Do Stress,Depression,and Anxiety Lead to Beliefs in Conspiracy Theories?

Abstract

Previous research has found positive correlations between manifestations of psychological distress, such as anxiety, depression, and stress, and belief in conspiracy theories. However, it remains unclear whether these relationships represent causal effects. We therefore tested whether anxiety, depression, and stress affect (and are affected by) belief in conspiracy theories in a preregistered longitudinal study. We sampled participants from Australia, New Zealand, and the United Kingdom (N = 970) in seven monthly waves (October 2022–March 2023). Using multiple-indicator random-intercept cross-lagged panel models, we found support for only one of 15 preregistered hypotheses: a small cross-lagged effect of anxiety on belief in conspiracy theories. We also found no evidence of belief in conspiracy theories itself provoking psychological distress. Our findings provide grounds for skepticism of the notion that beliefs in conspiracy theories are often motivated by psychological distress or feelings of “existential threat.”

Keywords

conspiracy longitudinal methods anxiety depression stress open data open materials preregistration

A conspiracy theory is an explanation of an event or observation as the result of a conspiracy—multiple actors secretly plotting to do something harmful or unlawful (Swami et al., 2016). Although conspiracies do happen, a nontrivial minority of the public express belief in conspiracy theories that are unwarranted or even strongly contradicted by evidence (for reviews, see Douglas et al., 2017, 2019). For example, Marques et al. (2022) found that 7% of a demographically representative sample of Australians and New Zealanders endorsed the theory that “vapor trails left by aircraft are actually chemical agents deliberately sprayed in a clandestine program directed by government officials” (p. 187). Such trails, of course, are simply contrails: frozen water vapor (Shearer et al., 2016).

Belief in Conspiracy Theories and Psychological Distress

In recent years, a number of studies have been dedicated to understanding the correlates, causes, and consequences of belief in conspiracy theories (for a review, see Uscinski et al., 2022). One well-replicated observation is that belief in conspiracy theories is positively correlated with manifestations of psychological distress, such as stress, anxiety, and depression. A meta-analysis by Bowes et al. (2023) found a mean correlation of $\bar{r} =$ .19 (k = 17 studies) between anxiety and belief in conspiracy theories. Another meta-analysis by Biddlestone et al. (2025) found a mean correlation with conspiracy theories of $\bar{r} =$ .16 for anxiety (k = 18 studies) and $\bar{r}$ = .08 for stress (k = 2 studies). Positive relationships between depression and belief in conspiracy theories were likewise reported by De Coninck et al. (2021) and Green et al. (2023). Why might manifestations of psychological distress and belief in conspiracy theories be positively related?

Theoretical Background: Existential Motives

A popular perspective argues that three core psychological motives underlie belief in conspiracy theories (Douglas et al., 2017). The first of these motives is epistemic: people’s desire to understand the world around them and avoid uncertainty. The second is social: the desire to maintain a positive image of the self or groups one belongs to. The third is existential: the desire to feel safe and in control, especially in the face of threat. It is this third motive that is most salient to explaining a relationship between belief in conspiracy theories and psychological distress.

The notion of existential motives driving belief in conspiracy theories was elaborated in the existential-threat model (van Prooijen, 2020). van Prooijen (2020) reasoned that the perception of existential threat will make people more attentive to their environments and increase “mental sense-making processes”—that is, attempts to understand the causes of events and especially whatever events or stimuli are causing them to experience existential threat. He suggested that this process, in turn, may lead to belief in conspiracy theories—but only given the existence of an antagonistic out-group that seems salient when people are making sense of distressing events.

Existential threat and psychological distress

van Prooijen (2020) defined existential threat in a broad fashion as “feelings of anxiety or uncertainty, often because of distressing events” (p. 16). He also interpreted empirical findings involving anxiety, negative emotions, powerlessness, and death-related anxiety as bearing on the validity of his existential-threat model. He stated that “feelings of anxiety and uncertainty that emerge due to [anxiety-provoking societal events] often stimulate belief in conspiracy theories” (p. 19). We therefore interpret van Prooijen’s theorizing as implying that psychological distress should have a positive causal effect on belief in conspiracy theories, at least assuming the presence of a salient antagonistic out-group.

Psychological distress encompasses several forms and often includes depressive symptoms in addition to symptoms of anxiety and stress. In this study, we chose to examine each of these three common forms of psychological distress while acknowledging that depression is not explicitly specified in the theorizing by van Prooijen (2020) and Douglas et al. (2017). Depression was included in the current study based primarily on empirical observations in literature (discussed further below) despite a more tentative theoretical rationale.

The existential-threat model therefore provides an explanation for the observed relationship between psychological distress and belief in conspiracy theories: The former causes the latter. But does it?

Empirical Evidence for the Effects of Psychological Distress on Belief in Conspiracy Theories

Although we know of no prior experimental studies testing for effects of depression or stress on belief in conspiracy theories, two experiments testing the effects of anxiety have been conducted. Grzesiak-Feldman (2013) found that assigning participants to complete a measure of belief in conspiracy before an examination (a high-anxiety condition) resulted in more conspiracy thinking about Jews than did a control condition. However, it is unclear whether Grzesiak-Feldman randomly assigned participants to conditions, raising the possibility that this observation could be attributed to preexisting differences. Radnitz and Underwood (2017) found that randomly assigning participants to an anxiety-provoking prime (writing about how they had been affected by the U.S. financial crisis) increased belief in conspiratorial explanations for events described in a fictional vignette. However, the estimated effect was small, and the vignette approach may have limited external validity.

Although these experimental studies are creative and informative, their findings leave a great deal of uncertainty. The most credible experiment design would involve a substantial manipulation of feelings of existential threat, random assignment to conditions, and a measure of belief in conspiracy theories about the real world. None of the prior studies we are aware of unambiguously meet these standards, and to do so would present nontrivial practical and ethical difficulties.

