assess these possibilities, we coded whether the sample was drawn from a university student or a
non-university-student population (e.g., hazardous drinkers, elementary school children).
Demographic characteristics. We coded the racial and gender distribution of each
sample to examine the generalizability of results to different demographic groups. Coders
recorded the number of participants who were White, non-White, or whose race was not
reported. Coders followed a similar process for gender distribution: male, female, or gender not
Methodological characteristics
Design (implicit κ = .86; explicit κ = .89; behavior κ = .96). The effects of procedures on
measured implicit bias may depend on whether participants completed an implicit measure
before the intervention (e.g., Lai et al., 2014). Thus, we assessed whether the implicit, explicit,
and behavioral measures were administered in a fully between-subjects design or in a mixed
design with between-subjects and within-subjects (i.e., pre-test and post-test) components.
Implicit measure (κ = .90). Different implicit measures may tap different constructs.
Implicit measures also vary in measurement reliability, which can depress the relationship
between manipulations and their effects on implicit bias. Thus, we coded whether a study’s
implicit measure was an IAT or not (e.g., the Affect Misattribution Procedure, Go/No-Go
Association Task, etc.).
Longitudinal (κ = .87). This variable assessed whether the implicit measure was
administered longitudinally (i.e., at least one of the measurements occurred after a delay that is
longer than one experimental session). As only 38 (6.6%) of 598 samples were longitudinal, we
did not use this variable for inferential analyses.
Manipulation length (κ = .64). This variable assessed whether the manipulation occurred
in a single experimental session or in multiple sessions. Only 17 (3.0%) of the 598 samples had
procedures occurring over multiple sessions, so we did not use this variable for inferential
Topic characteristics
Evaluative vs. conceptual associations (κ = .85). Implicit associations vary in whether
their content is more evaluatively (e.g.,, good/bad) or conceptually (e.g., mental/physical)
focused. Because different neural substrates are associated with affective and semantic memory
(Amodio & Devine, 2006; Amodio & Ratner, 2011), it is possible that the same procedure will
produce different effects on conceptual and evaluative associations. We therefore coded whether
the concepts involved in the target association were primarily evaluative (e.g., good/bad in a
self/other-good/bad IAT) or conceptual (e.g., science/humanities in a male/female-
science/humanities IAT). Some associations had both evaluative and conceptual content (e.g., a
Lexical Decision Task where the primes are pictures of Black people and the targets are negative
Black stereotypes). We handled these on a case-by-case basis.
Self-associations (κ = .85). The self is one of the most fundamental constructs in
psychology (James, 1890), and has long been an important construct in research on automatic
processes (Greenwald & Banaji, 1995). Whether self-associations should be more or less easy to
change than other associations is unclear. To assess the role of the self in implicit malleability,
we coded whether or not the concepts involved in the target association were related to the self.
Association domain (κ = .97). The topics studied by experiments in the meta-analysis
were diverse, ranging from anti-Arab/Muslim prejudice to dieting and exercise. Coders judged
whether the study’s topic was related to intergroup relations, health psychology, personality,
clinical psychology, political preferences, consumer preferences, or close relationships.
Article characteristics
Publication status. Larger significant effects are more likely to be published than smaller
non-significant effects (Stern & Simes, 1997). We assessed whether this was the case in this
literature by coding whether a study had been published in an academic journal or book at the
time of analysis. Many of the unpublished studies were dissertations and/or studies in a
researcher’s “file-drawer,” but some unpublished studies were studies that were in the process of
being prepared for publication.
Publication year. The effect size of early published studies is often larger than effect
sizes of later published studies on the same topic (Jennions & Møller, 2002), a result popularly
known as the decline effect. There are multiple possible reasons for the decline effect, including
publication bias, increasing sample heterogeneity, and loss of adherence to intervention quality
over time. We coded the year a study was published to see if a decline effect exists in this
literature. Unpublished studies were not included in any analyses involving publication year.
Study characteristics
Geographic region of sample (κ = .92). Published effect sizes from the United States in
the behavioral sciences tend to be larger than those published in other countries, perhaps due to
publication pressures (Fanelli & Ioannidis, 2013). To investigate whether this was the case in this
literature, we coded whether the studies were conducted in the United States, Europe, Israel,
Canada, Australia and New Zealand, Asia, Africa and Latin America, or multiple countries. For
analysis, we compared the effect sizes of studies published in the US and elsewhere.
Number of experimental groups (κ = .67). This variable represented the numbers of
groups in a study’s design. Sometimes this with synonymous with the number of conditions in an
experiment, but other times it was not (e.g., when a condition was excluded, when multiple
conditions were merged together for analysis).
Meta-analytic computations
Meta-analysis involves the synthesis of one or more effect sizes and the variance
components associated with those effect sizes. The breadth of this project demanded special
procedures to do so.
Standardized mean differences. Given our interest in the degree to which quantitative
measures differ between groups, the primary effect size computed for this project was the
standardized mean difference. For each comparison between procedures on the implicit, explicit,
and behavioral measures, we estimated Hedge’s g (Hedges & Olkin, 1985), which is a measure
of the standardized mean difference similar to Cohen’s d that corrects for small-sample bias. We
estimated Hedge’s g using the means, standard deviations, and number of participants within
each cell of a given sample’s design. If the total sample size was available but the number of
participants per group was not, we assumed equal sample sizes within each group. If the means
and/or standard deviations were missing, we attempted to back-calculate the missing descriptive
statistics or the standardized mean difference from other statistics reported in the article (see
Lipsey & Wilson, 2001). If this was not possible, we requested the required information directly
from the authors.
In multi-group designs (i.e., designs with more than two groups), we designated one
group the “reference group” and computed multiple effect sizes relative to this reference group
(Salanti, 2012; White et al., 2012). This yielded (g - 1) effect sizes, where g is the number of
groups in a study. Where possible, this reference group was a neutral condition. In studies that
lacked a neutral condition, we calculated effect sizes relative to a virtual neutral condition that
had an effect size of 0 and a standard error of 1000 (Higgins & Whitehead, 1996; White et al.,
2012). This computational device ensures that studies that lack a neutral condition will
contribute information during model fitting (Higgins & Whitehead, 1996) without directly
influencing meta-analytic estimates involving neutral conditions (White et al., 2012). The virtual
neutral conditions therefore play a similar role as continuity corrections to avoid divide-by-zero
errors when analyzing odds ratios: they allow estimation to proceed without inappropriately
impacting results.
We handled experiments with pre-test post-test designs by using the mean differences
from pre-test to post-test as the means within each condition and the pre-test standard deviations
as our standard deviations within each condition (Morris & DeShon, 2002; Morris, 2008). If the
pre-test standard deviations were unavailable but the standard deviations of the differences from
pre-test to post-test were available, we used the standard deviations of the differences instead,
then transformed this change score metric into one comparable to the pre-test standard deviation
metric (Morris & DeShon, 2002). If we were unable to obtain either the pre-test or difference
score data, we computed effect sizes with post-test data only. Some studies used dichotomous
outcomes to measure behavior. For these outcomes, we calculated log-odds ratios that we then
transformed into standardized mean differences (Cox & Snell, 1989; Sánchez-Meca et al., 2003).
Variance components. The variances of Hedge’s g in post-test only designs were
estimated using formulas developed by Hedges and Olkin (1985). In experiments with pre-test
post-test designs, we estimated the effect size variances using formulas that correct for the
correlation between pre-test and post-test (Morris & DeShon, 2002; Morris, 2008). For studies
missing the correlation between pre-test and post-test (27/84 implicit correlations; 11/35 explicit
correlations, 3/14 behavioral correlations), we imputed the missing correlation with its meta-
analytic estimate calculated from the rest of the sample (implicit r = .35, k = 57, 95% CI =
[.29, .41]; explicit r = .74, k = 24, 95% CI = [.68, .79]; behavioral r = .72, k = 11, 95% CI =
[.66, .78]). We estimated the variance components for effect sizes for dichotomous measures
using a formula described by Cox and Snell (1989).
Effect sizes extracted from a single study are typically non-independent, either because
they share a common reference group in multi-group studies or because the same participants
complete multiple measures (i.e., when participants take a measure of implicit bias and a
measure of explicit bias and/or behavior). Thus, in addition to the variances typically estimated
in pairwise meta-analyses, we also estimated covariances between each pair of effect sizes
derived from a given study in studies that yielded multiple effect sizes. For multi-group studies,
estimating the covariance between effect sizes only requires the number of people per condition
and the means and standard deviations of the outcome measure (Gleser & Olkin, 2009). For
studies that use multiple measures (i.e., an explicit and/or behavioral measure in addition to an
implicit measure), the calculation of these covariances requires the correlation between the two
types of measures. In studies where this correlation was unavailable (26/256 implicit-explicit
correlations; 12/92 implicit-behavioral correlations), we imputed the correlation using the meta-
analytic estimate from the remaining studies (implicit-explicit r = .14, k = 230, 95% CI =
[.12, .16]; implicit-behavioral r = .10, k = 80, 95% CI = [.06, .14]). We calculated the
covariances between different measures using formulas derived by Wei and Higgins (2013).
