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The rigidity-of-the-right hypothesis (RRH), which posits that cognitive, motivational, and ideological rigidity resonate with political conservatism, is an influential but controversial psychological account of political ideology. Here, we leverage several methodological and theoretical sources of this controversy to conduct an extensive quantitative review—with the dual aims of probing the RRH’s basic assumptions and parsing the RRH literature’s heterogeneity. Using multi-level meta-analyses of relations between varieties of rigidity and ideology measures alongside a bevy of potential moderators (s = 329, k = 708, N = 187,612), we find that associations between conservatism and rigidity are tremendously heterogeneous, suggesting a complex—yet conceptually fertile—network of relations between these constructs. Most notably, whereas social conservatism was robustly associated with rigidity, associations between economic conservatism and rigidity indicators were inconsistent, small, and not statistically significant outside of the United States. Moderator analyses revealed that non-representative sampling, criterion contamination, and disproportionate use of American samples have yielded over-estimates of associations between rigidity-related constructs and conservatism in past research. We resolve that drilling into this complexity, thereby moving beyond the question of if conservatives are essentially rigid to when and why they might or might not be, will help provide a more realistic account of the psychological underpinnings of political ideology.
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Journal of Personality and Social Psychology
Revisiting the Rigidity-of-the-Right Hypothesis: A Meta-Analytic Review
Thomas H. Costello, Shauna M. Bowes, Matt W. Baldwin, Ariel Malka, and Arber Tasimi
Online First Publication, November 3, 2022.
Costello, T. H., Bowes, S. M., Baldwin, M. W., Malka, A., & Tasimi, A. (2022, November 3). Revisiting the Rigidity-of-the-
Right Hypothesis: A Meta-Analytic Review. Journal of Personality and Social Psychology. Advance online publication.
Revisiting the Rigidity-of-the-Right Hypothesis: A Meta-Analytic Review
Thomas H. Costello
, Shauna M. Bowes
, Matt W. Baldwin
, Ariel Malka
, and Arber Tasimi
Department of Psychology, Emory University
Department of Psychology, University of Florida
Department of Psychology, Yeshiva University
The rigidity-of-the-right hypothesis (RRH), which posits that cognitive, motivational, and ideological
rigidity resonate with political conservatism, is an inuential but controversial psychological account of
political ideology. Here, we leverage several methodological and theoretical sources of this controversy
to conduct an extensive quantitative review with the dual aims of probing the RRHs basic assumptions
and parsing the RRH literatures heterogeneity. Using multilevel meta-analyses of relations between
varieties of rigidity and ideology measures alongside a bevy of potential moderators (s=329, k=708,
N=187,612), we nd that associations between conservatism and rigidity are tremendously heteroge-
neous, suggesting a complexyet conceptually fertilenetwork of relations between these constructs.
Most notably, whereas social conservatism was robustly associated with rigidity, associations between
economic conservatism and rigidity indicators were inconsistent, small, and not statistically signicant
outside of the United States. Moderator analyses revealed that nonrepresentative sampling, criterion
contamination, and disproportionate use of American samples have yielded overestimates of associations
between rigidity-related constructs and conservatism in past research. We resolve that drilling into this
complexity, thereby moving beyond the question of if conservatives are essentially rigid to when and why
they might or might not be, will help provide a more realistic account of the psychological underpinnings
of political ideology.
Keywords: political ideology, cognitive rigidity, rigidity-of-the-right, heterogeneity, meta-analysis
Supplemental materials:
Perhaps the most inuential psychological account of what dis-
tinguishes leftists from rightists is known as the rigidity-of-the-right
hypothesis (henceforth, RRH; Tetlock, 1983). Put plainly, the RRH
suggests that conservative political ideologywhich reects pre-
ferences for free-market economics, a limited social safety net,
traditional moral values, and conventional cultural normsis con-
genial to people who are cognitively, motivationally, and ideologi-
cally rigid (Adorno et al., 1950;Jost et al., 2003;Wilson, 1973).
The RRH has received extensive coverage in national news media
(e.g., Douthat, 2020) and popular trade books (e.g., Jost, 2021;
Lakoff, 2008;Westen, 2007); it is even a mainstay in public
discourse concerning partisanship and political polarization (e.g.,
Hetherington & Weiler, 2018). Nevertheless, the models validity
and usefulness remain a topic of protracted scientic controversy
(see Malka et al., 2017;Morgan & Wisneski, 2017;Zmigrod, 2020).
On the one hand, several prior meta-analytic reviews have reported
positive relations between political conservatism and rigidity-
related variables (e.g., Jost, 2017;Jost et al., 2003;Van Hiel
et al., 2016), prompting many scholars to champion and rene
the notion that leftists and rightists fundamentally differ in their
psychological proles. On the other hand, a number of critiques of
the RRH have emerged over the years, including arguments that
politically biased thinking is effectively equivalent across the
political spectrum (e.g., Ditto et al., 2019), that rigidity characterizes
political extremists on both the right and left (e.g., Tetlock et al.,
1984;Zmigrod et al., 2020; see also Costello et al., 2021), and that
recurrent methodological shortcomings have systematically
stacked the deckin favor of the RRH (e.g., Malka et al., 2017).
Debates concerning the relative rigidity of conservatives and
liberals have endured for decades––but why? We suspect that the
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Thomas H. Costello
The authors would also like to thank Crystal Liu for her work identifying
and coding studies, Omer Kirmaz for his work aggregating scores across
raters, and Julie Weissova for her insightful comments and annotations.
This project would not exist without the brilliance and stewardship of Scott
Lilienfeld, who passed away during the drafting process. The authors have
dedicated this article to his memory.
Thomas H. Costello played lead role in conceptualization, data curation,
formal analysis, investigation, methodology, visualization and writing of
original draft. Shauna M. Bowes played supporting role in conceptualization,
data curation, formal analysis, methodology and writing of review and
editing. Matt W. Baldwin played supporting role in conceptualization, formal
analysis, methodology, writing of original draft and writing of review and
editing. Ariel Malka played supporting role in conceptualization, investiga-
tion, methodology, writing of original draft and writing of review and
editing. Arber Tasimi played lead role in resources and supervision and
supporting role in conceptualization, investigation, writing of original draft
and writing of review and editing.