An alternative source of evidence is longitudinal research, which can rule out some threats to internal validity. For example, a cross-lagged analysis can rule out the possibility that an apparent relationship between predictor and outcome is due to an effect in the opposite direction to that hypothesized. This is a particularly important consideration for this topic: It is entirely plausible that beliefs involving powerful figures secretly seeking to do harm might provoke distress (as we discuss further below). Some analysis methods for longitudinal data can also rule out all time-invariant (i.e., stable) confounding variables. In particular, this is true of random-intercept cross-lagged panel models (RI-CLPMs; Hamaker et al., 2015). This capacity to rule out some alternative explanations for apparent relationships can mean that longitudinal studies can warrant credible, albeit tentative, causal inferences even if they cannot rule out all alternative explanations (cf. time-variant confounding variables; see Rohrer & Murayama, 2021). Beyond their capacity for supporting causal inferences, longitudinal studies also permit a focus on within-person variance—asking not just why some people believe conspiracy theories while others do not but also why people change their minds.

A small number of longitudinal studies estimating the effects of various forms of psychological distress on belief in conspiracy theories have been conducted. Leibovitz et al. (2021) found no significant relationship between anxiety and belief in conspiracy theories relating to COVID-19 in a panel study with two waves. In another study with two waves, Heiss et al. (2021) found some evidence that threat perceptions led to increased belief in conspiracy theories, albeit not general conspiracy thinking. Adamus et al. (2025) found no significant relationship between economic anxiety increasing belief in COVID-19 conspiracy theories in a three-wave study over 18 months. Likewise, Ballová Mikušková and Telicˇák (2024) found no significant effects of psychological distress increasing belief in COVID-19 conspiracy theories in a study with three waves over 18 months. However, all these studies used cross-lagged designs without random intercepts, meaning that their estimates could have been confounded by stable individual differences (see Hamaker et al., 2015).

In contrast, Chan et al. (2023) used an RI-CLPM, providing better protection against confounding by stable individual differences. They estimated reciprocal effects between psychological distress (measured using the Depression, Anxiety, and Stress Scale–21) and belief in COVID-19 conspiracy theories in a study with five waves. They found no significant cross-lagged effects. However, they used an RI-CLPM without multiple indicators (i.e., not fully accounting for measurement error), which could have biased their estimates.

A particularly rigorous longitudinal study was conducted by Liekefett et al. (2023). Liekefett et al. used the RI-CLPM with multiple indicators, explicitly accounting for the effects of measurement error. They conducted two studies: one with four waves over 2 months (N = 405) and one with four waves over 18 months (N = 1,012). In neither study did they find any evidence of cross-lagged effects of anxiety or existential threat on belief in conspiracy theories. That said, their studies each involved just four waves, and the power of the RI-CLPM can be sensitive to the number of waves (see Mulder, 2021). It is therefore important to subject these ideas to further tests.

Effects of Belief in Conspiracy Theories on Psychological Distress

Whether or not psychological distress affects belief in conspiracy theories, it is entirely possible that the converse is true: that developing beliefs in conspiracy theories can cause distress. Indeed, if a person genuinely believes that the world is beset with evil plots by secretive and powerful agents, it seems reasonable to expect that this might make the person perceive the world as stressful and threatening. This effect might, in turn, explain observed relationships between psychological distress and belief in conspiracy theories.

The empirical studies discussed above (and particularly those using longitudinal designs and the RI-CLPM) provide some useful evidence bearing on this question. However, Ballová Mikušková and Telicˇák (2024) found no evidence of cross-lagged effects of belief in COVID-19 conspiracy theories increasing psychological distress in their cross-lagged panel model. Likewise, Chan et al. (2023) found no evidence of cross-lagged effects of distress on belief in COVID-19 conspiracy theories in their RI-CLPM analysis. In contrast, Adamus et al. (2025) found evidence that a cross-lagged effect of COVID-19-related belief in conspiracy theories increased economic anxiety over time in a cross-lagged panel model. Liekefett et al. (2023) also found evidence of effects of conspiracy beliefs on anxiety and existential threat in Study 1 but not in Study 2.

Overall, these findings leave uncertainty about the effects of belief in conspiracy theories on psychological distress. Knowledge about such effects is important because it speaks to the general question of the risks posed by belief in conspiracy theories (see Douglas, 2021).

The Current Study

Considered in combination, the extant evidence indicates that various manifestations of psychological distress are positively correlated with belief in conspiracy theories. However, the evidence for a causal effect of distress on belief in conspiracy theories is much more tentative. Likewise, there is uncertainty about the degree to which belief in conspiracy theories itself causes psychological distress. We therefore designed a longitudinal study to answer these causal questions. We preregistered this study in detail to permit readers confidence that the hypotheses were subject to severe tests (see Lakens, 2019).

We focus specifically on stress, depression, and anxiety because these are archetypal forms of psychological distress and because all three have been subject to prior investigations in terms of their relationship with belief in conspiracy theories. Regarding stress, we studied both perceived stress and an additional measure of stressful life events (as did Swami et al., 2016).

We hypothesized that depression (Hypothesis 1), perceived stress (Hypothesis 2), stressful life events (Hypothesis 3), and anxiety (Hypothesis 4) would have positive cross-lagged effects on belief in conspiracy theories. We also hypothesized most of the converse effects: that belief in conspiracy theories would have positive cross-lagged effects on depression (Hypothesis 5), perceived stress (Hypothesis 6), and anxiety (Hypothesis 7). We did not make any hypothesis about whether belief in conspiracy theories would lead to more stressful life events (e.g., suffering a financial crisis, being a victim of crime). It is possible that increased belief in conspiracy theories could bring about such events, but we expected that if any such effect held, it would be too small relative to the other causes of such events to be detectable.

We also specified a hypothesis that tests a key proposition of the existential-threat model of belief in conspiracy theories: that is, that the effect of existential threats (or distress) on belief in conspiracy theories depends on the salience of antagonistic out-groups. To our knowledge, no prior study has specifically tested this implied interaction effect. We therefore hypothesized that the cross-lagged effect of perceived stress on belief in a specific conspiracy theory (COVID-19 is a bioweapon created by China) would be more positive among people who perceive the out-group implied in the conspiracy theory (the Chinese government) as threatening (Hypothesis 8).

Hypotheses about conspiracy mentality

Beliefs in conspiracy theories can be conceptualized literally as beliefs in specific theories, but they can also be conceptualized as indicators of a predisposition to conspiratorial explanations: a “conspiracy mentality” (see Imhoff & Bruder, 2014). Conspiracy mentality is conceptualized as a more stable individual difference than belief in conspiracy theories (Imhoff et al., 2022). Thus, given the longitudinal context of this study, we used belief in specific conspiracy theories as the key variable in our primary hypotheses (Hypotheses 1–8) above. However, whether conspiracy mentality is in reality more stable than belief in specific conspiracy theories remains an open question, and specifying hypotheses about conspiracy mentality allowed us to test our key claims using an alternative well-validated measure (see Bruder et al., 2013).

