Are Conservatives More Rigid Than Liberals? A Meta-Analytic Test of the Rigidity-of-the-

Right Hypothesis

Thomas H. Costello, Shauna M. Bowes

Emory University, Department of Psychology

Matt W. Baldwin

University of Florida, Department of Psychology

Scott O. Lilienfeld

Emory University, Department of Psychology

University of Melbourne, School of Psychological Sciences

Arber Tasimi

Emory University, Department of Psychology

This working manuscript is under review

11/06/21

Author Note We would like to thank Crystal Liu for her work identifying and coding studies; Omer Kirmaz for his work aggregating scores across raters; and Patricia Brennan for suggesting that we code political donations by study authors as a proxy for political ideology. Supporting materials for this manuscript, including data and analytic code, will be made openly available in a public repository upon publication of this manuscript. Correspondence should be addressed to Thomas H. Costello, 36 Eagle Row, Department of Psychology, Emory University, Atlanta, GA, 30322. E-mail: thcoste@emory.edu.

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Abstract

The rigidity-of-the-right hypothesis (RRH), which posits that cognitive, motivational, and

ideological rigidity resonate with political conservatism, is the dominant psychological account

of political ideology. Here, we conduct an extensive review of the RRH, using multilevel meta-

analysis to examine relations between varieties of rigidity and ideology alongside a bevy of

potential moderators (s = 329, k = 708, N = 187,612). Associations between conservatism and

rigidity were enormously heterogeneous, such that broad theoretical accounts of left-right

asymmetries in rigidity have masked complex—yet conceptually fertile—patterns of relations.

Most notably, correlations between economic conservatism and rigidity constructs were almost

uniformly not significant, whereas social conservatism and rigidity were significantly positively

correlated. Further, leftists and rightists exhibited modestly asymmetrical motivations yet closely

symmetrical thinking styles and cognitive architecture. Dogmatism was a special case, with

rightists being clearly more dogmatic. Complicating this picture, moderator analyses revealed

that the RRH may not generalize to key environmental/psychometric modalities. Thus, our work

represents a crucial launch point for advancing a more accurate—but admittedly more nuanced—

model of political social cognition. We resolve that drilling into this complexity, thereby moving

away from the question of if conservatives are essentially rigid, will amplify the explanatory

power of political psychology.

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Are Conservatives More Rigid Than Liberals? A Meta-Analytic Test of the Rigidity-of-the-

Right Hypothesis

How do the minds of right-wing and left-wing individuals differ? This has been one of

the essential questions of political psychology since the field’s inception in the mid-twentieth

century (e.g., Adorno et al., 1950; Hibbing et al., 2014; Jost et al., 2003; Rokeach, 1960; Wilson,

1973). A dominant—if not the dominant––psychological account of what distinguishes leftists

from rightists is known as the rigidity-of-the-right hypothesis (henceforth, RRH; e.g., Tetlock et

al., 1984). Put plainly, the RRH suggests that individuals who think of the world as

uncontrollable and difficult to understand have a motivational need to simplify reality; thus, they

adopt political ideologies that foster a sense of order and predictability to satisfy this need.

Because conservatism offers a sense of certainty by way of its support for current social norms

and hierarchies, rightists are disproportionately likely to be cognitively, ideologically, and

motivationally rigid.

Several prior meta-analytic reviews have reported reliable relations between political

conservatism and rigidity-related variables (e.g., Jost, 2017; Jost et al., 2003; Van Hiel et al.,

2016), prompting social scientists to continue to champion and refine the RRH in recent decades.

During this time, scholars have extended and conceptually replicated the RRH by identifying

left-right asymmetries in a diverse array of rigidity-adjacent contexts (for a review, see Hibbing

et al., 2014); these include ideological asymmetries in cognitive ability (e.g., rightists have an

impaired cognitive capacity to manage complexity; Kemmelmeier, 2008), word preferences

(e.g., rightists prefer nouns over verbs and adjectives because nouns facilitate clearer and more

definite perceptions of reality; Cichocka et al., 2016), and reactions to fake news (e.g., rightists

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are more likely to fall for fake news because they process new information less thoughtfully;

Pennycook & Rand, 2018), among many others.

That said, a burgeoning chorus of scholars have asserted that the relation between

conservatism and rigidity hinges crucially on a host of empirical (e.g., Ditto et al., 2019;

Federico & Malka, 2018; Feldman & Johnston, 2014; Kahan, 2016; Malka & Soto, 2015;

Zmigrod et al., 2019), methodological (e.g., Malka et al., 2017; Zmigrod, 2020), and meta-

scientific (e.g., Duarte et al., 2015; Jussim et al., 2016) factors, such that the RRH’s evidentiary

foundation may be grounded in a noisy and contradictory literature. To provide a sense of these

prior critiques, consider that many people identify as “socially liberal” and “economically

conservative” (or vice versa), suggesting that “liberalism” and “conservatism” may not be

psychologically coherent categories (Feldman, 2013; Kerr, 1952). Similarly, the umbrella

category of “rigidity” may be just as incoherent—the list of constructs that previous meta-

analyses of the RRH have used to operationalize rigidity is broad and includes dogmatism,

intolerance of ambiguity, cognitive and perceptual inflexibility, motivational needs for closure,

simple patterns of speech, and intuitive thinking styles (e.g., Houck & Conway, 2019; Jost et al.,

2003; Jost, 2017; Van Hiel et al., 2016). Overall, these criticisms point to the possibility that

research on the RRH—and within political psychology more generally—may mask a

considerable degree of heterogeneity in understanding both “the right” and “rigidity”.

Rather than simply highlight these problems, here we synthesize and meta-analytically

test them. We begin by providing a brief overview of the RRH and its evidentiary support, then

catalogue prominent challenges to the RRH and advance new ones. Synthesizing these

challenges, our meta-analysis indicates that the RRH understates the complexity of interrelations

among rigidity and political ideology. For research in this area to advance, we argue that political

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psychologists may do well to move the discussion away from if conservatives are rigid (and

otherwise psychologically distinct from liberals) to when politics and rigidity-related processes

intersect and why they do or do not.

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 of the RRH,

documenting differences like conservative U.S. Senators make less complex policy statements

than liberals (e.g., Tetlock, 1983; cf. Houck & Conway, 2019), conservatives show impoverished

abstract reasoning abilities (e.g., O’Connor, 1952) and are less tolerant of ambiguity (e.g., Block,

1951), conservatives exhibit differences in general neurocognitive functioning (e.g., Amodio et

al., 2007; Nam et al., 2021; cf. Rollwage et al., 2018), and conservatives favor distinct working

memory processes (i.e., inhibition) that may account for underlying ideological asymmetries in

mental flexibility (e.g., Buechner et al., 2021).

Although theoretical accounts of the RRH differ across scholars (e.g., Adorno et al.,

1950; Altemeyer, 1996; Hetherington & Weiler, 2018; Tetlock et al., 1984; Wilson, 1973), one

popular version of this hypothesis, as foreshadowed above, conceives of conservatism as

motivated social cognition (Jost et al., 2003). Indeed, in one of the most influential publications

in the history of political psychology, a meta-analysis of five decades worth of this literature

found that political conservatism arises as a consequence of basic cognitive (i.e., pertaining to

thinking, reasoning, or remembering) and motivational (i.e., the impetus that gives purpose or

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direction to behavior) processes concerning certainty/rigidity and safety/threat-sensitivity1 (Jost

et al., 2003).

This version of the RRH has served as the frontline for much research within political

psychology over the last two decades, stimulating a dramatic 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; Lakoff, 2008; Mooney, 2012; Oxley et al., 2008; Westen,

2007). This renaissance of theory and research, in turn, prompted additional meta-analyses of the

RRH, which generally continued to provide strong corroboration for the model (Houck &

Conway, 2019; Jost, 2017; Jost et al., 2003; Van Hiel et al., 2016). For instance, in a recent

review (Jost, 2017), significant meta-analytic estimates were revealed for conservatism and a

broad range of rigidity-related constructs. Critically, many of these relations seem to be robust

across Western, democratic cultural contexts (e.g., Chirumbolo et al., 2004; Kemmelmeier, 1997;

Malka et al., 2014, 2019) and measures of political ideology (e.g., Federico et al., 2012). Overall,

this veritable ocean of evidence seems to lead to one clear conclusion: that rightists are more

rigid than leftists.

But from our point of view, existing evidence is less supportive of the RRH than may

seem at first blush. As previously noted, extensive empirical, methodological, and meta-

scientific challenges to the validity and generalizability of the RRH have arisen in recent years,

raising the possibility that ideological symmetries and asymmetries exist across the political left

and right, depending on key moderators. In this paper, we synthesize, examine, and test these

wide-ranging concerns and controversies, which organize our quantitative review. Before we do,

1 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).

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we highlight what we consider to be among the most critical issues that permeate the literature

on the RRH.

What is “The Right”?

Politicians, political commentators, social scientists, and other politically engaged

members of the public have long conceived of political ideology as a unidimensional, left/liberal

vs. right/conservative political continuum, with the left pole reflecting preferences for change,

individualism, and egalitarianism, and the right pole reflecting preferences for stability,

authority, and hierarchy (Caprara & Vecchione, 2018; Johnston & Ollerenshaw, 2020). Political

discourse follows this left-right ideological divide in many Western nations (e.g., Benoit &

Laver, 2006; Kitschelt et al., 2010; Knight, 1999; McCarty et al., 2006), seemingly speaking to

the degree to which, as Emerson (1841) speculated over a century ago, the division between left-

and right-wing reflects an “irreconcilable antagonism [that] must have a correspondent depth of

seat in the human constitution… the appearance in trifles of the two poles of nature” (p. 293).

As parsimonious and appealing as this account may be, there are several problems with

treating political ideology in a binary or unidimensional manner. Consider, for example, the

predominant approach for measuring political ideology: single-item self-reports that ask

participants to indicate how liberal or conservative they are on a Likert-type scale. One recent

estimate suggests that 80% of studies in political psychology rely on this measure (Claessens et

al., 2020). Yet a plethora of research has found that the political spectrum can be decomposed

into two conceptually and empirically distinct subdimensions: social ideology and economic

ideology (e.g., Claessens et al., 2020; Costello & Lilienfeld, 2020; Duckitt & Sibley, 2009;

Federico & Malka, 2018; Feldman & Johnston, 2014; Johnston et al., 2017; Lameris et al., 2018;

Pan & Xu, 2018; see Johnston & Ollerenshaw, 2020, for a review). Whereas social ideology

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spans attitudes concerning progressive vs. traditional values, rules, and norms, economic

ideology spans attitudes concerning redistributive vs. free market economic systems (Claessens

et al., 2020; Malka et al., 2019). Thus, the question of “how liberal vs. conservative are you?”

may mean different things to different people. That is, some people’s responses may be rooted in

their social preferences and others in their economic preferences—which, in turn, introduces a

considerable degree of ambiguity in what constitutes “the right.”

Part of what makes this a problem is that most hypothesized mechanisms underlying the

RRH draw from conceptual connections between the shared epistemic qualities of social and

economic conservatism and rigidity. Hence, rigidity should be roughly equivalently associated

with all forms of conservatism (e.g., Jost et al., 2013, p. 1). But, if “the right” is not any one

thing, the RRH may commit a great error of oversimplification. To that end, whereas some

studies suggest roughly equivalent relationships between social and economic conservativism

and rigidity-related constructs (e.g., Azevedo et al., 2019; Cornelis & Van Hiel, 2006; Everett,

2013; Sterling et al., 2016), others have indicated that (1) social conservatism is consistently

positively associated with rigidity related variables, yet (2) economic conservatism manifests

null or even negative relations with many of these same variables (e.g., Carl, 2014; Carney et al.,

2008; Costello & Lilienfeld, 2020; Cizmar et al., 2014; Feldman, 2013; Hibbing et al., 2014; Van

Hiel et al., 2004; Yilmaz et al., 2016). What is more, social and economic conservatism tend to

be positively correlated among politically engaged, Western, Educated, Industrialized, Rich, and

Democratic participants (WEIRD; Henrich et al., 2010), yet are more often slightly negatively

correlated outside of Western democracies (Feldman & Johnston, 2014; Malka et al., 2017;

Malka et al., 2019; Marks et al., 2006). This string of findings further bolsters the notion that

social and economic ideology are not psychologically intertwined.