Indirect effects. For both explicit bias and behavior, we estimated effects from both a
mediation model and a reverse mediation model. The mediation model estimated the degree to
which the effects of procedures on the target outcome is mediated by change in implicit bias, and
the reverse mediation model estimated the degree to which the effects of procedures on implicit
bias is mediated by change in the target outcome. We constructed a series of 3 by 3 correlation
matrices representing the bivariate relationships between manipulations, implicit bias, and
explicit bias/behavior. The correlations between manipulations and other variables were
extracted for each study report by transforming the standardized mean differences on implicit
bias and explicit bias/behavior into correlation coefficients. These correlations were combined
with the correlation between implicit bias and explicit bias/behavior.
We only included two-
condition studies when constructing these correlation matrices because of ambiguity in how to
define the direct and indirect effects in multi-condition studies. We then used the delta method
to extract the standardized indirect effects and their asymptotic variances from these correlation
matrices (Cheung, 2009).
Network meta-analysis
We performed most of the analyses using a multivariate implementation of network
meta-analysis (Lu & Ades, 2004; Caldwell et al., 2005; Salanti, 2012). Multivariate network
meta-analysis treats each study in the meta-analysis as having multiple outcomes. Each of these
outcomes is a potential comparison between the two of the 12 categories of procedures coded for
the meta-analysis. Because studies that contain more than two categories of procedures yield
more than one two-group comparison, multivariate network meta-analysis also explicitly models
the interdependence between these multiple comparisons.
More formally, given k studies comparing g conditions, multivariate network meta-
analysis represents each study as a set of comparisons between one of the conditions (the
reference group r) and each other condition. Thus, study i yields a vector of (g - 1) effect sizes,
labeled yi, along with a (g - 1) by (g - 1) matrix of variances and covariances between the effect
sizes within study i, labeled Si. Given effect sizes yi and covariance matrices Si, one can estimate
coefficients α and the between-studies variance-covariance matrix Σ using the following
multivariate model (White et al., 2012):
yi ~ NXi, Σ + Si)
where Xi is a matrix of study covariates. If there are no study covariates and α and Σ are
assumed to be the same across studies, α represents the meta-analytic effect size estimates of
comparisons between the reference group and each other condition and Σ represents the between-
studies variance-covariance matrix for those effect sizes.
Although we imputed this correlation for the analysis of the consistency between effects on implicit bias and
explicit bias/behavior, we did not impute this correlation for the analysis of the indirect effects.
We also estimated the direct effects, their asymptotic variance, and the asymptotic covariance between the direct
and indirect effect so as to not bias the indirect effect estimates by fixing them to 0. We only report the indirect
effects here.
An advantage of this meta-analytic model is that it uses both direct information from the
comparisons within each study and indirect information from the pattern of comparisons across
studies (Higgins & Whitehead, 1996; Lu & Ades, 2004). For example, taking the difference
between the effect of the comparisons between procedures A & B and procedures A & C allows
for the indirect estimation of the comparison of procedures B & C. Direct and indirect
information can only be combined if a network of comparisons meets the consistency
assumption, which assumes that each procedure is similar regardless of which other procedures
appear alongside it in a given study (Salanti, 2012). We tested the viability of this assumption by
testing whether, within single treatment estimates, studies of different designs had different
effect sizes (the design by treatment interaction approach; Higgins et al., 2012; White, 2011).
They did not, χ2(69, k = 573) = 84.28, p = .102, indicating the consistency assumption was
reasonable for our data.
We fit all multivariate network meta-analytic models using the metaSEM package in R
(Cheung, 2015). To ensure model identifiability, we constrained the components of the between-
studies variance-covariance matrix Σ such that the variances were equal and the covariances
were equal (Higgins & Whitehead, 1996; Lu & Ades, 2009).
Descriptive information
Descriptive information about the articles, studies, samples, and measures included in the
meta-analysis is shown in Table 2. The data primarily came from published articles (80.5%),
studies conducted in the United States (53.0%), and from studies of intergroup relations (63.4%).
The participants in the meta-analysis reflect the demographics of students in Introductory
Psychology classes: 81.7% of samples were composed entirely of university students, and
samples were majority White (76.2%) and female (65.6%). The majority of the samples used
evaluative measures (65.1%), usually with an IAT (64.7%), and usually in a single-session, post-
test only design (16.1%). Only 38 (6.6%) of the samples used a longitudinal design to assess
change over time, and only 18 (3.1%) used intense, multi-session procedures. Finally, 45.7% of
the samples included an explicit measure, and 16.2% of the samples contained a behavioral
Some study characteristics were weakly to moderately related to each other. The
strongest relationships were that health/clinical studies were more likely to use a pre-test post-
test design (r = .41) and include a behavioral measure (r = .38) than studies in other domains. For
a complete correlation matrix of study characteristics, see
The network of comparisons between the 12 categories of procedures is shown in Figure
1. The most common procedure most frequently used in a study was the neutral category.
Indeed, most studies (74.9%) compared neutral procedures with one or more comparison
procedures. When studies made other types of comparisons, they most often (86.8%) compared
a procedure and its conceptual opposite (e.g., positive and negative affective states). Few studies
that made non-neutral comparisons used procedures in conceptually different categories (13.2%)
(e.g., weaken associations directly vs. threat).
Table 2. Characteristics of the final meta-analysis sample.
Note. Methodological, topic, and sample characteristics are presented in # of samples.
Gender/Race are presented in # of participants. Study characteristics are presented in # of
studies. Publication status is presented in # of papers, and publication date is presented in # of
published papers.
Figure 1. Network plot of procedures included in the meta-analysis. The radius of the category
circles = the number of procedures in that category, line width = the number of samples in which
a pair of conditions were directly compared.
What approaches to changing implicit bias are most influential?
We compared the effectiveness of procedures to change implicit bias by fitting a
multivariate network meta-analytic model with the neutral group as the reference category. As
shown in Figure 2, seven categories changed implicit bias relative to a neutral condition:
procedures that strengthen or weaken associations, either directly (gstrengthen = .21, 95% CI =
[.14, .29]; gweaken = -.23, 95% CI = [-.30, -.16]) or indirectly (gstrengthen = .14, 95% CI = [.04, .24];
gweaken = -.23, 95% CI = [-.30, -.16]), that induce goals (gstrengthen = .14, 95% CI = [.01, .28];
gweaken = -.29, 95% CI = [-.37, -.21]), and that deplete mental resources (g = .23, 95% CI =
[.07, .40]). In all cases, the effects were small by conventional standards (|d| < .35; Hyde, 2005)
and smaller than the typical effects reported in social psychology papers (median d = .37;
Richard, Bond, & Stokes-Zoota, 2003). Compared to a neutral procedure, procedures that that
produce threat (g = .08, 95% CI = [-.02, .18]), affirmation (g = -.01, 95% CI = [-.20, .17]),
positive affective states (g = -.06, 95% CI = [-.23, .11]), and negative affective states (g = -.12,
95% CI = [-.31, .07]) produced effects that were small and not distinguishable from zero.
We estimated the variation in effect sizes due to substantive differences between studies
using the multivariate R-based statistic developed by Jackson, White, and Riley (2011). This
statistic revealed high between-study variation (I2 = .798), a finding mirrored by the large
estimated effect size standard deviation (τ = .303). This reflects the diversity of disciplines,
theoretical approaches, and methodological approaches in this area.
Figure 2. Forest plot of the comparisons between each procedure and a neutral procedure. k
gives the number of studies that directly (or indirectly, listed in parentheses) compare the listed
procedure and a neutral procedure. g gives the estimated standardized mean difference and its
95% CI. Higher effect sizes reflect greater increases in implicit bias relative to a neutral
Are the sample, methodology, or topic of a study associated with the magnitude of implicit
bias change?
We tested whether effect sizes varied according to the sample, design, or topic of a study.