We therefore hypothesized that depression (Hypothesis 9), perceived stress (Hypothesis 10), stressful life events (Hypothesis 11), and anxiety (Hypothesis 12) would have positive cross-lagged effects on general conspiracy mentality and that general conspiracy mentality would have positive cross-lagged effects on depression (Hypothesis 13), perceived stress (Hypothesis 14), and anxiety (Hypothesis 15).

Transparency and Openness

Preregistration

The hypotheses, design, and analysis plan were preregistered before data collection at https://osf.io/5k4yb.

Data, materials, code, and online resources

The Supplemental Material is available online. Data, analysis code, and other materials are openly accessible at https://osf.io/365qr.

Reporting

We report how we determined our sample size, all data exclusions, all manipulations, and all measures in the study. This article arises from a longitudinal project with multiple preregistered components; thus, a number of measures were collected. These are described briefly below; for full copies of the questionnaires, see our OSF project.

Ethical approval

This study was approved by the Massey University Human Ethics Committee (Southern A, Application SOA 22/42). It was carried out in accordance with the provisions of the Declaration of Helsinki (World Medical Association, 2013).

Method

Sample-size determination

It is possible to conduct power analyses for the RI-CLPM via simulation, but the complexity of the multiple-indicator RI-CLPM means that fitting a single model to a data set can take several hours. Power analysis by simulation for most of the preregistered models was thus computationally infeasible. Therefore, two key considerations were used to determine the sample size and time points needed for appropriate power.

First, we conducted power analysis for the single-indicator RI-CLPM, a simpler model that we used for a subset of our analyses. We did this using the powRICLPM package (Mulder, 2022). This power analysis suggested that an estimated sample of 500 participants over seven waves would have 84% power to detect a relatively small cross-lagged effect of standardized b′ = 0.20. This is assuming an intraclass correlation coefficient (ICC) of .9 and large autoregressive effects (B = 0.70). This ICC and autoregressive effect are similar to that found in a descriptive longitudinal study over 6 months of belief in conspiracy theories by Williams et al. (2024).

Second, Liekefett et al. (2023, Study 2) conducted a four-wave study over 1 year focused on similar hypotheses and using the multiple-indicator RI-CLPM. Their sample size at Wave 1 was 1,012, declining to 437 at Wave 4. Despite this substantial attrition and the use of fewer waves than in this study, the standard error for cross-lagged effects was consistently relatively small in their models (e.g., standardized cross-lagged effect of anxiety on belief in conspiracy theories: SE = 0.04, 95% confidence interval [CI] = [−0.07, 0.11]).

Together, these considerations suggested that a sample size of approximately 1,000 and seven waves would allow the ability to estimate cross-lagged effects precisely, even with substantial attrition. Our target sample size for Wave 1 was therefore 1,000.

Participants and procedure

Participants were recruited from the crowdsourcing platform Prolific. The sample was drawn from participants ages 18 and over living in the United Kingdom, Australia, and New Zealand. These three countries were selected together to permit a sufficiently large sampling frame. All three countries are English-speaking Commonwealth countries with connected histories and similar political and cultural contexts. It was thus feasible to select conspiracy-theory items that were relevant in all three countries. A screening survey was applied to identify participants who wished to take part in the full longitudinal study; for more details, see the Supplemental Material.

The assumed target population for inferences was the population of adults residing in the United Kingdom, Australia, and New Zealand. That said, our use of convenience sampling means that substantial uncertainty surrounds our inferences about this population.

Wave 1 survey

The first wave of the survey was released on October 3, 2022. It was advertised to recruit 450 participants from the United Kingdom, 400 from Australia, and 150 from New Zealand, for a total of 1,000 participants. These differing targets were specified considering the size of the available pool of Prolific users in each country (which was especially small in New Zealand). The Wave 1 survey included 89 questions in total, and participants were paid GBP1.65. Seven days were allocated for Wave 1 data collection. However, all quotas for each country were filled within 3 days.

At Wave 1, 1,003 responses were received. The preregistered exclusion criteria were then applied. Participants were excluded if they indicated a country of residence other than the United Kingdom, Australia, or New Zealand; if they failed or did not answer either of two attention checks; if their study duration (in seconds) was fewer than the number of items (N = 89) multiplied by 2 (see Huang et al., 2012); if they did not reach the end point of the survey or their Prolific submission timed out; or if they returned their Prolific submission (i.e., revoking consent). The remaining participants (N = 995) were then invited for all subsequent waves.

After Wave 1, participants were invited to complete surveys every month for 6 months (seven waves total). The survey from Waves 2 to 6 was slightly shorter because the demographic items were removed, for a total survey of approximately 65 to 75 questions (the exact number varied because of some conditionally displayed questions). For Waves 2 to 7, participants were paid GBP1.30 each. Each survey in Wave 2 to 7 was available for 7 days, from the third to the 10th of each month.

Exclusion criteria

Exclusion criteria applicable at Wave 1 are described above; participants who met these criteria were excluded from the study in its entirety. Exclusion criteria were also set at the wave level. If a participant met any one of these criteria at a given wave, their responses from that wave were excluded, but their responses at other waves were retained, and they continued to receive invites for subsequent waves. The exclusion criteria were failing or not responding to any one of the two attention checks at each wave; a study duration in seconds fewer than the total number of items (N = 65) multiplied by 2 (see Huang et al., 2012); “returning” their submission on Prolific (i.e., revoking consent); duplicate response, as detected via Prolific ID; and a Qualtrics status other than 0 (normal response, i.e., excluding previews and suspected duplicates).

In addition to these wave-level criteria, participants who took part only in Wave 1 but no subsequent waves were excluded from analysis. This resulted in a final sample size of 970.

Attrition

Attrition was low (see Table 1). The median number of participants per wave after exclusions was 819 (82% of the Wave 1 sample size), and 764 participants were still taking part at Wave 7. In completed surveys, there were little missing data: just 10 missing data points across all 6,020 survey responses.

Table 1.

