Systematic review and meta-analysis of the evidence for an illusory truth effect and its determinants

Domain: chemistry
Published: 2026-02-27
Editorial outcome: accept

Abstract
Over the last four decades, studies provided evidence that individuals tend to rate
statements as being more truthful when they are re-exposed to them, the so-called
‘illusory truth effect’. In light of a growing number of studies published since the previous
meta-analysis in 2006 and concern of publishing biases, we conduct a meta-analysis on
182 studies and 366 effect sizes (N = 31,184 participants) published from 1977 to 2025.
After correcting for small-study effects, we observe a small illusory truth effect (g = 0.37,
95% confidence interval [0.30, 0.44]), with a substantial within and between-study
heterogeneity. Here, we show that multiple variables accounted for such heterogeneity,
including the type of item, the instructions during the first exposure, the presence of
veracity cues, and the duration of presentation on first exposure to the statement. We
highlight the importance of the initial exposure and discuss practical implications
regarding the current misinformation crisis.

Introduction
The illusory truth effect, or repetition-induced truth effect refers to the tendency
for individuals to judge repeated statements as more true than novel statements 1. In a
typical experiment, participants are first exposed to a set of ambiguous statements (i.e.,
statements for which participants are unlikely to know the actual truth status, as
established by pretests) or neutral statements (i.e., statements equally likely to be rated as
true in both their true and false version) during the exposure phase. At the test phase,
participants are instructed to judge the truth of another set of statements, usually
consisting of statements repeated from the exposure phase and new statements previously
unseen in a random order. The illusory truth effect is typically operationalized as the
difference in truth ratings between repeated and novel items.

While the design of primary studies varies considerably, the illusory truth effect
appears robust across populations and types of content 2,3. The effect is observed
regardless of the of the population type 4,5 (clinical vs typical), or of age 6,7 (from 5 to 80
years old). Additionally, the illusory truth effect seems to appear regardless of the source
of the information 8, or whether it is a trivia statement 9,10, a general knowledge question
7,11, a (fake) news headline 12,13, or less-tangible information such as a rumor 14, an opinion
in an argument 15, or a marketing claim 16. However, the effect of repetition on perceived
truth was not consistently observed. For instance, repetition did not reliably increase the
perceived truth for extremely implausible statements 12,17, or headlines in form of
questions 18.

The rise of digital media and the rapid pace of online communication have
amplified concerns about how repetition might increase belief in misinformation 19.
Repeated exposure to false news headlines not only increases perceived accuracy but can
also raise the intention to share such content on social media 20. While individual factors
such as motivation, cognitive abilities, thinking style, or knowledge influence belief in
misinformation 21,22, these factors appear to have little impact on the illusory truth effect.
The effect is robust across individual differences in cognitive abilities 10 and persists even
when participants are incentivized for accuracy 23, or possess relevant factual knowledge
7,24. Several intervention strategies have been tested to reduce or eliminate the illusory
truth effect. These include warning participants about the effect itself 25,26, alerting them
prior to initial exposure that some of the information might be false 27, or asking them to
rate the accuracy of information during initial exposure 11,28. However, other approaches
have produced mixed results. While labeling false information as disputed by a third-
party fact-checker had little impact, more explicit labels (e.g., false) successfully
eliminated the effect 29. Similarly, the benefit of labeling source reliability may depend
on whether participants recall this information during judgment 8,30,31. Given that false
information can spread more widely and rapidly than true information online 32,
understanding the determinants of the illusory truth effect has become increasingly
urgent. Such insights could clarify the conditions under which repetition amplifies
perceived truth, thereby guiding the design of targeted interventions to reduce the risk of
increasing gullibility to misinformation when people are massively exposed repeatedly to
them.

Previous research has proposed several theoretical frameworks to explain why
repetition increases perceived truth of information 33. Dominant explanations of the
illusory truth effect attribute a significant role to processing fluency, which is defined as
the perceived ease with which information is processed 34. According to this view,
repeated exposure to information increases processing fluency, which in turn increases
the perceived truth. Supporting this framework, prior research has shown that the illusory
truth effect can be reversed when participants form an implicit association between
fluency and falseness 35. While fluency can be a legitimate indicator of truth when it aligns
with valid cues 36,37, the illusory truth effect arises when people misattribute incidental
increases in fluency from mere repetition as evidence of truth.