We did this by using Wald χ2 tests that compared moderator models to models without any
moderators. Treating p < .05 as a strict criterion, there was evidence of variation based on
whether the sample was a student sample, χ2(9, k = 573) = 27.38, p = .001, the racial composition
Because the between-studies variances of the meta-analytic comparisons were constrained to be equal (Higgins &
Whitehead, 1996; Lu & Ades, 2009), we could not estimate how the between-studies variance differed for each
comparison between procedure categories.
of the sample, χ2(11, k = 248) = 20.59, p = .038, the measure used to assess implicit bias, χ2(10, k
= 573) = 27.62, p = .002, and whether the design included a pre-test assessment of implicit bias,
χ2(9, k = 573) = 36.44, p < .001. There was little evidence of variation by the number of
conditions compared within the study, χ2(11, k = 573) = 13.43, p = .266, the gender composition
of the sample, χ2(11, k = 483) = 14.94, p = .185, whether the target association was evaluative or
conceptual, χ2(11, k = 573) = 19.58, p = .050, whether the target association was an intergroup
association, χ2(11, k = 573) = 18.01, p = .081, whether the target association was related to health
or clinical issues, χ2(9, k = 573) = 8.16, p = .518, or whether the target association was related to
the self, χ2(8, k = 573) = 15.46, p = .051.
The specific differences for the significant moderators are shown in Figure 3. Most of
the moderator differences are driven by the effects of procedures that induce goals to weaken
associations. These procedures produced stronger effect sizes in non-student samples (gnon-student
= -.43, gstudent = -.23), samples with proportionately fewer White people (g60% White = -.30, g100%
White = -.07), studies that used an IAT (gIAT = -.38, gnon-IAT = -.14), and studies with a pre-test
assessment of implicit bias (gpre-test = -1.06, gpost-test only = -.23). These results suggest that there
are strong sample and methodological differences between studies that show a strong effect of
goals to weaken associations and studies that do not.
Student and non-student samples also tended to produce different effect sizes. In addition
to the difference between student and non-student samples for studies using weaken goals
procedures, student and non-student samples produced different effect sizes in studies that
weakened associations indirectly (gnon-student = -.09, gstudent = -.29) and that depleted cognitive
resources (gnon-student = -.15, gstudent = .32). Finally, in addition to these sample differences,
compared to studies that used a different implicit measure, studies using an IAT produced
stronger effects than non-IAT studies when they strengthened associations directly (gIAT = .26,
gnon-IAT = .09) and weakened associations indirectly (gIAT = -.28, gnon-IAT = -.12).
Figure 3. Moderation analyses. k gives the number of studies that directly (or indirectly, listed in parentheses) compare the listed
procedure and a neutral procedure for the displayed levels of the moderator. “Difference” represents the difference between the two
moderator levels and its 95% CI. Higher effect sizes reflect greater increases in implicit bias compared to a neutral procedure. Where
there was not enough data in one of the moderator levels for estimation, the overall model estimate is shown instead.
How do changes in implicit bias correspond with changes in explicit bias?
To test whether the effects on implicit bias are consistent with effects on explicit bias, we
fit a network meta-analytic model that allows the simultaneous analysis of two correlated
outcomes (Efthimiou et al., 2015; Achana et al., 2014). This model revealed that effects on
implicit bias differed from effects on explicit bias, χ2(11, k = 572) = 34.63, p < .001.
As shown
in Figure 4, although effects on explicit bias were non-zero, χ2(11, k = 572) = 68.87, p < .001,
they tended to be smaller than effects on implicit bias. Three of the eleven procedures had
effects on implicit bias that were significantly larger than their effects on explicit bias: weaken
associations directly, weaken associations indirectly, and weaken goals. The rest of the
procedures except for threat, affirmation, and negative affect had non-significantly larger effects
on implicit bias. Explicit effect sizes tended to be less variable than implicit effect sizes, both in
terms of the percentage of between-studies heterogeneity (I2implicit = .786, I2explicit = .751) and the
effect size standard deviations (τimplicit = .282, τexplicit = .231).
To test whether implicit bias change mediated the effects of procedures on explicit bias
and whether explicit bias change mediated the effects of procedures on implicit bias, we
synthesized the indirect effects extracted from the correlation matrices from each study using
two-stage meta-analytic structural equation modeling (Cheung & Chan, 2005; Cheung &
Cheung, 2016). We modeled the differences between the indirect effects resulting from different
procedure comparisons using a contrast-based approach, which represents direct comparisons
using dummy codes and indirect comparisons using treatment contrasts (Salanti, Higgins, Ades,
& Ioannidis, 2008). Because we only conducted these analyses with two-condition studies for
which we knew the implicit effect size, explicit effect size, and the correlation between implicit
and explicit bias, the results are based on fewer studies (k = 189) than the full set of studies that
contain an explicit measure (k = 262). All values from this analysis can be interpreted as the
product of a correlation and a semi-partial correlation.
As shown in Figure 5, the indirect effects are all quite small. A Wald χ2 test suggested
that we could not reject the null hypothesis that the indirect effects of procedures on explicit bias
through implicit bias change were zero, χ2(10, k = 189) = 17.94, p = .083. The same was true of
the reverse mediation estimating the effects of procedures on implicit bias through explicit bias
change, χ2(10, k = 189) = 7.74, p = .736. None of the estimates for the indirect effects of the
specific procedures was different from zero. There is little evidence in our data that is consistent
with a causal relationship between automatically and deliberately retrieved associations. There
was so little variation between studies in the magnitude of the indirect effects that the variation
had to be fixed to zero for the models to converge.
One study was removed from this analysis because its within-studies variance-covariance matrix of effects on
implicit and explicit bias was degenerate.
Figure 4. Forest plot of the consistency between effects on implicit and explicit bias. k gives the
number of studies with implicit and explicit measures that directly (or indirectly, listed in
parentheses) compare the listed procedure and a neutral procedure. “I - E” gives the difference
between the implicit and explicit effect sizes, “χ2” gives the 1 df Wald χ2 test of the difference,
and “p” gives its p-value.
Figure 5. Indirect effects (in the conventional mediation framework, the effect ab) of procedures
on explicit bias through changes in implicit bias (𝑃 → 𝐼 → 𝐸) and implicit bias through changes
in explicit bias (𝑃 → 𝐸 → 𝐼). k gives the number of studies that directly (or indirectly, listed in
parentheses) compare the listed procedure and a neutral procedure.
How do changes in implicit bias correspond with changes in behavior?
We performed a similar set of analyses on behavior as we did on explicit bias.
As with
explicit bias, effects on implicit bias differed from effects on behavioral outcomes, χ2(7, k = 489)
= 23.11, p = .002. As shown in Figure 6, procedures (with the exception of threat) had much
smaller effects on behavior than on implicit bias. Unlike with explicit bias, we did not reject the
null hypothesis that all behavioral effects were zero, χ2(7, k = 489) = 13.38, p = .063. Behavioral
effects were somewhat less variable than implicit effects, both measured in terms of the
percentage of between-studies heterogeneity (I2implicit = .777, I2behavior = .716) and the effect size
standard deviations (τimplicit = .299, τbehavior = .274).
As shown in Figure 7, we estimated both whether implicit bias change mediated the
effects of procedures on behaviors and whether behavior change mediated the effects of
procedures on implicit bias. As with our mediation analyses involving explicit bias, this analysis
is based on a set of samples (k = 62) that is smaller than the set of samples that contain a
behavioral measure (k = 93) because it only includes two-condition studies that had complete
data. There was no evidence that procedures had non-zero indirect effects, either on behavior
through implicit bias change, χ2(7, k = 62) = 11.20, p = .130, or on implicit bias through behavior
change, χ2(7, k = 62) = 4.69, p = .698. Only one of the indirect effects had a 95% confidence
interval that excluded zero, the reverse mediation effect for procedures that induce goals to
strengthen bias, and the indirect effect was in the opposite direction of the effect of the procedure
on implicit bias (g = .14, 95% CI = [.01, .28]). There is little evidence in our data that is
consistent with a causal relationship between automatically retrieved associations and behavior.
As with the indirect effects on explicit bias, there was so little variation between studies in the
size of the indirect effects that the variation had to be fixed to zero for the models to converge.
Studies with affirmation, positive or negative affect, or depletion procedures were excluded from this analysis
because there were no studies with behavioral measures that used these procedures. An additional study was
removed from this analysis because its within-studies variance-covariance matrix of effects on implicit and
behavioral bias was degenerate.
Figure 6. Forest plot of the consistency between effects on implicit bias and behavior. k gives
the number of studies with implicit and behavioral measures that also directly (or indirectly,
listed in parentheses) compare the listed procedure and a neutral procedure. “I - B” gives the
difference between the implicit and behavioral effect sizes, “χ2” gives the 1 df Wald χ2 test of the
difference, and “p” gives its p-value.
