Revisiting the Rigidity-of-the-Right Hypothesis: A Meta-Analytic Review
Thomas H. Costello, Shauna M. Bowes
Emory University, Department of Psychology
Matt W. Baldwin
University of Florida, Department of Psychology
Yeshiva University, Department of Psychology
Emory University, Department of Psychology
This project would not exist without the brilliance and stewardship of Professor Scott Lilienfeld, who
passed away during the drafting process. We dedicate this manuscript to his memory.
We 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.
Supporting materials for this manuscript, including data and analytic code, are openly available at
Correspondence should be addressed to Thomas H. Costello (email@example.com).
Manuscript accepted for publication at the Journal of Personality and Social Psychology.
Not the version of record.
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.
Keywords: political ideology, cognitive rigidity, rigidity-of-the-right, social conservatism,
economic conservatism, heterogeneity.
Perhaps the most influential psychological account of what distinguishes leftists from
rightists is known as the rigidity-of-the-right hypothesis (henceforth, RRH; Tetlock, 1983). Put
plainly, the RRH suggests that conservative political ideology—which reflects preferences for
free-market economics, a limited social safety net, traditional moral values, and conventional
cultural norms—is congenial to people who are cognitively, motivationally, and ideologically
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 model’s validity and usefulness remain a topic of protracted scientific
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 refine the notion that leftists and rightists
fundamentally differ in their psychological profiles. 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, 1984; Zmigrod et al.,
2019; see also Costello et al., 2021), and that recurrent methodological shortcomings have
systematically “stacked the deck” in 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 vast RRH literature contains a considerable degree of
theoretical and methodological heterogeneity, especially in how scholars conceptualize and
operationalize “the right” and “rigidity” as psychological constructs (e.g., Malka et al., 2017;
Zmigrod, 2020), leading competing camps to chronically talk past one another and leaving the
field mired in seemingly perpetual controversy.
Consider, for example, that political ideology can be disaggregated into at least two
conceptually distinct dimensions—social and economic ideology—and that these dimensions
may be rooted in distinct constellations of psychological processes (e.g., Costello & Lilienfeld,
2020; Duckitt & Sibley, 2009; Federico & Malka, 2018; Morgan & Wisneski, 2017; Treier &
Hillygus, 2009). By the same token, consider that the umbrella category of “rigidity” spans
dozens of constructs that are unlikely to reflect a single, stable dimension (Cherry et al., 2021),
yet these constructs are used interchangeably by proponents and critics of the RRH alike.
Reflecting such pervasive definitional wooliness, political conservatism has often been
operationalized in many studies using measures that include rigidity-related content, and vice
versa (Costello et al., 2022; Malka et al., 2017). Moreover, the magnitude and direction of
relations between “the right” and “rigidity” seem to vary greatly as a function of context,
methodology, and individual differences (e.g., from norms in political discourse to measurement
modality to people’s degree of political engagement; Federico, 2022; Johnston et al., 2017).
Given these concerns, scholarship primarily focusing on global differences in “rigidity”
between “liberals” and “conservatives” is 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 (1) when politics and rigidity-related
processes intersect and (2) why the RHH’s explanatory power varies across people and places.
Here we synthesize and meta-analytically parse these questions. Rather than focus solely
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 Rigidity-of-the-Right Hypothesis
The notion that there is a relation between rigidity and conservatism 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 left-right differences in domains such as complexity of policy statements made by
U.S. Senators and members of the British House of Commons (e.g., Tetlock, 1983; Tetlock,
1984), abstract reasoning abilities (e.g., O’Connor, 1952), tolerance of ambiguity (e.g., Block &
Block, 1951), general neurocognitive 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 influential
version of this hypothesis conceives of conservatism as motivated social cognition (Jost, 2021).
First articulated in a seminal meta-analysis spanning five 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- vs. 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 leftists.
But as foreshadowed above, existing evidence provides less conclusive support for the
RRH than may seem at first blush. Hidden moderators, recurring methodological problems, and
inconsistent 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 researchers’ answers
to two key questions: (1) What is the right? and (2) What is rigidity?
Vis-à-vis safety and threat-sensitivity, which we do not focus on in the present work, it is theorized that
conservatism satisfies existential needs to preserve safety and security and to reduce danger and threat (Jost, 2017).
However, as we elaborate upon in the Discussion, 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 findings make this
clear (e.g., Brandt et al., 2021; Crawford, 2017; Johnston & Ollerenshaw, 2022).
What is “The Right”?
Political ideology is typically conceived in terms of a unidimensional left/liberal vs.
right/conservative political continuum. Generally speaking, the left pole is thought to reflect
preferences for egalitarian social and economic change and cultural progressivism, and the right
pole is thought to reflect 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 no economic redistribution, tolerance of
economic inequality, traditional sexual morality stances, and traditional cultural preferences.
More than anything, the left-right spectrum simplifies reasoning and communication
about political preferences (Downs, 1957; Hinich & Munger, 1994). Indeed, political conflict
largely occurs along a left-right ideological divide in many Western nations (e.g., Benoit &
Laver, 2006; Kitschelt et al., 2010; Knight, 1999; McCarty et al., 2006). That said, there are
several drawbacks to relying on the left-right 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
liberal” or vice versa (Drutman, 2017). Corroborating this observation, factor analytic
investigations tend to identify distinct social and economic dimensions of political conservatism
(vs. liberalism) that seem to be moored in separate networks of psychological processes (e.g.,
Claessens et al., 2020; Costello & Lilienfeld, 2020; 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 people’s 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)
. By contrast, if “the right” is 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 oversimplification.
Multi-item 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 conservatism 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 left-right ideology in a coherent way (Kalmoe,
2020; Kalmoe & Kinder, 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 vs. left dimension than politically disengaged individuals (Baldassarri &
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 hierarchies), on the
one hand, and rigidity, on the other.
Goldberg, 2014; Kozlowski & Murphy, 2021), attesting to the role of top-down information
environment influences (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; Clifford et al., 2015;
Kossowska & Van Hiel, 2003; Everett, 2013; Sterling et al., 2016; Carl, 2015; Carney et al.,
2008; Costello & Lilienfeld, 2020; Cizmar et al., 2014; Feldman, 2013; Hibbing et al., 2014;
Johnson & Tamney, 2001; Malka et al., 2014; Van Hiel et al., 2004; Yilmaz 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 constructs are correlated with right-wing
economics in the United States and Britain, perhaps because free market economics are branded
as “conservative” in American political discourse. These findings further testify to the possibility
that social and economic ideology are not psychologically intertwined (e.g., via the bottom-up
influence of rigidity) but can be bound together via top-down environmental influences (Federico
& Malka, 2018; Layman & Carsey, 2002; Noel, 2014; Zaller, 1992).