Supporting materials for this article, including data and analytic code, are
openly available at
Correspondence concerning this article should be addressed to Thomas
H. Costello, Department of Psychology, Emory University, 36 Eagle Row,
Atlanta, GA 30322, United States. Email:
Journal of Personality and Social Psychology:
Personality Processes and Individual Differences
© 2022 American Psychological Association
ISSN: 0022-3514
vast RRH literature contains a considerable degree of theoretical and
methodological heterogeneity, especially in how scholars concep-
tualize and operationalize the rightand rigidityas psychological
constructs (e.g., Malka et al., 2017;Zmigrod, 2020), leading
competing camps to chronically talk past one another and leaving
the eld mired in seemingly perpetual controversy.
Consider, for example, that political ideology can be disaggre-
gated into at least two conceptually distinct dimensionssocial and
economic ideologyand that these dimensions may be rooted in
distinct constellations of psychological processes (e.g., Costello &
Lilienfeld, 2021;Duckitt & Sibley, 2009;Federico & Malka, 2018;
Morgan & Wisneski, 2017;Treier & Hillygus, 2009). By the same
token, consider that the umbrella category of rigidityspans dozens
of constructs that are unlikely to reect a single, stable dimension
(Cherry et al., 2021), yet these constructs are used interchangeably
by proponents and critics of the RRH alike. Reecting such perva-
sive denitional wooliness, political conservatism has often been
operationalized in many studies using measures that include
rigidity-related content, and vice versa (Malka et al., 2017). More-
over, the magnitude and direction of relations between the
rightand rigidityseem to vary greatly as a function of context,
methodology, and individual differences (e.g., from norms in
political discourse to measurement modality to peoples degree
of political engagement; Federico, 2022;Johnston et al., 2017).
Given these concerns, scholarship primarily focusing on global
differences in rigiditybetween liberalsand conservativesis
likely to underestimate the complexity of interrelations among
psychological processes and political ideology, thereby hindering
meaningful, risky tests of the RRH (see Meehl, 1978). Accordingly,
for research in this area to advance, political psychologists may do
well to move the discussion away from if conservatives are more
rigid than (and otherwise psychologically distinct from) liberals to
(a) when politics and rigidity-related processes intersect and (b) why
the RHHs explanatory power varies across people and places.
Here, we synthesize and meta-analytically parse these questions.
Rather than focussolely on reporting and interpreting point estimates
of main effects (i.e., overall relations between conservatism variables
and rigidity variables), we focally emphasize estimates of substantive
heterogeneity (i.e., the degree of difference in true effects across
observations) and boundary conditions (i.e., for who, where, and
when the RRH holds true).
The notion that there is a relation between rigidity and conserva-
tism has been with us for many decades (e.g., Adorno et al., 1950;
Freud, 1921;Katz, 1960;Kaufman, 1940;McClosky, 1958). During
this time, social scientists have conducted hundreds of tests bearing
on the RRH, describing leftright differences in domains such as
complexity of policy statements made by U.S. Senators and mem-
bers of the British House of Commons (e.g., Tetlock, 1983;Tetlock
et al., 1984), abstract reasoning abilities (e.g., OConnor, 1952),
tolerance of ambiguity (e.g., Block & Block, 1951), general neu-
rocognitive functioning (e.g., Amodio et al., 2007;Nam et al.,
2021), and working memory processes (e.g., Buechner et al., 2021).
Although theoretical accounts of the RRH vary (e.g., Adorno
et al., 1950;Altemeyer, 1996;Hetherington & Weiler, 2018;
Wilson, 1973; see Tetlock, 1983), a particularly inuential version
of this hypothesis conceives of conservatism as motivated social
cognition (Jost, 2021). First articulated in a seminal meta-analysis
spanning ve decades of literature, this motivated social cognition
account posits that political conservatism is a consequence of basic
cognitive (i.e., pertaining to thinking, reasoning, or remembering)
and motivational (i.e., the impetus that gives purpose or direction to
behavior) processes concerning certainty/rigidity and safety/threat-
(Jost et al., 2003). Under this account, people who have
a motivational need to simplify reality may satisfy this need by
adopting political ideologies that (promise to) foster a sense of order
and predictability. Because conservatism ostensibly offers a sense of
certainty by way of its support for prevailing social norms and
hierarchies, rightists are disproportionately likely to be cognitively,
ideologically, and motivationally rigid.
This version of the RRH has served as the frontline for much
research within political psychology over the last two decades,
stimulating a surge in studies of the psychological correlates (and
theorized causes) of left- versus right-wing ideology (e.g., Dean,
2006;Hibbing et al., 2014;Inbar et al., 2009;Mooney, 2012;Oxley
et al., 2008;Westen, 2007). This renaissance of theory and research
has, in turn, prompted additional meta-analyses of the RRH, which
have generally continued to provide strong evidence of positive
correlations between rigidity and conservatism measures (e.g.,
Houck & Conway, 2019;Jost, 2017;Jost et al., 2003;Van Hiel
et al., 2016). If taken at face value, these meta-analyses seem to
clearly support the conclusion that rightists are more rigid than
But as foreshadowed above, existing evidence provides less
conclusive support for the RRH than may seem at rst blush.
Hidden moderators, recurring methodological problems, and incon-
sistent conceptual foundations permeate the literature and raise
challenges to the validity and generalizability of the RRH. From
our point of view, these wide-ranging concerns and controversies
can ultimately be understood as a function of heterogeneity in
researchersanswers to two key questions: (a) What is the right?
and (b) What is rigidity?
What Is The Right?
Political ideology is typically conceived in terms of a unidimen-
sional left/liberal versus right/conservative political continuum. Gen-
erally speaking, the left pole is thought to reect preferences for
egalitarian social and economic change and cultural progressivism,
and the right pole is thought to reect preferences for maintaining
social and economic hierarchy and traditional authority (e.g., Caprara
& Vecchione, 2018;Johnston & Ollerenshaw, 2020). What this
means is that political preferences characteristically regarded as
liberal involve government economic intervention, redistributive
policy, reduction of inequality, and progressive sexual morality
and cultural positions. By contrast, those characteristics regarded
as conservative involve favoring free-market economics, limited or
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Vis-à-vis safety and threat sensitivity, which we do not focus on in the
present work, it is theorized that conservatism satises existential needs to
preserve safety and security and to reduce danger and threat (Jost, 2017).