Figure 7. Indirect effects (in the conventional mediation framework, the effect ab) of procedures
on behavior through changes in implicit bias (𝑃 → 𝐼 → 𝐵) and implicit bias through changes in
behavior (𝑃 → 𝐵 → 𝐼). k gives the number of studies that directly (or indirectly, listed in
parentheses) compare the listed procedure and a neutral procedure.
Is there evidence that the size of reported effects is biased?
We tested for biases in effect sizes by assessing funnel plot asymmetry
and by assessing
whether effect sizes varied by publication status, year, or geographic location. Funnel plots
show study effect sizes plotted against their standard errors (Egger et al., 1997). Funnel plots of
an unbiased literature have a fan shape, with studies centering around a single effect size,
regardless of precision, but with a greater scatter around the effect size in low-precision studies.
Bias causes asymmetry in funnel plots by preventing a subset of low-precision studies (e.g.,
those with non-significant results) from entering the meta-analysis.
Comparison-adjusted funnel plots are funnel plots adapted to network meta-analysis
(Chaimani et al., 2013). Although they cannot accommodate multiple effects from the same
study, they can accommodate studies that examine different sets of comparisons between
procedures. They account for these different comparisons by subtracting the relevant meta-
analytic comparison estimate (e.g., threat vs. neutral, weaken goals vs. neutral) from each study
estimate prior to plotting. As in a normal funnel plot, one can then examine the comparison-
adjusted plots for asymmetry, which suggests that some process differentially affected high and
low precision studies (e.g., publication bias).
To select a set of two-group studies (published and unpublished) in which most
researchers would make similar predictions, we made the following three generic predictions.
First, the weaken associations directly, weaken associations indirectly, and weaken goals
procedures will result in decreased implicit, explicit, and behavioral bias relative to a neutral
procedure. Second, the strengthen associations directly, strengthen associations indirectly,
strengthen goals, and deplete resources procedures will result in increased bias relative to a
neutral procedure. Third, procedures in the first group will result in less bias than procedures in
the second.
The funnel plots of the comparison-adjusted effect sizes for these studies on implicit,
explicit, and behavioral measures are shown in Figure 8. The figure reveals asymmetry in all
plots in that high-precision effect sizes tended to be smaller than their corresponding overall
meta-analytic estimates. This observation was supported by the results of mixed-effect
regression analyses (Sterne & Egger, 2005) testing the relationship between implicit standard
errors and effect sizes, z = 3.62, p < .001 and explicit standard errors and effect sizes, z = 2.99, p
= .003. There was no significant relationship between the behavioral standard errors and effect
sizes, z = 1.40, p = .163, though this last relationship was also estimated with much less precision
than the implicit and explicit relationships. If the funnel plot asymmetry is caused by processes
that systematically prevent small, non-significant effect sizes from entering the meta-analysis
(e.g., publication bias, p-hacking), this suggests that implicit and explicit effects in this meta-
analysis are inflated relative to their population values.
Several other methods of detecting bias are available, such as p-curve analysis (Simonsohn, Nelson, & Simmons,
2014) and contour-enhanced funnel plots (Peters et al., 2008). We did not use these methods because many of them
depend on assumptions of homogeneity and have not been adapted to examining bias in a network of interventions
where heterogeneity is expected a priori (for a review, see Efthimiou et al., 2016).
Figure 8. Comparison-adjusted funnel plots of effect sizes vs standard errors for implicit, explicit, and behavioral measures. Positive
numbers are more extreme relative to the meta-analytic comparison a study contributes to and negative numbers less extreme. The red
dashed line represents the fit from a mixed-effects regression; a line that departs from the vertical suggests the presence of small-study
Funnel plots do not distinguish between the many processes that could lead to
asymmetry. In contrast, testing whether specific moderators such as publication year, are related
to effect sizes is more specific. We therefore supplemented our analysis of funnel plot
asymmetry with analyses using publication year, publication status, and geographic region.
These analyses allowed us to test for evidence of a decline effect (Jennions & Møller, 2002),
publication bias (Stern & Simes, 1997), and a United States bias (Fanelli & Ioannidis, 2013),
Implicit effect sizes varied by publication year, χ2(11, k = 464) = 25.64, p = .007.
shown in Figure 9, there was a general tendency for more recent studies to yield smaller effect
sizes. There were two exceptions: strengthen associations indirectly, for which effect sizes
remained constant across all publication years, B = .006, 95% CI = [-.025, .038], and goals to
weaken bias, for which there was a growth effect rather than a decline effect more recent
studies have larger (more negative) effect sizes, B = -.029, 95% CI = [-.062, -.007]. This last
relationship may be driven by research on the susceptibility of implicit measures to show no bias
or a reverse bias through strategic responding (e.g., implementation intentions to reduce bias on a
shooter bias task, Mendoza, Gollwitzer, & Amodio, 2010, instructions to Germans to fake a pro-
Turkish IAT score, Fiedler & Bluemke, 2005). Early studies suggested that implicit measures
were resistant to strategic responding (Banse, Seise, & Zerbes, 2001; Egloff & Schmukle, 2002;
Kim, 2003), whereas more recent studies have suggested that strategic responding is possible,
particularly with sufficiently specific instructions (Fiedler & Bluemke, 2005; Lai et al., 2014;
2016; Stewart & Payne, 2008). Effect sizes did not depend on publication status, χ2(11, k = 573)
= 18.01, p = .081, or geographic location, χ2(11, k = 573) = 5.63, p = .897.
We did not do any moderator analyses with the explicit or behavioral data because there was not sufficient
variability in the moderators across the intervention categories.
Figure 9. Relationship between publication year and effect sizes on implicit bias. Larger points
represent effect sizes that are estimated with greater precision. Only direct comparisons between
each listed procedure and a neutral procedure are shown as points.
General Discussion
Our meta-analysis is the first large-scale quantitative synthesis of research on change in
implicit bias. We found that implicit bias can be changed across many areas of study,
populations, implicit measures, and research designs. The type of approach used to change
implicit bias mattered greatly. Some procedures were effective at changing implicit bias, whereas
others were not. Procedures to change implicit bias produced similar but smaller changes in
explicit bias, and there was no strong evidence that they produced any change in behavior at all.
Further, changes in implicit bias did not mediate changes in explicit bias or behavior, nor did we
find evidence that changes in explicit bias or behavior mediated change in implicit bias.
Relative effectiveness of procedures to change implicit bias
We developed a taxonomy for understanding how procedures to change implicit bias
differed. Using this taxonomy, we found that procedures that directly or indirectly targeted
associations, depleted mental resources, or induced goals all changed implicit bias relative to
neutral procedures. In contrast, procedures that induced threat, affirmation, or affective states
had small and/or inconsistent effects. These results support the theoretical portrayal of
automatically retrieved associations as sensitive to pairings of information in the social
environment (Gawronski & Bodenhausen, 2006). These results also support the importance of
goal-directed motivation and cognitive resources in changing the expression of automatically
retrieved associations (Fazio & Olson, 2014; Gawronski & Payne, 2010; Devine, 1989).
However, even the procedures that produced robust effects on implicit bias had “small”
effect sizes by conventional standards (Hyde, 2005) and as compared to typical effect sizes in
social psychology (Richard, Bond, & Stokes-Zoota, 2003). Our funnel plot analyses suggest that
the true population effects of these procedures may be even smaller than our meta-analytic
estimates due to publication bias, p-hacking, and/or other related processes.
Generalizability of implicit bias change
We also uncovered evidence of large variation in the size of the effects produced by
procedures to change implicit bias. Some of the sources of this variation reveal complexities in
evaluating the impact of the procedures on implicit bias. First, researchers’ choices of samples
have constrained the generalizability of the available evidence (Henrich, Heine, & Norenzayan,
2010). Most studies have been conducted with samples whose demographic characteristics
(students, mostly White, mostly female) strongly resemble those of Introductory Psychology
classrooms in the United States. Although the gender composition of the sample was not
associated with the size of effects, both the racial composition of the samples and whether the
samples were drawn from university student populations were. Student samples in particular
produced different effect sizes than non-student samples for three of the nine procedure
comparisons that we examined (strengthen associations directly vs. neutral, weaken associations
indirectly vs. neutral, goals to weaken bias vs. neutral).
Because studies with university student samples often address different research
questions than studies with non-university student samples and because university students are
psychologically different from the general population (Henrich et al., 2010; Sears, 1986), the
precise cause of these different effect sizes is unclear. Regardless, these results suggest that it
would be prudent to directly test whether the effects of manipulations are generalizable to other
populations. Combating societal problems such as discrimination and addiction requires
exploration of how the problems operate outside of the college campus, and answering questions
of human nature depends on sampling from a population that represents humankind.