Altogether, whether and to what extent “conservatives” are rigid may depend crucially on
how conservatism is defined and operationalized, 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/social
dominance orientation; see Duckitt & Sibley, 2009; Thorisdottir et al., 2007), and others use
single-item indicators of partisan or ideological 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 artificially obscuring
psychological differences across social and economic ideology that manifest in most non-
American national contexts (Johnston & Wronski, 2015; Malka et al., 2014; Malka & Soto,
2015; Malka et al., 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, 2012). Thus, it is important for meta-analytic reviews of the RRH to distinguish between (1)
social and economic political ideology, (2) types of political ideology measures, and (3)
sampling contexts, and to examine these domains as potential sources of heterogeneity. Ours is
the first 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 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 consensus
exists concerning the precise boundaries of rigidity (Furnham & Marks, 2013; Sternberg &
Grigorenko, 1997; Zmigrod et al., 2019). Indeed, there are few systematic accounts of conceptual
distinctions across variables typically thought to reflect 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 identified 25 competing conceptualizations assessed
across 23 measures. If these constructs are only loosely coupled, which appears plausible given
their definitional heterogeneity, they are unlikely to share specific psychological mechanisms
linking them to political conservatism.
For this reason, how best to meta-analytically compare (or disaggregate) 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, inflexible thinking styles,
cognitive complexity; Newton et al., 2021; Lauriola et al., 2016; 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
identified four domains of rigidity that are differentiable in their relations with one another and
Often, rather than referring to “rigidity” per 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 vs. closed” personality 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 conservatism
themselves) (e.g., Jost et al., 2007; Johnston and Wronski, 2015; 2018; 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, one’s
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).
relevant external criteria (see Supplemental Figure 1): (1) rigid thinking styles, (2) motivational
rigidity, (3) cognitive inflexibility, and (4) ideological rigidity (i.e., dogmatism).
These four domains, as we discuss below, have little definitional overlap, are not strongly
correlated, and tend to be studied in disparate subfields. We suspect that this schema offers an
empirically 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 reflective (i.e., slow, conscious, and deliberative)
cognitive processes (Kahneman, 2011). Dozens of studies have found that individuals vary in
cognitive reflectivity, and that these individual differences have broad patterns of relevance to
myriad behaviors and attitudes (e.g., Toplak et al., 2011; see Pennycook 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 reflectivity, such as the Cognitive Reflection 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.
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 reflects 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 constructs 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 inflexibility 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 multi-tasking (Diamond, 2013; Miyake & Friedman, 2012). Specifically,
cognitive inflexibility is thought to reflect an inability to change perspectives, shift approaches
efficiently, and take advantage of unexpected opportunities (Cools & Robbins, 2004). Drawing
from the RRH literature, neuropsychological and behavioral measures of cognitive inflexibility
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
inflexibility measures and measures of other rigidity constructs (e.g., motivations, intuitive
thinking, dogmatism). Moreover, cognitive inflexibility and other rigidity constructs massively
diverge in their relations with external criteria (Lauriola et al., 2016; Stoycheva et al., 2020). We
therefore distinguish cognitive inflexibility from other rigidity domains.
Ideological Rigidity (i.e., Dogmatism)
The storied construct of dogmatism has variously been defined as generalized
authoritarianism (Rokeach, 1960) and, later, as “relatively unchangeable, unjustified certainty”
(Altemeyer, 1996, p. 201). Factor analytic investigations have indicated dogmatism is relatively
unidimensional and manifests positive 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; see Rönkkö & Cho, 2022). We therefore treat
dogmatism as a standalone 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
RRH’s 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 right” and “rigidity” raise 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 dimension).
Perhaps no methodological obstacle in the RRH literature illustrates this dynamic better
than criterion contamination (Cronbach & Meehl, 1955; Messick, 1995) in measures of
conservatism and rigidity (Malka et al., 2017). Specifically, a large proportion of studies
reviewed in prior meta-analyses have used measures of “conservatism” that rest on the
theoretical assumption that conservatism is heavily imbued with rigidity or associated non-
political content. These measures—which include the Fascism Scale (e.g., Adorno et al., 1950),
the Right-wing Authoritarianism Scale (e.g., Altemeyer, 1996), and the Wilson-Patterson
Conservatism Scale (e.g., Wilson & Patterson, 1968)—were designed to assess rigidity and
conservatism 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 Wilson-
Patterson Conservatism Scale includes non-political items that are intended to assess uncertainty
avoidance (e.g., dislike of jazz music), and the RWA scale includes content pertaining to
religiosity, aggression, and obsequious deference to authority (Duckitt et al., 2010). Other
“conservatism” measures used in RRH research include content pertaining to parent-child
relationships, ethnocentrism, dogmatism, basic motivational values reflecting 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 et al., 2022).
Just as publication bias (e.g., “file drawer” effects) and questionable research practices
have been shown to systematically distort meta-analytic findings (Thornton & Lee, 2000;
Rosenthal, 1979), the presence of rigidity-related content in political ideology measures may
yield exaggerated meta-analytic results
. Hence, in the present review, we examine the degree to
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. 121-122). For example, manipulations and measures relevant to perception of
terrorism-related threats are often found to predict conservatism and are consequently taken as support for the RRH
(Jost et al., 2007, Study 3; Thorisdottir & Jost, 2011, Study 2). Further, many studies rely on Rokeach’s 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 longstanding finding 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).
which biased measures inflate 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 “overall” effect size estimate for the core
psychological mechanism(s) ostensibly underlying such a vast range of effects glosses over the
more difficult 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 find that the relation between “conservatism” and “rigidity” (e.g., r = .15) is half as large as
the standard deviation of true effects across all studies (e.g., SDr = .30). Roughly speaking, this
would suggest that many samples in the literature reflect 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., SDr = .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 reporting 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 interdependently inform
interpretations of meta-analytic findings. Accordingly, 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 dissertations, Master’s theses, books, and unpublished
data) with the dual aims of probing the RRH’s basic assumptions and parsing the RRH
literature’s considerable heterogeneity. We leverage divergent conceptualizations and measures
of political ideology and rigidity to facilitate these tests, allowing us to clarify the coherence and
utility of approaching political ideology and rigidity as unidimensional constructs in the context
of the RRH. Further, we examine methodological 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
considerably larger and broader in the number of samples, effect sizes, and participants. What is
more, our meta-analysis is the first 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 manuscript, including raw data and analytic code, are
openly accessible at [link available upon publication].
Studies were obtained using several search strategies (updated a final 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 first author and
were based on our review of the literature
. Searches covered English-language articles, books,
Master’s 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
datasets (e.g., YourMorals.org) 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 first 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
identification, support for conservative/liberal values, vote choice, or some combination thereof);
and (c) sufficient data provided for calculating individual effect sizes. Effect sizes that were
either observed following an experimental manipulation or reported alongside statistically
Search terms were entered as variations of the following Boolean phrase: “(political AND (orientation OR
ideology OR conservatism OR attitudes)) AND (cognitive reflection OR dogmatism OR need for cog* OR need for
closure OR rigidity OR flexibility OR inflexibility OR executive function* OR motiv* OR intolerance of
significant covariates (e.g., beta weights 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. Five open datasets that met
inclusion criteria were also identified and used to calculate effect sizes. A final round of
searching was conducted in January 2021, which resulted in the addition of 7 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 “purer” measures of conservatism.
Twenty-five percent of studies were randomly selected and independently reviewed and
coded by the second author to assess reliability of study coding. Interrater reliability coefficients
(i.e., κ for categorical variables and ICC 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 Supplementary Table 1 and the full meta-analytic
dataset is provided at [link available upon publication].