Dates of Survey Waves

Wave	Survey open dates	N	Percentage of final sample
1	October 3–5, 2022	970	100
2	November 3–10, 2022	884	91
3	December 3–10, 2022	851	88
4	January 3–10, 2023	851	88
5	February 3–10, 2023	844	87
6	March 3–10, 2023	829	85
7	April 3–10, 2023	798	82

Note: The survey at Wave 1 met its quota much more quickly than the remaining waves because of being open to a wide sampling frame. Subsequent surveys were open only to participants who had completed a survey at Wave 1, necessitating the full 7 days.

Demographic characteristics

Of the final sample, 38.9% resided in Australia, 15.1% resided in New Zealand, and 46.1% resided in the United Kingdom; 44.4% described themselves as men, 54.4% described themselves as women, and 0.9% described themselves as nonbinary. Participants varied in age from 18 to 85 years (M = 40.3, SD = 13.1). A large majority (76.5%) held a university or other tertiary qualification. On a political-orientation scale, where 0 = extreme left and 10 = extreme right, the median response was 4 (i.e., slightly left of center). Most participants were of European ethnicities (see Table 2). For more information about participants’ demographic characteristics, see the Supplemental Material.

Table 2.

Participant Ethnicities

Ethnicity	Frequency	Percentage
United Kingdom (n = 447)
White	397	88.8%
Asian/Asian British	24	5.4%
Black/Black British	20	4.5%
Other	10	2.2%
Australia (n = 377)
European/White	266	70.6%
Asian (including South Asian)	103	27.3%
Aboriginal or Torres Strait Islander	4	1.1%
Other	19	5.0%
New Zealand (n = 146)
European or Pa-keha-	101	69.2%
New Zealand Ma-ori	10	6.8%
Asian (including South Asian)	39	26.7%
Pacific peoples	3	2.0%
Other	10	6.8%

Note: The percentages in each country sum to more than 100% because participants could select multiple ethnicities.

Measures

The following measures were used in all waves. Full copies of all questionnaires are available on our OSF project.

Beliefs in specific conspiracy theories

Belief in conspiracy theories was measured with items pertaining to 11 specific conspiracy theories (see Table 3). This measure was adapted from a measure constructed by Williams et al. (2024), who, in turn, drew items from a range of sources. A small number of revisions were made for the current study to enhance the contemporary relevance of items. Participants responded to each item on a 5-point scale with options of strongly disagree = 1, somewhat disagree = 2, neither agree nor disagree = 3, somewhat agree = 4, and strongly agree = 5. Cronbach’s alpha = .92 at Time 1.

Table 3.

Items in the Belief-in-Conspiracy-Theories Measure

	Item	Original source
1.	COVID-19 is a biological weapon intentionally created and released by China.	Adapted from Miller (2020)
2.	A powerful and secretive group, known as the New World Order, are planning to rule the world.	Adapted from Swami et al. (2011)
3.	Telecommunication companies are covering up the health risks of the 5G cellular network.	Adapted from Marques et al. (2021)
4.	I think that the government wants to limit the rights and freedoms of citizens using the pretext of fighting the COVID-19 pandemic.	Adapted from Oleksy et al. (2021)
5.	The trails left behind airplanes are toxic chemicals released as part of a secret government program.	Adapted from Oliver and Wood (2014)
6.	Fluoride is added to the water supply by governments to make people less intelligent and easier to control.	Adapted from Marques et al. (2021)
7.	The claim that the climate is changing due to emissions from fossil fuels is a hoax perpetrated by corrupt scientists who want to spend more taxpayer money on climate research.	Adapted from Lewandowsky et al. (2013)
8.	Vaccines are harmful, and this fact is covered up by governments and pharmaceutical companies.	Adapted from Jolley and Douglas (2014)
9.	Democrats stole the 2020 U.S. presidential election from Donald Trump by creating fraudulent ballots.	Paraphrased from a Wikipedia page (Attempts to Overturn the 2020 United States Presidential Election, 2023)
10.	Pharmaceutical companies (“Big Pharma”) know of a cure for cancer, but they are keeping it secret to protect their profits.	Constructed for this study
11.	Governments and agricultural businesses are hiding evidence that genetically modified organisms (GMOs) harm human health.	Constructed for this study

Note: These items were prefaced with the instructions, “Please indicate the extent to which you agree with each of the statements below. Please answer carefully and honestly; we’re interested in what you really think.”

Conspiracy mentality

Conspiracy mentality was measured using the five-item Conspiracy Mentality Questionnaire (Bruder et al., 2013). Each question was prefaced with “I think that,” and an example question is, “Events which superficially seem to lack a connection are often the result of secret activities.” Participants responded to each item on an 11-point scale with options from 0 (0% = certainly not) to 10 (100% = certain). Cronbach’s alpha = .86 at Time 1.

Depression

Depression was measured using the eight-item Patient Health Questionnaire (PHQ-8), a measure of depression severity in the general population (Kroenke et al., 2009). The PHQ-8 differs from the better-known nine-item Patient Health Questionnaire by excluding an item about thoughts of suicide. It asks about participants’ depressive symptoms over the previous 2 weeks, and they respond to each item on a 4-point rating scale with options not at all, several days, more than half the days, and nearly every day. Cronbach’s alpha = .90 at Time 1.

Anxiety

Anxiety was measured using a brief seven-item Generalized Anxiety Disorder (GAD-7) questionnaire (Spitzer et al., 2006). The measure asks participants about the degree to which they felt anxiety symptoms (e.g., worrying, nervous, on edge, and restless) over the previous 2 weeks. The response format is the same as the PHQ-8. Cronbach’s alpha = .92 at Time 1.

Perceived stress

Perceived stress was measured using the 10-item Perceived Stress Scale (PSS; S. Cohen et al., 1983). The measure asks questions regarding the subject’s thoughts and feelings over the past month. However, to align with the GAD-7 and PHQ-8 and to ensure the recall period did not overlap across measurement, we changed the wording to refer to “the past 2 weeks.” Participants respond to each item on a 5-point rating scale with options of never, almost never, sometimes, fairly often, and very often. Items 4, 5, 7, and 8 were reverse-coded. Cronbach’s alpha = .92 at Time 1.

Stressful life events

Although we regarded the PSS as our primary measure of stress, we also included a scale measuring stressful life events scale (Hasin & Grant, 2015; Lin et al., 2020). An example item is, “In the last month, were you unemployed and looking for a job?” Participants respond on a dichotomous scale with the response options yes = 1 and no = 0.