Another limit to generalizability is a lack of research interest in change beyond the
confines of a single experimental session. Only 17 (3.0%) samples used procedures that took
longer than one session to complete. Only 38 (6.6%) samples in the meta-analysis collected
longitudinal outcomes and therefore had the opportunity to examine whether the procedures they
investigated produce long-term changes. Short-term changes in implicit bias do not necessarily
generalize to longer-term changes (Devine, Forscher, Austin, & Cox, 2012; Forscher et al., 2017;
Forscher & Devine, 2014; Lai et al., 2016; Lai, Hoffman, & Nosek, 2013; Miller, Dannals &
Zlatev, 2017). As such, the present meta-analysis speaks more to the processes that change
implicit bias in the short-term rather than to processes that change implicit bias in the long-term.
These points are particularly salient given theorizing that implicit bias is created and sustained by
repeated pairings of information in the social environment. That means that without active efforts
to sustain short-term shifts created in the lab, these shifts are likely to be wiped away upon re-
exposure to the social environment (Forscher et al., 2017; cf. De Houwer, 2009; Mann &
Ferguson, 2017). In fact, one recent series of studies found that nine interventions that reduced
implicit race bias immediately showed little to no lasting impact days later (Lai et al., 2016).
What processes determine whether a shift in implicit bias will be temporary or long-lasting?
When will a shift in implicit bias translate into a permanent change in orientation? Theory and
practice-oriented researchers alike must contend with these open questions.
Effect sizes also differed according to a study’s methodological features. Studies using
an IAT produced effects that were often larger than studies that did not, and studies with a pre-
test post-test design that induced a goal to weaken bias produced larger effects than studies that
only included a post test measurement. The large IAT effects could be driven by the IAT’s
reliability, which is typically higher than the reliability of most other implicit measures (Bar-
Anan & Nosek, 2014; Bosson et al., 2000). We speculate that the larger effects for pre-test post-
test designs could be driven by effects in studies examining strategic responding on implicit
tasks, as such research has revealed that strategic responding is particularly easy with past task
experience (Fiedler & Bluemke, 2005).
The effects of interventions did not vary much based on their topic. Studies that targeted
evaluative associations did not differ from studies that targeted conceptual associations, and
effect sizes did not differ as a function of domain (e.g., intergroup relations, clinical/health).
Implicit bias and explicit bias
Most studies of the relationship between the implicit and explicit bias are observational
studies that administer implicit and explicit measures within the same study. These relationships
can be very low or very high, and are highest when using the IAT at least when the target
concepts are not socially sensitive, when people’s thoughts about the concepts are well-
elaborated, when the concepts are diametrically opposed (e.g., liberals vs. conservatives), and
when people perceive that their opinions about the concepts are distinct from the opinions of
others (Nosek, 2005). Although it was not the primary purpose of our meta-analysis, we found
that the correlation between implicit and explicit bias in our sample of experimental studies was
quite low (rI-E = .14). This is a marked difference from the median (rI-E = .38) of large-sample
studies (N > 100,000) investigating highly heterogeneous topics in highly heterogeneous
samples. In fact, compared to 95 examined topics, the estimate from this meta-analysis was
smaller than all but one (Nosek & Hansen, 2008).
There are good reasons expect a different correlation in experimental studies than in
observational studies. The correlation between implicit and explicit bias will vary according to a
manipulation’s causal impact on implicit and explicit bias. However, other features besides a
manipulation’s causal impact also differ between observational studies of the correlation
between implicit and explicit bias and the experimental studies examined in this meta-analysis.
The experimental studies tended to use relatively homogeneous White student samples, single-
session manipulations, and tended to focus on a limited range of topics. For example, the most
common topic in this meta-analysis was intergroup relations (63.4% of studies), an area known
for low implicit-explicit correlations in observational studies (Hofmann et al., 2005; Nosek,
2005, 2007). This homogeneous sampling may have constrained the magnitude of the correlation
between implicit and explicit bias beyond what might be expected due to the causal impact of
experimental manipulations.
Our focus on randomized studies also gave us an opportunity to go beyond correlational
evidence by examining whether procedures that attempt to change implicit bias also produce
change in explicit bias, and whether change in explicit bias mediated change in implicit bias. We
found that many of the procedures that change implicit bias also produce change in explicit bias,
though the magnitude of change in explicit bias was weaker and less variable. Simultaneously,
there was no evidence that changes in implicit and explicit bias were mediated by each other.
One possibility suggested by these data is that there is no relationship between changes in
implicit and explicit bias. This possibility would reduce support for theoretical perspectives that
posit interdependence between automatic and deliberate processes that are presumed to underlie
implicit and explicit bias (e.g., Gawronski & Bodenhausen, 2006; c.f. Smith & DeCoster, 2000).
However, even if this is true, we cannot eliminate the possibility that the relationship is stronger
in other samples or topics.
It is not possible from these data to determine whether increasing diversity in samples,
designs, and topics would yield substantively different mediation results. The most productive
next step is to evaluate these possibilities directly. There are some hints that such investigations
would yield stronger mediation evidence. For example, Smith, Ratliff, and Nosek (2012) had
large samples of participants (N’s = 732; 621) form attitudes toward novel policy proposals that
were randomly attributed to Democrats or Republicans. Implicit and explicit attitudes toward the
plans were strongly correlated (r’s = .48, .51/.59) and implicit attitudes fully mediated the effect
of the experimental intervention on explicit attitudes, but not the reverse, both immediately and 5
days after the intervention.
This example was not included in this meta-analysis because we only examined studies
of pre-existing biases. As a consequence, this and all other studies of the formation of new
associations were excluded. This creates an interesting mystery to be solved. The association
formation literature provides substantial experimental evidence for the interdependence of
automatically and deliberately retrieved associations (e.g., Gawronski & Bodenhausen, 2006,
2011; Gawronski & LeBel, 2008; Gawronski, Rydell, Vervliet, & De Houwer, 2010; Moran,
Bar-Anan, & Nosek, 2015; Ranganath & Nosek, 2008). In contrast, this meta-analysis on pre-
existing associations provides little evidence of interdependence. Whatever the explanation,
resolving the apparent discrepancy between research on new and pre-existing associations
provides an exciting opportunity to advance theory about implicit bias.
Implicit bias and behavior
Previous investigations of implicit-behavior relations have also relied on observational
studies. Meta-analytic estimates of this relationship vary substantially (Greenwald et al., 2009 rI-
B = .27; Cameron et al., 2012 rI-B = .28; Oswald et al., 2013 rI-B = .14; Carlsson & Agerström,
2016 rI-B = .15). The correlations between implicit bias and behavior tend to be smallest for
topics in which automatic and deliberate processes are least likely to facilitate each other, such as
race relations (Greenwald et al., 2009). The overall correlation between implicit bias and
behavior in our meta-analysis was small and closer to the estimates in the meta-analyses on these
topics (rI-B = .10).
On the surface, this research is about prediction, but of course, the interest is also about
causation. Indeed, many researchers use evidence of correlations between implicit bias and
behavior to argue for the causal importance of automatically retrieved associations (e.g.,
Dovidio, Kawakami, & Gaertner, 2002; Green et al., 2007; Kang & Banaji, 2006; Devine et al.,
2012; Banaji, Bhaskar, & Brownstein, 2015). For example, Devine, Forscher, Austin, and Cox
(2012) argue on the basis of correlational studies that “accumulating evidence reveals that
implicit biases are linked to discriminatory outcomes ranging from the seemingly mundane, such
as poorer quality interactions (McConnell & Leibold, 2001), to the undeniably consequential,
such as constrained employment opportunities (Bertrand & Mullainathan, 2004) and a decreased
likelihood of receiving life-saving emergency medical treatments (Green et al., 2007). [...]
[Implicit bias] leads people to be unwittingly complicit in the perpetuation of discrimination.”
Of course, correlations between variables can be produced by many relationships besides
ones that are causal. To get closer to questions of causality, we looked at whether changes in
implicit bias correspond with and mediate changes in behavior in our sample of randomized
experiments. We found no little evidence that procedures that change implicit bias also produce
change in behavior. We also found no evidence that changes in implicit bias mediate changes in
behavior, nor that changes in behavior mediate changes in implicit bias.
The lack of evidence for mediation is difficult to reconcile with the correlational evidence.