Figure 1. Flowchart of the screening process. The term “record” refers to a discrete source of
data (e.g., a study, which may contain many effect sizes, or a dataset from which effect sizes can
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 affiliation 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, redistribution of wealth, and/or the economic choices available to its citizens. Inter-
rater 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 authors’
designations wherever possible. For instance, if the authors indicated that they had created a
composite self-report measure of dogmatism, we coded said measure as “dogmatism.” 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 “trademark” measures 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 reflection is typically assessed with the Cognitive
Reflection Test (Frederick, 2005). Hence, between the authors’ stated designations and this
heuristic, most studies in our pool could be categorized straightforwardly. Second, observations
were independently coded as reflecting the broad categories of rigid thinking styles, motivational
rigidity, dogmatic certitude, or cognitive inflexibility (i.e., using the taxonomic scheme outlined
in the Introduction).
Content overlap. Judgments concerning whether measures of political ideology are
marked by content overlap were initially made by the first 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 vs. 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., 2006), all versions of the SDO scale (e.g., Leone &
Chirumbolo, 2008), all versions of the System Justification 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 aforementioned measures.
Sample characteristics. For each sample, we extracted nationality (κ = .98) and
participant composition (e.g., university students, non-representative internet-recruited,
community, nationally representative, government officials; κ = .76).
WEIRDness. 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 specific
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 vs. 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),
unspecified 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 unspecified (i.e., all other cases where the
authors left their measure of ideology unspecified). Including these categories, a total of 23
categories with k > 2 were present.
Self-report vs. performance-based measures. Effect sizes derived from self-report
rigidity measures were coded as such (i.e., self-report), whereas effect sizes derived from
behavioral and/or objectively scored measures were coded as performance-based (κ = .89).
All extracted effect sizes were transformed into Fisher’s z (Cohen et al., 2014) to account
for the slight negative bias in Pearson’s r (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) in R (version 4.2.1; R Core Team, 2022) to conduct all analyses. The R code
used to generate our results is provided on OSF.
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 one), variation across outcomes
within each sample (level two), and variation across samples (level three). Although such
multilevel models are said to require that residuals at each level are independent, Van den
Noortgate and colleagues (2013) demonstrated in simulation studies that the three-level approach
successfully handles dependencies due to correlated sampling errors, resulting in accurate
standard errors and point estimates (see also Van den Noortgate et al., 2003, 2015). We chose to
use three-level meta-analysis because, unlike most other statistical techniques 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.
Heterogeneity. We report several indices of heterogeneity. First, H2 (Higgins &
Thompson, 2002), which represents the difference between the ratio of the observed variance
(i.e., Cochran’s Q) and the expected degree of variance due to sampling error. Higgins and
Thompson (2002) suggest that H2 = 1 indicates that the population of studies is homogeneous,
whereas H2 > 1.5 indicates that substantial heterogeneity is present. Second, we report I2(2) and
I2(3), which describe residual variance relative to the total variance (i.e., variance in true effects
plus sampling variance) between-samples and within-samples, respectively. I2 indicates, in other
words, the percentage of total variance not caused by sampling error. Third, we report σ12 and
σ22, which describe the variance of the effect sizes in our meta-analytic dataset (within- and
between-samples, respectively). Fourth, we report the standard deviation of the true effect sizes,
σ, which is computed as √𝜎1
2. Given that σ is on the same scale as the meta-analytic effect
size, r, it serves as an easily interpretable metric of substantive heterogeneity (with r and σ being
comparable to a mean and standard deviation). Fifth and finally, we report 95% prediction
intervals for each estimated effect—the 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 reflect 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.,
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 classification
schemes. We then estimated meta-regression models with categorical moderators for these
classifications (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 “full” multiple 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 non-reference 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 allows for better control of Type I error rate (i.e.,
tests of sets of model coefficients were F-tests).
We interpreted moderators with significant omnibus tests based on (a) t-tests of the
differences between each level of the moderator and (b) point estimates and confidence intervals
of each conservatism-construct coefficient at a reference level of the moderator in question. Still,
these models, which include only main effects, carry the assumption that the influence 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 (1) the distribution of all effect sizes against their
precision (1/SE), including the variance from each level of the three-level model, with the
reference line set at the estimated overall effect size, and (2) 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 PET-PEESE method (Lehtonen et al., 2018). Finally, as an additional
and more direct means of assessing publication bias, we examined the degree to which published
vs. unpublished studies influenced the full model via fixed-effects moderator analyses.
The final dataset 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 supplementary materials).
Tables S2 and S3 present the number of effect sizes at each level of each categorical moderator
and descriptive statistics for continuous moderators
. Unless stated otherwise, all results are
To account for the possibility of outlying observations distorting our conclusions, we removed observations with
standardized residuals that deviated from the expected asymptotic distribution. This procedure was done iteratively
at both the 95% and 99% confidence levels (visualized with the white and grey areas, respectively, of Supplemental
reported with content overlap effect sizes (N = 139) removed, but we report sibling analyses
using all effect sizes (i.e., including content overlap) in the online supplementary 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.
Figure 2. Number of effect sizes for each rigidity domain and political ideology dimension.
Figure 2). Forty-four observations (7.2%) were removed for p < .05 and 18 observations (2.9%) were removed at p
< .01. Together, the three pools of studies (i.e., raw, trimmed at p <.05, and trimmed at p < .01) allowed for
sensitivity analyses, although the raw pool of studies remained our primary object of analysis.
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) = 4361, p < .001; 12 = .005 and 22 = .012; H2 =
6.71; I2(2) = 66% and I2(3) = 25%. In absolute terms, this indicates that the standard deviation in
true effects from one study to the next (i.e., ) is .13, or roughly as large as the overall effect size
estimate. The 95% prediction interval was -.12 to .30, which may explain the field’s
longstanding difficulty arbitrating between proponents 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 I2 values, the degree
of substantive heterogeneity in level 2 (i.e., across observations 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 moderators that tend to occur within
samples (e.g., multiple operationalizations 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
A three-level model (i.e., with random effects at the sample level) was better fitting than the traditional, two-level
model (ΔBIC = 35.25). We proceeded to compute a four-level model (i.e., random effects for each study, each
sample within each study, and each effect size), which incremented the three-level model in terms of fit (ΔBIC =
103.90). Nevertheless, the third level of this four-level model did not account for a significant degree of residual
heterogeneity, so we next compared the four-level model with a three-level model with random effects for each
study and each effect size within each study (i.e., we removed the sample level), which modestly incremented the fit
of the four-level model (ΔBIC = 2.00). Hence, we proceeded with this final three-level model.
Results were reduced only slightly (differences in r < .01) when outliers were removed at either the 99th and 95th
percentile; subsequent analyses were based on the full dataset.
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 statistically significant, F (3,
563) = 141.17, p < .001. Residual variance was modestly reduced but not eliminated (QE  =
3597, p < .001; 12 = .006 and 22 = .009; H2 = 5.35; I2(2) = 55% and I2(3) = 34%), such that =
.12. Table 4 presents estimated effect sizes, alongside 95% confidence intervals, 95% prediction
intervals, ks, Ns, p-values, and within-construct heterogeneity statistics.
Correlational point estimates for all three types of ideology significantly and positively
deviated from both zero and one another
. More specifically, economic conservatism was less
strongly related to rigidity than general conservatism (t = 5.43, p < .001), which manifested a
small-to-moderate positive relation with rigidity, and social conservatism (t = 9.37, p <.001),
which manifested a moderate positive relation with rigidity; general conservatism was less
strongly related to rigidity than was social conservatism (t = 4.61, p <.001).