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Altogether, the left/liberal vs. right/conservative political spectrum appears to be a

straightforward heuristic for explaining patterns of ideological clustering—especially in cultural

contexts such as the U.S. where psychological scientists have typically studied the RRH (as we

discuss later)—but it may not be a fact of human nature. To our knowledge, no prior meta-

analytic reviews of the RRH have examined the differential correlates of social versus economic

political ideology.

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. For

example, one recent review (Cherry et al., 2021) of the cognitive rigidity literature identified 25

competing conceptualizations assessed across 23 measures. To that end, little scholarly

consensus exists concerning the precise boundaries of rigidity (Furnham & Marks, 2013;

Sternberg & Grigorenko, 1997; Zmigrod et al., 2019), such that 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. 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 have, however, emerged in

recent years (e.g., executive functioning, intolerance of ambiguity, inflexible thinking styles;

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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 manner2. Based on these provisional taxonomies of rigidity dimensions, we have

identified four domains of rigidity (see Figure 1) that are reasonably differentiable in their

relations with both one another and relevant external criteria: (1) rigid thinking styles, (2)

motivational rigidity, (3) cognitive inflexibility, and (4) ideological rigidity (i.e., dogmatism).

As we discuss below, these domains have little definitional overlap, are not strongly

correlated, and tend to be studied in disparate subfields. We suspect that this schema offers a

data-driven 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 formal investigations of the taxonomy of rigidity. Accordingly, as with the “the

right,” we anticipate inconsistencies across elements of “rigidity” in the RRH literature. In other

words, some—but not all—forms of rigidity may be related to conservatism.

Rigid Thinking Styles

Many or most theoretical accounts of human decision-making draw upon a broad

distinction between two types of cognitive processes: intuitive (i.e., rapid, unconscious, and

automatic) and reflective (i.e., slow, conscious, and deliberative; Kahneman, 2011). Many

dozens of research investigations have found that individuals vary in this cognitive reflectivity,

and that these thinking styles have strong and broad patterns of relations with 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

2Drawing on these provisional taxonomies of rigidity dimensions in future research may be a useful factor in developing actionable and detailed mechanistic accounts of the structure and dynamics of mechanisms underlying the RRH (e.g., Rollwage et al., 2019).

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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

constructs that have been used in tests of the RRH (e.g., need for closure, intolerance of

ambiguity, and dogmatism; Newton et al., 2021). Given these findings—and that cognitive

reflectivity accounts for a greater degree of unique variance in many different (irrational)

heuristics and cognitive biases than intelligence, executive functioning, and actively open-

minded thinking (e.g., Toplak et al., 2011)—we treat rigid thinking styles as a distinct “rigidity”

domain.

Motivational Rigidity

As with rigid thinking styles and cognitive inflexibility, 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 “the individual’s

desire for a firm answer to a question and an aversion toward ambiguity” (Kruglanski &

Webster, 1996, p. 264; Kruglanski & Webster, 1996; Kruglanski et al., 2006). Specifically, need

for cognitive closure includes five conceptually distinctive, if not empirically distinct,

subdimensions (see Roets et al., 2006; cf. Neuberg et al., 1997): preference for order, preference

for predictability, discomfort with ambiguity, closed-mindedness, and decisiveness. Many tests

of the RRH have revealed a relation between need for cognitive closure (and related motivational

needs) and conservatism (see Federico & Goren, 2009). Other constructs potentially indicative of

need for certainty, such as risk aversion, also exhibit modest relations with elements of

conservatism (Kam, 2012; Kam & Simas, 2012; Kemmelmeier, 2008). To evaluate this

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possibility, we collapse motivational rigidity variables, such as need for cognitive closure and

motivational elements of intolerance of ambiguity, in our primary analyses.

Cognitive Inflexibility

Cognitive inflexibility can be understood as part of a broader suite of psychological

processes involved in executive functioning (i.e., 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; Diamond, 2013).

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 and downstream consequences thereof (e.g., Buechner et al., 2021;

Sidanius, 1978; Zmigrod, 2020). To our knowledge, though, 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, on the one hand, manifest

differential relations with external criteria, on the other (e.g., differences as large as r = .40 for

various personality traits; Lauriola et al., 2016; Stoycheva et al., 2020). Similarly-sized

differences in these rigidity variables’ relations with conservatism, or even far smaller

differences, would carry notable implications for the generalizability and explanatory power of

the RRH. Given these uncertainties, we distinguish cognitive inflexibility from other rigidity

domains.

Ideological Rigidity (i.e., Dogmatism)

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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 (see Duckitt, 2009)— in the studies referenced above, no correlation between

dogmatism scores and the individual differences variables was > .31, providing strong evidence

for its empirical distinctiveness (see Ronkko & Cho, 2020). Moreover, the primary measure of

dogmatism in the literature, the DOG Scale, may be confounded with religiosity and social

conservatism (Conway et al., 2016; Duckitt, 2009; see Stanovich & Toplak, 2019)3. Given these

considerations, as well as the fact that dogmatism is quite theoretically distinct from all other

“rigidity” variables (Johnson, 2009), we treat dogmatism as a standalone rigidity domain in the

present review.

3Stanovich and Toplak (2019) found that religious individuals respond differently than non-religious individuals to Actively Openminded Thinking (AOT) Scale items that include the word “belief.” Individuals with strongly held religious views generally take “beliefs” to mean “religious beliefs,” whereas non-religious individuals generally take “beliefs” to mean “opinions.” After the offending items were removed, Stanovich and Toplak (2019) found that AOT-religiosity correlations were reduced from roughly r = -.60 to roughly r = - .20. Perhaps notably, several other oft-used measures in social and personality psychology frequently use the word “belief” in a similar manner, including Altemeyer’s (1996) DOG Scale, the most popular psychological measure of dogmatism, which does so in 6 of its 22 items (and is correlated with religious fundamentalism such that r = .60; Altemeyer, 1996). Duckitt (2009) has similarly suggested that the DOG Scale potentially assesses “religious dogmatism specifically and not dogmatism in other spheres of belief”.

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Figure 1. A provisional taxonomy of rigidity variables in political psychology.

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Excluded rigidity variables. Having defined the rigidity variables we will focus on, we

now briefly discuss some constructs that are sometimes regarded as part of an extended family of

rigidity-related indicators—insofar as they are used in efforts to evaluate the RRH—that relate to

“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). Some constructs that are not directly rigidity-related but are sometimes regarded as part of

this extended family are fear of death, perceptions of various threats, reversed openness to

experience (or facets thereof), conscientiousness (or facets thereof), and the conservation vs.

openness value axis (e.g., Jost et al., 2007; Johnston and Wronski, 2015; 2018; Federico &

Malka, 2018). Although these constructs may bear some theoretical and empirical relations with

our outlined rigidity domains, they are only indirectly relevant to them. To minimize the risk of

introducing construct-irrelevant variance, we therefore exclude findings involving extended-

family rigidity indicators from the present meta-analysis.

Circular Measurement: Some Measures of Conservatism Directly Measure Rigidity

So far, we have predominantly focused on conceptual and taxonomic reasons that the

RRH’s evidentiary basis may be less clear-cut than previously thought. Yet, from our point of

view, among the most critical obstacles to useful meta-analytic tests of the RRH are

methodological in nature. To elaborate, a large proportion of early studies used measures of

“conservatism” that rest on the theoretical assumption that conservatism is heavily imbued with

rigidity. These measures—which include the Fascism Scale (e.g., Adorno et al., 1950), the Right-

wing Authoritarianism Scale (e.g., Altemeyer, 1996), and the Conservatism Scale (e.g., Wilson

& Patterson, 1968)—were designed to assess rigidity and conservatism simultaneously (e.g.,

Wilson, 1973). For instance, the Conservatism Scale asks participants to indicate their support

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for “general attitudes concerning uncertainty avoidance” (Jost et al., 2003, p. 340), artistic

movements that often involve ambiguity (e.g., jazz music, modernism), and specific social-

political issues that carry authoritarian or prejudicial connotations (e.g., censorship, white

superiority, church authority, women judges).

This imprecise and criterion-contaminated historical measurement practice poses an

obstacle to meta-analytic tests of the RRH because, until recently, studies relying on criterion-

contaminated measures of conservatism made up a not insubstantial proportion of the RRH

literature. In the first meta-analytic test of the RRH (see Jost et al., 2003), for example, the

Wilson-Patterson Conservatism Scale was used to measure right-wing ideology in 38% of the

rigidity-related studies (with an additional 22% of studies using either the Fascism Scale or

Right-wing Authoritarianism Scale). Thus, a full 60% of studies relied on conservatism measures

imbued with rigidity. Later meta-analyses of the RRH comprise a similar proportion of studies

with biased measures, even explicitly operationalizing right-wing attitudes as authoritarianism,

ethnocentrism, and dogmatism (Van Hiel et al., 2010; 2016).

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

similarly yield exaggerated meta-analytic results (see Malka et al., 2017, pp. 119-121)4.

4Content 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).

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Moreover, the inflation of rigidity-conservatism correlations may obscure many key boundary

conditions of the RRH. For example, if the global correlation between economic conservatism

and cognitive inflexibility is ρ = -.10, but meta-analytic estimates are biased by +.20 due to

criterion contamination, researchers may draw erroneous conclusions about the RRH’s

explanatory power for economic ideology. Hence, in the present review, we examine the degree

to which biased measures inflate effect sizes and estimate rigidity-conservatism relations in a

way that is not distorted by content overlap.

Meta-scientific Concerns: Heterogeneity, the “Crud Factor,” and Political Bias

It is perhaps unsurprising that previous meta-analytic reviews of the RRH have revealed

ample substantive heterogeneity in the associations between conservatism and rigidity. Point

estimates for conservatism-rigidity correlations reported in peer-reviewed articles range from r =

-.58 (Durrheim, 1998) to r = .82 (Pettigrew, 1958). This degree of heterogeneity is consistent

with the vast range of constructs, measures, and environments that scholars have used to test the

RRH. Attempting to meta-analytically estimate an “overall” effect size estimate for the relation

between conservatism and rigidity glosses over the more difficult—and, arguably, more

interesting—question of when and why these effects (1) occur, (2) are large vs. small, and/or (3)

positive vs. negative. In other words, previous reviews have largely neglected to empirically

parse the heterogeneity of the RRH literature, which is perhaps the chief insight provided by

meta-analysis (Higgins & Thompson, 2002).

Further, the RRH advances forceful claims about fundamental cognitive differences

between liberals and conservatives, yet proponents of the model have generally taken left-right

differences of any magnitude as evidence in support of ideological asymmetries (Jost, 2017),

potentially rendering the RRH difficult to falsify (see also Lakens et al., 2018; Meehl, 1992).

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Because any given psychological variable tends to be at least slightly correlated with any other

(Lykken, 1991; cf. Orben & Lakens, 2019), with a large enough k and adequate study quality,

appropriately powered meta-analyses will virtually always return a non-null effect, regardless of

the truth of the substantive theory in question (Meehl, 1978). Certain small effects can have

profound real-world implications (Funder & Ozer, 2019), yet one obstacle to interpreting the

RRH literature is that there is no established or consensual size of “difference” between the left

and right that scholars consider meaningful. Statistical significance notwithstanding, how much

more rigid must the right be for us to conclude that the right is, in fact, rigid compared with the

left (see Lakens et al., 2018)?