As with explicit bias, the fact that the studies in our meta-analysis disproportionately used
primarily White student samples, single-session manipulations, and a narrow range of topics
provides an important limit to the generalizability of our conclusions. However, even if the
relationship between changes in implicit bias and changes in behavior is truly smaller in the
domains sampled by this meta-analysis (i.e., intergroup relations, addiction, clinical psychology)
than in other domains (e.g., political attitudes), our results suggest a constraint on the conditions
under which changing implicit bias will predict or cause corresponding changes in unwanted
Potential explanations for implicit bias’s relationships with explicit bias and behavior
Even if we accept that our explanations of our explicit bias and behavior findings do not
generalize to all samples and topics, we are left with specifying what those explanations are. We
offer four possibilities.
First, our inclusion criteria for explicit and behavioral measures may have led to the
inclusion of measures that should not be theoretically expected to change after a change in
automatically retrieved associations. We included any measure that we judged to be
correspondent with the study’s implicit measure, regardless of whether they are expected to
change after the manipulation. If the theoretical conditions under which a change in
automatically retrieved associations will influence deliberately retrieved associations and
behavior are narrower than mere correspondence, our meta-analysis would not be sensitive to
those conditions. For example, if the implicit measure was a Black/White good/bad IAT, we
included any explicit or behavioral measure that connected race and valence. Correspondent
explicit measures ranged from a simple feeling thermometer that assesses perceived warmth
toward Whites vs. Blacks (Rudman, Dohn, & Fairchild, 2007) to the Symbolic Racism Scale that
assesses the degree to which participants blame Black people for their current social standing
(Inzlicht, Gutsell, & Legault, 2012). Correspondent behavioral measures ranged from how close
a person sits to a Black confederate (Mann & Kawakami, 2012) to decisions about donating to
children in South African vs. Colombian slums (Schwab & Greitemeyer, 2015). Oftentimes,
experimental manipulations are designed to create dissociations that target mental processes
relevant to implicit biases but not explicit biases or behavior. For example, exposure to
counterstereotypical exemplars is often found (and expected) to change implicit racial attitudes
without having corresponding effects on explicit racial attitudes (Dasgupta & Greenwald, 2001;
Cullen, Barnes-Holmes, & Barnes-Holmes, 2009; Lai et al., 2014; McGrane & White, 2007).
Perhaps stricter inclusion criteria that were more sensitive to specific theoretical conditions
where implicit change was expected to relate to explicit or behavioral change would have
revealed stronger evidence for mediation.
Second, perhaps confounds introduced after the manipulations obscured the evidence for
mediation. Statistical mediation analysis relies on the untestable assumption of a lack of
confounding of the post-manipulation mediator-outcome relationship (Bullock, Green, & Ha,
2010). Most, but not all, sources of confounding will overstate the evidence for mediation
(Bullock et al., 2010). However, confounding that reduces evidence for mediation could explain
the null results. That may happen, for example if a second mediator that opposes the causal
influence of implicit bias was also changed by many of the procedures examined in the meta-
analysis. We cannot rule out this explanation, but we also cannot identify what these confounds
would be.
Third, measurement issues may obscure the evidence for mediation within our studies.
No measure provides a pure estimate of a latent construct (Borsboom, 2006), and implicit
measures are no exception (Conrey et al., 2005; Calanchini & Sherman, 2013; Payne, 2001).
Performance on implicit measures reflects the contribution of associative processes,
measurement error, and non-associative processes such as task-switching ability, recoding,
inhibition of impulses, and guessing (Calanchini et al., 2013; 2014; Klauer & Mierke, 2005).
High levels of measurement error, as is characteristic of implicit measures (Buhrmester, Blanton,
& Swann, 2011; Olson & Fazio, 2002; Bosson et al., 2000) could obscure evidence that changes
in implicit bias mediate changes in other processes.
It is also possible that many of the procedures we examined produced change in
measured implicit bias through non-associative processes. At least some of the procedures did
do so. For example, a subset of studies that used goals to strengthen or weaken bias gave
participants instructions to strategically respond or fake an implicit measure (e.g., Banse, Seise,
& Zerbes, 2001; Fiedler & Bluemke, 2005). If many of our procedures produced change through
non-associative processes, our analyses would bear on the effectiveness of these non-associative
processes for producing change in explicit bias and behavior rather than the effectiveness of
automatically retrieved associations. Without tools that isolate the contributions of associative
and non-associative processes, we cannot definitively rule this possibility out.
Fourth, perhaps automatically retrieved associations really are causally inert. Accepting
this conclusion would force reevaluation of some of the central assumptions that drive implicit
Measurement error in implicit measures would not explain the lack of an overall effect of procedures on
behavioral outcomes, although measurement error in behavioral measures might. A recent meta-analysis (Carlsson
& Agerström, 2016) found that behavioral measures in research on the IAT and discrimination lacked validity and
reliability. Many of the behavioral measures in this meta-analysis appeared to suffer from similar measurement
issues. For example, many behavioral outcomes were based on as a single behavior (rather than an aggregate of
multiple behaviors) and were not based on standardized procedures where the validity and reliability is well-known.
bias research. For example, instead of acting as a “cognitive monster” that inevitably leads to
bias-consistent thought and behavior (e.g., Bargh, 1999; Tajfel, 1982), automatically retrieved
associations could reflect the residual “scar” of concepts that are frequently paired together
within the social environment. From this view, implicit biases are a side effect of living in a
particular social environment. Similarly, a scar interpretation would suggest that changes in
implicit bias represent epiphenomenal changes rather than changes in the causal processes that
drive deliberately retrieved associations or behavior.
This is not to say that the measurement of implicit bias would be unproductive even
under this interpretation. Demographic variables such as life expectancy are often used to predict
other consequential outcomes within a population, despite lacking causal force themselves. By
the same token, levels of implicit bias could be used to predict the prevalence of certain
judgments or behaviors within a population. However, under this interpretation, although the
presence of an implicit bias would speak to the structure of the social environment, efforts to
change behavior by changing implicit bias would be misguided. It would be more effective to
rid the social environment of the features that cause biases on both behavioral and cognitive
outcomes (Beaman, Duflo, Pande, & Topalova, 2012) or equip people with strategies to resist the
environment’s biasing influence (Devine et al., 2012; Cohen & Sherman, 2014) rather than
trying to alter the biases themselves.
A new account of automatically retrieved associations as non-causal requires theoretical
integration of findings that do not converge with the results of this meta-analysis. Although the
scar interpretation of implicit bias explains correlations between implicit bias, explicit bias, and
behavior as resulting from the shared cause of the social environment, this interpretation is
nonspecific and does not explain why certain correlations between implicit bias and other
variables are stronger than others. For example, well-elaborated concepts have stronger levels of
convergence between implicit and explicit bias (Nosek, 2005), and people who have higher
levels of working memory have lower levels of convergence between implicit bias and behavior
(Hofmann, Gschwendner, Wiers, Friese, & Schmitt, 2008; Perugini, 2005; for a review, see
Perugini, Richetin, & Zogmaister, 2010). A non-causality account would also have to integrate
studies on novel associations that, as noted above, provide stronger evidence for mediation, at
least in the case of explicit bias (e.g., Gawronski & Bodenhausen, 2006, 2011; Gawronski &
LeBel, 2008; Gawronski et al., 2010; Moran et al., 2015; Ranganath & Nosek, 2008). Presently,
it is unclear how to theoretically integrate the scar interpretation with this evidence.
This meta-analysis found that implicit bias can be changed, and identified the approaches
that are most successful in doing so. However, we also found little evidence that changes in
implicit bias translated into changes in explicit bias and behavior, and we observed limitations in
the evidence base for implicit malleability and change.
These results produce a challenge for practitioners who seek to address problems that are
presumed to be caused by automatically retrieved associations, as there was little evidence
showing that change in implicit biases will result in changes for explicit biases or behavior. This
is particularly true for the domains of greatest interest to many practitioners intergroup bias,
health psychology, and clinical psychology. Our results suggest that current interventions that
attempt to change implicit bias will not consistently change behavior in these domains.
These results also produce a challenge for researchers who seek to understand the nature
of human cognition because they raise new questions about the causal role of implicit bias. The
results of the current meta-analysis do not lend themselves to a single interpretation. To better
understand what the results mean, future research should innovate with more reliable and valid
implicit, explicit, and behavioral measures, intensive manipulations, longitudinal measurement
of outcomes, heterogeneous samples, and diverse topics of study.