Cronbach’s alpha at Time 1 was low, α = .55, presumably because the items in this scale are not indicators of some single underlying construct. Rather, this scale can be considered a formative measure (see Borsboom, 2008): The experiences probed in the items cause stress rather than the other way round. Given the formative status of the model, we did not treat it as reflective in latent-variable models but instead created a stressful-life-events score by summing each participant’s responses to the 12 items at each wave. We then used this score as a single indicator of stressful life events.

Salience of an antagonistic out-group (intergroup threat)

The salience of an antagonistic out-group plays a key role as a moderator in van Prooijen’s (2020) existential-threat model. However, we were unable to identify any existing measure of this specific construct. We therefore chose to draw on the more established concept of intergroup threat perception (see Stephan et al., 2016). We reasoned that if a person perceives another group as threatening, it implies that the person perceives this group as antagonistic to at least some degree.

We opted to select one specific theory in our measure of belief in specific conspiracy theories to link to a salient antagonistic out-group. We selected the item “COVID-19 is a biological weapon intentionally created and released by China.” This item was useful in this context given that it clearly implicates a specific group. As a measure of intergroup threat (and consequently, salience of an antagonistic out-group), we presented the item, “I feel threatened by the Chinese Government.”

We provided four response options: strongly disagree, somewhat disagree, somewhat agree, and strongly agree. This allowed us to split participants into a low-intergroup-threat group (strongly and somewhat disagree) and a high-intergroup-threat group (strongly and somewhat agree). Doing so allowed us to treat intergroup threat as a dichotomous grouping variable, permitting us, in turn, to test for moderation in a multigroup RI-CLPM. For more information, see Data Analyses below.

Attention checks

Two types of attention-check questions were used at each wave: a nonsensical item and an instructional manipulation check. For a complete list of attention checks, see the Supplemental Material.

Additional measures

This study forms part of an overarching longitudinal project incorporating several preregistered studies. Consequently, several other measures were included in the surveys that were not used in the data analyses reported here. These items included a four-item measure of trust (Marques et al., 2021), three items from the Socio-Political Control subscale (Paulhus & Christie, 1981), a single item probing sympathy for violent protests (Bhui et al., 2014), and a single item measuring belief in modern medicine (Pennycook et al., 2020).

In the first wave only, participants were also asked whether they had heard of the specific claim made by each conspiracy theory in Table 3. The surveys in second and subsequent waves also prompted participants with an open-ended question if a substantial change in their agreement with a specific conspiracy theory was detected in comparison with the previous time they had responded. Most participants prompted thusly either skipped the question (which was explicitly described as optional) or provided very brief responses (length: Mdn = 14 words).

More information can be found in the full copies of the surveys on our OSF project.

Data analyses

All data analysis was completed using RStudio (Version 12.0+343) and the R programming language (Version 4.0.2; R Core Team, 2021). We relied heavily on the packages lavaan (Rosseel, 2012), tidyverse (Wickham et al., 2019), ICC (Wolak et al., 2012), psych (Revelle, 2024), and here (Mueller, 2020).

The majority of hypotheses were tested using multiple-indicator RI-CLPMs (Mulder & Hamaker, 2021). The exceptions were the models used to test Hypothesis 3 (the effect of stressful life events on belief in conspiracy theories), Hypothesis 8 (the moderating effect of perceived out-group threat on the effect of perceived stress on belief in a specific conspiracy theory), and Hypothesis 11 (the effect of stressful life events on conspiracy mentality). The models for Hypotheses 3 and 11 incorporated the stressful-life-events variable, which cannot be considered as a reflective construct (as discussed above), whereas the model for Hypothesis 8 included just a single conspiracy theory. For these analyses, the single-indicator RI-CLPM (Hamaker et al., 2015) was used. For Hypotheses 3 and 11, this was a deviation from the preregistration; we discovered during analysis that models including both multiple-indicator variables (belief in conspiracy theories, conspiracist mentality) and variables with single indicators (stressful-life-event score) in the same RI-CLPM could not converge.

We tested relationships between pairs of constructs (e.g., depression and belief in conspiracy theories) in separate models rather than including all variables in one extremely large model. Doing so mitigated the risk of convergence failure in overly complex models.

We estimated models using full information maximum likelihood. This allowed us to account for missing data (see Enders & Bandalos, 2001), which was a substantial concern given the use of a longitudinal design. Although our analyses assumed multivariate normality, we report robustness checks using “MLR” estimation (maximum likelihood with robust standard errors) in the Supplemental Material. These analyses leave the vast majority of our substantive conclusions unchanged.

Measurement invariance

In multiple-indicator RI-CLPMs, reported below, we assumed strong factorial invariance (i.e., loadings and intercepts were held constant across time). We also constrained the cross-lagged coefficients to equality across waves. This had two main advantages. First, it reduced the number of free parameters and therefore the risk of convergence failures. Second, for cross-lagged coefficients specifically, this facilitated clear inferential criteria (whereas if cross-lagged coefficients were permitted to vary over time, each hypothesis would involve six different cross-lagged coefficients).

Our preregistration specified our decision to apply these constraints. However, we also report tests of measurement invariance below to gauge the accuracy of the assumptions represented by these constraints. The invariance-testing process consisted of estimating a sequence of nested models with increasing constraints, consistent with procedures outlined by Mulder and Hamaker (2021).

For multiple-indicator models, this process involved four steps. In the first step, we estimated models applying configural invariance (no constraints). In the second step, we applied weak factorial invariance (equal loadings). In the third step, we applied third-strong factorial invariance (equal intercepts and loadings). In the final step, we applied structural invariance (equal intercepts, loadings, and autoregressive and cross-lagged regression coefficients). For single-indicator models, there were just two steps: models with and without regression coefficients constrained over time.

Our preregistration indicated that we would conduct measurement-invariance tests as exploratory analyses following Mulder and Hamaker (2021), but we did not specify precise criteria for determining invariance. In comparing the models in adjacent steps, we used Chen’s (2007) recommended thresholds for changes in goodness-of-fit indices: change in comparative fit index ≤ .01, change in root mean square error of approximation ≤ .015, and change in standardized root mean squared residual ≤ .03 (≤ .01 for strong invariance). For a comparison of changes in goodness-of-fit indices for all models, see the Supplemental Material.