An emerging alternative, non-exclusive explanation is the referential theory. This
framework argues that truth judgments are driven by the presence and coherence of
corresponding references in an individual’s semantic memory 38. When processing a
statement, individuals rely on pre-existing memory nodes – concepts and associations
linked to the statement’s referents. According to this theory, repeated exposure to a
statement activates these memory nodes, but also strengthens the connections between
them, leading to a more integrated and coherent network. This coherence makes repeated
statements easier to retrieve and process, thereby enhancing their perceived truthfulness
in later evaluations. Udry and Barber 39 argue that the corresponding references must also
be semantically coherent across the repetitions (i.e., repeated statements must convey the
same meaning to exhibit the illusory truth effect). For instance, even if repeated
statements share some of the referents, they will not induce the illusory truth effect if
these referents are associated in semantically inconsistent ways. This suggests that both
fluency and strengthened connections between concepts alone are insufficient to increase
the perceived truth of information without maintaining semantic consistency.

Dechene et al.’s meta-analysis 2 of 51 studies published up to 2006 and reporting
102 effect sizes revealed a small (d = 0.39, 95% confidence interval [0.32, 0.47]) to
medium (d = 0.50, 95% confidence interval [0.43, 0.57]) illusory truth effect across
studies depending on the type of analysis (i.e., fixed-effects model or random-effects
model) and the method used to compute the effect (i.e., within-item or between-item
criterion). In particular, the illusory truth effect seems to be smaller when the truthfulness
ratings for the same items are compared between the exposure and the test phases (within-
item criterion, d = 0.39) compared to when repeated items are compared with new items
in the test phase (between-item criterion, d = 0.53).

This first meta-analysis on the illusory truth effect provided a valuable foundation
by synthesizing early evidence for the phenomenon. Since then, the field has expanded
rapidly, with increasing diversity in study designs, populations, and materials, warranting
an updated and more comprehensive synthesis. At the same time, concerns have been
raised about the evidential quality of the literature: a recent review found that 96% of
studies on the illusory truth effect reported statistically significant results, raising the
possibility of publication bias 3.

The present meta-analysis was designed to address these developments through
four core objectives. First, to provide an updated and comprehensive estimate of the
illusory truth effect by synthesizing the greatly expanded body of research with 182
studies and 366 effect sizes published between 1977 and 2025. Second, to improve the
estimation of the effect size of the illusory truth effect and the potential moderators of
such effect by applying more advanced techniques than the ones available when the
previous meta-analysis was conducted. These include three-level random-effects models
to account for the non-independence of multiple estimates from the same sample40,41,
publication bias diagnostics 42, risk of bias assessments (RoB2 43), multivariate
imputation for missing moderator data, and sensitivity analyses to evaluate the impact of
missing outcome data. Third, to examine a broader set of moderators to investigate the
boundary conditions of the illusory truth effect (see Table 1). Moderator selection
prioritized variables with practical relevance (e.g., misinformation susceptibility) and
empirical prevalence. The results are discussed within the processing fluency account and
the referential theory of the truth effect, while also considering alternative explanations
for moderators not directly addressed by these frameworks. Fourth, drawing from this
moderator analysis, to identify those with direct implications for misinformation
mitigation, including the design of effective interventions.

In this work, we confirm that repeated exposure produces a small but robust
increase in perceived truth (bias-corrected g = 0.37, 95% CI [0.30, 0.44]). The effect is
systematically moderated by the nature of the item type and the design of the initial
exposure, particularly the initial task, the presentation duration and the presence of
explicit veracity cues. The meta-regression indicates that the combined moderators
account for approximately 37% of the between-study variance, highlighting their
explanatory value. Together, these findings suggest the importance of designing
interventions that target the initial moments of exposure. Encouraging early truth
evaluation or embedding explicit accuracy signals during initial encounters with
information may significantly reduce the later influence of repetition.

Results
Study Selection and Study Characteristics

The current meta-analysis included n = 99 articles describing k = 182 studies from
which u = 366 effect sizes were extracted from 31,184 participants. Of the 93 articles
identified in Henderson et al. 3, 27 were excluded according to our inclusion and exclusion
criteria. Compared to a previous meta-analysis conducted by Dechêne et al. 2, 6 out of 25
articles were excluded. Included articles were published between 1977 and 2025, with a
median year of 2019. Most studies were published in a journal (n = 77) while other were
unpublished studies (n = 9) or data set (n = 1), PhD (n = 6) or Master’s thesis (n = 5) and
conference presentations (n = 1). Most studies were conducted in Europe (n = 49) and in
North America (n = 47), with a few in Oceania (n = 3), Asia (n = 1), and South America
(n = 1). Characteristics and references for all studies included in the meta-analysis are
provided in the Supplementary Data 1 and the Supplementary References.

Publication Bias

Visual inspection of the contour-enhanced funnel plot 42 revealed asymmetry in
the distribution of effect sizes (see Figure 1). Most imprecise studies (lower part of the
plot) fall in the p < .05 regions to the right of zero, whereas few comparable studies appear
in the adjacent above the conventional 0.05% area. This pattern suggests that
non-significant or negative small-study results are underrepresented. Additionally, most
highly precise estimates at the top of the funnel cluster around the bias-adjusted effect
size, whereas the unadjusted pooled effect estimate falls farther to the right, implying
inflation by small‑study effects. This observation was confirmed using an Egger’s
regression test 44 accounting for dependencies across effect sizes 45. Results indicate
asymmetry in the funnel plot, t(364) = 9.77, p < .001, which suggests the presence of
small-study effects, one possible component of publication bias 46.