Given that the RRH implies causality, or at least that conservatism and rigidity share

antecedents, we posit that the criterion for accepting a meaningful effect should be relatively

strict: Ideological asymmetries should be reasonably robust, not wobbling near zero. If we use

Cohen’s effect size benchmarks, intended to describe the meaningfulness of a result (e.g., a small

effect size can only be detected via careful study whereas a medium effect size is visible to “the

naked eye of a careful observer”), r = .10, r = .30, and r = .50 represent small, medium, and large

effect sizes, respectively. Hence, we would begin to gain confidence in the RRH as correlations

approached a range of r = .25 to r = .35, and our confidence would increase dramatically as

effect sizes approached r = .40. By the same token, effect sizes from r = .05 to r = .15 would

support the possibility that the RRH is of dubious practical value, and we would treat effect sizes

below r = .05 as falsifying the model.

An additional source of bias may be attributable to the fact that we live in an extremely

polarized and politicized world, and psychologists, being humans, are not immune from the

biases that tend to accompany partisanship. Namely, several authors (e.g., Duarte et al., 2015;

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Honeycutt & Jussim, 2020) have suggested that the RRH has benefited from the

disproportionately left-leaning political preferences of social psychologists (Haidt, 2011;

Langbert et al., 2016; von Hippel & Buss, 2017), which may have biased the literature in

undetermined ways. All meta-analyses are liable to poor statistical accuracy due to biases

introduced during the dissemination of results (e.g., publication bias) and/or those borne of

correlated error variance across multiple studies. Similarly, allegiance biases serve a similar

function in meta-analyses of controversial topics. For instance, Gaffan and colleagues (1995)

famously found that, in a meta-analytic review of the efficacy of various psychotherapeutic

approaches, researchers’ allegiance to a given therapeutic approach accounted for up to half of

the difference between said approach and other treatments. The same may be true of political

allegiance (Duarte et al., 2015). Still, evidence is for this possibility is mixed (e.g., a recent

adversarial collaboration found that political allegiance is not related to replicability; Reinero et

al., 2019) and warrants further examination.

The Present Review

Taken together, previous reviews’ failure to sufficiently account for the heterogeneity of

conservatism and rigidity, among other considerations, renders their estimated effect sizes

difficult to interpret. In 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

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meta-scientific obstacles to substantive tests of the RRH, such as publication and political bias,

sampling bias, and criterion contamination in ideology and rigidity measures. We also examine

the statistical impact of other potential moderating variables; these include rigidity measure type

(i.e., self-report vs. performance-based), political ideology measure type, peer-review status, type

of sample, WEIRDness, and nationality.

Relative to previous reviews, the current meta-analysis is considerably larger and broader

in the number of independent samples, effect sizes, and unique 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. To do so, we employ a three-level (i.e., “multi-level”)

meta-analytic approach to facilitate the inclusion of all relevant observations, including those

drawn from the same participants, without artificially inflating confidence in our estimates (Van

den Noortgate et al., 2015).

Method

Literature Search

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; they 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

ambiguity)”. Searches covered English-language articles, books, Master’s theses, and

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dissertations published from 1950 to 2020. 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 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 of 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, self-

report questionnaire, 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 significant covariates (e.g., beta

weights from multiple regression analyses) were excluded. No studies were excluded on the

basis of participant characteristics (e.g., age, ethnicity, native language).

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. 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

21

disagreements were resolved by discussion. An overview of included citations, study

characteristics, and effect sizes is provided in Supplementary Table 1.

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 are based on political ideology constructs that overtly assess prejudice,

authoritarianism, and rigidity. 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.

Figure 2. 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 be calculated).

Data Coding

22

Descriptive statistics for each moderator variable are presented in Tables 1 and 2.

Allegiance associations. Theoretical allegiance to the RRH was coded categorically as

one of three categories: (1) supports RRH, (2) neutral towards RRH/does not mention RRH, and

(3) challenges RRH. We modeled our coding strategy on procedures from Gaffan, Tsaousis, and

Kemp-Wheeler (1995). Accordingly, studies were considered to be non-neutral toward the RRH

if their Introduction section fulfilled any of the following criteria: (a) explicitly hypothesized that

rightists will demonstrate cognitive rigidity than leftists, or vice versa; (b) included a description

of the RRH (or a competing hypothesis) that was at least 10 lines longer than descriptions of

other models; (c) were authored by a creator of a RRH-aligned theory (or a competing theory);

and/or (d) mentioned only the RRH (or a competing model). If a manuscript did not fulfill any of

the aforementioned criteria, it was coded as neutral towards the RRH. Rater agreement was

substantial, κ = .69.

To further investigate the potential role of political bias in the RRH literature, we also

coded for author’s political allegiance. Given that this information is difficult to ascertain from

research articles, we employed a proxy measure of authors’ political ideology: whether and to

what extent authors had contributed to political organizations. Donation information for the first

and last authors of each study was obtained via the Center for Responsive Politics’ database of

Federal Election Commission records, which comprises receipts from political donations,

including donations to political action committees (PACs). These analyses were by necessity

limited to authors who are U.S. citizens. We attributed political contributions to an author only if

our search yielded a match for their (a) first and last name and either (b) employer (e.g., their

university) or (c) their current or past location (i.e., as determined by the location of one’s

employer and/or information on publicly available CVs). We computed one categorical variable

23

(donated to right, did not donate, or donated to left) and one continuous variable (frequency of

donation), with donations to the right arbitrarily coded with negative values and those to the left

arbitrarily coded as positive values).

Sample characteristics. We extracted the following continuous variables for sample-

level characteristics: country of origin (κ = .98), mean age (ICC = .98), and gender composition

(ICC = .98). We also coded participant composition categorically (e.g., university students,

online, 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, support for issues/policies, vote choice, party

identification, 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.

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. 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-

24

Scale (e.g., Kirton, 1978)5, 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.

As a means of evaluating the first-author’s coding decisions, we recruited a small online

community sample from Amazon’s Mechanical Turk (N = 150) to provide judgments about (a)

six of the most commonly used and/or representative non-overlap measures of political ideology

(i.e., symbolic identification, vote choice, the Social and Economic Conservatism Scale, a

modernized C-Scale, party preferences, and the Political-Economic Conservatism Scale) and (b)

a priori content overlap measures. After reading each measure, participants responded to the

following items: (1) “A person's answers on this measure will accurately reflect whether they

hold right-wing vs. left-wing political views”; (2) “This measure contains content related to

psychological rigidity (e.g., inflexibility in thinking, dislike of uncertainty, dogmatism, etc.)?”;

and (3) “This measure contains content that is not directly related to political ideology”. Five-

point Likert-type response scales were used6. Responses on the three items were averaged (with

item 1 reverse scored) to yield a score for lay appraisals of content overlap and face validity.

Using these scores, we conducted a dependent samples t-test of differences between lay

appraisals of measures categorized by the first author as containing content overlap vs. lay

appraisals of measures not containing overlap. Scores for overlap and non-overlap measures

suggested that non-overlap measures had better face validity, t = 12.96, p < .001, d = 1.19.

5With the exception of modern variants of the C-Scale, such as that used in Deppe et al. (2015). 6For items 1 and 3, response options ranged from Definitely True (1) to Definitely False (5); for item 2, response options were Not at All (1), Somewhat (2), Half and Half (3), Primarily (4), and Exclusively (5).

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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).

Dimension of political ideology. Measures of political ideology were coded as one of

three categories: general conservatism, social conservatism, or economic conservatism. General

conservatism, 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 conservatism 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; self-report measures that yield a social conservatism subscale;

and policy preferences for issues related to social conservatism (e.g., abortion rights or gay

marriage). Economic conservatism was assessed in the same manner as social conservatism, 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. Rater agreement

was substantial, κ = .90.

Rigidity. When coding each observation, we used a two-pronged approach. First, we

examined the rigidity constructs individually, coding them on the basis of 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

26

(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) based on the first author’s judgment.

Statistical Analyses

All extracted effect sizes were transformed into Fisher’s z (Cohen, West, & Aiken, 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; Raudenbush & Bryk,

2002). We used the metafor package (Viechtbauer, 2010) in R (version 3.6.1; R Core Team,

2019) to conduct all analyses.

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 each sample (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

27

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. Another advantage of the three-level model is that it characterizes the

amount of heterogeneity due to differences both within (e.g., both economic and social

conservatism being reported in a single study) and between studies. Further, if heterogeneity is

present, the global three-level model may be extended to include relevant predictors (e.g.,

construct and conservatism type) without assuming that said predictors explain all variance

among outcomes within studies.

We computed three indices of heterogeneity. First, we computed Cochran’s Q. To

account for the misleading inflation of Q that occurs with a large pool of studies, we also

calculated H2 (Higgins & Thompson, 2002), or Q/k – 1, which represents the differences between

Q and its expected value when heterogeneity is not present. H2 allows for the comparison of

heterogeneity across different meta-analytic models, as it does not increase with the number of

studies included in each estimate. Higgins and Thompson (2002) recommended the following

guidelines for interpreting H2 values: H2 = 1 indicates that the population of studies is

homogeneous, whereas H2 > 1.5 indicates that substantial heterogeneity is present.

Lastly, we calculated the percentage of total heterogeneity due to substantive

heterogeneity from level 2 of the three-level model (variation across outcomes within each

sample), I2(2), and level 3 of the three-level model (variation across each sample), I2(3). Much like

the traditional I2 statistic for random-effects models, introduced by Higgins and Thompson

28

(2002), I2(2) and I2(3) estimate heterogeneity relative to the total variance (i.e., variance in true

effects plus sampling variance) with the additional step of splitting the variance in true effects

into between-cluster (sample) heterogeneity and within-cluster heterogeneity.

Meta-analytic models. Determining the extent to which scientific constructs should be

lumped together or split apart is a longstanding philosophical and practical conundrum (e.g.,

McKusick, 1969; Simpson, 1945). As such, 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, following Glassian thinking (Glass, 2015), we estimated an overall model,

collapsing across rigidity constructs and types of conservatism to yield an overall meta-analytic

estimate. 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

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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.

A reduction in substantive heterogeneity as the meta-analytic models increase in

complexity allows us to examine whether our boundary conditions are explaining additional

residual variance. For instance, we can separately observe the reduction in heterogeneity

attributable to distinguishing between social and economic conservatism, different rigidity

domains, and so on, thereby clarifying the degree the latent meaning of the RRH literature and/or

the likelihood that similar mechanisms underly most rigidity-conservatism relations. 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]). Although interactions may be present, we did not have

adequate statistical power to conduct the 3-way interaction analyses that would have been

necessary (e.g., moderator variable by conservatism domain by rigidity type).

Publication bias. The methods for assessing publication bias are limited in the multi-

level model. Hence, to assess for publication bias, we proceeded in several steps. To initially

investigate reporting and/or publication bias, we created two contour-enhanced 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

30

conservatism type. Traditionally, funnel plots were used to visualize publication bias via

asymmetrically distributed studies (i.e., as standard errors increase, the tails of the distribution of

effect sizes should widen asymmetrically under conditions of publication bias). One limitation of

traditional funnel plots, however, is that asymmetry may be attributable to substantive

heterogeneity (i.e., differing true effects across studies), rather than publication bias (Egger et al.,

1997). Thus, we employed procedures proposed by Soveri et al. (2017) that partially resolve this

limitation by, in effect, controlling for major moderating variables that might plausibly account

for substantive heterogeneity.

Next, to further probe, and potentially correct for, the possibility of asymmetry in the

effect size distribution while maintaining the three-level model, we followed the method of

entering either the standard error or variance for each observed effect size into each model as an

additional predictor (i.e., moderator). Some authors argue that this approach can be considered

closely equivalent to the PET-PEESE method (Lehtonen et al., 2018). In the PET-PEESE

method, a precision-effect test (PET) is first conducted by regressing the effect sizes on their

standard errors in a weighted least-squares regression; a statistically significant relation between

effect sizes and standard errors points to publication bias. Next, a precision-effect test with

standard error (PEESE) is conducted, which entails replacing the standard error with the

variance; relative to a PET, a PEESE better estimates the model’s unbiased effect size (i.e., the

intercept of the weighted least-squares regression) under certain circumstances (Stanley &

Doucouliagos, 2014). A PET that yields a statistically significant relation between the effect

sizes and standard errors is typically followed by a PEESE. 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.