Results were effectively unchanged after removing outliers (change in β < .02 for all three outcomes).
Table 4. Meta-analytic Results for Rigidity Domain and Ideology Domain
Rigid Thinking Style
Note. k = observations, n = unique participants. = standard deviation in true effects between observations in
a subgroup analysis, β = meta-regression coefficient in a model with the categorical moderator of either
ideology domain or rigidity domain, 95% PI = prediction interval (range within which the true effect size of a
new study would fall if selected at random from the meta-analytic population), 95% CI = confidence interval.
For economic ideology, was twice as large as β, with a prediction interval reflecting, on
one pole, a moderately-sized negative effect and, on the other pole, a moderate-to-large positive
effect. For general ideology, was slightly smaller than β, reflecting a prediction interval with a
small-to-moderate negative endpoint and a large positive endpoint. Finally, for social ideology,
was much smaller than β; but, given the large correlational point estimate, the absolute degree of
heterogeneity was roughly similar to that for economic and general ideology. Accordingly, the
prediction interval endpoints for social ideology ranged from small, in the negative direction, to
exceptionally large in the positive direction. For both social and economic ideology, most of this
residual variance was explained by differences within rather than across studies, whereas the
opposite was the case for general ideology—perhaps speaking to the greater specificity of the
former two ideology-types (i.e., measures of general ideology are more heterogeneous than
measures of economic or social ideology).
Model 3: Rigidity Domains
We next sought to clarify the relations between individual rigidity domains and political
ideology, adapting the three-level model by dropping the intercept and regressing the observed
effect sizes on a set of nominal variables for each of the four rigidity domains. An omnibus test
suggested the presence of moderation, F(4, 561) = 128.83, p < .001. Relative to the overall
model (Model 1), the residual variance was reduced somewhat but not eliminated (QE  =
3246, p < .001; H2 = 4.75; 12 = .002 and 22 = .011; I2(2) = 74% and I2(3) = 14%), with = .11
and roughly five times more substantive heterogeneity being attributable to within-sample
differences than to between-sample differences.
All rigidity constructs were statistically significantly related to political conservatism (see
Table 4), yet main effect sizes were uniformly and, in some cases, substantially smaller than
previously reported estimates (e.g., the most recent prior meta-analytic estimate for cognitive
inflexibility was r = .38, see Jost, 2017; our estimate was β = .07). Cognitive inflexibility and
rigid thinking did not significantly differ from one another (t = 0.17, p = .865), demonstrating
small effects (i.e., βs < .07); motivational rigidity manifested a small-to-modest positive
association with political conservatism (β = .15); and dogmatism manifested a moderately-sized
positive association with conservatism (β = .22). Motivational rigidity manifested a significantly
larger effect than both cognitive inflexibility (t = 3.63, p < .001) and rigid thinking (t = 5.74, p <
.001); dogmatism manifested a larger relation than all other domains (ts from 4.11 to 8.47, ps <
Nevertheless, these main effects were dwarfed by the degree of substantive heterogeneity
within each rigidity domain. All prediction intervals crossed zero and s ranged from .08
(thinking style) to .15 (dogmatism). Prediction interval endpoints at the negative pole ranged
from moderately-sized (cognitive inflexibility) to small-to-moderate (motivations). Positive
endpoints ranged from moderately-sized (thinking style) to exceptionally large (dogmatism). For
motivational rigidity and thinking styles, much of this substantive heterogeneity was attributable
to differences within, rather than across, samples, while the heterogeneity was roughly evenly
distributed between these two levels of analysis for dogmatism and cognitive inflexibility.
The Full Model
We next regressed all non-overlap effect sizes on 12 dummy-coded moderator variables,
one for each potential combination of ideology-type and rigidity domain (e.g., dogmatism by
economic ideology). The test of moderation was statistically significant, F (12, 544) = 56.20, p <
.001. Residual heterogeneity was reduced further but remained present and substantial, QE (554)
= 2470, p < .001; H2 = 3.36; 12 = .003 and 22 = .008; I2(2) = 62% and I2(3) = 24%, such that =
.10. Most of the substantive heterogeneity was found within, rather than across, samples. Results
are presented in Figure 3.
All rigidity variables, except dogmatism, manifested correlations with economic ideology
that were not significantly different from zero (using an alpha level of .01), with s (ranging
from .06 to .16) around three times as large as the β (ranging from .00 to .04), such that
prediction interval widths (i.e., the range of the two poles) ranged from .24-units to .68-units. In
contrast, dogmatism demonstrated a statistically significant positive correlation with economic
conservatism with a roughly 2/3 as large as its β. Meta-analytic estimates for relations between
rigidity domains and social conservatism were considerably larger than those for economic
conservatism (βs ranged from .11 to .32; s ranged from .03 to .12). A pronounced degree of
heterogeneity was present for motivational rigidity and dogmatism’s relations with social
ideology, with prediction interval widths of .56- and .53-units, respectively; far less
heterogeneity was present for cognitive inflexibility and thinking style, which exhibited
narrower, largely positive, prediction intervals. Effect sizes for general ideology typically fell
between those for economic and those for social (βs from .06 to .22; s from .08 to .16;
prediction interval widths from .19-units to .67-units), with the exception of cognitive
inflexibility, which manifested an equivalently sized effect for general and social conservatism.
These results demonstrate that distinguishing between domains of “rigidity” and “the
right” offers clear utility in clarifying when and why the intersections between left-right politics
and rigidity-related processes vary. Namely, doing so explains 20% of the substantive
heterogeneity present in the dataset and illustrates clear differences in the magnitude and
distribution of effects across domains of rigidity and political ideology. Nevertheless, a stark
Figure 3. Results for the full meta-analytic model.
degree of heterogeneity remains. For example, 10 of 12 prediction intervals crossed zero even as
7 of these 12 prediction intervals contained r = .29 (i.e., the 75th percentile of field-wide
correlational effect sizes magnitudes per Gignac and Szodorai ). This indicates that most
combinations of political ideology domain and rigidity domain yield true effects that, depending
on yet-unknown key moderators, may be negative or positive—with effect size magnitudes
ranging from negligible to incontrovertibly large. A systematic analysis of potential moderators
may clarify some of this residual variance.
Nations/regions with k > 2 were Brazil, Canada, Flanders, Germany, Hong Kong,
Hungary, Italy, the Netherlands, Poland, South Africa, Sweden, Turkey, the United Kingdom,
and the United States. We collapsed countries with k < 2 into European, South/Central
American, Asian, and Oceanian categories. Results are presented in Table S7 and Figure 4. A
significant moderation effect was present for nationality in the overall model, F (19, 522) =
18.99, p < .001. After controlling for rigidity and ideology domain
, F (19, 511) = 1.72, p = .03.
Heterogeneity was reduced, but remained high, H2 = 2.93; 12 = .008 and 22 = .003; = .10; I2(2)
= 64% and I2(3) = 21%.