However, as we elaborate upon in the Discussion section, we believe that
much research supportive of this view suffers from the same methodological
issues that we describe here (Malka et al., 2017), and that recent ndings
make this clear (e.g., Brandt et al., 2021;Crawford, 2017;Ollerenshaw &
Johnston 2022).
no economic redistribution, tolerance of economic inequality, tradi-
tional sexual morality stances, and traditional cultural preferences.
More than anything, the leftright spectrum simplies reasoning
and communication about political preferences (Downs, 1957).
Indeed, political conict largely occurs along a leftright ideological
divide in many Western nations (e.g., Benoit & Laver, 2006;
Kitschelt et al., 2010;Knight, 1999;McCarty et al., 2016). That
said, there are several drawbacks to relying on the leftright
spectrum in research concerning the psychological causes and
correlates of political ideology (Morgan & Wisneski, 2017). For
one, it is not uncommon to hear someone volunteer that they are
socially conservative and economically liberalor vice versa
(Drutman, 2017). Corroborating this observation, factor analytic
investigations tend to identify distinct social and economic dimen-
sions of political conservatism (vs. liberalism) that seem to be
moored in separate networks of psychological processes (e.g.,
Claessens et al., 2020;Costello & Lilienfeld, 2021;Duckitt &
Sibley, 2009;Federico & Malka, 2018;Feldman & Johnston,
2014;Johnston et al., 2017;Laméris et al., 2018;Pan & Xu,
2018; see Johnston & Ollerenshaw, 2020, for a review). Were
political conservatism a (roughly) coherent psychological entity,
then we might anticipate social and economic conservatism to be
inextricably bound together in most peoples minds. Indeed, one
popular instantiation of the RRH suggests that economic and
social conservatism are psychologically intertwined precisely
because both are rooted in rigidity (Azevedo et al., 2019).
contrast, if the rightis not any one thing, then the RRH (and by
extension all models that seek to understand the psychological
determinants of unidimensional conservatism) may commit a
great error of oversimplication.
Multiitem measures of social and economic ideology are, indeed,
highly correlated (e.g., rs>.50) within contemporary American
samples (e.g., Azevedo et al., 2019), but there are many reasons to
expect that this strong link is a product of circumstance and context,
rather than a fundamental psychological concordance between the
two dimensions. For instance, when one takes a global view by
including representative samples from developing and non-Western
countries, positive correlations between cultural and economic con-
servatism are uncommon (Malka et al., 2019). This dovetails with a
prominent strain of thinking within political science that suggests
most people do not naturally use leftright ideology in a coherent way
(Kalmoe, 2020;Kinder & Kalmoe, 2017). Further, the positive
correlation between social and economic conservatism in American
samples has increased over the last two decades (Kozlowski &
Murphy, 2021), which is consistent with the possibility that this
strong link is a product of particular people, places, and/or times
(Federico & Malka, 2022). For instance, politically engaged
individuals are consistently more inclined to structure their social
and economic attitudes on the right versus left dimension than
politically disengaged individuals (Baldassarri & Goldberg, 2014;
Kozlowski & Murphy, 2021), attesting to the role of top-down
information environment inuences (e.g., cues from elites) on
political attitude structure.
Further complicating the picture, many studies show reliable
correlations between social conservatism and rigidity indicators,
yet relations between economic conservatism and rigidity indicators
tend to be directionally inconsistent (e.g., Azevedo et al., 2019;Carl,
2014;Carney et al., 2008;Cizmar et al., 2014;Clifford et al., 2015;
Costello & Lilienfeld, 2021;Everett, 2013;Feldman, 2013;Hibbing
et al., 2014;Johnson & Tamney, 2001;Kossowska & Van Hiel,
2003;Malka et al., 2014;Sterling et al., 2016;Van Hiel et al., 2004;
Yılmaz et al., 2016). Accumulating data suggest that rigidity-related
constructs are correlated with left-wing economic preferences
among people whose political preferences are not subject to strong
environmental pressures, perhaps because government economic
intervention is likely to provide security and certainty (Czarnek &
Kossowska, 2021;Johnston et al., 2017;Malka et al., 2014;
Ollerenshaw & Johnston, 2022). By contrast, rigidity-related con-
structs are correlated with right-wing economics in the United States
and Britain, perhaps because free-market economics are branded as
conservativein American political discourse. These ndings
further testify to the possibility that social and economic ideology
are not psychologically intertwined (e.g., via the bottom-up inuence
of rigidity) but can be bound together via top-down environmental
inuences (Federico & Malka, 2018;Layman & Carsey, 2002;Noel,
2014;Zaller, 1992).
Altogether, whether and to what extent conservativesare rigid
may depend crucially on how conservatism is dened and oper-
ationalized, where the data are collected, and who populates the
sample. And, indeed, a review of the literature reveals that political
ideology is measured in a wide variety of ways. Whereas some
researchers use assessments of concrete policy preferences (e.g.,
Carmines et al., 2012;Everett, 2013), others use psychologically
expansive measures premised on theoretical models that posit core
orientations underlying ideology (e.g., opposition to vs. acceptance
of change, Right-wing Authoritarianism [RWA]/Social Dominance
Orientation [SDO]; see Duckitt & Sibley, 2009;Thorisdottir et al.,
2007), and others use single-item indicators of partisan or ideologi-
cal identity (e.g., Federico & Goren, 2009). Meanwhile, sampling
practices may be overly narrow. Despite being politically atypical,
American samples are vastly overrepresented in tests of the RRH
(e.g., American samples represent 59% of all observations in the
present review), potentially articially obscuring psychological
differences across social and economic ideology that manifest in
most non-American national contexts (Johnston & Wronski, 2015;
Malka & Soto, 2015;Malka et al., 2014,2017). By the same token,
demographically representative samples, which may contain a larger
proportion of people free from top-down, discursive pressures on
ideological preferences, represent a small fraction of tests of the
RRH (roughly 8%, by our estimate)potentially upwardly biasing
population estimates for the RRH (Mercer et al., 2017;Xie et al.,
2012). Thus, it is important for meta-analytic reviews of the RRH
to distinguish between (a) social and economic political ideology,
(b) types of political ideology measures, and (c) sampling contexts,
and to examine these domains as potential sources of heterogeneity.