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Results

The final dataset comprised 708 observations, 329 samples, and 173 studies (unique N =

187,612). 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). Table 2 presents the number of effect sizes at each

level of each categorical moderator; Table 3 presents descriptive statistics for each continuous

moderator7. Unless stated otherwise, all results are reported with content overlap effect sizes (N

= 139) removed.

Figure 3. Number of effect sizes for each rigidity domain and political ideology dimension.

7To 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 Figure 7). 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.

32

Table 2. Number of effect sizes for categorical moderators with k > 3. Moderator k κ

Sample .76 Students 321 Online 143 Community 110 Nationally Representative 56 YourMorals.org 17 Mixed 8 Government officials 5 Soldiers 3

Rigidity Measures .89 Self-report 493 Performance-based 170

Political Measures .79 Left-right self-placement 305 Issues 48 F-Scale 40 Party Identification 40 RWA 28 C-Scale (Modified) 25 Composite 19 Political-Economic Conservatism Scale 17 Economic Conservatism Scale 15 Cultural Conservatism Scale 14 Conservatism-Liberalism Scale 13 Social and Economic Conservatism Scale 12 Vote 11 C-Scale (Original) 11 Unspecified self-report 10 System Justification 10 S4 Conservatism Scale 7 Social Dominance Orientation 6 Current Political Beliefs Questionnaire 5 Unspecified 5 Original/ad-hoc 5 Economic System Justification 3 Core Conservatism Scale 3

Country .98 USA 417 Flanders 40 Poland 30 UK 24 Canada 22 Turkey 20 Sweden 17 South Africa 16

Italy 15 Hungary 13 Germany 6 Belgium 5

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Netherlands 4 Brazil 3

Asia 5 Europe 10 Oceania 3 South/Central America 4

Peer-review status .93 Journal 459 Dissertation 102 Unpublished 78 Replication 44 Supplementals 15 Book 7 Note. We separate Flanders from the rest of Belgium as the papers from which these effects are drawn analyze these regions separately given that there are substantial differences in the political culture in Flanders relative to the rest of Belgium.

Table 3. Descriptive statistics for continuous moderators. k M SD Median Min Max Allegiance 658 1.20 .69 1 0 2 Year 660 2004 16.47 2011 1955 2020 Age 349 28.51 10.68 27.57 18 52 % Female 394 59% 19% 57% 0% 100% WEIRD 655 .80 .13 .84 .21 .94 Donations (First) 289 .13 .39 0 -1 1 Donations (Last). 187 .34 .48 0 0 1 Frequency (First) 274 .16 .75 0 -4 5 Frequency (Last) 163 2.71 7.67 0 0 45 Sample size 706 510.52 1263 223 12 18, 817

Model 1: Global Result

Supporting the RRH in its broadest-brush predictions, our overall analysis indicated a

small statistical association between rigidity and political conservatism, r = .13, 95% CI (.11,

15). Importantly, a considerable degree of heterogeneity was present in the model, Q(565) =

4363, p < .001; H2 = 6.71; I2(2) = 66% and I2(3) = 25%. As indicated by the I2 values, only 9% of

this heterogeneity is attributable to error variance, whereas 91% is attributable to differing true

effect sizes across studies, with the degree of substantive heterogeneity in level 2 (i.e., within

samples) being somewhat greater than that accounted for by variance in level 3 (i.e., across

34

samples). Results were reduced only slightly (differences in r < .01) when outliers were

removed; thus, the subsequent analyses were based on the full dataset.

Model 2: The Multidimensionality of Political Ideology

To arrive at an estimate of the main effect for each type of conservatism, 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 conservatism, social conservatism, and general

conservatism, respectively. An omnibus test was statistically significant, F (3, 563) = 141.17, p <

.001. Residual heterogeneity was reduced but not eliminated (QE [563] = 3596, p < .001; H2 =

5.35; I2(2) = 55% and I2(3) = 34%), with more variance being attributable to within-sample

differences. Table 4 presents estimated effect sizes, alongside 95% confidence intervals, ks, Ns,

p-values, and heterogeneity statistics (the latter of which were derived by-necessity from

individual subgroup analyses involving only a single type of conservatism). All three types of

conservatism positively and significantly deviated from zero. Results were effectively unchanged

after removing outliers (change in r < .02 for all three outcomes). Each type of conservatism

differed significantly from the other two. 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 to 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).

Subgroup analyses indicated that all three types of conservatism demonstrated a

considerable degree of heterogeneity. As reported in Table 4, for both social and economic

conservatism, most of the total variance was explained by differences within studies, whereas for

general conservatism, most of the total variance was explained by differences among studies,

35

perhaps speaking to the greater specificity of the former two conservatism-types (e.g., because

measures of general conservatism are more heterogeneous than measures of economic or social

conservatism).

Table 4. The effect of political ideology dimension for rigidity-ideology relations. k n H2 I2 (2) I2 (3) r 95% CI

Economic 112 49,885 4.26 54% 33% .05 .02, .08 General 394 132,000 4.85 37% 50% .13 .12, .15 Social 98 54,259 7.10 64% 27% .20 .17., .23 Note. k = observations, n = unique participants.

Model 3: Rigidity Domains

We next sought to clarify the relations between individual rigidity domains and political

conservatism, 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.

Subsequently, to parse the heterogeneity within and across these domains, we conducted a

number of standalone meta-analytic models (i.e., subgroup analyses) with effect sizes variously

grouped by rigidity domain and individual rigidity constructs. An omnibus test suggested the

presence of moderation for domain, F (3, 562) = 128.92, p < .001. Relative to the overall model,

the residual heterogeneity, most of which was attributable to within-sample variance, was

reduced somewhat but not eliminated, with more variance being attributable to within-sample

differences (QE [562] = 3256.70, p < .001; H2 = 4.74; I2(2) = 74% and I2(3) = 14%).

Consistent with the RRH, all constructs were statistically significantly related to political

conservatism. Still, estimated effect sizes were uniformly and, in most cases, considerably

smaller than previously reported estimates (e.g., the most recent prior meta-analytic estimate for

cognitive inflexibility was r = .38, while our estimate was r = .07; Jost, 2017). See Table 6 for

point estimates, 95% confidence intervals, ks, ns, p-values, and heterogeneity statistics.

36

Removing outliers did not influence results and the PET was not statistically significant, p =

.128. Cognitive inflexibility and rigid thinking demonstrated trivial effects (i.e., rs < .07);

motivational rigidity manifested a small-to-modest positive association with political

conservatism; and dogmatism manifested a moderately-sized positive association with

conservatism. Thus, motivational rigidity manifested a significantly larger effect than both

cognitive inflexibility (t = 3.63, p < .001) and rigid thinking (t = 5.74, p < .001), and dogmatism

manifested a larger relation than all of the other three domains (ts ranged from 4.11 to 8.47, ps <

.001). Rigid thinking and cognitive inflexibility did not significantly differ from one another (t =

0.17, p = .865).

Looking at the construct rather than domain level, an omnibus test suggested the presence

of moderation, F (6, 598) = 86.45, p < .001, QE (598) =3342.79, p < .001, H2 = 4.53; I2(2) = 72%

and I2(3) = 15%. With the exception of dogmatism, which manifested a moderately-sized positive

association with political conservatism (in the presence of considerable substantive

heterogeneity), all meta-analytic estimates fell between r = .07 and r = .15.

Table 6. Subgroup analyses for rigidity-ideology relations. k n H2 I2

(2) I2 (3) r 95% CI

Rigidity Domain Cognitive Inflexibility 68 7,926 2.35 38% 54% .07 .03, .11 Motivational Rigidity 256 50,507 4.31 80% 8% .15 .13, .17 Rigid Thinking Style 144 86,410 4.81 57% 22% .07 .05, .09 Dogmatic Certitude 98 27,666 7.40 44% 48% .22 .19, .25

Rigidity Construct Closure, Order, & Structure 266 53,608 4.20 .76 .08 .15 .13, .16 Dogmatism 103 29,504 7.11 .40 .51 .22 .19, .25 (Low) Cognitive Reflection 95 39,678 4.29 .85 .01 .07 .04, .10 Cognitive Rigidity 53 6,090 1.58 .07 .72 .10 .05, .14 (Low) Need for Cognition 51 51,250 5.03 .00 .90 .07 .03, .10 Intolerance of Ambiguity 36 10,525 3.96 .82 .09 .11 .06, .16 Note. k = observations, n = unique participants.

37

The Full Model

We next regressed all non-overlap effect sizes on 12 dummy-coded moderator variables,

one for each potential combination of conservatism-type and rigidity domain (e.g., dogmatism by

economic conservatism). Residual heterogeneity was reduced further but remained present and

substantial, Q (554) = 2470, p < .001; H2 = 3.36; I2 (2) = 62% and I2 (3) = 24%, with most being

attributable to within-sample heterogeneity. The test of moderation was statistically significant,

F (12, 544) = 56.20, p < .001. Results are presented in Table 7.

All rigidity variables, except dogmatism, manifested correlations with economic

conservatism that were not significantly different from zero (rs ranged from .00 to .04). In

contrast, dogmatism demonstrated a small, statistically significant, positive correlation with

economic conservatism (r = .16). As expected, meta-analytic estimates for relations between

rigidity domains and social conservatism were considerably larger than those for economic

conservatism (rs ranged from .11 to .32). As illustrated in Figure 4, the differences between

social and economic ideology were particularly stark for all rigidity domain (difference between

rs > .10).

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Table 7. Results for the full model. k s N r 95% CI p

Economic Cognitive Inflexibility 26 8 1,402 .00 -.06, .06 = .935 Motivational Rigidity 45 28 11,933 .04 .01, .08 = .018 Dogmatism 23 18 8,691 .16 .11, .21 < .001 Thinking Style 23 21 32,560 .02 -.02, .07 = .324 General Cognitive Inflexibility 30 19 6,707 .11 .06, .16 < .001 Motivational Rigidity 170 91 36,243 .16 .14, .19 < .001 Dogmatism 58 48 18,811 .22 .18, .25 < .001 Thinking Style 98 83 64,300 .06 .04, .09 < .001 Social Cognitive Inflexibility 12 5 1,087 .11 .02, .19 = .012 Motivational Rigidity 41 27 12,347 .23 .19, .27 < .001 Dogmatism 17 13 10,232 .32 .27, .38 <.001 Thinking Style 23 22 33,386 .15 .10, .19 < .001 Note. k = observations, s = samples, n = unique participants.

39

Figure 4. Relations between rigidity variables and social and economic conservatism (with 95%

confidence intervals).

40

Moderators

We extended both the overall model (i.e., no moderators) and full model (i.e., categorical

moderators for political ideology dimension and rigidity domain) to include moderator variables

representing plausible boundary conditions of the RRH. Namely, these were political ideology

measure type, rigidity measure type, nationality, sample type, and WEIRDness.

Political Measures

As reported in Table 8 and as expected, there was significant variation in conservatism-

rigidity relations across political ideology measures in the overall model, F(32, 635) = 22.36, p <

.001, such that the effect sizes across measures (with k > 2) ranged from non-significant to

extremely large. By far the largest effect sizes were found using the F-Scale, RWA Scale, and

original Wilson-Patterson Conservatism Scale. Estimated effects for content overlap measures

were larger than the estimated overall effect excepting the System Justification Scale. Content

overlap was examined as a binary moderator variable (i.e., overlap vs. no overlap; see Figure 5),

revealing a significant moderation effect, F(2, 668) = 277.72, p < .001, such that non-overlap

political measures manifested only a small association with rigidity, r = .13, 95% CI (.11, 15),

whereas overlap measures manifested a large statistical association with rigidity, r = .39, 95% CI

(.35, .43).