Following the evidence of funnel-plot asymmetry, we implemented a Precision-
Effect Estimate with Standard Error (PEESE) correction to obtain a bias-adjusted overall
effect. Furthermore, this adjusted model served as the baseline for all subsequent
moderator analyses to support an unbiased interpretation of moderator effects.

Overall Effect Size and Sensitivity Analysis

The three-level meta-analysis of the illusory truth effect for 366 effect sizes
retrieved from 182 studies described in 99 unique articles yielded an estimated small to
medium size effect. The PEESE-corrected overall effect size ranged from g = 0.35, 95%
CI [0.29, 0.42] to g = 0.44, 95% CI [0.37, 0.51] depending on the values imputed for
missing standard deviations (u = 136) and missing correlation coefficients (u = 282). This
interval was obtained from a sensitivity analysis using the minimum and maximum
estimated values (i.e., minimum/maximum of previously observed values) for imputed
standard deviations and correlation coefficients. When the median estimated values were
taken, we found an effect size g = 0.37, 95% CI [0.30, 0.44] (see Table 2).

Additionally, a substantial variability was found both for effect sizes extracted
from the same study (i.e., level 2 within-study heterogeneity) and from different studies
(i.e., level 3 between-study heterogeneity). Depending on the computed missing values,
the estimated variance components varied for τ² = 0.054 to 0.101 and τ² = 0.099
Level 2 Level 3
to 0.148. The related I² value indicated that 26% to 36% of the total variance could be
attributed to within-study differences in effect sizes, and that between-study
heterogeneity explained I² = 36% to 70% of the total variation. We found that the three-
level model provided a significantly better fit compared to a two-level model with level
3 heterogeneity constrained to zero (χ²(1) = 32.65; p < .001).

The strong within and between-study heterogeneity, Q(364) = 4445, p < .001, calls
for caution in interpreting the estimated overall effect size and suggests that differences
in the methods used in the different studies may be at the root of the observed
heterogeneity (see the meta-regression below for such analysis).

To investigate whether heterogeneity in standard deviations contributed to
variation in effect sizes, we conducted a three-level meta-regression using the coefficient
of variation (CV) as a moderator. This analysis revealed a significant negative
relationship between CV and the standardized mean differences, b = -0.53, 95% CI [0.39,
0.58], t(330) = -4.30, p < .001, indicating that effect sizes were smaller in studies with
higher relative dispersion of truth judgments. This finding suggests that variability in
outcome precision may partially account for between-study heterogeneity.

Risk of Bias

Using the RoB-2 framework, 43 of the 182 studies were judged at low overall risk,
while the remaining 139 raised some concerns. Among the five RoB-2 domains, deviation
from intended intervention (Domain 2) raised concerns in 86 studies and selection of the
reported results (Domain 5) in 138 studies, primarily resulting from lack of pre-
registration processes. Supplementary Data 2 describes every study by the five RoB-2
domains. Figure 2 provides a weighted summary.

A three-level meta-regression using overall RoB grade as a moderator showed no
significant difference between effect sizes from studies at low risk of bias and those with
some concerns, b = 0.12, 95% CI [-0.02, 0.2 6], t(363) = 1.63, p = .104. Thus, the risk-of-
bias analyses suggested that the pooled illusory truth effect remained stable after
controlling for study-level biases.

Meta-regression

We performed a meta-regression to investigate the moderating factors at the root
of the within-study and between-study heterogeneity. To handle missing values in
moderator variables, we used multivariate imputation by chained equations (mice) 47.
This method fills in missing moderator values by estimating them based on patterns in
the observed data (e.g., other moderators and effect sizes), preserving the relationships
among variables and reducing the loss of information that would result from excluding
cases with missing values. We created 20 imputed data sets, each with a maximum of 20
iterations to ensure convergence of the chained equations. We then pooled the resulting
coefficients and their variances according to Rubin’s rules to obtain the meta-analytic
estimates 47. As a result, the adjusted degrees of freedom associated with t-statistics also
account for the variability introduced by multiple imputations 48. The results of each meta-
regression reported below presents the effect of one moderating factor while all other
moderating factors are held constant. To provide an overview of effect sizes within each
subgroup, we also report the subgroup estimates. Because these values are not adjusted
for the other moderators, they are not directly comparable to the coefficients from the
multivariate meta-regression. Supplementary Data 3 summarizes the subgroup analyses
contrasted with Dechêne et al.’s meta-analysis 2. A visualization of the meta-regression
results is presented in Figure 3.