Across all multiple-indicator models, changes in fit indices remained within the thresholds suggested by Chen (2007), supporting the constraints applied. For the single-indicator models (Models 3, 5, and 8), there was evidence against the regression coefficients being invariant over time. However, the results remained largely consistent when we reran these analyses without these constraints (see the Supplemental Material).

Results

Descriptive statistics

To describe interindividual variation in responses, we calculated each participant’s mean response to all six measures at each time point (see Table 4). The mean conspiracy-theory scores indicated that participants typically disagreed with each conspiracy theory. Participants’ mean depression, anxiety, and perceived-stress scores were consistent with the presence of mild symptoms. Means were relatively stable over time for most variables.

Table 4.

Means for Main Variables Over Time

	Time 1	Time 2	Time 3	Time 4	Time 5	Time 6	Time 7	Range
Belief in conspiracy theories	1.81	1.79	1.81	1.85	1.81	1.87	1.79	1–5
Conspiracy mentality	5.38	5.23	5.21	5.19	5.12	5.13	5.16	0–10
Depression	6.48	6.37	6.37	6.13	6.07	6.08	5.98	0–24
Anxiety	5.60	5.56	5.42	5.05	5.33	5.36	5.21	0–21
Perceived stress	15.35	15.37	15.21	14.30	14.83	14.91	14.60	0–40
Stressful life events	0.79	0.62	0.61	0.55	0.57	0.57	0.50	0–12

Note: Means were calculated using full information maximum likelihood.

ICCs were calculated using participants’ overall scores for each measure at each time point. The ICC for belief in conspiracy theories was r = .92, indicating that across the seven waves, most of the observed variance was due to stable, between-persons differences, with relatively minimal within-person changes. The remaining measures ranged from r = .84 to r = .79, with one exception for stressful life events (r = .40). The ICC for stressful life events is understandably low given that it is a questionnaire about events in the last month rather than stable individual differences. For further details, see the Supplemental Material.

Confirmatory analyses

Each of the RI-CLPMs we estimate contain many “nuisance” parameters (e.g., variances, factor loadings, autoregressive effects). For the sake of brevity, we therefore focus our reporting below on the cross-lagged coefficients from the models. These are the coefficients that provide credible estimates of causal effects and that we used to test our hypotheses via our preregistered inferential criteria.

For cross-lagged and autoregressive coefficients for Models 1 to 4 (the models involving belief in specific conspiracy theories), see Table 5. Of the seven hypotheses tested via the output in Table 5, only one was supported: The estimated effect of anxiety on belief in conspiracy theories was positive and statistically significant. Autoregressive effects for all measures of psychological distress and belief in conspiracy theories were positive and statistically significant.

Table 5.

Cross-Lagged and Autoregressive Coefficients: Random-Intercept Cross-Lagged Panel Models Including Belief in Specific Conspiracy Theories

Model	Estimated effect	b [95% CI]	p	Estimated effect	b [95% CI]	p
1	Depression → belief in conspiracy theories (Hypothesis 1)	0.03 [−0.01, 0.06]	.111	Belief in conspiracy theories → depression (Hypothesis 5)	0.05 [−0.03, 0.12]	.237
	Depression (AR)	0.25 [0.20, 0.30]	< .001	Belief in conspiracy theories → belief in conspiracy theories (AR)	0.29 [0.23, 0.35]	< .001
2	Perceived stress → belief in conspiracy theories (Hypothesis 2)	0.02 [−0.01, 0.05]	.118	Belief in conspiracy theories → perceived stress (Hypothesis 6)	0.06 [−0.03, 0.15]	.193
	Perceived stress → perceived stress (AR)	0.29 [0.23, 0.34]	< .001	Belief in conspiracy theories → belief in conspiracy theories (AR)	0.29 [0.23, 0.35]	< .001
3	Stressful life events → belief in conspiracy theories (Hypothesis 3)	−0.01 [−0.02, 0.00]	.191	Belief in conspiracy theories → stressful life events (no hypothesis)	−0.04 [−0.14, 0.04]	.456
	Stressful life events → stressful life events (AR)	0.18 [0.14, 0.21]	< .001	Belief in conspiracy theories → belief in conspiracy theories (AR)	0.16 [0.12, 0.19]	< .001
4	Anxiety → belief in conspiracy theories (Hypothesis 4)	0.03 [0.00, 0.05]	.042	Belief in conspiracy theories → anxiety (Hypothesis 7)	0.07 [−0.02, 0.15]	.130
	Anxiety → anxiety (AR)	0.21 [0.16, 0.26]	< .001	Belief in conspiracy theories → belief in conspiracy theories (AR)	0.29 [0.23, 0.35]	< .001

Note: CI = confidence interval; AR = autoregressive coefficient.

For the cross-lagged and autoregressive coefficients for Models 6 to 9 (the models involving conspiracy mentality), see Table 6. Of the seven hypotheses tested via the output in Table 6, none were supported. The effect of conspiracy mentality on stressful life events, about which we had made no hypothesis, was positive and statistically significant. The autoregressive coefficients for all constructs in these models were positive and statistically significant.

Table 6.

Cross-Lagged and Autoregressive Coefficients: Random-Intercept Cross-Lagged Panel Models Including Conspiracy Mentality

Model	Estimated effect	b [95% CI]	p	Estimated effect	b [95% CI]	p
6	Depression → conspiracy mentality (Hypothesis 9)	−0.09 [−0.26, 0.08]	.301	Conspiracy mentality → depression (Hypothesis 13)	0.00, [−0.02, 0.03]	.840
	Depression → depression (AR)	0.25 [0.20, 0.31]	< .001	Conspiracy mentality → conspiracy mentality (AR)	0.78 [0.71, 0.85]	< .001
7	Perceived stress → conspiracy mentality (Hypothesis 10)	−0.03 [−0.13, 0.08]	.625	Conspiracy mentality → perceived stress (Hypothesis 14)	0.01 [−0.01, 0.03]	.412
	Perceived stress → perceived stress (AR)	0.29 [0.24, 0.34]	< .001	Conspiracy mentality → conspiracy mentality (AR)	0.30 [0.23, 0.36]	< .001
8	Stressful life events → conspiracy mentality (Hypothesis 11)	−0.02 [−0.06, 0.01]	.210	Conspiracy mentality → stressful life events (no hypothesis)	0.03 [0.00, 0.06]	.050
	Stressful life events → stressful life events (AR)	0.18 [0.14, 0.21]	< .001	Conspiracy mentality → conspiracy mentality (AR)	0.16 [0.13, 0.20]	< .001
9	Anxiety → conspiracy mentality (Hypothesis 12)	−0.12 [−0.25, 0.01]	.061	Conspiracy mentality → anxiety (Hypothesis 15)	0.00 [−0.03, 0.03]	.847
	Anxiety → anxiety (AR)	0.21 [0.16, 0.26]	< .001	Conspiracy mentality → conspiracy mentality (AR)	0.78 [0.70, 0.85]	< .001

Note: CI = confidence interval; AR = autoregressive coefficient.