Ours is the rst to do so.
What Is Rigidity?
Much like the commonplace practice of collapsing social and
economic ideology into a single category (or not measuring them
separately at all), prior tests of the RRH have tended to subsume a
host of loosely interrelated variables under the broad heading of
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Indeed, hypothesized mechanisms underlying the RRH draw from
conceptual connections between the shared epistemic qualities of social
and economic conservatism (e.g., upholding prevailing norms and hierar-
chies), on the one hand, and rigidity, on the other.
rigidity. Scholars supportive (Hibbing et al., 2014;Jost, 2021) and
critical (Johnston et al., 2017;Malka & Soto, 2015) of the RRH have
followed this convention,
perhaps because little scholarly consen-
sus exists concerning the precise boundaries of rigidity (Furnham &
Marks, 2013;Sternberg & Grigorenko, 1997;Zmigrod et al., 2020).
Indeed, there are few systematic accounts of conceptual distinctions
across variables typically thought to reect rigidity, let alone
empirical evidence to guide the construction of valid and reliable
rigidity dimensions. One recent review (Cherry et al., 2021) of the
cognitive rigidity literature identied 25 competing conceptualiza-
tions assessed across 23 measures. If these constructs are only
loosely coupled, which appears plausible given their denitional
heterogeneity, they are unlikely to share specic psychological
mechanisms linking them to political conservatism.
For this reason, how best to meta-analytically compare (or disag-
gregate) rigidity constructs remains a matter of open debate (see, e.g.,
Cherry et al., 2021, for a review; Kipnis, 1997). Several taxonomies
of distinctions within rigidity constructs, however, have emerged in
recent years (e.g., executive functioning, intolerance of ambiguity,
inexible thinking styles, cognitive complexity; Lauriola et al., 2016;
Newton et al., 2021;Stoycheva et al., 2020;Woznyj et al., 2020),
providing some basis for distinguishing between rigidity variables
in a theoretically informed manner. Based on these provisional
taxonomies of rigidity dimensions, we have identied four do-
mains of rigidity that are differentiable in their relations with one
another and relevant external criteria (see Supplemental Figure 1):
(a) rigid thinking styles, (b) motivational rigidity, (c) cognitive
inexibility, and (d) ideological rigidity (i.e., dogmatism).
These four domains, as we discuss below, have little denitional
overlap, are not strongly correlated, and tend to be studied in
disparate subelds. We suspect that this schema offers an empiri-
cally informed and useful means of resolving the lumper-splitter
problem(i.e., balancing precision and parsimony when placing
individual cases into categories; Simpson, 1945) in the absence of an
empirically derived taxonomy of rigidity.
Rigid Thinking Styles
Theoretical accounts of human decision-making often distinguish
between intuitive (i.e., rapid, unconscious, and automatic) and reec-
tive (i.e., slow, conscious, and deliberative) cognitive processes
(Kahneman, 2011). Dozens of studies have found that individuals
vary in cognitive reectivity, and that these individual differences
have broad patterns of relevance to myriad behaviors and attitudes
(e.g., Toplak et al., 2011;seePennycook et al., 2015). Drawing from
the RRH literature, several authors have suggested that conservatives
may be more intuitive (i.e., less analytic) thinkers than liberals
(Talhelm et al., 2015;cf.Kahan, 2012). Nevertheless, common
operationalizations of cognitive reectivity, such as the cognitive
reection test and the Need for Cognition Scale (Cacioppo & Petty,
1982), are negligibly related to measures of other rigidity constructs
that have been used in tests of the RRH (e.g., need for closure,
intolerance of ambiguity, and dogmatism; Newton et al., 2021). We
therefore treat rigid thinking styles as a distinct rigidity domain.
Motivational Rigidity
As with rigid thinking styles, motivational rigidity is not highly
correlated with other rigidity domains, suggesting that it may bear
unique or divergent associations with political ideology (Lauriola
et al., 2016). Many such motives are subsumed by need for cognitive
closure, a widely known construct that broadly reects ambiguity
aversion and desires for clear answers (Kruglanski & Webster,
1996). Many tests of the RRH have revealed a relation between
need for cognitive closure (and related motivational needs) and
conservatism indicators (see Federico & Goren, 2009). Other con-
structs potentially indicative of need for certainty, such as risk
aversion and cognitive ability, also exhibit modest relations with
elements of conservatism (Kam, 2012;Kemmelmeier, 2008). For
our primary analyses, we presently collapse motivational rigidity
variables, such as need for closure and the motivational elements of
ambiguity intolerance.
Cognitive Inexibility
Cognitive inexibility can be understood as part of a broader suite
of psychological processes involved in executive functioning, which
refers to high-level cognitive control functions that are involved in
complex mental processes, such as planning, focusing attention,
working memory, and multitasking (Diamond, 2013;Miyake &
Friedman, 2012). Specically, cognitive inexibility is thought to
reect an inability to change perspectives, shift approaches ef-
ciently, and take advantage of unexpected opportunities (Cools &
Robbins, 2004). Drawing from the RRH literature, neuropsychologi-
cal, and behavioral measures of cognitive inexibility have been
leveraged to suggest that leftists and rightists may differ in their basic
cognitive architecture (e.g., Buechner et al., 2021;Sidanius, 1978;
Zmigrod, 2020). To our knowledge, no systematic data are publicly
available concerning the convergence between these cognitive inex-
ibility measures and measures of other rigidity constructs (e.g.,
motivations, intuitive thinking, and dogmatism). Moreover, cognitive
inexibility and other rigidity constructs massively diverge in their
relations with external criteria (Lauriola et al., 2016;Stoycheva et al.,
2020). We therefore distinguish cognitive inexibility from other
rigidity domains.