41

Table 8. Subgroup analyses for all political ideology measures. k n H2 I2

(2) I2 (3) r 95% CI

Symbolic 305 140,966 6.58 72% 17% .13*** .11, .14 Policy Preferences 48 12,115 3.20 49% 34% .11*** .07, .15 Fascism Scale 40 6,387 45.49 48% 49% .54*** .41, .67 Party Identification 40 20,003 4.05 17% 70% .11*** .06, .16 Right-wing Authoritarianism 28 5,345 4.70 49% 37% .34*** .27, .41 W-P Conservatism Scale (Modernized)

25 2,809 8.29 88% 5% .05 -.06, .17

Composite 19 6,308 2.53 6% 84% .07 -.01, .14 Political-Economic Conservatism Scale

17 1,722 6.75 3% 82% .22** .09, .34

Economic Conservatism Scale 15 1,315 3.13 27% 60% .11 -.02, .25 Cultural Conservatism Scale 14 1,379 10.87 79% 13% .32*** .19, .45 Conservatism-Liberalism Scale 13 1,070 1.39 55% 8% .12*** .06, .19 Social and Economic Conservatism Scale

12 1,793 11.39 15% 79% .21* .04, .39

Vote 11 11,130 1.94 0% 69% .19*** .11, .26 W-P Conservatism Scale (Original)

11 1,902 14.21 95% 0% .37*** .21, .52

System Justification 10 2,443 7.05 74% 16% .08 -.02, .18 S4 Conservatism Scale 7 180 0 NA NA .15* .05, .25 Social Dominance Orientation 6 2,019 3.61 41% 41% .17* .03, .30 Economic System Justification 3 919 1.28 36% 36% .18 -.09, .46 Note. k = observations, n = unique participants.

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Figure 5. Comparison of overlap vs. non-overlap effect sizes.

Further, after excluding content overlap measures, political ideology measure type

significantly moderated the relation between rigidity and conservatism in the full model (i.e.,

controlling for political ideology dimension and rigidity domain), F (16, 533) = 3.29, p < .001;

H2 = 2.98. Still, results suggested little heterogeneity across commonly used measures of

political ideology in contemporary political psychology. Relative to symbolic ideology, which

comprised the largest proportion of effect sizes, only 2 of the 16 measures (with k > 2) yielded

significantly different point estimates, one of which was a measure of social conservatism,

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specifically, and the other of which was our catch-all category for self-report measures that were

not specified in the study text. That so few differences arose across diverse measures such as

vote choice, party preference, issue preferences, and various common self-report measures of

ideology suggests that variation across non-overlap measures of ideology is not a substantial

source of heterogeneity (results held after controlling for rigidity-type and ideology dimension).

Nationality

A significant moderation effect was present for nationality in the overall model, F (18,

523) = 19.57, p < .001. 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 also collapsed countries with k < 2 into European,

South/Central American, Asian, and Oceanian categories. Results are presented in Table 9 and

Supplemental Figure 1. Heterogeneity was reduced, but remained high, Q(523) = 3476, p < .001;

H2 = 5.43; I2(2) = 66% and I2(3) = 22%. 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 r(USA) = .15, 95% CI (.13, .17) and

r(Non-USA) = .09, 95% CI (.07, .12).

As visualized in Figure 6, the difference between the USA other countries appeared to be

driven by differences across economic ideology, such that allowing the binary USA vs. non-USA

factor to interact with political ideology revealed a significant interaction effect, F(2, 536) =

5.46, p = .005. Specifically, effects were relatively consistent across US and non-US samples for

social ideology (r[USA] = .21, 95% CI [.15, .26]; r[non-USA] = .22, 95% CI [.18, .25]; F =

.070, p = .792); only modestly, albeit significantly, different for general ideology (r[USA] = .15,

95% CI [.13, .18]; r[non-USA] = .11, 95% CI [.08, .14]; F = 5.64, p = .018); and substantially

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and significantly different for economic ideology (r[USA] = .10, 95% CI [.06, .13]; r[non-USA]

= -.03, 95% CI [-.07, .02]; F = 16.34, p < .001). Controlling for rigidity domain (and the

interaction between rigidity domain and US vs. non-US) did not reduce the strength or

significance of this interaction effect.

Figure 6. Social and economic ideology’s correlation with rigidity in the USA vs. other

countries.

45

Table 9. Meta-analytic results for nationality. Economic Social General

k r 95% CI k r 95% CI k r 95% CI Asia 0 – – 0 – – 5 -.01 -.13, .11 Belgium 0 – – 1 .41 .13, .69 1 .17 -.12, .47 Brazil 1 .11 -.14, .37 1 .19 -.12, .49 1 -.05 -.34, .25 Canada 4 .02 -.11, .15 4 .09 -.08, .26 14 .04 -.05, .14 Europe 1 .04 -.16, .24 1 .19 -.08, .46 8 .05 -.06, .16 Flanders 10 .04 -.04, .11 8 .21 .09, .34 21 .29 .19, .39 Germany 0 – – 0 – – 6 .11 -.01, .23 Hong Kong 1 -.09 -.31, .13 1 .12 -.16, .40 1 .05 -.22, .31 Hungary 0 – – 0 – – 3 -.11 -.25, .04 Italy 2 .03 -.14, .19 1 .19 -.10, .48 9 .17 .08, .26 Netherlands 0 – – 0 – – 3 .14 -.01, .29 Oceania 1 -.13 -.39, .14 1 .57 .28, .87 1 .17 -.12, .47 Poland 4 -.19 -.31, -.08 4 .28 .13, .44 21 .18 .08, .28 South Africa 15 -.02 -.10, .06 0 – – 1 .28 -.03, .58 South/Central America 0 – – 0 – – 4 .04 -.11, .18 Sweden 5 -.01 -.12, .10 1 .13 -.14, .40 9 .03 -.09, .15 Turkey 3 .01 -.12, .12 2 .15 -.04, .35 11 .13 .06, .21 UK 1 .12 -.18, .42 1 .29 -.08, .66 15 .08 .01, .16 USA 62 .09 .06, .12 58 .22 .18, .26 213 .15 .13, .17 Note. k = observations. Bolded indicates p < .01.

Sample-type

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, 555) =

66.63, p < .001 (see Table 10 and Supplementary Figure 2). The smallest effect size was for

samples matched to the demographic characteristics of the national population (r = .03, 95% CI

[-.01, .07]), and the largest effect size was for government officials (r = .24, 95% CI [.09, .39]).

Heterogeneity was reduced, but remained high, after accounting for sample-type, Q(555) = 3747,

p < .001; H2 = 5.67; I2(2) = 75% and I2(3) = 14%. Controlling for ideology and rigidity (i.e., the

46

full model) revealed similar results, F (7, 550) = 9.93, p < .001, H = 2.88. 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 (r = +.06, 95% CI [+.02,

+.10], k = 266), online samples (r = +.09, 95% CI [+.05, +.13], k = 135), yourmorals.org (+.06,

95% CI [+.00, +.11], k = 17), community samples (r = +.14, 95% CI [+.10, +.19], k = 86), and

government officials (r = +.14, 95% CI [.01, .28], k = 5).

Table 10. Political Measure Type as a Moderator of the Full Model

r 95% CI

(lower) 95% CI (upper)

Predicted Effect (for General Conservatism and Cognitive Inflexibility) Sample Type Community .16 *** .11 .21 Government Officials .16 * .03 .29 Mixed .03 -.07 .13 Nationally Representative .02 -.04 .07 Online .11 *** .07 .15 Students .08 *** .04 .11 YourMorals.org .08 * .02 .13

Change in Estimated Effect for Each Level of the Moderators Change in Predicted Effect Across Levels of Political Conservatism (Reference = General Conservatism) Economic -.08 *** -.11 -.05 Social +.07 *** .04 .10 Change Across Levels of Rigidity (Reference = Cognitive Inflexibility)

Dogmatism +.14 *** .10 .18 Motivation +.06 ** .02 .10 Thinking Style -.01 -.05 .04 Note. * p < .05; ** p < .01; *** p < .001.

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Self-report vs. Performance-based Rigidity Measures

Consistent with the findings of Van Hiel et al. (2016), 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 (r = .06, 95% CI [.03, .09])

but self-reports manifested a small statistical association (r = .16, 95% CI [.14, .18]). It is worth

noting, however, that relations for both types of measures were small.

WEIRDness

As shown in Table 11, nations categorized as Western and/or rich demonstrated

significantly larger conservatism-rigidity correlations than non-Western and/or non-Rich nations

in the overall model. Further, when standardized scores for Industrialization, Education, and

level of Democracy were entered as continuous moderators of the relation between conservatism

and rigidity, Education accounted for a significant degree of residual heterogeneity, whereas

Industrialization and Democracy did not. After controlling for ideology and rigidity type,

however, WEIRD estimates did not account for a significant degree of residual heterogeneity,

either individually or simultaneously (see Supplemental Table 2 for details).

Table 11. Results for WEIRDness. Categorical Moderators

k n r 95% CI Test of Moderation

Western 514 86,607 .14* .12, .15 F(2, 537) = 143.10, p < .001 Non-Western 25 6,324 .08* .01, .14

Rich 492 85,643 .14* .12, .16 F(2, 537) = 149.38, p

< .001 Non-rich 47 7,228 .07* .02, .11 Continuous Moderators

95% CI B 95% CI p

Intercept .12, .15 .13* .12, .15 < .001

48

Education .01, .04 .03* .01, .04 .002

Industrialization -.03, .02 -.005 -.03, .02 .712

Democracy -.03, .02 -.0004 -.03, .02 .973 Note. k = observations, n = unique participants. * indicates p < .01.

Publication Bias

We first examined the distribution of study outcomes via two contour-enhanced funnel

plots, using the methods described (see Figure 7). These analyses were conducted with content

overlap effect sizes removed from the study pool, as they 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. The outliers that remained were relatively symmetrical. As such, neither

plot provided clear evidence of publication bias. Nevertheless, only 34.5% of studies were

sufficiently powered to detect an effect size of ρ = .10, while a true effect of ρ = .15 would be

necessary to achieve median statistical power of 66% (see Supplemental Figure 3).

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Figure 7. Contour enhanced funnel plots.

PET analysis indicated that there was no statistically significant association between

effect sizes and their standard errors for any of the four models (i.e., overall, political ideology

dimension, rigidity domain, and full model) providing little evidence of publication bias. Still, a

significant moderation effect was present for publication-type in the overall model (F[2, 563] =

161.43, p < .001), such that relative to effect sizes drawn from initial peer-reviewed journal

articles (r = .14, 95% CI [.13, .16]), all other effect sizes were smaller (r = .11, 95% CI [.09,

.14]). This result held true in the full model, such that non-peer-reviewed studies were

significantly smaller in magnitude than those from peer reviewed studies, F (1, 584) = 4.66, p =

.031 with a relatively small difference in effect size, r = -.03, 95% CI (-.05, -.00), suggesting the

potential presence of publication bias in favor of the RRH.

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Table 12. Moderation results for publication status. r 95% CI p Test of Moderation

Relative to Journal: F (5, 580) = 1.18, p = .318

Dissertation -.03 -.07, .01 .090

Book -.02 -.11, .07 .646

Replication -.05 -.10, .01 .085

Supplementals -.01 -.08, .07 .817

Unpublished -.02 -.05, .02 .348 F (1, 584) = 4.66, p = .031

All Non-Journal -.03 -.05, -.00 .031

Allegiance Associations

In the overall model, first-authors’ political donations significantly moderated the relation

between conservatism and rigidity, F (3, 286) = 55.44, p < .001. This result was not consistent

with prediction, however, in that first-authors who donated to the political left (r = .10, 95% CI [-

.06, .15]) did not significantly differ from those who donated to the political right (r = .09, 95%

CI [-.03, .22]), whereas non-donators reported the largest effect sizes (r = .15, 95% CI [.13, .17]).

Authors’ theoretical allegiance was also a significant moderator F (3, 552) = 102.62, p < .001.

Pro-RRH papers (r = .17, 95% CI [.14, .19]) reported the largest effect sizes, followed by anti-

RRH papers (r = .12, 95% CI [.10, .14]), and neutral papers (r = .10, 95% CI [.06, .14]).