These innovations may yet reveal stronger evidence for the causal importance of
automatically retrieved associations. It would not be the first time that the conclusions of a
review were overturned by later advances. Following Wicker’s (1969) review showing a weak
correlation between explicit attitudes and behavior, better measurement and theory revived the
relevance of attitudes for understanding thought and action. As they did in response to Wicker,
we hope that researchers take our findings as a challenge to improve theory and method and
advance our understanding of human cognition.
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... However, while implicit biases can be reduced, the effectiveness of those strategies and reduction on behavior is inconsistent. To offer a clearer picture of this inconsistence, a systematic review of 494 studies by Forscher et al. (2019) concluded that there is little evidence that a reduction in implicit biases will translate into changes in behaviors. This is problematic, because while a bias is a mental inclination, discrimination is biases in action. ...
... To address this thorny question, reviews have suggested improvement in methodologies, pools of participants, categories of biases, implicit vs. explicit measures, and especially caution in using the IAT as a behavioral predictor (e.g. Amodio, 2008;Greenwald et al., 2009;Cameron et al., 2012;Carlsson and Agerström, 2016;Forscher et al., 2019). But most importantly, FitzGerald et al. (2019) suggested a paradigm shift, focusing on how to reduce the negative impact of implicit biases in behaviors rather than just reducing implicit biases themselves. ...
... Second of all, change management has a strong focus on explicit changes at both individual and organizational level (Buckworth et al., 2007;Burke, 2017), which is not too far from a goal of bias management in term of aiming for actual changes in behaviors. Third of all, this discipline strives for systematic changes rather than a quick fix, which also addresses a major limitation of implicit bias interventions where 97% of the studies used procedures that took one single experimental session to complete (Forscher et al., 2019). The shared idea between change management and studies of implicit bias strategies is that "people can change, " and if change management has successful strategies, then bias management could benefit from this wide array of concepts and methods that change management and adjunct disciplines have to offer. ...
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This paper conducted a preliminary study of reviewing and exploring bias strategies using a framework of a different discipline: change management. The hypothesis here is: If the major problem of implicit bias strategies is that they do not translate into actual changes in behaviors, then it could be helpful to learn from studies that have contributed to successful change interventions such as reward management, social neuroscience, health behavioral change, and cognitive behavioral therapy. The result of this integrated approach is: (1) current bias strategies can be improved and new ones can be developed with insight from adjunct study fields in change management; (2) it could be more sustainable to invest in a holistic and proactive bias strategy approach that targets the social environment, eliminating the very condition under which biases arise; and (3) while implicit biases are automatic, future studies should invest more on strategies that empower people as “change agents” who can act proactively to regulate the very environment that gives rise to their biased thoughts and behaviors.
... Furthermore, on a methodological level, the study reported by Hofmann et al. (2010, Study 2) is not informative about whether the observed reduction in positivity towards chocolate was a consequence of the verbal stimulus-response contingency or a consequence of highlighting the goal of eating less chocolatea goal that was not present in the control condition. A similar conceptual ambiguity can be found in a recent meta-analysis (Forscher et al., 2019), where the authors categorized the procedure used by Stewart and Payne (2008) as a goal-induced effect. Thus, empirically and theoretically, it is not clear whether the previously observed effects are a consequence of (or attributed to) mechanisms of goal setting or merely to encountering a stimulusresponse contingency (in a verbal format). ...
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Repeatedly experiencing a specific stimulus-affect contingency influences subsequent evaluative responses towards the respective stimulus (e.g., evaluative conditioning). In the present research, we provide further evidence that verbally processed stimulus-affect contingencies in the form of if-then plans have comparable evaluative consequences. We present three studies (N = 323) in which participants verbally linked cupcakes to either a positive ("delicious") or a negative ("disgusting") affective response while being instructed with the same health-related goal. We tested the evaluative consequences of processing these verbal stimulus-affect plans in a valence-based response-compatibility paradigm (Implicit Association Test, IAT) and self-reported liking ratings. We failed to observe the predicted effect in the first study and updated the methodology for the following two studies. With the updated procedure (two studies, N = 239), we found the hypothesized effect that processing a verbal stimulus-affect plan influences subsequent responses in the IAT and self-reported ratings in an eval-uatively congruent direction. We discuss these results in relation to similar effects following directly experienced stimulus-affect contingencies and instructed evaluative conditioning. Furthermore, our present research highlights the potential to use verbal self-instruction in a stimulus-affect format to self-regulate one's evaluative responses towards specific stimuli (e.g., unhealthy snacks).
Clinician bias has been identified as a potential contributor to persistent healthcare disparities across many medical specialties and service settings. Few studies have examined strategies to reduce clinician bias, especially in mental healthcare, despite decades of research evidencing service and outcome disparities in adult and pediatric populations. This manuscript describes an intervention development study and a pilot feasibility trial of the Virtual Implicit Bias Reduction and Neutralization Training (VIBRANT) for mental health clinicians in schools—where most youth in the U.S. access mental healthcare. Clinicians (N = 12) in the feasibility study—a non-randomized open trial—rated VIBRANT as highly usable, appropriate, acceptable, and feasible for their school-based practice. Preliminarily, clinicians appeared to demonstrate improvements in implicit bias knowledge, use of bias-management strategies, and implicit biases (as measured by the Implicit Association Test [IAT]) post-training. Moreover, putative mediators (e.g., clinicians’ VIBRANT strategies use, IAT D scores) and outcome variables (e.g., clinician-rated quality of rapport) generally demonstrated correlations in the expected directions. These pilot results suggest that brief and highly scalable online interventions such as VIBRANT are feasible and promising for addressing implicit bias among healthcare providers (e.g., mental health clinicians) and can have potential downstream impacts on minoritized youth’s care experience.
Paraphilic interests are a cornerstone of forensic assessment. Self-reports of sexual inclinations are fraught with limitations when working with individuals who face extensive personal ramifications from the justice system. A brief overview of indirect measures of pedohebephilic interest as diagnostic adjunct is given focusing on Viewing Time measures and Implicit Association Tests. Introducing the Explicit and Implicit Sexual Interest Profile, we outline the diagnostic potential of combining conceptually different measures into a test battery. We underscore the importance of measurement reliability for applied diagnostic decisions at the individual level. Underlying psychological processes of Viewing Time measures and their relation to fakeability are explained. Summarizing the state of the art, we conclude with open questions and venues for future research that are relevant to applied forensic contexts.
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Through a dozen in-depth interviews of urban planning professionals in Brisbane, Australia, this study examines the relationship between the experience of women in the planning profession and the consideration of women’s issues in the city. The study reveals that Brisbane’s planning industry continues to be perceived by those who work within it as an ‘old-boys-club’. Planning practitioners are acquiring gender biases during their university education and possibly earlier – much before planning graduates enter the profession. Although the planning industry is adopting more inclusive leadership and management approaches and becoming more feminised, patriarchal relationships remain strong. Brisbane’s neoliberal planning and governance systems, and conservative business sector encourages and rewards ‘male’ behaviours in the workplace. The findings mostly corroborate earlier studies on gender issues in organisations. In the planning sector, gender issues are more concerning because they affect planning outcomes across the city, as well as the lived experiences and needs of women and other vulnerable groups.
Objective Racism is a public health crisis impacting children’s mental health, yet mental health service systems are insufficiently focused on addressing racism. Moreover, a focus on interpersonal racism and on individual coping with the impacts of racism has been prioritized over addressing structural racism at the level of the service system and associated institutions. In this paper, we examine strategies to address structural racism via policies impacting children’s mental health services. Method First, we identify and analyze federal and state policies focused on racism and mental health equity. Second, we evaluate areas of focus in these policies and discuss the evidence base informing their implementation. Finally, we provide recommendations for what states, counties, cities, and mental health systems can do to promote antiracist evidence-based practices in children’s mental health. Results Our analysis highlights gaps and opportunities in the evidence base for policy implementation strategies including: mental health services for youth of color, interventions addressing interpersonal racism and bias in the mental health service system, interventions addressing structural racism, changes to provider licensure and license renewal, and development of the community health workforce. Conclusion Recommendations are provided both within and across systems to catalyze broader systems transformation.