For brevity, omnibus test results described below are those obtained using the
median to impute missing standard deviations and correlation coefficients. Any
inconsistent results obtained through sensitivity analyses of the missing outcome of
interest (i.e., minimum-maximum estimations) are further specified. Supplementary Data
4 provides the full comparative results of the moderator analysis, including sensitivity
analysis with the minimum and maximum estimations for missing outcomes.

Studies on the illusory truth effect use a variety of materials such as trivia
statements, topic-specific or general knowledge statements, social media news headlines,
conspiracy theories, political claims, marketing advertisements, and meaningless
sentences. In our coding, these were grouped in three categories: standard statements,
headlines, and claims. The illusory truth effect was significantly larger in studies using
standard statements (g = 0.41, 95% CI [0.33, 0.48]; observed u = 309) compared to
headlines (g = 0.17, 95% CI [0.01, 0.34]; observed u = 43), b = 0.25, 95% CI [0.01, 0.48],
t(147) = 2.10, p = .038, but not compared to claims (g = 0.47, 95% CI [0.20, 0.73];
observed u = 12), t(147) < 1. Effect sizes did not significantly differ between news
headlines and opinion-based claims, t(138) < 1.

Repetition can be manipulated either within-participants (e.g., each participant
judges both repeated and new items), or between-participants (e.g., one group judges only
repeated items and another only new items). The illusory truth effect did not significantly
differ whether repetition was manipulated within-participants (g = 0.38, 95% CI [0.30,
0.45]; observed u = 361) or between participants (g = 0.17, 95% CI [-0.28, 0.61]; observed
u = 5), t(252) < 1.

In primary studies, the task participants perform during initial exposure to
information varies widely, from passively reading statements, to making unrelated
judgments (e.g., rating interestingness, categorizing), to explicitly evaluating
truthfulness. A significant moderating effect was found for the content of the task used
during the exposure phase. When participants were asked for a truth judgment during the
exposure phase (g = 0.10, 95% CI [-0.103, 0.23]; observed u = 78), the illusory truth effect
was consistently reduced compared to irrelevant tasks (g = 0.42, 95% CI [0.34, 0.50];
observed u = 213), b = -0.32, 95% CI [-0.47, -0.16], t(264) = 4.02, p < .001, or passive
processing (g = 0.47, 95% CI [0.34, 0.60]; observed u = 73), b = -0.46, 95% CI [-0.70, -
0.23], t(200) = 3.94, p < .001. However, the illusory truth effect did not significantly vary
when the exposure task involved passive processing compared to performing an irrelevant
task, t(195) = 1.69, p = .093.

Some studies warn participants that some information may be false, either before
the exposure phase or before the test phase. We coded these as separate moderators
because their timing may inform of the engagement of different cognitive processes.
Providing a truth warning did not moderate the illusory truth effect at either phase of the
experiment. During the exposure phase, the effect did not differ significantly with a truth
warning (g = 0.34, 95% CI [0.25, 0.43]; observed u = 163) or without one (g = 0.44, 95%
CI [0.32, 0.57]; observed u = 41), after controlling for other moderating variables, t(86)
< 1. Similarly, the illusory truth effect with a warning (g = 0.38, 95% CI [0.27, 0.48];
observed u = 66) did not differ compared to no warning (g = 0.37, 95% CI [0.26, 0.49];
observed u = 41) in the test phase, t(27) < 1.

Veracity cues refer to any explicit or implicit indicators of a statement’s truth
status, such as labels (disputed by a third-party fact-checker), epistemic qualifiers (it is
unlikely that…), source reliability cues (all statements voiced by female are false), or
corrective feedback (e.g., immediately after initial exposure, or at the end of exposure
phase). In our coding scheme, we classified these cues by valence (e.g., true, false, or no
cue) regardless of the type of cue. The valence of veracity cues significantly moderated
the illusory truth effect. Across cue types (e.g., any timing or format), providing false
cues during the exposure phase (g = -0.18 , 95% CI [-0.33, -0.03]; observed u = 40)
decreased the effect compared to no cues (g = 0.43, 95% CI [0.36, 0.50]; observed u =
287), b = -0.66, 95% CI [-0.83, -0.49], t(219) = 7.70, p < .001, and providing true cues (g
= 0.70, 95% CI [0.51, 0.88]; observed u = 33), b = -0.86, 95% CI [-1.04, -0.68], t(244) =
9.47, p < .001). Additionally, explicitly labelling statements as true yielded a larger
illusory truth effect compared to no veracity indication, b = 0.20, 95% CI [0.01, 0.40],
t(229) = 2.05, p = .042. However, this was not robust with sensitivity analysis using
maximum estimates of missing values, t(275) = 1.15, p = .253. No other moderating
effects were found.