The storied construct of dogmatism has variously been dened
as generalized authoritarianism (Rokeach, 1960) and, later, as
relatively unchangeable, unjustied certainty(Altemeyer,
1996, p. 201). Factor analytic investigations have indicated dog-
matism is relatively unidimensional and manifests positive
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Often, rather than referring to rigidityper se, scholars refer to the
psychological orientations that may underlie conservatism as uncertainty
intolerance and threat sensitivity(e.g., Jost et al., 2003), needs for security
and certainty(Malka et al., 2014), or an open versus. closedpersonality
superfactor (Johnston et al., 2017). Indicators of these orientations have
included measures focused on fear of death, perceptions of various threats,
reversed openness to experience (or facets thereof), conscientiousness (or
facets thereof), and values having to do with obedience, conformity, and
religiosity (which also, tautologically, often appear in measures of conser-
vatism themselves; e.g., Jost et al., 2007;Johnston & Wronski, 2015;
Federico & Malka, 2018). Although these constructs clearly bear theoretical
and empirical relations with rigidity, they are only indirectly relevant to
rigidity. In addition, recent evidence suggests that in certain contexts where
conservatives and liberals are polarized, ones political orientation might
motivate one to adopt or present oneself as having what are thought to be
ideology-consistent levels of these constructs (Bakker et al., 2021;Ludeke
et al., 2016;Margolis, 2018).
correlations with theoretically relevant variables, including belief in
certain knowledge, resistance to belief change, closed-mindedness,
need for cognition, need for structure, and need to evaluate
(Altemeyer, 2002;Crowson, 2009;Crowson et al., 2008). Still,
dogmatism is conceptually and empirically distinct from these and
other rigidity constructs (Duckitt, 2009;Johnson, 2009;seeRönkkö
&Cho,2022). We therefore treat dogmatism as a stand-alone rigidity
domain in the present review.
Circular Measurement: Some Measures of
Conservatism Directly Measure Rigidity
Thus far, we have predominantly focused on conceptual and
taxonomic reasons that the RRHs evidentiary basis may be less
clear-cut than previously thought. Namely, shaky conceptual
foundations and a paucity of consensus concerning the nature
and boundaries of both the rightand rigidityraise the specter
of hidden moderators that are as or more explanatorily relevant
than main effects. Yet, theoretical acuity and methodological
validity are deeply intertwined. Most critical theoretical obstacles
to useful meta-analytic tests of the RRH manifest, in practice, as
methodological choices (e.g., measuring ideology as a single
Perhaps no methodological obstacle in the RRH literature illus-
trates this dynamic better than criterion contamination (Cronbach &
Meehl, 1955;Messick, 1995) in measures of conservatism and
rigidity (Malka et al., 2017). Specically, a large proportion of
studies reviewed in prior meta-analyses have used measures of
conservatismthat rest on the theoretical assumption that conser-
vatism is heavily imbued with rigidity or associated nonpolitical
content. These measureswhich include the Fascism Scale (e.g.,
Adorno et al., 1950), the RWA Scale (e.g., Altemeyer, 1996), and
the WilsonPatterson Conservatism Scale (e.g., Wilson &
Patterson, 1968)were designed to assess rigidity and conserva-
tism simultaneously (e.g., Wilson, 1973). For instance, the Fascism
Scale assesses unquestioned faith in a supernatural power and a
critical view of bad manners, the WilsonPatterson Conservatism
Scale includes nonpolitical items that are intended to assess uncer-
tainty avoidance (e.g., dislike of jazz music), and the RWA Scale
includes content pertaining to religiosity, aggression, and obse-
quious deference to authority (Duckitt et al., 2010). Other con-
servatismmeasures used in RRH research include content
pertaining to parentchild relationships, ethnocentrism, dogma-
tism, basic motivational values reecting self-enhancement and
intolerance of change, religiosity, and political intolerance (see
Malka et al., 2017). These imprecise and criterion-contaminated
historical measurement practices pose an obstacle to meta-analytic
tests of the RRH because, until recently, studies relying on said
measures made up a majority of the RRH literature (Costello,
Clark, et al., 2022).
Just as publication bias (e.g., le drawereffects) and question-
able research practices have been shown to systematically distort
meta-analytic ndings (Rosenthal, 1979;Thornton & Lee, 2000),
the presence of rigidity-related content in political ideology mea-
sures may yield exaggerated meta-analytic results.
Hence, in the
present review, we examine the degree to which biased measures
inate effect sizes and estimate rigidity-conservatism relations in a
way that is less distorted by content overlap.
Beside the Point Estimate: The Central Role
of Heterogeneity
Given the vast range of constructs, measures, and environments
that scholars have used to test the RRH, it is perhaps unsurprising
that point estimates for conservatism-rigidity correlations reported
in peer-reviewed articles range from r=.58 (Durrheim, 1998)to
r=.82 (Pettigrew, 1958). Attempting to interpret an overalleffect
size estimate for the core psychological mechanism(s) ostensibly
underlying such a vast range of effects glosses over the more
difcult and, arguably, more interesting questions of when and
why these effects vary. Addressing these questions will entail
mapping the substantive variation in true effect sizes across the
RRH literature, which is perhaps the chief insight provided by meta-
analysis (Higgins & Thompson, 2002).
Thus, point estimates of main effects are only one piece of the
puzzle in the present meta-analysis. To illustrate the importance of
this distinction (see Wiernik et al., 2017), suppose that we nd that
the relation between conservatismand rigidity(e.g., r=.15) is
half as large as the standard deviation of true effects across all
studies (e.g., SD
=.30). Roughly speaking, this would suggest that
many samples in the literature reect a modest conservatism-rigidity
correlation, yet in a substantial minority of samples the true relation
between conservatism and rigidity is either considerably larger (e.g.,
r>.45) or directionally opposing (e.g., r<.15). By contrast,
suppose that the overall relation (e.g., r=.15) was twice as large as
the standard deviation of true effects (e.g., SD
=.075). This would
suggest that a modest positive correlation characterized rigidity-
conservatism relations, regardless of where, how, and with whom a
given study was conducted. In both cases, however, merely report-
ing the overall point estimate would not enable readers to draw
informed conclusions about the meaning of the RRH literature.