Allegiance effects remained significant after controlling for heterogeneity across political

ideology and rigidity domain, such that first-authors’ political donations significantly moderated

the relation between conservatism and rigidity, F (2, 256) = 3.82, p = .023. Consistent with our

expectations, relative to first authors who had not donated to political causes, first authors who

had donated to right-wing causes reported effect sizes that were significantly smaller (r = -.16 [-

.28, -.04], p = .007). In contrast, authors who donated to left-wing causes reported effect sizes

that did not statistically differ from non-donators (r = -.02 [-.07, .03], p = .382). Last authors who

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donated to left-wing causes did not report effect sizes that differed significantly from those who

had not donated (r = .02 [-.03, .08], p = .42). No last authors had donated to right-wing causes.

Neither donation amount nor donation frequency accounted for a statistically significant amount

of variance in the full model. Theoretical allegiance also significantly moderated the relation

between conservatism and rigidity in the full model, F (3, 548) = 6.16, p < .001. Pro-RRH

authors reported significantly larger effect sizes than neutral authors (r = +.05, 95% CI [.02, .08],

t = 3.34, p < .001) and anti-RRH reported smaller effect sizes than neutral authors (r = -.03, 95%

CI [-.07, .01], t = 1.55, p = .123).

Discussion

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 conflagratory scientific debate. The present meta-analytic review, which spanned

303 independent samples, 607 effect sizes, 35 nations, and more than 180,000 unique

participants, (1) provides a precise estimate of the magnitude and direction of the relation

between political conservatism and rigidity, (2) catalogues the extent to which effect sizes of

individual studies in the literature are distributed around said estimate, and (3) elucidates

moderator variables that account for these differences across studies. We hope that our findings,

which we discuss below, herald the beginning of the end of the longstanding controversy

surrounding the RRH.

Major Findings: A Birds-eye View

Broad theoretical accounts of ideological asymmetries (or symmetries) in rigidity have

masked complex and often-divergent—yet conceptually fertile—patterns of relations in the

literature. Most notably, correlations between economic conservatism and rigidity variables were

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almost uniformly not statistically different from zero, whereas social conservatism and rigidity

variables were moderately-to-strongly positively correlated. Thus, the RRH appears to apply to

social, but not economic, conservatism. Further, estimated effects were inconsistent across levels

of rigidity-related phenomena: population estimates were marginal for rigid thinking styles and

basic cognitive mechanisms and processes, larger for motivations to avoid complexity and

ambiguity in everyday life, and quite large for ideological rigidity (dogmatism). Accordingly, the

political left and right evince asymmetrical rigidity-related motivations yet closely symmetrical

cognitive architecture and thinking styles. Dogmatism appears to be a special case, with

conservatives seeming to be clearly more dogmatic than members of the political left.

Complicating this picture, methodological moderators (e.g., type of sample or nationality)

frequently accounted for additional variance, suggesting that many previous findings have been

amplified by, or are even contingent upon, systematic error variance (or, at the very least, do not

generalize to critical environmental and psychometric modalities). For instance, nationally

representative samples did yield significant effects, and the meta-analytic estimate for economic

conservatism was negative, albeit non-significant, in non-United States samples.

Depending on one’s theoretical perspective, these findings might be construed as a

demonstration of either (a) the RRH’s limited predictive accuracy and generalizability, which are

not commensurate with the model’s strong claims, or (b) the strongest evidence to date that

certain strains of conservatism tend to be psychologically affiliated with certain strains of

rigidity, even when accounting for methodological bias. We have a somewhat different

assessment. Namely, the model, which is now over 70 years old, has outlived its heuristic value.

Political psychology has grown beyond comparisons of the “right” and “left”—indeed, that

differences exist between any two groups, let alone demographically and culturally opposed

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groups, is in some critical sense trivial. If we are interested in the psychological causes and

correlates of political ideology, we will do well to articulate when politics and cognitive-

motivational processes intersect—and why they do or do not—rather than if differences exist

between the boxes of “left” and “right”. What follows are several places to begin this

conversation.

A Classic Social-Psychological Approach

For starters, we might consider returning to our social-psychological roots and recall

Lewin’s (1936) classic formula describing behavior (B) as a function (f) of the person (P) and

their environment (E), which includes both physical and social influences: B = f(P, E).

Our assessment of the RRH literature is that it has overly focused on the “P” in that equation—

assuming that rigidity is fundamentally different between persons on the left and right and

attempting to explain why that difference exists. Less work has focused on the “E” in the

equation and less still has investigated the “f” (i.e., function), namely, the ways in which people

interact with their environment.

Applying such a socioecological lens (i.e., accounting for physical, societal, and

interpersonal environments; Oishi & Graham, 2010) allows for rigidity to be conceptualized as

an emergent property—stemming from certain configurations of traits, environments, and the

ways in which they interact, rather than existing in a social or cultural vacuum. Notwithstanding

the degree to which people actively create physical and psychological environments compatible

with their dispositional drives and traits (Bouchard, 2016), this socioecological approach allows

for new predictions concerning when and why rigidity varies across the political spectrum,

including instances of rigidity-of-the-left and rigidity being equally high or low across the left

and right. In fact, these hypotheses may be the most interesting, as they are potentially

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surprising. Theorizing about these surprising associations is not due to a lack of evidence that

they exist. The data across this meta-analysis reveal a non-negligible number of negative

correlations between conservatism and rigidity in the distributions of effect sizes, especially for

non-overlap measures (Figure 4) and when looking at economic (vs. social) conservatism (Figure

5) in non-US (vs. US) samples (Figure 6). Rather than treating these effects as noise, an

explanatorily powerful psychology of political ideology would aim to explain rigidity on both

left and right and how it manifests across diverse contexts. Doing so would not undermine any

true main effect of conservatism; indeed, no cross-national meta-analytic estimate presented here

was significantly negative. But if no one is looking for nuance, nuance is unlikely to be found.

Social, But Not Economic, Conservatism

Despite the popularity of the left vs. right political spectrum among researchers, the

psychological antecedents of political ideology are better understood in the context of their

natural correspondence to differing social and economic ideologies than in terms of a global left

vs. right distinction. If mechanisms specific to social conservatism drive conservatism-rigidity

relations, then epistemic features that are common to social and economic conservatism are of

dubious explanatory value. Indeed, in light of our findings, any conceptual resonance between

the philosophical tenets of broad-based political conservatism (e.g., system justification) and

psychological characteristics (e.g., rigidity) are probably not relevant to the question of why

people adopt conservative beliefs. 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 (e.g., both ostensibly promise to justify extant hierarchies and systemic

inequalities). Hence, analyzing the epistemic differences between social and economic

conservatism may be as or more informative than comparing across the political right and left.

55

To this end, how do social and economic conservatism epistemically diverge? Malka and

colleagues (2017) speculate that motivations for governmental protection (vs. motivations for

individual freedoms) may lead people to adopt both culturally right-wing attitudes and

economically left-wing attitudes (in the absence of countervailing environmental pressures; see

also Lefkofridi et al., 2014). Whereas free-market (i.e., right-wing) economic ideology leaves

individuals to be buffeted by the harsh winds of uncertainty, competition, and entropy, left-wing

economic ideology offers a safeguard. Similarly, whereas left-wing social ideology embraces

difference and change as a force for good—implicitly confronting adherents with how much of

the world is unfamiliar and uncertain—traditionalist, socially conservative attitudes assure

adherents that there are clear answers to life’s stickiest questions (e.g., good and bad, life after

death), and create rigid taboos that leave little room for thoughtful deliberation and personal

responsibility (Popper, 1945, p. 164). These epistemic gaps across social and economic

conservatism offer an explanatory lens with which to understand psychological differences

between social and economic conservatives.

Where do these findings leave us? Insofar as economic and social ideology are

sometimes strongly correlated (e.g., in certain educated subsets of the U.S. population; Federico

& Malka, 2021), the field should no longer presume that psychological factors drive this

coherence—not least because social and economic ideology are nearly orthogonal within many

countries around the world (Malka et al., 2019). One straightforward implication of this

conclusion is that there is considerable downside to political psychologists focusing on a

unidimensional conservative vs. liberal ideology construct (e.g., Feldman & Johnston, 2014).

Further, many canonical findings in the ideological asymmetries literature are based on global

assessments of political ideology. As one of numerous examples, studies of neurophysiological

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asymmetries in political ideology have relied overwhelming on global measures (e.g., Nam et al.,

2018; Oxley et al., 2008; Smith et al., 2011). Another famous pillar of political psychology—the

notion that trait openness to experience is related to conservatism—is also worth reexamining.

Vitriol et al. (2019) found that Openness within the Five Factor Model is significantly negatively

related to global political conservatism in a meta-analytic summary of 10 nationally

representative datasets (N = 75,994) with an effect size of r = -.10. If, as with rigidity, these

effects are driven by social conservatism (e.g., we might presume a population effect of r = -.25),

they may be null or even positive for economic conservatism (e.g., a population effect of r =

.05).

These considerations illustrate a broader conceptual point that we will deliberately

underscore: The complex reality of belief systems outpaces present psychological knowledge.

Different components (e.g., social vs. economic) of a single belief system (e.g., conservatism)

can satisfy competing or even opposing psychological causes, leading a highly psychologically

heterogeneous group of individuals to proclaim their adherence to what is, nominally, the same

ideology. Further, in the absence of consistent directional bottom-up (i.e., psychological)

influences on entire belief systems, top-down (i.e., environmental) effects—such as the

information environment and its associated partisan pressures, group memberships, and the

like—may be especially salient. As we argue above, adopting approaches that treat the

environment as a unit of analysis with independent influence over psychological outcomes and

behaviors may help to shed light on the degree to which ideology emerges from the dynamic

interaction between people and the worlds they inhabit (see Fiedler, 2007; Fiedler & Wänke,

2009). Moreover, it is increasingly plausible that far-right, far-left, and religiously

fundamentalist ideologies are in part caused by the same or similar psychological mechanisms

57

(e.g., Zmigrod, 2021) while differing dramatically from one another in other ways (e.g.,

Federico, 2021).

Parsing and classifying these variegated influences on ideology is a critical task that we

believe has been obscured by a dominant focus on the left-right spectrum. As such, we suspect

that when focusing specifically on organic links between dispositional attributes and politics,

researchers should approach politics at the level of individual beliefs and policy preferences,

such as opposition to gun-control or support for paid paternity leave, insofar as they are more

likely to have epistemic commonalities that are shared across members of the public and,

consequently, reasonably accessible psychological causes and correlates. At the same time,

researchers should also focus on the top-down influences that bring these individual attitudes

together into a belief system.

Symmetrical Cognitive Architecture, Asymmetrical Motivations

The predominant version of the RRH is rooted in motivated social cognition, suggesting

that people who are especially averse to uncertainty, ambiguity, and risk feel compelled to

defend the status-quo and systematic cultural and economic hierarchies as just and necessary by

adopting ideologies that imply as much, such as conservatism (Jost & Hunyady, 2005; Wakslak,

Jost, Tyler, & Chen, 2007). Although we find it likely that individuals gravitate toward belief

systems out of motivation to satisfy psychological needs, it is also likely the case that a broader

profile of individual differences shape and influence one’s willingness and ability to engage

with, understand, and arbitrate between ideological options. Indeed, a variety of cognitive and

meta-cognitive traits appear to foster different elements of ideological thinking, such as

extremism and propensity for violence (Zmigrod, 2020). Critically, this distinction (i.e., needs

vs. other individual difference domains) bears considerably on the psychological mechanisms

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that might plausibly underlie ideology-rigidity relations. Needs connote one set of mechanisms,

thinking styles connote a largely separate set, and so on. Thus, distinguishing between these

constructs allows us to falsify (though not confirm) the various causal “stories” of the RRH,

whereas collapsing across these rigidity variables obscures more than it illuminates.

For instance, cognitive psychologists have posited that dispositional tendencies towards

intuitive thinking yield a special affinity for conservative political principles, suggesting a

principally cognitive mechanism underlying the RRH (Talhelm et al., 2015). Conservatives may

be more intuitive (less analytic) thinkers because they tend to come from cultures with tight

social bonds and many interconnected groups, such as churches and fraternities, which causes

them to think more holistically (Talhelm et al., 2015; cf. Kahan, 2012). Our data provide little

support for this perspective. Although cognitive reflectivity (analytic thinking) was modestly

negatively related to social conservatism, few other significant effects were present.