We also conducted an exploratory analysis to assess the effect of the type of cue
on the illusory truth effect. We found a significant decrease in the illusory truth effect
when using false cues involving epistemic qualifiers (g = -0.57, 95% CI [-0.87, -0.29];
observed u = 7), source reliability cues (g = -0.73, 95% CI [-0.95, -0.50]; observed u =
16), immediate feedback (g = -0.91, 95% CI [-1.44, -0.39]; observed u = 2), and delayed
feedback (g = -1.12, 95% CI [-1.51, -0.73]; observed u = 7). Among these, false delayed
feedback was significantly more effective than false epistemic qualifiers in reducing the
effect (b = –0.55, 95% CI [–1.04, –0.06], t(263) = 2.20, p = .029). In contrast, false labels
showed no reliable effect (g = 0.04, 95% CI [-0.29, 0.38]; observed u = 5). Given the
small number of effect sizes in several categories, these findings should be interpreted
cautiously (see Supplementary Methods).

The length of time between initial exposure to information and subsequent truth
judgment varies considerably across studies, ranging from immediate testing to delays of
several weeks. We coded this as a four-level moderator: no delay, within day delay, up to
one week delay, and more than one week delay. The illusory truth effect was significantly
smaller when the test phase followed the exposure phase in the same day (e.g., after a
distractor task) (g = 0.33, 95% CI [0.23, 0.43]; observed u = 138) compared to when test
phase followed exposure phase in the same week (g = 0.36, 95% CI [0.21, 0.50]; observed
u = 47), b = -0.20, 95% CI [-0.37, 0.03], t(278) = 2.29, p = .023, and compared to no
delay conditions; however, this difference did not reach significance (g = 0.46, 95% CI
[0.35, 0.56]; observed u = 135), b = 0.12, 95% CI [-0.26, 0.01], t(254) = 1.82, p = .070.
No significant difference was found when comparing studies with a same day delay to
those with a delay over a week (g = 0.25, 95% CI [0.06, 0.44]; observed u = 41), t(82) =
1.07, p = .290. The difference between no delay and a same day delay was not robust
using maximum estimates for estimating missing data t(301) < 1. No other moderating
effect of delay was found.

Repeated information can be presented verbatim (e.g., identical wording as in the
initial exposure), or as a gist repetition (e.g., preserves the core meaning while altering
surface details). No moderating effect of the repetition type was found. The illusory truth
effect did not differ significantly between studies in which the statement was repeated
verbatim (g = 0.36, 95% CI [0.29, 0.44]; observed u = 350) or gist (g = 0.63, 95% CI
[0.35, 0.91]; observed u = 16) in the test phase, t(243) = 1.19, p = .237.

Repeated statements are presented either visually (e.g., written text), verbally
(e.g., spoken), or through a combination of both modalities. No effect of the presentation
mode on the illusory truth effect was found. The effect sizes did not differ between study
designs with visually presented statements (g = 0.38, 95% CI [0.31, 0.46]; observed u =
257), compared to verbally presented statements (g = 0.30, 95% CI [0.12, 0.48]; observed
u = 62), t(158) < 1, or both modes of presentation (g = 0.32, 95% CI [0.02, 0.62]; observed
u = 17), t(61) < 1.

Across studies, the duration participants are given to view or hear each statement
varies considerably, both during the initial exposure and at the later truth judgment. To
ensure a balanced distribution of effect sizes across categories, we coded presentation
time into three categories: 5 seconds or less, more than 5 seconds, and participant-paced.
By coding presentation time at both stages, we can assess whether the illusory truth effect
is more strongly moderated by encoding or retrieval conditions.

During the exposure phase, studies with a presentation time longer than 5 seconds
reported larger effect sizes (g = 0.48, 95% CI [0.33, 0.63]; observed u = 92) than those
with self-paced presentation time (g = 0.34, 95% CI [0.26, 0.43]; observed u = 179), b =
0.37, 95% CI [0.12, 0.61], t(184) = 2.96, p = .003, and those with a presentation time 5
seconds or less (g = 0.39, 95% CI [0.26, 0.52]; observed u = 77), b = 0.39, 95% CI [0.15,
0.64], t(214) = 3.14, p = .002. However, in sensitivity analysis using maximum estimates,
the effect size difference was only marginal between self-paced presentation and
presentations of more than 5 seconds, t(189) = 1.86, p = .065, and non-significant between
presentations of 5 seconds or less and more than 5 seconds, t(186) = 1.62, p = .108. Effect
sizes did not differ between studies in which presentation time was 5 seconds or less and
those in which presentation was self-paced, t(265) < 1.