Rather, heterogeneity estimates and point estimates should interde-
pendently inform interpretations of meta-analytic ndings. Accord-
ingly, we adopt such an interdependent approach in the present
review, focally emphasizing estimates of substantive heterogeneity
and boundary conditions alongside main effects.
The Present Review
We meta-analytically examine the full body of currently available
literature (including peer-reviewed journal articles, doctoral disser-
tations, masters theses, books, and unpublished data) with the dual
aims of probing the RRHs basic assumptions and parsing the RRH
literatures considerable heterogeneity. We leverage divergent con-
ceptualizations and measures of political ideology and rigidity to
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Content overlap such as this has also taken the form of inclusion of
political content in measures of rigidity-related constructs (Malka et al.,
2017, pp. 121122). For example, manipulations and measures relevant to
perception of terrorism-related threats are often found to predict conserva-
tism and are consequently taken as support for the RRH (Jost et al., 2007,
Study 3; Tho´risdo´ttir & Jost, 2011, Study 2). Further, many studies rely on
Rokeachs Dogmatism (D) scale as a rigidity indicator, despite the presence
of right-wing political content in this scale (see Conway et al., 2016).
Similarly, the long-standing nding that political conservatism is associated
with prejudice (see Hodson & Dhont, 2015, for a review) appears to dissipate
when groups that are perceived as ideologically dissimilar to political
liberals, such as Christian fundamentalists and wealthy individuals are
included as targets in measures of prejudice (Brandt & Crawford, 2019;
Crawford, 2017).
facilitate these tests, allowing us to clarify the coherence and utility of
approaching political ideology and rigidity as unidimensional con-
structs in the context of the RRH. Further, we examine methodolog-
ical and conceptual obstacles to substantive tests of the RRH, such as
publication bias, hidden moderators (e.g., sample type, nationality,
WEIRDness, rigidity measure type, political ideology measure type)
and criterion contamination in ideology and rigidity measures.
Relative to previous reviews, the current meta-analysis is consider-
ably larger and broader in the number of samples, effect sizes, and
participants. Whatis more, our meta-analysis is the rst review of the
RRH to statistically model dependencies among effect sizes extracted
from the same samples (Van den Noortgate et al., 2015).
Transparency and Openness
Supporting materials for this article, including raw data and
analytic code, are openly accessible at
Literature Search
Studies were obtained using several search strategies (updated a
nal time in January of 2021). First, we conducted targeted searches of
online databases (i.e., ProQuest Dissertations & Theses, PsycINFO,
Google Scholar, and the Emory University Libraries search tool,
discoverE, which comprises 18 relevant databases). The search
terms were developed by the rst author and were based on our
review of the literature.
Searches covered English-language arti-
cles, books, masters theses, and dissertations published from 1950
to 2021. Second, we drew from published and unpublished studies
included in previous meta-analyses of the RRH. Third, we employed
a snowballing procedure that entailed reviewing lists of studies that
have cited widely used measures of political ideology and rigidity.
Finally, we searched publicly and privately available data sets (e.g., to manually calculate effect sizes of interest.
Our initial database search yielded 1,416 studies, and abstracts of
these studies were then screened for initial inclusion. A total of 489
studies were deemed appropriate for full-text review; removing
duplicates reduced this number to 371. The remaining full texts
were read by the rst author. For a study to be included, it needed to
meet all the following criteria: (a) assessment of one or more of the
rigidity constructs of interest; (b) an assessment of political ideology
(e.g., symbolic self-placement, support for conservative/liberal
policies, party identication, support for conservative/liberal values,
vote choice, or some combination thereof); and (c) sufcient data
provided for calculating individual effect sizes. Effect sizes that
were either observed following an experimental manipulation or
reported alongside statistically signicant covariates (e.g., βweights
from multiple regression analyses) were excluded. No studies were
excluded based on participant characteristics (e.g., age, ethnicity).
A total of 140 articles met inclusion criteria and were coded (see
Figure 1). Five open data sets that met inclusion criteria were also
identied and used to calculate effect sizes. A nal round of searching
was conducted in January 2021, which resulted in the addition of
seven studies. After completing our initial literature review, we
expanded our study pool to include any effect sizes from the most
comprehensive previous meta-analytic review of the RRH (i.e., Jost
et al., 2017) that involved political ideology measures including overt
prejudice, authoritarianism, or rigidity content. An additional 102
effect sizes and 6,275 participants were added. Secondary analyses
were conducted to facilitate the comparison of our results before and
after excluding these effects sizes, affording the opportunity to meta-
analytically examine the differences between proxy measures of
conservatism and purermeasures of conservatism.
Twenty-ve percent of studies were randomly selected and
independently reviewed and coded by the second author to assess
reliability of study coding. Interrater reliability coefcients (i.e., κ
for categorical variables and intraclass correlation coefcient for
continuous variables) are provided below. Coding disagreements
were resolved by discussion. An overview of included citations,
study characteristics, and effect sizes is provided in Supplemental
Table S1, and the full meta-analytic data set is provided at https://osf
Data Coding
Domain of Political Ideology
Measures of political ideology were coded as belonging to one of
three categories: general ideology, social ideology, or economic
ideology. General ideology, which comprised the largest proportion
of observations, included generic self-placement items, party aflia-
tion or membership, vote history or preference, and self-report scales
that contain both social and economic content but report only a single
score (e.g., the Political-Economic Conservatism Scale). Social
ideology was measured by self-placement items; self-report measures
that rely heavily on content related to the endorsement of traditional
values, social rules, and norms (vs. progressive values, rules, and
norms); self-report measures that yield a social ideology subscale; and
policy preferences for issues related to social ideology (e.g., abortion
rights or gay marriage). Finally, economic ideology was assessed in
the same manner as social ideology, but with measures and policies
that focus on government involvement in private enterprise, redistri-
bution of wealth, and/or the economic choices available to its citizens.
Interrater agreement was substantial, κ=.90.
Domain of Rigidity
When coding each observation, we used a two-pronged approach.