Given that the majority of effect sizes were observed in the United States, we also
compared US and non-US samples, which revealed a significant difference, such that F(2, 540) =
149.23, p < .001, where β(USA) = .15, 95% CI (.13, .17) and β(non-USA) = .09, 95% CI (.07,
.12). As visualized in Figure 5, this difference was driven by variation across economic ideology,
such that allowing the binary USA vs. non-USA factor to interact with political ideology domain
Although the p-value exceeds our alpha level of .01, the results of this analysis are of limited interpretability given
that our dataset only contains one nation with all rigidity and ideology variables: the United States.
revealed a significant interaction effect, F(2, 535) = 5.48, p = .004. Specifically, effects were
relatively consistent across US and non-US samples for social ideology (β[USA] = .21, 95% CI
[.15, .26] vs. β[non-USA] = .22, 95% CI [.18, .25]), F = .070, p = .792; only modestly, albeit
significantly, different for general ideology (β[USA] = .15, 95% CI [.13, .18] vs. β[non-USA] =
.11, 95% CI [.08, .14]), F = 5.64, p = .018; and substantially and significantly different for
economic ideology (β[USA] = .10, 95% CI [.06, .13] vs. β[non-USA] = -.03, 95% CI [-.07,
.02]), F = 16.34, p < .001. Controlling for rigidity domain (and its interaction with US vs. non-
US) did not reduce the strength or alter the significance of this interaction effect (ps < .005).
The type of sample from which each observation was collected accounted for a
significant degree of residual heterogeneity when entered into the overall model, F (7, 522) =
66.09, p < .001 (see Figure 4). The smallest effect size was for samples matched to the
demographic characteristics of the national population (β = .036, 95% CI [-.01, .07]), and the
largest effect size was for government officials (β = .240, 95% CI [.09, .39]). Controlling for
ideology and rigidity (i.e., the full model; see Table S8) revealed similar results, F (7, 517) =
6.32, p < .001, with residual variance such that QE (517) = 2116, p < .001; H2 = 3.00; 12 = .008
and 22 = .001; = .10; I2(2) = 13% and I2(3) = 71%. Relative to nationally representative samples
(k = 45), which are considered least likely to be at risk for bias (Higgins & Green, 2011), 7 of 8
sample-types exhibited significantly larger effects. Namely, results relative to nationally
representative samples were larger for students (β increased by .06, 95% CI [+.02, +.10], k =
266), non-representative internet-recruited samples (β increased by .09, 95% CI [+.05, +.13], k =
135), yourmorals.org (β increased by .06, 95% CI [+.00, +.11], k = 17), community samples (β
increased by .14, 95% CI [+.10, +.19], k = 86), and government officials (β increased by .14,
95% CI [.01, .28], k = 5).
Self-report vs. Performance-based Rigidity Measures
Performance-based outcome measures yielded significantly smaller estimated effects than
did self-report outcome measures in the overall model, F(2, 661) = 186.65, p < .001, such that
performance-based measures of rigidity manifested a trivial statistical association with
conservatism (β = .065, 95% CI [.04, .09], k = 493) but self-reports manifested a small statistical
association (β = .159, 95% CI [.14, .18], k = 170). Controlling for political ideology domain did
not reduce the magnitude or alter the significance of this effect, F(2, 560) = 30.41, p < .001.
As shown in Tables S2 and S9, nations categorized as Western (β = .136, 95% CI [.12,
.15]) demonstrated significantly larger conservatism-rigidity correlations than non-Western
nations (β = .079, 95% CI [.02, .14]), F(2, 536) = 143.00, p < .001; similarly, nations categorized
as Rich (β = .140, 95% CI [.13, .16]) demonstrated significantly larger correlations than those
categorized as non-Rich, (β = .067, 95% CI [.02, .12]), such that F(2, 536) = 149.18, p < .001.
Nevertheless, controlling for ideology and rigidity domain reduced these moderation effects to
non-significance. Further, when standardized scores for Industrialization, Education, and degree
of Democracy were individually entered as continuous moderators of the relation between
ideology and rigidity, Education accounted for a significant degree of residual heterogeneity
(intercept = .133, β = .022, 95% CI [.01, .04], p = .003), whereas Industrialization and
Democracy did not. Once again, however, after controlling for ideology and rigidity type,
Education did not account for a significant degree of residual heterogeneity (see Supplemental
Table 4 for details).
Figure 4. Meta-analytic results by country and sample-type.
Figure 5. Social and economic ideology’s correlation with rigidity in the USA vs. other
Content Overlap and Political Measures
Introducing political measures with rigidity-related content (i.e., “content overlap”) into
the meta-analytic dataset revealed significant variation in conservatism-rigidity relations across
political ideology measures with- and without criterion contamination, F(2, 668) = 277.72, p <
.001, such that non-overlap political measures manifested only a small association with rigidity,
β = .136, 95% CI (.12, 15), whereas overlap measures manifested a large statistical association
with rigidity, β = .375, 95% CI (.34, .41). Controlling for rigidity domain
diminished the effect (F[1, 663] = 125.76, p < .001)—content overlap measures yielded larger
effect sizes such that the difference in β = .217, 95% CI (.18, .26). A large degree of
heterogeneity remained in this expanded dataset, QE (663) = 5907, p < .001, H2 = 7.84; 12 = .016
and 22 = .005; = .14; I2(2) = 22% and I2(3) = 71%.
Further, we found significant differences among the non-content-overlap political
ideology measures, F (16, 530) = 23.57, p < .001 (see Figure 6 for point estimates of all political
ideology measures and Table S6), but this finding did not hold true after controlling for rigidity
and ideology domain, F (16, 519) = 1.93, p = .016, such that QE (519) = 2019, p < .001; H2 =
2.86; 12 = .003 and 22 = .007; = .10; I2(2) = 63% and I2(3) = 22%. Moreover, little easily
interpretable heterogeneity was evident across measures. Relative to symbolic ideology, only 3
of the 16 measures (with k > 2) yielded significantly different point estimates, one of which was
a measure of social ideology, specifically, whereas the other was a catch-all category for self-
report measures that were not specified in the study text.
We did not control for political ideology domain as content overlap measures typically could not be classified as
reflecting economic, general, or social conservatism.
We first examined the distribution of study outcomes via two contour-enhanced funnel
plots (see Supplemental Figure 2). These analyses were conducted with content overlap effect
sizes removed from the study pool, which may otherwise give the false appearance of
publication bias. In the first plot, many effect sizes were outside of the anticipated range given
their SEs, which is to be expected in the presence of considerable heterogeneity. Still, there was
no clear asymmetry in the distribution of these outliers. When considering the second plot, in
which a greater degree of substantive heterogeneity is accounted for, far fewer outliers were
present and those outliers that remained were relatively symmetrically distributed. As such,
neither plot provided clear evidence of publication bias. Nevertheless, a power analysis indicated
that only 34.5% of studies were sufficiently powered to detect an effect size of ρ = .10, while a
true effect of ρ = .18 would be necessary to achieve Cohen’s (1965) widely accepted power
benchmark of 80% (see Supplemental Figure 3).