During the test phase, no moderating effect of presentation time on the magnitude
of the illusory truth effect was found. A self-paced presentation yielded similar effect
sizes (g = 0.37, 95% CI [0.30, 0.45]; observed u = 314) compared to a presentation of 5
seconds or less (g = 0.42, 95% CI [0.19, 0.64]; observed u = 29), t(245) = 1.16, p = .246,
or more than 5 seconds (g = 0.27, 95% CI [-0.02, 0.56]; observed u = 19), t(125) < 1.
Similarly, no difference of effect was found for a presentation of 5 seconds or less or a
presentation of more than 5 seconds, t(122) = 1.08, p = .281.

In primary studies, truth judgments can be assessed using different response
formats, such as binary (e.g., true/false), Likert-type scales, or continuous sliders. In our
coding, we grouped these into three categories: binary, Likert, and 100-point slider scale.
We also distinguished scales with an odd number of points (i.e., allowing a midpoint)
from those with an even number of points (i.e., forcing a choice). The size of the illusory
truth effect did not vary between studies using Likert Likert (g = 0.36, 95% CI [0.29,
0.44]; observed u = 269) vs. binary scales (g = 0.43, 95% CI [0.30, 0.56]; observed u =
91), t(260) < 1, or 100-point sliders (g = 0.23, 95% CI [-0.17, 0.62]; observed u = 6),
t(212) = 1.45, p = .148. Similarly, the effect size did not vary between odd (g = 0.30, 95%
CI [0.18, 0.43]; observed u = 119) vs. even (g = 0.40, 95% CI [0.32, 0.47]; observed u =
241) scales, t(267) < 1

The factual status of items varies across experiments. In addition, the overall
proportion of true statements in the stimulus set differs across studies, from 0 (all false)
to 100 (all true), with many using mixed proportions. We coded these features as two
moderators: statements’ veracity (true, false, none), and proportion of true statements
(continuous variable from 0 to 1). The size of the illusory truth effect was not modulated
the factual truth of the exposed statements. Repetition of true statements (g = 0.46, 95%
CI [0.36, 0.56]; observed u = 83) yielded similar effect sizes compared to false statements
(g = 0.33, 95% CI [0.23, 0.42]; observed u = 81), t(63) < 1, or non-verifiable statements
(e.g., opinions, meaningless statements) (g = 0.31, 95% CI [0.12, 0.49]; observed u = 12),
t(52) = 1.40, p = .167. Similarly, the proportion of true or false statements showed no
influence on the effect size (b = -0.02, 95% CI [-0.39, 0.35]; observed u = 339), t(175) <
1, indicating that the illusory truth effect is similar across different proportions of true vs.
false statements.

Studies on the illusory truth effect have been conducted in both face-to-face
laboratory settings and online environment with surveys. The illusory-truth effect did not
differ between online (g = 0.40, 95% CI [0. 32, 0.48]; observed u = 196) and face-to-face
(g = 0.31, 95% CI [0.20, 0.43]; observed u = 169) testing contexts, t(231) < 1.

Averaged across the 20 multiple imputed datasets, the pseudo-R² for the between-
study variance was 0.37 (range = 0.35-0.41). On average, 37% of the between-study
heterogeneity relative to the PEESE-adjusted baseline model was accounted for by the
moderator set. Supplementary Figures 1-16 display forest plots stratified by item type,
exposure instructions, veracity cues, and presentation time at exposure.

Methods
Transparency and Openness

We followed the PRISMA 2020 guidelines for systematic reviews67 (with the
checklist available in Supplementary Table 1). Data analysis and visualization were
conducted in the statistical environment R (v.4.4.2) 68 running under RStudio
(2024.12.1+563) 69, with the code written following 70 guidelines and using the package
“metafor” (v.4.8.0) 71. Data processing and reshaping were performed using “tidyverse”
(v.2.0.0)72, visualizations were produced with “ggplot2” (v.3.5.1)73, missing-data patterns
were inspected using “VIM” (v.6.2.2)74, and risk-of-bias figures were generated using
“robvis” (v.0.3.0)75. Missing moderating factors were imputed with the package “mice”
(v.3.17.0)47. This review was not pre-registered. No review protocol was prepared.

Eligibility Criteria

Relevant studies were identified based on the following inclusion criteria:
1. Population: human population of any age, including those from clinical groups
2. Intervention: verbatim or gist repetition of statements (e.g., trivia, political,
marketing) presented verbally or visually
3. Comparator: within-subjects (repeated vs. non-repeated statements) or between-
subjects (non-repetition control vs. repetition group)
4. Outcome: numerical (Likert-type scale, slider or similar) or binary (true/false)
measure of subjective truth judgments, comparing truth ratings for new versus
once-repeated items and non-repeated items (between-item criterion)
5. Study type: empirical quantitative studies