Moreover, modern neuropsychological accounts of cognitive inflexibility (Cools &

Robbins, 2004; Diamond, 2013) have been leveraged to characterize differences between the

political left and right (e.g., Zmigrod, 2020). This literature is often taken to suggest that leftists

and rightists differ in their basic cognitive architecture. For instance, one finding indicates that

conservatives and liberals favor distinct working memory processes (i.e., inhibition and

updating, respectively), which may account for underlying ideological asymmetries in mental

flexibility (Buechner et al., 2020). Yet we found only limited evidence for this possibility.

Although general and social conservatism manifested a small positive correlation with

neuropsychological measures of cognitive inflexibility, economic conservatism yielded a non-

significant and negligible point estimate. Hence, rightists and leftists do not appear to differ

greatly in their ability to change perspectives spatially and interpersonally, shift approaches

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when one’s solution to a problem is not working, inhibit one’s preexisting perspectives to store

different perspectives in working memory, change priorities, and/or take advantage of

unexpected opportunities (Cools & Robbins, 2004; Diamond, 2013).

Our results for motivational rigidity provided greater support for both the RRH and the

popular conceptualization of political conservatism as motivated social cognition (Jost et al.,

2003), which focuses on motivational needs for certainty (e.g., need for cognitive closure).

Namely, our findings revealed a moderately-sized positive correlation between motivational

rigidity and social conservatism. By the same token, the correlation between motivational

rigidity and economic conservatism quite small; as such, motivational needs for certainty appear

to have little explanatory power for economic ideology. Economic conservatism may be subject

to a set of motivational dispositions that remain obscure—a possibility that is a fruitful focal

point for future work.

Having evaluated the degree to which conservatives and liberals differ in their

motivations, thinking styles, and cognitive architecture, we now turn to rigidity in one’s beliefs

(i.e., dogmatism), where there was the greatest degree of support for the RRH. Specifically,

dogmatism manifested a positive relation with both economic and social conservatism, clearly

supporting the RRH. We consider three potential interpretations for this finding. First,

conservatives may be more dogmatic than liberals. This is both perhaps the most likely

possibility and well-worn ground that many other scholars have thoughtfully tread (e.g.,

Altemeyer, 2002; Duckitt, 2009; Crowson, 2009). Conservatives tend to closely embrace

absolutist and intuitive ideas and practices, which is quite congenial to dogmatism (Jost et al.,

2003). Second, 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; see

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Stanovich & Toplak, 2019). Thus, our findings 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 a major step towards resolving the magnitude of any such error variance.

Third, social conservatives may be motivated to describe and understand themselves as

dogmatic. Social conservatism arguably reflects the values of what Popper described as the

closed society: “held together by semi-biological ties—kinship, living together, sharing common

efforts, common dangers, common joys, and common distress…its institutions, including its

castes, are sacrosanct—taboo” (pp. 165-166). In this environment, dogmatism offers individuals

protection from ostracism and protects their group identity from the spread of “dangerous”

ideologies and practices, which ostensibly act as harmful destabilizing forces. Mirroring this

pattern, the “binding” moral foundations favored by conservatives (i.e., “binding individuals into

roles and duties in order to constrain their imperfect natures”) align with positive views towards

dogmatism (i.e., it upholds the larger group’s core beliefs), whereas “individualizing”

foundations favored by liberals (i.e., “teaching individuals to respect the rights of other

individuals”) align with negative views towards dogmatism (i.e., it devalues the perspectives of

other people). Arbitrating between these three possibilities is an important avenue for future

research.

In sum, our findings indicate that thinking styles and cognitive inflexibility are of dubious

relevance to left-right differences in political ideology, motivational rigidity may play a modest,

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or even notable role in shaping ideology, and dogmatism is a clearly delineated axis of difference

between the political left and right.

Self-report vs. Behavioral Measures of Rigidity

Consistent with Van Hiel and colleagues’ (2010, 2016) meta-analytic reviews,

performance-based measures of cognitive rigidity differed considerably from self-reports, with

self-reports yielding effects r = .16 larger than performance-based measures after accounting for

variance attributable to rigidity construct and ideology type. Given that self-reports constituted

approximately 70% of all effect sizes in our review, and that previous reviews presumably

contained a similar proportion of self-reports, our replication and extension of the finding to four

additional constructs suggests yet another potentially important boundary condition to the RRH.

Still, what might account for such a dramatic split? Notwithstanding the possible

influence of method artifacts such as content overlap, common method variance, semantic

overlap, and/or acquiescence response bias (e.g., Peabody, 1961; Rokeach, 1967; Rorer, 1965),

one reasonably straightforward interpretation has been advanced by Kahan (2016), who noted

that idiosyncrasies of information processing are not easily accessible to introspective

observation, such that “there is thus little reason to believe a person’s own perception of the

quality of his reasoning is a valid measure of it” (p. 5). 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). A recent

meta-analytic review of the relation between self-report and neuropsychological tests of rigidity

found no significant relation, leading the authors to conclude that self-report tests are not valid

proxies for cognitive flexibility (Howlett et al., 2021). Differences between the left and right on

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self-report measures of rigidity, absent equivalent differences on behavioral measures, may

corroborate the possibility that self-report measures of cognitive style differ substantially from

behavioral measures in their validity—and that the evidence for the RRH, which is largely

predicated on self-reports measures, is far less compelling than it initially appears.

Another plausible explanation for the self-report vs. performance-based split is more

charitable to the RRH. Ostensibly “objective” measures of cognitive style may be unreliable or

otherwise demonstrate poor construct validity, perhaps because of their high situational

specificity and resulting poor replicability (e.g., Epstein & O’Brien, 1985). Most trait-behavior

correlations famously have a ceiling of roughly .30 or at best .40 when the measured behaviors

are not aggregated across multiple situations (Kenrick & Funder, 1988; Mischel, 1968). Studies

examining a wide-range of self-reports and performance-based measures of rigidity within a

latent variable framework, which to our knowledge are not present in the literature, are likely

necessary to resolve this question. Still, the limited pool of evidence suggests that performance-

based measures of rigidity tend to overlap in expected directions with self-report measures of

rigidity (e.g., scores on the CRT are correlated .18 to .21 with need for cognition; Burger et al..

2020). Such results provide modest support for interrelations among these measures while

raising questions concerning the extent of their convergent validity.

Of course, perhaps the most likely possibility is that behavioral measures and self-reports

each have their own sets of psychometric strengths and weaknesses and detect related but distinct

constructs. Future research investigating the reasons for left/right differences across behavioral

and self-report measures of cognitive style may, therefore, be of considerable utility in clarifying

the psychological processes underlying political ideology.

National- and Sample-level Differences in Rigidity-Conservatism

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Prominent studies have argued that an overreliance on WEIRD, politically engaged

samples in the literature has biased conclusions in favor of the RRH due to “reversal effects,”

whereby ideologically constrained environments (i.e., those with a strict, unidimensional

normative structuring of political ideology) lead highly politically engaged individuals to adopt

hierarchically structured political attitudes (e.g., Malka et al., 2017). Hence, examining the RRH

disproportionately in politically engaged populations might obscure differential relations across

economic and social conservatism. We could not test this possibility directly in the present

review, as too few studies reported participants’ levels of political engagement. Still, moderator

analyses for sample composition provided indirect support for this hypothesis (e.g., Malka et al.,

2014). In particular, the relation between conservatism and rigidity was typically non-significant

in nationally representative samples and was smaller in such samples than in all other sample

types. As such, scholars’ reliance on results drawn from highly engaged samples (i.e., student

and online samples comprised approximately 70% of effect sizes in the current review) may have

resulted in estimates favoring the RRH. Perhaps running counter to this interpretation, however,

is that sample WEIRDness was not a significant moderator in the full model. Further efforts to

conduct research outside of the Western political landscape are needed to clarify the extent to

which political engagement within and across cultures bears on the RRH.

Relatedly, critics of the RRH have noted that an ideological restriction of range in U.S.

samples may result in spurious support for the RRH in the presence of underlying curvilinear

effects (Greenberg & Jonas, 2003). Specifically, given that far-left and far-right ideological

extremism is associated with rigidity (e.g., Harris & Van Bavel, 2020), and the U.S. has many

more right-wing extremists than left-wing extremists, only the rightward half of the rigidity-

extremism curve would be clearly visible in most U.S. samples. Of course, one could view such

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a lack of left-wing extremism as evidence in favor of the RRH. But it may be worth comparing

rigidity-conservatism relations across nations that are more balanced in the degree to which

norms lean towards capitalism vs. communism. Indeed, Canada, Hungary, Japan, Sweden, and

UK samples demonstrated significantly smaller effects than US samples, whereas only Spanish

samples demonstrated larger effects than the US. As 417 of the 708 effect sizes in the present

review were drawn from U.S. samples, the present review is not immune from this issue.

Delving further into the nation-level findings, in recent years, relatively radical socialist

parties have seen growing popularity in a handful of European Union countries (e.g., the Dutch

Socialist Party; Germany’s “die Linke”). Countries such as Canada, where, in contrast, far-left

and far-right politics have never been a prominent force (Ambrose & Mudde, 2015), may also be

informative to examine. To that end, neither the Netherlands (r = .10, 95% CI [-.05, .26], k = 4)

nor Germany (r = .10, 95% CI [-.13, .24], k = 6) showed significant effects for general

conservatism. Canada similarly demonstrated non-significant effect for general conservatism (r =

.05, 95% CI [-.01, .11], k = 14). Countries currently dominated by conservative parties, such as

Turkey (r = .13, 95% [.10, .16], k = 13) and Poland (r = .20, 95% CI [.15, .25], k = 21), however,

tended to show significant conservatism-rigidity effects (although, notably, results for economic

conservatism were non-significant and slightly negative in Turkey and significant and negative

with a moderately-sized point estimate in Poland). Studies carried out with citizens of presently

socialist countries, such as China, Cuba, Laos, Algeria, Venezuela, or Nicaragua, are not

presently available in the literature. Still, few countries evinced negative point estimates,

suggesting that the RRH may be relatively robust in many nations.

How Biased is the RRH Literature?

Semantic Overlap

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Our results demonstrate that rigidity-related content in popular measures of political

conservatism has inflated previous meta-analytic estimates. Jost et al. (2017) meta-analytically

estimated the overall relations between political conservatism, on the one hand, and dogmatism

and cognitive/perceptual rigidity, on the other, to be r = .51 and r = .38, respectively, and Van

Hiel et al. (2016) estimated the relation for cognitive/perceptual rigidity to be r = .24 (they did

not examine dogmatism as an outcome). In contrast, after removing criterion-contaminated

measures such as the F Scale, RWA Scale, and C Scale from our study pool (i.e., leaving only

relatively non-overlap measures of ideology, such as policy preferences or self-identification as a

liberal vs. conservative), dogmatism and cognitive rigidity’s relations were far smaller. This

discrepancy is consistent with the large moderator effect we found for content overlap—the use

of such measures increased effect sizes with a magnitude of r = .26. Hence, previous authors’

reliance on measures imbued with rigidity content has almost certainly distorted the field’s

conclusions in favor of the RRH.

These results, and the problem of overlap more broadly, can perhaps be understood as a

function of theory-ladenness (see Brewer & Lambert, 2002). The interdependence of theory and

measurement in psychological science (i.e., one needs to have an initial theory or at least a

conceptual sketch of a construct to design a measure of it) may limit opportunities to identify

biases that are simultaneously embedded in a measure and the theory underlying said measure.

Although this paradox can be resolved by adopting multi-method approaches, theory-ladenness

has rarely been accounted for in political psychology.

Moreover, our meta-analytic estimates do not account for other potentially important

forms of semantic content overlap, such as the contaminating influence of content related to

political conservatism in measures of rigidity. The Gough-Sanford Rigidity Scale, for instance,

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includes items that almost certainly reflect social conservatism, such as “I never miss going to

church.” Based on our review of the literature, the Gough-Sanford Scale is far and away the most

used self-report measure of cognitive rigidity. Hence, “true” effect sizes for conservatism-

rigidity relations may be even smaller than we have estimated, and are perhaps even barely

distinguishable from zero, although future work using non-contaminated measures is needed to

better characterize this association.