PET analysis indicated that there was no statistically significant association between
effect sizes and their standard errors for any of the four primary models (i.e., no moderators,
political ideology domain moderators, rigidity domain moderators, and political ideology +
rigidity domain moderators). Still, a significant moderation effect was present for publication-
type (F[2, 563] = 161.43, p < .001), such that relative to effect sizes drawn from initial peer-
reviewed journal articles (β = .14, 95% CI [.13, .16], k = 459), all other effect sizes were smaller
(β = .11, 95% CI [.09, .14], k = 246). This result was reduced to non-significance after
controlling for rigidity and political ideology domain, F (1, 584) = 4.66, p = .031, such that non-
peer-reviewed studies contained effects smaller in magnitude than those from peer reviewed
studies, with the reduction in β = -.03, 95% CI (-.05, -.00).
Figure 6. Differences across measures of political ideology with- and without rigidity content overlap.
The rigidity-of-the-right hypothesis, which posits that politically conservative beliefs
appeal to people who are cognitively, motivationally, and ideologically rigid, has been subjected
to decades of debate. The present meta-analytic review, which spanned 313 independent
samples, 704 effect sizes, 35 nations, and more than 180,000 unique participants, (1) provides
precise estimates of the magnitude and direction of the relation between conservatism and
rigidity, (2) catalogues the extent to which true effect sizes in the literature are distributed around
these meta-analytic estimates, and (3) elucidates moderator variables that account for these
differences across studies.
The current review offers several central concrete takeaways, but the foremost is this: the
variation in true effects (heterogeneity) among the population of studies in the RRH literature is
both objectively large and theoretically consequential (Linden & Honekopp, 2021). Although the
overall correlation between conservatism and rigidity was r = .13, a random study drawn from
the RRH literature is about equally likely to yield a small negative effect (r ~ -.10) as it is a large
positive effect (r ~ .30). This finding seems to partially explain the RRH’s controversial status
among social scientists. We also think it raises two key, interlinked questions: when and why do
relations between rigidity and conservatism vary?
The “When”: Main Effects, Heterogeneity, and Boundary Conditions
Estimated population correlations for relations between economic conservatism and the
rigidity variables (apart from dogmatism) tended not to statistically differ from zero, whereas
estimated population correlations between social conservatism and the four rigidity variables
were larger and uniformly statistically significant. Further, rigid thinking styles and basic
cognitive mechanisms and processes manifested modest-to-small meta-analytic correlations with
both general and social conservatism. Population estimates were larger for motivations to avoid
complexity and ambiguity and largest for ideological rigidity (dogmatism).
Accordingly, titrating the conceptual and methodological precision of our meta-analytic
models by distinguishing between political ideology in the social/cultural vs. economic domains,
on the one hand, and between constructs reflecting distinct classes of rigidity, on the other,
reduced total heterogeneity by 20%. Yet much theoretically provocative heterogeneity
remained—made evident, most plainly, by 95% prediction intervals that crossed zero for 10 of
the 12 combinations of rigidity-type and conservatism-type.
By incorporating moderating variables such as nationality, culture, sampling context, and
measurement approach into our meta-analytic models, we successfully sourced some of this
residual heterogeneity. For example, positive relations between rigidity and economic
conservatism did not generalize beyond the U.S., whereas social conservatism was significantly
positively related to rigidity across national contexts. Relatedly, demographically representative
samples yielded negligible effects, whereas community samples and samples of government
officials yielded large effects. When it came to measurement, performance-based measures of
rigidity (e.g., cognitive tests) manifested a small statistical association with conservatism,
whereas self-reports manifested a larger statistical association. By contrast, most political
ideology measures did not differ significantly from one another, with the major exception of
ideology measures that reflect rigidity or rigidity-adjacent constructs, which yielded considerably
larger effects. See “The ‘Why?’: Theoretical Implications for the Psychological Underpinnings
of Ideology” below for a discussion of these results.
Answering the question of “when” requires us to situate main effects (population
estimates) alongside the degree of variance in the true effects underlying them and moderators
that in part explain said variance (Schmidt & Hunter, 2014). Given that the most generative and
stark differences in the present meta-analysis were identified across social and economic
ideology—and that many canonical findings in the ideological asymmetries literature are based
on global assessments of political ideology (Jost, 2021)—we now provide such an interwoven
account of the population correlation estimates, heterogeneity, and moderators for social vs.
economic ideology. Notably, this account also engages with the implications of differences
across rigidity variables’ relations with social vs. economic ideology.
Putting It All Together: Social vs. Economic Ideology
Let us first consider social conservatism (vs. liberalism), which manifested meta-analytic
population correlations with rigidity-related constructs that ranged from r = .11 to r = .32
(overall r = .22). Correlations of this magnitude have traditionally been characterized as small-
to-moderate in terms of their theoretical implications (Cohen, 1992; cf. Gotz et al., 2022), yet
they are typical-to-large for individual differences research (i.e., falling between the 25th and 81st
percentiles of all such differential psychology sizes; Gignac & Szodorai, 2016). Given that many
scholars have deemed effects of these magnitudes to possess theoretical and practical importance
for other notable predictors of social conservatism (e.g., low educational attainment; Lipset,
1959; Schoon et al., 2010), it seems reasonable, at first blush, to conclude that rigidity is
meaningfully related to social conservatism. Moreover, even certain “small” effects can have
profound real-world implications (Abelson, 1985; Funder & Ozer, 2019) and some authors posit
that, like genetics, psychology comprises networks of complex phenomena that are an outcome
of the additive influence of small effects, which may be meaningful in aggregate and/or
longitudinally (Gotz et al., 2022; Primbs et al., 2022; see Supplemental File 3 for an in-depth
discussion of our effect size magnitudes).
Still, the heterogeneity accompanying social conservatism’s population estimate was
sizable. For instance, the range of true effects for motivational rigidity veered into the negative
domain (i.e., including negative point estimate with a magnitude in the 12th percentile of all in
differential psychology; Gignac & Szodorai, 2016), while its larger (positive) effect sizes
extended to the 98th percentile of effect size magnitudes. Although social conservatism’s effects
varied across sampling contexts and measurement modalities (as described above), these
moderators were not powerful enough to account for such a large degree of residual
heterogeneity. All told, in any given new study of the relation between conservatism and rigidity,
moderately sized positive correlations between social conservatism and rigidity can be expected,
both large correlations and null correlations are less common but not entirely atypical, and both
small negative correlations and exceptionally large positive correlations will be rare. Taken in
concert with our finding that relations between rigidity and social conservatism are robust across
nations—which was not the case for economic conservatism—our view is that the present meta-
analysis corroborates a “rigidity-of-the-social-right” hypothesis. Nevertheless, further research is
needed to recognize the precise circumstances and variables that amplify (vs. nullify) these
effects to such a considerable degree (Cumming, 2014).
When considering economic conservatism, a markedly different story emerges.
Population estimates for economic conservatism and rigidity in motivations, cognitive abilities,
and thinking styles were consistently small (rs from .00 to .04)—and would arguably contravene
the RRH if considered in isolation (Ferguson & Heene, 2021; Lykken, 1991; Meehl, 1978). That
said, the population estimate for ideological rigidity, or dogmatism, was far larger (r = .16). True
effects were widely distributed around zero, amounting to a similar degree of heterogeneity as
was present for social ideology (e.g., most starkly, the 95% prediction interval for basic cognitive
processes included both -.30 and +.30, or the 75th percentile of effect size magnitudes per Gignac
and Szodorai ). Accordingly, when it comes to economic conservatism, the RRH holds
under some circumstances, is rejected under others, and is directionally incorrect under others
still. Moderator analyses identified several such boundary conditions. Positive correlations for
economic conservatism were overrepresented in American samples, which yielded an estimated
effect size of r = .10, whereas non-American samples yielded an estimated effect size of r = -.03.