Any document written in English with unique data was considered regardless of
publication status, publication type, or year of release. We used several exclusion criteria
to reduce heterogeneity in effect sizes. We excluded studies that involved (1) veracity
cues during truth judgment in the test phase, (2) multiple exposure to a statement before
evaluation (e.g., participants are exposed to a same statement twice or more before test
phase), (3) labels tagging repeated and new statements, or (4) an intervention to reduce
the illusory truth effect. We also excluded studies in which the illusory truth effect was
measured (5) by repeating contradictory or incongruent statements compared to the first
exposure to that statement. (6) In contrast to the previous meta-analysis 2, all studies that
used a within-item criterion to detect the illusory truth effect were excluded because most
studies since 2006 have used the between-item criterion to measure illusory truth effect.
Moreover, we excluded studies that (7) did not ask participants to rate the veracity of the
statements (e.g., agreement or belief ratings), (8) did not report effect sizes or enough data
to compute such effect sizes (i.e., mean of repeated or new statements). Finally, we
excluded any (9) duplicated data. If the same data from multiple eligible publications
fitted our inclusion criteria, we included only the data from the first peer-reviewed
publication.

Information Sources, Search Strategy and Selection Process

First, we retrieved all articles (n = 89) included in the most recent systematic
literature review of the illusory truth effect 3. To identify articles published since the ones
included in the systematic review (i.e., from February 2020), we screened the following
database EBSCOHOST (APA PsycArticles, APA PsycInfo, Business Source Premier,
EconLit, Psychology and Behavioral Sciences Collection), NBCI (PubMed), Elsevier
(Scopus), Web of Sciences, OSF Preprints (PsyArXiv, Thesis Commons), Google
Scholar, and ProQuest (Dissertations & Thesis) with the keywords used by Henderson et
al. 3: “illusory truth”, “illusory truth effect”, “illusions of truth”, “reiteration effect”,
“repetition induced truth effect”, “repetition based truth effect”, “truth effect”, "truth
judgment". These keywords were validated by Henderson et al. 3 to identify a
predetermined set of 20 eligible articles in Web of Science and Scopus. Additionally, we
searched database using their extensive revised keywords (cf. Supplementary Methods).

We used “Zotero” and “Publish or Perish” 76 software to export results and retrieve
the title and the abstract of each article. This combined search conducted in September
2022 yielded a total of 2166 articles, from which 192 duplicates were removed using an
automatic tool from Zotero, and 37 additional articles were manually identified as
duplicates and were removed. Out of the 1971 remaining articles, we added the articles
identified by Henderson et al. 3, for a total of 2027 articles. Titles and abstracts were
screened to determine whether full text should be retrieved based on relevance (i.e.,
experimental articles, mention of repetition or fluency…). All titles and abstracts were
screened by two reviewers (S.Y. & M.G.) independently, and every article selected by
any of the two reviewers was retained for the full-text check. The title and abstract check
yielded a total of 135 articles, for which full texts were retrieved. Finally, inclusion and
exclusion criteria were assessed for each full text article by three reviewers (S.Y., M.G.,
& Y.B.).

We conducted an update to the systematic review on 24 February 2025, using the
same databases, keyword string, and screening procedures that were applied to the
original review. Limiting to records published after September 2022 returned 2433
titles/abstracts. After removing 1234 duplicates with Zotero’s automatic tool and 26
duplicates through manual inspection, 1173 unique records remained. Title and abstract
screening excluded 1117 of these records, leaving 56 additional articles to be assessed for
eligibility, 10 of which could not be retrieved even after messaging the authors. Figure 4
provides the flow diagram of systematic review and study selection, and Supplementary
Data 5 lists all excluded effect sizes and studies with justifications.

Data Extraction and Coding

The following information was extracted from each study: (1) year of publication,
(2) publication journal (i.e., name of the journal, or unpublished manuscript/thesis),
(3) sample size, (4) country in which the study was conducted, (5) experimental design, (6)
design of repetition manipulation (e.g., within-participants, between-participants), (7)
type of stimulus (e.g., trivia statements, news headlines…), (8) means and standard
deviations for repeated and new statements, (9) reported effect size, (10) reported effect
size’s standard error, (11) correlation between repeated and new statements. For all
outcome of interest that were not reported, the reviewers searched in open data and
supplementary materials when available.

When a study included multiple conditions such that only some conditions met
our inclusion criteria, we extracted data exclusively from those qualifying conditions.
Specifically, if a study provided distinct outcome metrics for each condition or made raw
data available, we retained only the eligible subsets that satisfied our criteria and excluded
the ineligible ones. In instances where outcomes for eligible and ineligible conditions
were reported only as combined results, making it impossible to isolate appropriate data,
we excluded the entire study to maintain methodological consistency.

In total, three reviewers collected data from every article independently: S.Y.
coded data for all articles, M.G. coded data of half of the articles (first half ranked in
alphabetical order of articles’ first author name), and Y.A. coded data of the other half of
the articles. All the 135 articles selected by title and abstract were at least double-checked,
and the final 70 included articles based on full text check of inclusion and exclusion
criteria were double-coded. The intercoder agreement for inclusion/exclusion was 91%
(Kappa = 0.84). All disagreements between reviewers were discussed until consensus was
reached.