Salience of antagonistic out-groups

To test if the effect of perceived stress (summed score) on belief in a specific conspiracy theory (“COVID-19 is a bioweapon created by China”) was the same for participants with high levels of intergroup threat versus participants low in intergroup threat, we performed a multiple-group RI-CLPM as a test of moderation (see Mulder & Hamaker, 2021). For a detailed analysis plan and inferential criteria, see the preregistration.

First, we fitted a model (M5a) with no constraints across groups. Next, we fitted a model in which all parameters could vary across groups except for the cross-lagged parameter of perceived stress on belief in a specific conspiracy theory (M5b). In Model M5a, the estimated effect of perceived stress on belief in the theory in participants who perceived the Chinese government as threatening was b = 0.00, 95% CI [−0.01, 0.01], p = .781. For participants who did not perceive the Chinese government as threatening, this estimated effect was nearly identical, b = 0.00, 95% CI [−0.00, 0.01], p = .494. The chi-square difference test of Models M5a and M5b was Δχ²(1) = 0.04, p = .849, implying no evidence to reject a null hypothesis that the cross-lagged parameter is identical in these two populations. Therefore, Hypothesis 8 was not supported.

For fit statistics of the estimated models, see the Supplemental Material.

Exploratory analyses

Although not preregistered, we also calculated fractional Bayes factors for each of our hypothesized effects using a method described by Hoijtink et al. (2019). All Bayes factors (with the null model in the numerator) exceeded 3, and many were in the range of 20 to 30. These findings reflected positive to strong evidence in support of the null hypotheses. For detailed Bayesian results, see the Supplemental Material.

We also estimated exploratory versions of our models in which we permitted cross-lagged effects to vary over time but formed inferences based on the mean cross-lagged effects in each model. These models produced broadly similar conclusions, and the vast majority of hypotheses remained unsupported. For more detailed results, see the Supplemental Material.

Discussion

Overall, we found almost no evidence for any effects of anxiety, depression, perceived stress, or stressful life events on belief in conspiracy theories or conspiracy mentality. Just one of the 15 preregistered hypotheses was supported, with a significant positive cross-lagged effect of anxiety on belief in conspiracy theories. That said, this coefficient did not remain significant when applying robust standard errors (see the Supplemental Material). Set against the number of hypotheses we tested, we thus consider this only very tentative evidence of an effect of anxiety on belief in conspiracy theories.

Our findings cohere with the closely related longitudinal work of Liekefett et al. (2023), who found no evidence that anxiety, uncertainty aversion, or existential threat produced increased belief in conspiracy theories. Considered in conjunction with Liekefett et al.’s findings, our findings provide reason for skepticism about the notion that psychological distress or existential threats (as suggested by van Prooijen, 2020) play a substantial role in motivating belief in conspiracy theories.

That said, there is a potential critique of the degree to which our results test the existential-threat model of van Prooijen (2020). This model suggests that existential threat will lead to belief in conspiracy theories only when an antagonistic out-group is salient. For most of the theories in our survey, we have no way of knowing whether our participants did perceive some antagonistic out-group to be salient to the events described. That said, in Model 5 (Hypothesis 8) we specifically tested this feature of van Prooijen’s model. We found that the estimated effect of stress on belief in a conspiracy theory implicating the Chinese government was tiny and nonsignificant in both people who perceived the Chinese government as threatening (i.e., antagonistic) and people who did not, and there was no evidence of interaction. Overall, our findings are not consistent with van Prooijen’s existential-threat model, albeit they do not refute it with certainty. Future investigations of this model could specifically measure existential threat (as opposed to distress broadly) and further test the implied interaction between existential threat, salience of an antagonistic out-group, and belief in conspiracy theories.

Why might manifestations of psychological distress not have substantially affected our participants’ beliefs in conspiracy theories in our study? One explanation is simply that personal experiences of distress hold no obvious information value in respect to such theories, and therefore, there is no reason participants should take them into account when considering the merits of various theories. Obviously, feeling depressed, stressed, or anxious about some event might lead one to seek explanations for that event, but people tend to enthusiastically seek explanations of events around them regardless: Humans are curious creatures (see Kidd & Hayden, 2015).

Effects of conspiracy beliefs on psychological distress

Considering the content of the conspiracy theories we canvased, it is surprising that we also found no evidence of effects of belief in conspiracy theories (or conspiracy mentality) on anxiety, perceived stress, or depression. After all, the theories in our scales referred to powerful people acting in a furtive and malevolent fashion. We expected that accepting such theories should cause people some degree of emotional turmoil. That said, people’s own mental health may often have much more important drivers (in their genetics, biology, personal lives, and economic circumstances) than abstract beliefs about large-scale societal events. This could mean that if the effects of belief in conspiracy theories on mental health exist, they could be readily drowned out by statistical noise.

One of only two significant cross-lagged effects in our study was one about which we had made no hypothesis: a positive effect of conspiracy mentality on stressful life events. It is possible that such an effect holds in reality: For example, perhaps increased conspiracy mentality might strain relationships at home or at work (Toribio-Flórez et al., 2023; van Prooijen et al., 2022). That said, this finding was not preregistered and occurred in the context of nonsignificant effects of conspiracy mentality on anxiety, perceived stress, and depression. The coefficient also did not remain significant in a robustness analysis in which we permitted regression coefficients to vary over time (see the Supplemental Material). It should therefore be regarded as very tentative until replicated.

Limitations

By using the RI-CLPM with longitudinal data, we were able to rule out biases that were due to stable confounding variables or were from effects in the opposite directions to those hypothesized. However, our estimates could still be biased by confounds that vary over time (see Rohrer & Murayama, 2021).