Similarly, in the handful of U.S. nationally representative samples where economic conservatism
was assessed, the main effect was reduced to non-significance, r = -.02, 95% CI [-.13, .07]), k =
5. Considering that meta-analyses of the RRH (including the present investigation) vastly
overrepresent American samples, we wish to underscore the importance of this finding—a
“rigidity-of-the-economic-right hypothesis” does not seem to hold much water beyond non-
representative samples in the United States.
The “Why?”: Theoretical Implications for the Psychological Underpinnings of Ideology
Where do the present findings leave us? One plausible account of our findings is that
mechanisms and/or epistemic features specific to social conservatism drive conservatism-rigidity
relations, and that economic conservatism is merely “along for the ride” in certain environments
(Malka & Soto, 2015). This conclusion is consistent with prior evidence demonstrating that
social and economic conservatism are negatively correlated, or effectively orthogonal, in many
nations around the globe (Malka et al., 2019) and that features of the information environment
and its associated partisan pressures, such as cues from elite political coalitions (and one’s
degree of exposure to them), seem to drive these instances of coherence vs. incoherence
(Baldassarri & Goldberg, 2014; Kozlowski & Murphy, 2021; Layman & Carsey, 2002; Malka et
al., 2019; Noel, 2014; Zaller, 1992; cf. Azevedo et al., 2019). Our results are consistent with this
conclusion insofar as (1) social conservatism was related to rigidity with relatively large effect
sizes that are robust across nations and sampling contexts; (2) economic conservatism was not
correlated with rigidity on average but was correlated with rigidity in the United States, where
social and economic conservatism are structured together (Federico & Malka, 2022); and (3)
rigidity did not predict economic conservatism in representative national samples (which include
many politically disengaged individuals), even within the United States.
Despite the popularity of the left vs. right political spectrum among researchers, the
psychological antecedents of political ideology may be better understood in the context of their
correspondence to differing social and economic ideologies than in terms of a global left vs. right
distinction (Duckitt & Sibley, 2009; Saucier, 2013). Consequently, any conceptual resonance
between the philosophical tenets of broad-based political conservatism (e.g., system justification)
and psychological characteristics are probably of limited use for explaining links between
rigidity and conservatism (e.g., Costello et al., 2022). Note that this conclusion runs counter to
nearly every instantiation of the RRH but is unavoidable given that both economic and social
conservatism are “right-wing” belief systems (i.e., both ostensibly promise to justify extant
hierarchies and systemic inequalities; Jost, 2021). Analyzing the philosophical and practical
incongruities of social and economic conservatism (vs. liberalism), perhaps including emphases
on governmental protection vs. individual freedoms, may offer a fruitful explanatory lens with
which to understand psychological differences in rigidity (Federico & Malka, 2018).
Another significant aspect of the present review is our comparison of ideological,
motivational, cognitive, and neurocognitive rigidity. Our results clearly show that social
conservatism is, on average, a positive correlate of all four rigidity domains. Still, clear
differences across rigidity domains emerged. Dogmatism and motivational rigidity yielded
considerably larger main effect sizes and heterogeneity than did thinking styles and cognitive
inflexibility. The former domains (dogmatism and motivational rigidity) demonstrated sizeable
overall correlations with social conservatism embedded within sweeping ranges of true effects
and the latter domains (thinking styles and cognitive inflexibility) demonstrated modest overall
correlations embedded within narrow ranges of true effects. These findings are consistent with
the possibility that rigidity in higher-order mental phenomena (i.e., ideology and motivations)
transacts with the political environment to a greater extent than does rigidity in basic cognitive
processes. Specifically, dogmatism and motivational rigidity may be related to politics in a way
that is especially malleable and responsive to contextual moderators. Understanding the causes
of these differences in volatility and magnitude across rigidity domains is a promising endeavor
for future research (Bryan et al., 2021).
Additional grist for the interpretive mill may be had by examining the proportion of
heterogeneity attributable to variation within- vs. between-samples. In the full model (i.e.,
accounting for differences across political ideology and rigidity types), roughly 2.5 times more
substantive heterogeneity was attributable to observations drawn from the same sample than
from observations drawn from different samples. This indicates either that yet-unknown
individual-level moderators/confounds shape relations between specific pairings of ideology-
type and rigidity-type (e.g., perhaps religiosity, which accompanies social conservatism,
amplifies dogmatism specifically) or that our coding scheme was not sufficiently narrow to
identify meaningful distinctions within our ideology and rigidity typologies (e.g., perhaps
motivational rigidity meaningfully fractionates into need for order vs. ambiguity intolerance, and
so on, and these facets manifest divergent relations with political ideology). In both cases,
however, developing mechanistic accounts of the nexus between ideology and cognition seems
to require that social scientists abandon blunt, foggy conceptualizations of “conservatism” or
“rigidity” in favor of specific, narrow constructs that lend themselves to piecemeal, cumulative
theory development (Fried, 2020).
Parsing and classifying these variegated influences on rigidity-ideology relations is a
crucial task that we believe has been obscured by a dominant focus on mean-level differences
between the left and right (Hanel et al., 2019). Researchers who downwardly mine instances
where the RRH does (vs. does not) hold will be well placed to clarify mechanisms linking
psychological rigidity to ideologies and attitudes (i.e., including those other than conservatism;
Zmigrod et al., 2021). In other words, asking questions like “why do people who score highly on
dogmatism tend to endorse social, but not economic, conservatism in most of the world?”, or
“what are the circumstances under which social conservatism is not meaningfully associated with
cognitive inflexibility?”—rather than “are conservatives more rigid than liberals?”—may offer a
meaningful path forward.
To our knowledge, this manuscript describes the most comprehensive quantitative
synthesis of literature bearing on the RRH. Nevertheless, the following important limitations
should temper the strength of inferences drawn from our findings.
Evidence is accumulating that many constructs once thought to be exogenous to political
ideology are, in part, influenced by political ideology, at least in certain contexts (Bakker et al.,
2021; Egan, 2020; Jost et al., 2014; Luttig, 2021; Margolis, 2018; Salfate et al., 2022). Given that
the present review comprises entirely observational research, often involving only a single
measurement occasion, our findings do not inform us about temporal antecedence, let alone
causality. Multiple causal explanations are consistent with the results.
Conceptual and Methodological Scope
We only examine a subset of psychological variables that are commonly framed as
causes or correlates of political ideology in the present investigation. Perhaps most importantly,
we did not include measures relevant to threat sensitivity and existential needs, from
physiological indicators (Bakker et al., 2020) to negativity bias (Johnston & Madson, 2022) to
trait neuroticism (Federico, 2022), which feature prominently in several explanatory accounts of
political ideology (Hibbing et al., 2014; Jost, 2017). That said, the literature on these accounts is
murky and either does not appear to replicate (Bakker et al., 2020; Johnston & Madson, 2022) or
differs in both direction and magnitude across threat sensitivity indicators, conservatism
indicators, and contexts (Bergh & Brandt, 2021; Brandt & Bakker, 2022; Kahn et al., 2021).