First, we examined the rigidity constructs individually, coding them
based on study authorsdesignations wherever possible. For
instance, if the authors indicated that they had created a composite
self-report measure of dogmatism, we coded said measure as dog-
matism.When this was not possible, we relied on the fact that many
of the varieties of rigidity used in the current review are tied to
trademarkmeasures that are most frequently used to operationalize
them. For instance, motivations for certainty are typically assessed
with the Need for Closure Scale (Kruglanski et al., 1993)and
cognitive reection is typically assessed with the cognitive reection
test (Frederick, 2005). Hence, between the authorsstated designa-
tions and this heuristic, most studies in our pool could be categorized
straightforwardly. Second, observations were independently coded
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Search terms were entered as variations of the following Boolean phrase:
(political AND (orientation OR ideology OR conservatism OR attitudes))
AND (cognitive reection OR dogmatism OR need for cog*OR need for
closure OR rigidity OR exibility OR inexibility OR executive function*
OR motiv*OR intolerance of ambiguity).
as reecting the broad categories of rigid thinking styles, motiva-
tional rigidity, dogmatic certitude, or cognitive inexibility (i.e.,
using the taxonomic scheme outlined in the Introduction section).
Content Overlap
Judgments concerning whether measures of political ideology are
marked by content overlap were initially made by the rst author
based on a careful reading of each measure (and assessed using a
small online community sample; see online Supplemental Materials).
We then constructed a dummy-coded moderator variable for overlap
versus no overlap. The following measures were categorized as
containing content overlap: the original C-Scale (e.g., Kirton, 1978),
all versions of the F-Scale (e.g., Davids, 1955;Kohn, 1974), all
versions of the RWA Scale (e.g., Crowson et al., 2005), all versions
of the SDO scale (e.g., Leone & Chirumbolo, 2008), all versions of
the System Justication Scale (e.g., Hennes et al., 2012), the
Personal Conservatism Scale (e.g., Olcaysoy & Saribay, 2014),
and all ad hoc measures that borrowed items from the aforemen-
tioned measures.
Sample Characteristics
For each sample, we extracted nationality (κ=.98) and partici-
pant composition (e.g., university students, nonrepresentative
internet-recruited, community, nationally representative, govern-
ment ofcials; κ=.76).
We followed procedures described in the Many Labs 2 project
(i.e., Klein et al., 2018; see also Yilmaz & Alper, 2019) to quantify
sample WEIRDness via the sample country of origin (see https://osf
.io/b7qrt/for/ more detailed information).
Measure of Political Ideology
We coded the political ideology measure used for each observation
as a categorical moderator using both broad and narrow coding
strategies. Individual measures with k>2 were coded as an
individual category. Further, the following specic categories
were used: symbolic self-placement (e.g., on a scale from 1 to 7,
how left-wing vs. right-wing are you?), support for liberal versus
conservative issues/policies (e.g., opposition to abortion or raising
taxes on the wealthy), having voted for a left-wing or right-wing
political party, membership in a left-wing or right-wing political
party, ad hoc measures (i.e., designed for purposes of a single study),
composites (i.e., a combination of multiple measure types), unspeci-
ed self-report (i.e., studies that noted that a self-report measure of
ideology was used but did not name it or provide items), and other
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Figure 1
Flowchart of the Screening Process
Note. The term recordrefers to a discrete source of data (e.g., a study, which may contain many
effect sizes, or a data set from which effect sizes can be calculated).
unspecied (i.e., all other cases where the authors left their measure
of ideology unspecied). Including these categories, a total of 23
categories with k>2 were present.
Self-Report Versus Performance-Based Measures
Effect sizes derived from self-report rigidity measures were coded
as such (i.e., self-report), whereas effect sizes derived from behav-
ioral and/or objectively scored measures were coded as perfor-
mance-based (κ=.89).
Statistical Analyses
All extracted effect sizes were transformed into Fishersz(Cohen
et al., 2014) to account for the slight negative bias in Pearsonsr
(Card, 2012), and weighted according to the inverse of their variance
(i.e., sampling error), such that larger samples contributed more to
the aggregate effect size estimate than smaller ones (Lipsey &
Wilson, 2001). We used the metafor package (Viechtbauer,
2010)inR(Version 4.2.1) to conduct all analyses. The Rcode
used to generate our results is provided on open science framework.
The Three-Level Model
To account for dependencies across effect sizes, and particularly
for correlated sampling errors due to multiple effect sizes drawn
from the same sample, we used a three-level meta-analytic approach
with restricted maximum likelihood estimation. In contrast to the
traditional (two level) random effects model, in which effect sizes
are assumed to vary due to sampling variance and systematic
variance between studies, the three-level model also accounts for
systematic variance across outcomes from the same sample. Using
this approach, we modeled the sampling variance for each effect size
(Level-1), variation across outcomes within each sample (Level-2),
and variation across samples (Level-3). Although such multilevel
models are said to require that residuals at each level are indepen-
dent, Van den Noortgate et al. (2013) demonstrated in simulation
studies that the three-level approach successfully handles depen-
dencies due to correlated sampling errors, resulting in accurate
standard errors and point estimates (see also Van Den Noortgate
& Onghena, 2003;Van den Noortgate et al., 2015). We chose to use
three-level meta-analysis because, unlike most other statistical tech-
niques for handling correlated sampling errors (e.g., multivariate
meta-analysis with robust estimation), the three-level approach does
not require that correlations among reported outcomes be known.
We report several indices of heterogeneity. First, H
(Higgins &
Thompson, 2002), which represents the difference between the ratio
of the observed variance (i.e., CochransQ) and the expected degree
of variance due to sampling error. Higgins and Thompson (2002)
suggest that H
=1 indicates that the population of studies is
homogeneous, whereas H
>1.5 indicates that substantial hetero-
geneity is present. Second, we report I
and I
, which describe
residual variance relative to the total variance (i.e., variance in true
effects plus sampling variance) between-samples and within-
samples, respectively. I
indicates, in other words, the percentage
of total variance not caused by sampling error. Third, we report σ2
and σ2
2, which describe the variance of the effect sizes in our meta-
analytic data set (within- and between-samples, respectively).