Our estimates might also be biased if causal effects truly are present but occur more slowly (or more quickly) than implicitly assumed by the 1-month interval between waves. Unfortunately, no existing theoretical framework explicitly specifies how long causal effects of psychological distress on belief in conspiracy beliefs (and the opposite direction) might take to emerge. The monthly interval in this study was selected based on practical constraints, consistency with prior research, and our own judgment that this would plausibly be enough time for effects to emerge.

In the reported multiple-indicator RI-CLPMs, we assumed strong factorial invariance. Tests of measurement invariance were generally consistent with these assumptions. However, we cannot conclusively rule out breaches of invariance over time, and this could add additional uncertainty to our estimates. We also assumed that regression coefficients were stable over time. Invariance tests suggest this assumption was plausible for the multiple-indicator models but not the single-indicator models—although our results remained substantively similar when we loosened this assumption in supplementary analyses.

Although our sample size (in terms of both participants and waves) was large, we did not complete a priori power analyses for multiple-indicator RI-CLPMs but just for single-indicator RI-CLPMs. Furthermore, in this power analysis, we specified an effect size of standardized b′ = 0.20, which we considered to be relatively small relative to J. Cohen’s (1988) benchmarks for correlations (which are scaled similarly to standardized cross-lagged coefficients). However, recent benchmarking by Orth et al. (2024) found that effects in RI-CLPMs are much smaller than this, with a median cross-lagged coefficient in the literature of just b′ = 0.05. Consequently, our study may not have been as well powered as we hoped. This said, the CIs surrounding our estimates were fairly narrow. For example, the 95% CI for the effect of depression on belief in conspiracy theories ranged from −0.01 to just 0.06. Thus, although we cannot confidently rule out the presence of any effects whatsoever, our findings allow us to credibly rule out the presence of large effects (for most of the effects examined).

One possible criticism of our study could be that its focus on within-person effects may have hidden the presence of substantial between-persons effects. In other words, perhaps stable individual differences in anxiety, stress, or depression might have causal effects on belief in conspiracy theories, which were, in turn, ignored in our analysis. This is possible but not especially plausible considering that even the between-persons correlations between these variables and belief in conspiracy theories tend to be relatively small in the literature (see the meta-analyses by Biddlestone et al., 2025; Bowes et al., 2023; Stasielowicz, 2022).

Finally, we used convenience sampling via Prolific. Thus, we cannot be confident that our findings generalize to the wider populations of New Zealand, Australia, and the United Kingdom.

Future directions

Although longitudinal research on this topic has value, it could be possible for future studies to experimentally manipulate psychological distress to test for consequent effects on belief in conspiracy theories. The Trier Social Stress Test (Kirschbaum et al., 2008) or the Sing-a-Song Stress Test (Brouwer & Hogervorst, 2014) could be useful for this purpose.

Alternatively, it could be useful to investigate other symptoms of psychopathology that might have more substantial effects on belief in conspiracy theories. Liekefett et al. (2024) theorized that ruminating about distressing events could narrow a person’s attention to a view of the world that is negatively biased, which might, in turn, make conspiracy theories seem more attractive. Indeed, Liekefett et al. found that experimentally inducing brooding (a form of rumination) produced an increase in conspiracy beliefs that was statistically significant, d = 0.19, albeit small. Although rumination can induce negative affect (Blanke et al., 2022), it may not be negative affect or distress per se that affects belief in conspiracy theories but rather, rumination as a cognitive process. It may be useful to subject this idea to further testing in other contexts.

To better understand why people believe conspiracy theories, it may also be necessary to investigate which experiences reinforce belief in conspiracy theories. The theoretical frameworks we applied in this study (e.g., Douglas et al., 2017; van Prooijen, 2020) imply that conspiracy beliefs are adopted during times of existentially threatening events as a coping response, potentially providing short-term relief from distress. However, few studies have directly demonstrated this short-term relief in distress following belief adoption (for indirect evidence, see Samayoa et al., 2025). One challenge is that the initial formation of a conspiracy belief may occur too rapidly for typical longitudinal designs (such as ours) to detect effects. Intensive longitudinal methods, such as ecological momentary assessment (Shiffman et al., 2008), could better track short-term fluctuations in psychological distress and conspiracy beliefs immediately following a major stressor. Such studies could produce a better understanding of short-term underlying processes that might have been missed in longer-term studies such as ours.

Clinical implications

Several authors have advocated interventions aimed at addressing psychological distress (especially stress-reduction interventions) as a strategy to reduce belief in conspiracy theories (e.g., Fournier & Varet, 2024; Pfeffer et al., 2024; Scheffer et al., 2022; Swami et al., 2016). Although we did not directly test the impact of distress-reduction strategies on conspiracy beliefs, the findings from this study—and other longitudinal studies—suggest the effects of stress and anxiety on belief in conspiracy theories (if any) are likely to be small. Furthermore, the effects of stress-reduction interventions on anxiety and stress levels are themselves likely to be small (for a meta-analysis, see Fischer et al., 2020). Although more research on this topic is necessary, stress-reduction interventions—although undoubtedly useful and justifiable for other reasons—may not be promising candidates for reducing belief in conspiracy theories.

Supplemental Material

sj-docx-1-cpx-10.1177_21677026251370092 – Supplemental material for Do Stress, Depression, and Anxiety Lead to Beliefs in Conspiracy Theories?

Supplemental material, sj-docx-1-cpx-10.1177_21677026251370092 for Do Stress, Depression, and Anxiety Lead to Beliefs in Conspiracy Theories? by Nick D. Fox, Matt N. Williams and Stephen R. Hill in Clinical Psychological Science

Footnotes

Acknowledgements

The original submitted version of this article is also available as a preprint at .

Transparency

Action Editor: Pim Cuijpers

Editor: Jennifer L. Tackett

Author Contributions

Nick D. Fox: Conceptualization; Data curation; Investigation; Methodology; Writing–original draft; Writing–review & editing.

Matt N. Williams: Conceptualization; Funding acquisition; Investigation; Methodology; Project administration; Supervision; Writing–original draft; Writing–review & editing.

Stephen R. Hill: Conceptualization; Supervision; Writing–review & editing.

ORCID iDs

Nick D. Fox

Matt N. Williams

Supplemental Material

Additional supporting information can be found at

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