Further, our chosen rigidity domains do not include the large literature concerning
integrative complexity—a kind of rigidity assessed via the complexity of spoken or written
thought or explanations for one's beliefs that has been widely used to test the RRH (e.g.,
Suedfeld et al., 1992). Houck and Conway (2019) recently meta-analytically examined the
relation between political ideology and integrative complexity, finding that most liberals and
conservatives do not differ from one another in integrative complexity (r = -.01, 95% CI [-.07,
.05]), but conservative political leaders, specifically, use much less complex language than their
liberal counterparts (r = -.37, 95% CI [-.47, -.26]). This finding is broadly consistent with
differences in rigidity-conservatism correlations across national and sampling contexts revealed
in the present investigation—which we have attributed to environmental moderators pertaining
to political norms and information.
To that end, another limitation of our review is that we did not code for differences across
levels of political engagement. As we have described, mounting evidence shows that relations
between rigidity and conservatism tend to be stronger, and are sometimes exclusively found,
among people who are politically engaged (Feldman & Johnston, 2014; Federico & Goren, 2009;
Johnston et al., 2017; Kalmoe, 2020; Ollerenshaw & Johnston, 2022). Although we did not
explicitly test this moderation effect, our findings and theoretical conclusions concerning the
nature of ideology, and its psychological origins, are consistent with the growing literature on the
importance of political information environment.
Relatedly, the RRH literature is predominantly composed of American samples, and as
such our meta-analysis does not support precise conclusions about differences in support for the
RRH across countries other than the U.S. (Henrich et al., 2010). The clearest drawback of this
over-representation of American samples is that the U.S. is characterized by both an unusual
degree of partisan polarization and merely two (large) political parties that provide little
differentiation between economic and social policy (e.g., governments comprised of many viable
parties typically include those with an admixture of socially liberal and economically
conservative policies, or vice versa; Noel, 2014). Perhaps consequently, we found that the U.S.
displays a small but globally unusual link between rigidity and economic conservatism. In future
research, it would be ideal to examine whether cross-national differences in levels of economic
development (Inglehart & Welzel, 2005), historical cultural and religious traditions (Benoit &
Laver, 2006), and ecological features (Conway et al., 2020; Gotz et al., 2020) account for
variation in the psychological correlates of ideology.
Our meta-analysis also did not examine plausible theoretical alternatives to the RRH. The
ideological extremity hypothesis, which has seen a growing degree of evidentiary support in the
literature, predicts a curvilinear relation between ideological extremity on both the left and right,
on the one hand, and rigidity, on the other, rather than simple left-right differences (e.g., Costello
& Bowes, 2022; Zmigrod et al., 2019). A meta-analytic test of curvilinearity in the relation
between political conservatism and cognitive rigidity would require access to the raw data used
to calculate each effect size to derive semi-partial correlations (e.g., Williams & Livingstone,
1994), which was not feasible for the current review. With the rise of open science and the
increasing frequency with which authors make raw data publicly available, however, future
meta-analytic research will hopefully be able to test for the presence curvilinearity.
Measurement and Construct Validity
Another limitation of the present work is the underdeveloped validity of many or most
rigidity constructs and measures. For instance, the idiosyncrasies of information processing are
not easily accessible to introspective observation (see Kahan, 2016). Indeed, cognitive
psychology and neuropsychology typically rely on behavioral tasks to assess cognition (e.g.,
cognitive ability or memory are rarely measured using self-reports), in part because self-
assessments of cognitive performance are frequently inaccurate (Furnham, 2001; Kruger &
Dunning, 1999). Yet, ostensibly “objective” measures of cognition traits are often unreliable
and/or demonstrate poor construct validity for individual differences, perhaps because of their
high situational specificity and resultingly poor replicability (e.g., Epstein & O’Brien, 1985;
Hedge et al., 2018). The most likely possibility may be that behavioral measures and self-reports
each have their own sets of psychometric strengths and weaknesses and tap related but distinct
Further, while we accounted for the presence of rigidity content in ideology measures, we
did not code for the presence of ideology content in rigidity measures. For example, the primary
measure of dogmatism in the literature, the DOG Scale, seems to be confounded with religiosity
and social conservatism (Conway et al., 2016; Duckitt, 2009). Thus, our findings concerning
dogmatism’s outsized correlations with conservatism, relative to other rigidity variables, may be
attributable to measurement error. While important to consider, this possibility may not be
especially explanatorily powerful given that only a handful of items seem to be confounded in a
way that has been empirically documented for similar measures (e.g., Stanovich & Toplak,
2019). Still, future work addressing measurement invariance and test bias across the political left
and right for dogmatism measures would be useful. A related limitation involves “jingle-jangle”
fallacies (Block, 1995). For example, although we opted to aggregate Rokeach’s (1960)
Dogmatism Scale and Altemeyer’s (1996) DOG Scale in our analyses, the two measures may
operationalize dogmatism quite differently. Still, our use of multiple meta-analytic models that
differ in specificity may buffer against interpretative errors owing to loose nomological networks
and jingle-jangle fallacies.
The Pitfalls of Meta-regression
We predominantly relied on meta-regression, rather than subgroup analyses, to address
the problem of confounded moderators (Lipsey, 2003). As underscored by Schmidt (2017), the
statistical and meta-scientific obstacles of traditional regression also apply to meta-regression.
For instance, because we did not correct for measurement error in our observed rs, the true
strength of all values (but especially those of our moderators) may be larger than our estimates
(Schmidt & Hunter, 2014). Moreover, our more complex analyses may suffer from low statistical
power. Although we had a relatively stable sample size (k > 700, or roughly the size of a
moderately-sized internet-recruited sample), some non-significant categorical moderators with
few observations at certain levels (e.g., esoteric measures of political ideology) may be false
negatives. We also did not test for many 3-way statistical interactions when examining potential
moderators (i.e., rigidity construct by conservatism-type by third moderator) owing to inadequate
statistical power. Our approach therefore typically assumes that each moderator’s impact on the
relation between a given level of political conservatism (e.g., economic) and a given rigidity
variable (e.g., dogmatism) is equivalent to that moderator’s impact on all other levels of
conservatism for all other rigidity variables. A related problem is that we did not preregister the
potential moderators to be examined in meta-regression, or how they would be operationalized,
which raises the specter of data dredging (referred to by Thompson and Higgins  as “the
principal pitfall in meta-regression”). The next meta-analysis of the RRH and/or the
psychological causes and correlates of political ideology should ideally follow a prospectively
registered analysis plan and protocol (Quintana, 2015).
We hope that the present review allows for more nuanced accounts of the psychological
correlates of political ideology to emerge. Our meta-analysis suggests that research on
psychological dispositions and ideology ought to put the distinction between social and
economic conservatism front-and-center (Claessens et al., 2020), address contextual factors that
condition ideological coherence (Jost et al., 2009; Federico & Malka, 2018, Johnston et al., 2017;
Malka & Soto, 2015), and formulate and evaluate theories on the basis of accounting for
heterogeneity (in addition to the traditional yardsticks; Linden & Honekopp, 2021). We welcome
and anticipate challenges to our conclusions, but hope, at the very least, that psychological
science will be somewhat closer to reconciling an intellectual conflict that has worn on for well-
over half a century.
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