We call for psychologists to expand their thinking on fair and just public safety by engaging with the “Abolition Democracy” framework that W. E. B. Du Bois articulated as the need to dissolve slavery while simultaneously taking affirmative steps to rid its toxic consequences from the body politic. Because the legacies of slavery continue to produce disparities in public safety in the United States, both harming Black people and the institutions that could keep them safe, psychologists must take seriously questions of history and structure in addition to immediate situations. In this article, we consider the state of knowledge regarding psychological processes that contribute to discriminatory public safety. We also identify ways in which theorizing about discriminatory public safety can be improved by appreciating the historical and sociopolitical context in which policing occurs. © 2021 The Society for the Psychological Study of Social Issues
Neighborhood racial composition contributes to racial disparities in arrests, but prior research has almost exclusively focused on the magnitude of a minority population with somewhat mixed findings. We investigate whether racial disparities in arrests perpetuate when the racial composition reaches a particular threshold to assess whether the accumulation of race matters, and to what degree. To expand upon prior research, we include a range of part 2 crimes—public drunkenness, drug offenses, and disorderly conduct—“lower level” crimes which may allow for greater police discretion. We conduct negative binomial regression analyses using arrest data from a mid-sized city in the South between 2010 and 2015. Results show evidence of a threshold effect, but this pattern differs across race and crime type. There is no evidence that Whites are more likely to be arrested in Black neighborhoods. This suggests that race-specific arrest rates may be driven by offense type and neighborhood racial composition.
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Recent interest in the implicit self-esteem construct has led to the creation and use of several new assessment tools whose psychometric properties have not been fully explored. In this article, the authors investigated the reliability and validity of seven implicit self-esteem measures. The different implicit measures did not correlate with each other, and they correlated only weakly with measures of explicit self-esteem. Only some of the implicit measures demonstrated good test–retest reliabilities, and overall, the implicit measures were limited in their ability to predict our criterion variables. Finally, there was some evidence that implicit self-esteem measures are sensitive to context. The implications of these findings for the future of implicit self-esteem research are discussed.
The present research examines the effects of gender on performance attributions and perseverance in different academic domains. Three studies tested whether men and women's reactions to negative or positive feedback differed across academic domains. In Study 1, attributions to ability were influenced by gender: women were more likely to attribute failure on a putative math test to a lack of ability than failure on a putative verbal test, whereas men showed a nonsignificant tendency to attribute failure on a putative verbal test to a lack of ability than failure on a putative math test. Study 2 replicated the findings of Study 1 for failure and showed that gender differences in attributions for alleged failure persisted when statistically controlling for past math experience. In addition, the more women attributed failure on a math test to their ability, the less likely they were to persevere in the math domain, suggesting that performance attributions affect subsequent motivation. In Study 3, women were given a test described as either of their math ability or their general cognitive ability and their implicit and explicit gender-math stereotypes were assessed. Stereotype threat did not influence performance attributions. Contrary to predictions, in the threat condition, but not the reduced threat condition, the more women implicitly stereotyped women, the less they attributed mathematical failure to their own ability. Findings are discussed in terms of gender stereotypes influencing performance attributions and perseverance following setbacks. Gender-math stereotypes are known to undermine women's confidence and performance on mathematical tasks (e.g. Spencer, Quinn & Steele, 1999). Thus, stereotypes may also affect women's attributions for their math performance and their motivation to succeed in quantitative fields.
Skepticism about the explanatory value of implicit bias in understanding social discrimination has grown considerably. The current article argues that both the dominant narrative about implicit bias as well as extant criticism are based on a selective focus on particular findings that fails to consider the broader literature on attitudes and implicit measures. To provide a basis to move forward, the current article discusses six lessons for a cogent science of implicit bias: (1) There is no evidence that people are unaware of the mental contents underlying their implicit biases. (2) Conceptual correspondence is essential for interpretations of dissociations between implicit and explicit bias. (3) There is no basis to expect strong unconditional relations between implicit bias and behavior. (4) Implicit bias is less (not more) stable over time than explicit bias. (5) Context matters fundamentally for the outcomes obtained with implicit bias measures. (6) Implicit measurement scores do not provide process-pure reflections of bias. The six lessons provide guidance for research that aims to provide more compelling evidence for the properties of implicit bias. At the same time, they suggest that extant criticism does not justify the conclusion that implicit bias is irrelevant for the understanding of social discrimination.
For 40 years, research on impression formation and attitudes has relied on dual-process theories that represent knowledge in a single associative network. Although such models explain priming effects and some implicit responses, they are generally silent on other forms of learning and on the interface of social cognition with perception and action. Meanwhile, advances in cognitive neuroscience reveal multiple, interacting forms of learning and memory (e.g., semantic associative memory, Pavlovian conditioning, and instrumental learning), with detailed models of their operations, neural bases, and connections with perceptual and behavioral systems. This memory systems perspective offers a more refined, neurally plausible model of social cognition and attitudes that, I argue, provides a useful and generative account of human social behavior.
This article challenges the highly intuitive assumption that prejudice should be less likely in public compared with private settings. It proposes that stereotypes may be conceptualized as a type of dominant response (C. L. Hull, 1943; R. B. Zajonc, 1965) whose expression may be enhanced in public settings, especially among individuals high in social anxiety. Support was found for this framework in an impression formation paradigm (Experiment 1) and in a speeded task designed to measure Stereotypic errors in perceptual identification (Experiment 2). Use of the process dissociation procedure (B. K. Payne, L. L. Jacoby, & A. J. Lambert, in press) demonstrated that these effects were due to decreases in cognitive control rather than increases in stereotype accessibility. The findings highlight a heretofore unknown and ironic consequence of anticipated public settings: Warning people that others may be privy to their responses may actually increase prejudice among the very people who are most worried about doing the wrong thing in public.
The goal of the research reported in this article was to examine whether automatic group attitudes and stereotypes, commonly thought to be fixed responses to a social category cue, are sensitive to changes in the situational context. Two experiments demonstrated such variability of automatic responses due to changes in the stimulus context. In Study 1 White participants' implicit attitudes toward Blacks varied as a result of exposure to either a positive (a family barbecue) or a negative (a gang incident) stereotypic situation. Study 2 demonstrated similar context effects under clearly automatic processing conditions. Here, the use of different background pictures (church interior vs. street corner) for Black and White face primes affected participants' racial attitudes as measured by a sequential priming task. Implications for the concept of automaticity in social cognition are discussed.
Research on implicit stereotypes has raised important questions about an individual's ability to moderate and control stereotypic responses. With few strategies shown to be effective in moderating implicit effects, the present research investigates a new strategy based on focused mental imagery. Across 5 experiments, participants who engaged in counterstereotypic mental imagery produced substantially weaker implicit stereotypes compared with participants who engaged in neutral, stereotypic, or no mental imagery. This reduction was demonstrated with a variety of measures, eliminating explanations based on response suppression or shifts in response criterion. Instead, the results suggest that implicit stereotypes are malleable, and that controlled processes, such as mental imagery, may influence the stereotyping process at its early as well as later stages.
The present research suggests that automatic and controlled intergroup biases can be modified through diversity education. In 2 experiments, students enrolled in a prejudice and conflict seminar showed significantly reduced implicit and explicit anti-Black biases, compared with control students. The authors explored correlates of prejudice and stereotype reduction. In each experiment, seminar students' implicit and explicit change scores positively covaried with factors suggestive of affective and cognitive processes, respectively. The findings show the malleability of implicit prejudice and stereotypes and suggest that these may effectively be changed through affective processes.
Two experiments used a priming paradigm to investigate the influence of racial cues on the perceptual identification of weapons. In Experiment 1, participants identified guns faster when primed with Black faces compared with White faces. In Experiment 2, participants were required to respond quickly, causing the racial bias to shift from reaction time to accuracy. Participants misidentified tools as guns more often when primed with a Black face than with a White face. L. L. Jacoby's (1991) process dissociation procedure was applied to demonstrate that racial primes influenced automatic (A) processing, but not controlled (C) processing. The response deadline reduced the C estimate but not the A estimate. The motivation to control prejudice moderated the relationship between explicit prejudice and automatic bias. Implications are discussed on applied and theoretical levels.
We argue that psychologists who conduct experiments with long lags between the manipulation and the outcome measure should pay more attention to behavioral processes that intervene between the manipulation and the outcome measure. Neglect of such processes, we contend, stems from psychology’s long tradition of short-lag lab experiments where there is little scope for intervening behavioral processes. Studying process in the lab invariably involves studying psychological processes, but in long-lag field experiments it is important to study causally relevant behavioral processes as well as psychological ones. To illustrate the roles that behavioral processes can play in long-lag experiments we examine field experiments motivated by three policy-relevant goals: prejudice reduction, health promotion, and educational achievement. In each of the experiments discussed we identify various behavioral pathways through which the manipulated psychological state could have produced the observed outcome. We argue that if psychologists conducting long-lag interventions posited a theory of change that linked manipulated psychological states to outcomes via behavioral pathways, the result would be richer theory and more practically useful research. Movement in this direction would also permit more opportunities for productive collaborations between psychologists and other social scientists interested in similar social problems.