Publication Bias

By and large, our meta-analytic examination provided mixed evidence for publication

bias in the RRH literature. Admittedly, however, the options for evaluating publication bias via

the multi-level model are limited. Although PET-PEESE and examination of the funnel plots did

not reveal publication bias, both approaches are flawed in important ways (Gervais, 2015; Lau et

al., 2006), especially under conditions of high effect size heterogeneity (Renkewitz & Keiner,

2018). Arguably the most direct means of probing publication bias, a moderator analysis for

published vs. unpublished effect sizes, revealed significantly higher effect sizes in published than

unpublished manuscripts. Replication studies, particularly, reported the smallest overall effects.

This finding is consistent with Kvarven et al. (2020), who found that meta-analytic effect sizes

are typically three-times larger than preregistered replications carried out across multiple

laboratories (and that methods of correcting meta-analyses for bias do not improve meta-analytic

results). Accordingly, given our overall meta-analytic estimate of r = .13, a multi-lab replication

of the RRH might be expected to produce a point estimate of roughly r = .04 to .05.

Further, assuming a true effect of r = .10, only 34.5% of studies in our meta-analytic pool

were sufficiently powered to detect the effect reliably. This finding provides further evidence

that our overall meta-analytic estimate is likely to be inflated. Issues of low statistical power may

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also explain the large degree of heterogeneity that was present after accounting for moderator

variables.

Political Bias

In the wake of psychology’s replication crisis, political bias has been highlighted as a

potentially important source of non-replicable research findings (e.g., Jussim et al., 2016; cf.

Reinero et al., 2019), perhaps because the ratio of liberals to conservatives within social and

personality psychology has been estimated from 8:1 to nearly 100:1 (Haidt, 2011; Inbar &

Lammers, 2012; Langbert, Quain, & Klein, 2016; von Hippel & Buss, 2017). Such a political tilt

by itself may not be worrisome if scholars can maintain a reasonably objective stance toward

politically-tinged scientific claims that activate their congeniality bias, a variant of

confirmation bias in which individuals are especially likely to accept assertions that accord with

their broader worldviews (Hart et al., 2009). Still, in a survey of 506 members of the Society for

Personality and Social Psychology, Inbar and Lammers (2012) found that a substantial

proportion of left-leaning respondents were openly willing to discriminate against right-leaning

applicants in hiring, symposia invitations, journal reviews, and grant reviews. This finding is

consistent with past research suggesting that grant proposals and Institutional Review Board

submissions are sometimes rejected due to their political implications (see Ceci & Williams,

2018, for a review).

Our results provided provisional although hardly conclusive support for this possibility.

Although authors’ theoretical allegiance and political ideology were significant moderators of

the relations between conservatism and cognitive rigidity in the expected direction, results were

modest in magnitude. Still, pro-RRH authors reported larger effect sizes and anti- RRH authors

reported smaller effect sizes. Similarly, authors who donated to right-wing organizations

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reported smaller effect sizes than both non-donators and authors who donated to left-wing

organizations, although non-donators and left-wing donators did not significantly differ from one

another. We can envision plausible, mutually compatible, interpretations for this latter result, one

of which is consistent with the RRH and one of which is not. First, right-wing authors may be

more susceptible to ideological bias than other authors (Baron & Jost, 2019), although the

relative paucity of right-wing authors in the literature makes interpreting the size of this potential

asymmetry difficult. Second, given that social and personality psychologists overwhelmingly

hold left-wing views (Inbar & Lammers, 2012), perhaps authors who donated to left-wing causes

were not any more liberal, on aggregate, than those who had no record of political donations.

Such a severe restriction of range could account for the statistical similarity between non-

donators and left-wing donators, and therefore could raise the specter of undetected bias in the

literature, as right-wing donators reported smaller effects. Given that there were only a handful

of first authors and zero last authors who had donated to right-wing organizations, however, the

sufficiency of either account remains difficult to evaluate.

Limitations and Future Directions

Our review, although by far the most comprehensive quantitative synthesis of literature

bearing on the RRH, is not without limitations. One limitation is the possibility of correlated

error variance across multiple studies; a likely source of systematic error is the underdeveloped

validity of many or most rigidity constructs. Given that loose nomological networks can limit the

falsifiability of the auxiliary hypotheses that are often implicit in psychological research (e.g., the

assumption that one’s measurement instruments work), the possibility that we were merely

aggregating systematic error is an unavoidable limitation of the present review (Cronbach &

Meehl, 1955/1973).

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A related limitation is our reliance on authors’ language when coding rigidity variables.

Although this approach had the advantage of minimizing our own biases, it is susceptible to

those of the study authors, including “jingle-jangle” fallacies (Block, 1995). Jingle fallacies

entail the erroneous assumption that two measures with the same or similar names (e.g., the

Dogmatism Scale and the DOG Scale) reflect the same construct, whereas jangle fallacies entail

the erroneous assumption that two measures with different names (e.g., the Intolerance of

Ambiguity Scale and the Need for Cognitive Closure Scale) reflect different constructs. 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

differently8. These issues intersect with the previously described questionable construct-

validational properties of self-report measures of rigidity. 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.

Another limitation, in this case concerning our analytical approach, is that we did not test

for many 3-way statistical interactions when examining potential moderators (i.e., construct by

conservatism-type by third moderator) owing to inadequate statistical power. This approach

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. Hence,

interpretations of moderator effects in models with multiple moderators (i.e., all except for

Model 1) should be made according to the broader pattern of changes rather than individual

8Altemeyer’s DOG scale discards central elements of Rokeach’s conceptualization, deemphasizing cognitive-organizational aspects and newly emphasizing belief certainty. The DOG Scale also excludes content related to disdain for, and disgust towards, individuals who challenge one’s core beliefs, these being integral to emotional and behavioral characteristics of dogmatism, per Rokeach (1960) and some other theorists (Johnson, 2009).

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effect size estimates. We discourage interpretation of specific meta-regression coefficients across

levels of a given moderator in multi-meta-regression models. For example, despite the negative

meta-regression coefficients for certain conservatism-construct pairings on performance-based

measures, we cannot necessarily conclude that economic conservatism is negatively related to

cognitive rigidity as measured by performance-based instruments. Rather, our results suggest

that, by and large, sizeable relations between conservatism and rigidity are considerably smaller

for performance-based measures of rigidity vs. self-reports.

Moreover, future research administering domain-general self-report measures, such as the

DOG Scale, in complement with measures that assess rigidity in the context of several specific

domains (e.g., politics, movies, sports) or issues may be one means of addressing problems of

measurement non-invariance across the political left and right. One crucial step in further

evaluating the RRH will be to evaluate the degree to which well-established, ideologically

neutral, performance-based measures from the neuropsychology literature, on the one hand, and

self-report measures of cognitive rigidity, on the other, predict phenotypically diverse criterion-

related outcomes. Future research might consider such criterion-related outcomes as: (a)

behavioral aggression towards entities that threaten one’s beliefs; (b) between-group differences

(e.g., cult members vs. lawyers); (c) stability across time and domain, assessed either by the

consistency of a single belief (e.g., Christianity) or the extremity of one’s beliefs in general, even

as they shift in content (e.g., Christian fundamentalists who become militant atheists); (e) various

cognitive biases (see Ditto et al., 2019); (f) partisan moral disengagement and partisan

schadenfreude (Kalmoe & Mason, 2018); (g) metacognitive sensitivity (Rollwage et al., 2018);

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(h) the taxonicity9 of one’s political views (e.g., in referring to environmental mold taxa, Meehl

[1992] noted that “the unquestioned existence of such highly cohesive and dynamically effective

taxa as Trotskyism, Baptist Fundamentalism, or Frenzied Egalitarianism—one could exemplify

with a variety of political, economic, religious, and even esthetic types—should suffice to

persuade us that strong and important taxa in the personality domain need not originate in germs,

genes, or single dramatic environmental happenings” p. 148); and, finally, (i) the incremental

validity of self-report and performance-based measures of rigidity for the criteria already

mentioned over and above related, but conceptually distinct, constructs (e.g., low openness,

right- and left-wing authoritarianism, affective polarization).

Another future direction concerns symmetries and asymmetries in existential needs to

preserve safety and security and to reduce danger and threat, the other major prong of the theory

conceptualizing conservatism as arising from motivated social cognition. A meta-analysis of Jost

and colleagues (2017) attempted to shed light on this prong but fell prey to many of the same

objections that we outlined in the current research, most notably content overlap, as many of the

threat measures deal with politically relevant threats. Further calling previous findings into

question are recent large-scale failures to replicate (a) ideological asymmetries in

psychophysiological reactions to threatening stimuli (Osmundsen et al., 2020) and (b) the effects

of mortality salience posited by terror management theory, which bears on existential motives

9To briefly elaborate on point (h), Meehl’s (1992) “favorite example” (p. 334) of an environmental mold taxon was Trotskyism (although he also offered examples pertinent to far-right wing ideology): “As an undergraduate…I quickly learned that there was a pair of beliefs that, taken jointly, were pathognomic of the ‘Trotskyist syndrome.’ If a student opined that (a) the Soviet Union is a workers’ state and must be defended at all costs against anybody, including the USA and (b) Stalin is a stupid counter-revolutionary bureaucrat, one could predict—not with 90% or 95% but with 100% accuracy—that the person would hold a dozen or more other beliefs…the statistical tightness of the Trotskyist syndrome was greater than any nosologically entity in psychopathology” (p. 334). This observation seems prima facie pertinent to rigidity, especially given evidence that individuals who exhibit particular clusters of core beliefs, attitudes, and behaviors that are predictive of ideological extremism demonstrate 95-99% within-group agreement on a host of topics that are otherwise controversial among moderates and centrists (Hawkins et al., 2018).

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(Klein et al., 2019). Whether previous results are due to publication bias and Type 1 error, or

whether the effects in question are simply more nuanced than previously thought, such

replication failures suggest that the associations between existential needs and political

conservatism should be thoroughly scrutinized. A more comprehensive and nuanced meta-

analysis of the purported link between conservatism and existential threat is necessary.

A more general limitation of the political asymmetry hypothesis is that the basis for left-

right differences is reliant on correlational evidence and does not speak directly to the absolute

level of rigidity in either group. Indeed, a correlation may suggest that conservatives and liberals

differ, even if both exhibit similarly high (or low) scores on a measure of some epistemic

motivation. For instance, liberals and conservatives could both exhibit low levels of cognitive

rigidity (as indicated by average scores below the midpoint of the scale) even if the correlation

between conservatism and rigidity were significant and positive. Consider that the mean and

standard deviation for dogmatism in one study were M = 2.94, SD = .86 on a 6-point scale

(Crowson, DeBacker, & Davis, 2007). Thus, most participants scored below the midpoint of the

scale (3.5), suggesting that most participants were slightly non-dogmatic, presuming, of course,

that this midpoint is psychologically interpretable as reflecting a moderate level of the construct

(see Blanton & Jaccard, 2006). Nevertheless, the correlation between dogmatism and

conservatism in this study was significant and positive (r = .37). When converted to Cohen’s d

and then used to estimate plausible mean differences across liberals and conservatives in the

sample, the mean conservative score could be expected to be around 3.28 and the mean liberal

score could be expected to be around 2.69. Note that both groups still score below the midpoint

of the scale on average; the political asymmetry found in this study does not allow one to

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conclude that conservatives are, in an absolute sense, dogmatic, whereas liberals are not (see

Reyna, 2017).

Conclusion

We hope that the present review allows for more nuanced, albeit perhaps more

ambiguous, accounts of the psychological correlates of political ideology to emerge in place of

the RRH. Accordingly, our results may be cause for optimism. As William James (1896) noted,

“Science, like life, feeds on its own decay. New facts burst old rules; then newly divined

conceptions bind old and new together into a reconciling law” (p. 320). 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. It suffices to say, however, that we cannot be absolutely certain.

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