Fourth, we report the standard deviation of the true effect sizes,
σ, which is computed as ffiffiffiffiffiffiffiffiffiffiffiffiffiffiffi
p:Given that σis on the same
scale as the meta-analytic effect size, r, it serves as an easily
interpretable metric of substantive heterogeneity (with rand σ
being comparable to a mean and standard deviation). Fifth and
nally, we report 95% prediction intervals for each estimated
effectthe interval within which the effect size of a novel study
would fall if said study was selected randomly from the same
population as the meta-analytic study pool. Correctly interpreting
prediction intervals depends not only on their width, but on the
range of correlations that they span (e.g., a prediction interval with
endpoints of r=.50 and r=.85 would always reect a very large
true effect, whereas an equally wide interval with endpoints of
r=.05 to r=.30 would indicate theoretically meaningful
variability; see Wiernik et al., 2017).
Meta-Analytic Models
It is unclear whether either the different types of rigidity or the
various domains of conservatism should be conceptualized as
comprising two larger constructs. As a means of engaging with
this problem, we used the following nested analytic approach.
First, we estimated an overall model (Glass, 2015), collapsing
across rigidity constructs and types of conservatism to yield an
overall meta-analytic evaluation. Second, we conducted subgroup
analyses for each political ideology and rigidity variable across all
classication schemes. We then estimated meta-regression models
with categorical moderators for these classications (e.g., social vs.
general vs. economic ideology), which we evaluated with omnibus
tests of the null hypothesis that all levels of the moderator are equal
to zero simultaneously. Finally, we estimated a fullmultiple meta-
regression model by simultaneously regressing effect sizes on
categorical moderators for rigidity domain and political ideology
domain, which we then extended to additional moderators of
interest, such as publication status, sample type, author allegiance,
and so on. Continuous moderators were mean centered to facilitate
interpretation. This produced predicted values for each of the four
rigidity domains at the reference level of each moderator, as well as
effect size estimates for each nonreference level of each moderator
(i.e., how much the predicted values for each rigidity domain would
change if the reference level for a given moderator changed). We
employed the Knapp and Hartung (2003) adjustment to standard
Wald-type tests, which allow for better control of Type I error rate
(i.e., tests of sets of model coefcients were Ftests).
We interpreted moderators with signicant omnibus tests based on
(a) ttests of the differences between each level of the moderator and
(b) point estimates and condence intervals of each conservatism-
construct coefcient at a reference level of the moderator in
question. Still, these models, which include only main effects,
carry the assumption that the inuence of multiple factors is
additive (i.e., that differences between levels of each moderator
do not vary across levels of the other moderator[s]).
Publication Bias
To initially investigate reporting and/or publication bias, we created
two contour-enhanced funnel plots visualizing (a) the distribution of
all effect sizes against their precision (1/SE), including the variance
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from each level of the three-level model, with the reference line set at
the estimated overall effect size, and (b) the distribution of internally
standardized residuals (i.e., observed residuals in the full model
divided by their corresponding standard errors) after accounting for
rigidity construct and conservatism type. Next, to further probe, and
potentially correct for, asymmetry in the effect size distribution
while maintaining the three-level model, we entered either the
standard error or variance for each observed effect size into each
model as an additional predictor (i.e., moderator). This approach can
be considered closely equivalent to the precision-effect test and
precision-effect estimate with standard errors method (Lehtonen
et al., 2018). Finally, as an additional and more direct means of
assessing publication bias, we examined the degree to which
published versus unpublished studies inuenced the full model
via xed-effects moderator analyses.
The nal data set comprised 708 observations, 329 samples, and
173 studies (unique N=187,612; individual sample sizes ranged
from n=12 to n=18,817). Figure 2 depicts the number of effect
sizes for each construct, segmented by the frequency of each
political ideology type within each construct (see also the full
data set provided in online Supplemental Materials). Supplemental
Tables S2 and S3 present the number of effect sizes at each level of
each categorical moderator and descriptive statistics for continuous
Unless stated otherwise, all results are reported with
content overlap effect sizes (N=139) removed, but we report
sibling analyses using all effect sizes (i.e., including content over-
lap) in the online Supplemental Materials. Further, because political
orientation is typically assessed using bipolar measures (i.e., with
liberalism on one end and conservatism on the other), observations
are coded such that positive meta-analytic correlations indicate a
positive correlation between conservatism and rigidity.
Model 1: Global Result
Our overall analysis
indicated a small statistical association
between rigidity and political conservatism, r=.133, 95%
CI [.12, 15].
Importantly, a considerable degree of heterogeneity
was present in the model, Q(565) =4,361, p<.001; σ2
1=.005 and
2=.012; H
=6.71; I
=66% and I
=25%. In absolute terms,
this indicates that the standard deviation in true effects from one study
to the next (i.e., σ) is .13, or roughly as large as the overall effect size
estimate. The 95% prediction interval was .12 to .30, which may
explain the elds long-standing difculty arbitrating between pro-
ponents and opponents of the RRH: the empirical distribution of true
effects in the literature extends well beyond zero in the negative
direction at one endpoint yet includes moderate-to-large positive
effects at the other endpoint. Accordingly, moderating variables are
likely to have a strong impact. As indicated by the I
values, the
degree of substantive heterogeneity in Level 2 (i.e., across observa-
tions drawn from the same sample) was roughly 2.5 times greater
than that accounted for by variance in Level 3 (i.e., observations
drawn from different samples). Thus, we can broadly expect mod-
erators that tend to occur within samples (e.g., multiple operatio-
nalizations of ideology and/or rigidity) to be more explanatorily
powerful than that tend to occur across samples (e.g., sample-type,
nationality) in the global model.
Model 2: The Multidimensionality of Political Ideology
We adapted the three-level model by dropping the intercept and
regressing the observed effect sizes on a set of dummy-coded
variables for economic ideology, social ideology, and general
ideology, respectively. An omnibus test for moderation was statis-
tically signicant, F(3, 563) =141.17, p<.001. Residual variance
was modestly reduced but not eliminated, Q
(563) =3,597, p<
.001; σ2
1=.006 and σ2
2=.009; H
=5.35; I
=55% and I
34%, such that σ=.12. Table 1 presents estimated effect sizes,
alongside 95% condence intervals, 95% prediction intervals, ks,
Ns, pvalues, and within-construct heterogeneity statistics.
Correlational point estimates for all three types of