Extraction of Moderating Variables

To determine whether the size of the illusory truth effect was moderated by
specific variables, we systematically coded a targeted set of information for each study.
When recoding was necessary, especially in cases where theoretical guidance for
categorization was limited, we ensured a balanced distribution of effect sizes across
categories to ensure that each category was adequately represented. When a study
included effect sizes potentially matching multiple categories of a moderator, we
extracted each effect size individually whenever the data (e.g., distinct outcomes or open
datasets) permitted clear separation. In instances where effect sizes were reported in a
combined form and could not be disentangled by moderator category, we coded the
moderator as missing. The intercoder agreement for moderating variables was on average
92% (ranging from 60% to 100%).

Item type. We included item type (e.g., trivia, headlines, opinions) to examine
whether the illusory truth effect generalizes across common real-world formats,
especially given the prominence of news headlines and unverifiable claims in online
misinformation. We coded the item type used in each study to examine differences in
effect sizes across three categories: standard statements (u = 309), defined as any
declarative sentences; headlines (u = 43), defined as items formatted as social media news
headlines, and claims (u = 12) included unverifiable assertions (e.g., any kind of opinions
or marketing claims).

Repetition study design. To evaluate whether the illusory truth effect varies
based on repetition format, we examined whether participants were exposed to repeated
and new statements within the same condition or in isolation. We coded whether the effect
size was extracted from a within-participant (u = 361) or a between-participant (u = 5)
manipulation of the repetition. In between-participant designs, two groups of participants
evaluated either all-repeated or all-new statements during the test phase.

Instructions during the exposure phase. We examined the moderating effect of
participants’ task during the initial exposure to determine how different levels of
cognitive engagement during encoding influence susceptibility to the illusory truth effect.
Participants completed a range of tests (e.g., read, rate interestingness, categorize,
rate veracity, rate familiarity, evaluate the source of information, evaluate belief or doubt,
guess the gender of the author, rate humor, rate sharing intention, rate understanding, or
shake/nod their head). Participants could also perform more than one task (e.g., evaluate
interest and veracity of a statement). These categories were recoded in three categories:
truth judgment (u = 78, including all effect sizes in which participants had to rate veracity
during exposure phase), passive processing (u = 73, including all effect sizes in which
participants had to read, listen, or perform any action not requiring to process and
manipulate information in working memory such as nodding or shaking their head), and
irrelevant task (u = 213, including all effect sizes in which participants had to manipulate
information in working memory, or perform a judgment unrelated to veracity rating).

Truth warning at the exposure phase. This moderator reflected whether
explicitly alerting participants to potential falsehoods prior to exposure modulates the
illusory truth effect. We coded whether participants were explicitly instructed that some
or half of the statements were true or false in the exposure phase, including the presence
of cues (u = 163), or did not provide any explicit warning (u = 41). To prevent any risk
of miscategorization, we coded studies that did not specify whether participants were
warned about the statement’s veracity or did not provide the full verbatim of the
instructions to participants as missing data (u = 162). Instructions to rate the truth of
statements were not coded as explicit warnings.

Truth warning at the test phase. As warnings at test and exposure are likely to
influence truth judgments through distinct cognitive mechanisms and serve different
theoretical functions 27, we coded truth warnings at the exposure and test phases as
separate moderators. We followed the same procedure as for the warning during the
exposure phase, coding studies in which participants were warned (u = 66) or not (u = 41)
that statements could be false in the test phase. Similarly, we coded missing data (u =
259) if the warning status is not specified (or respecified for the test phase).

Veracity cues. We included the valence of veracity cues as a moderator to
examine the impact of cues that signal truth or falsity, which are commonly used in
misinformation interventions such as fact-checking. We coded each effect size that
involved any indication of a statement’s factual status during the exposure phase. We
classified veracity cues into three subgroups: true cues (n = 33), false cues (n = 40), or
uncued (n = 287).

Delay. We examined the influence of delay between exposure and test to assess
the temporal durability of the illusory truth effect. This moderator helps understanding
the long-term influence of repeated information in both experimental and applied settings.
We coded each study for the delay introduced between the exposure and test phases, from
no delay to a few minutes to a few months, in 4 categories: no delay (u = 135, with effect
sizes extracted from a procedure involving test phase immediately following exposure
phase), within day (u = 138, including all effect sizes with a delay ranging from a few
minutes to one day), up to a week (u = 47, including all effect sizes with a delay ranging
from two days to one week), more than a week (u = 41, when the delay was superior to a
week). When the delay was not specified, we assumed that the test phase immediately
followed the exposure phase.

Repetition type. This moderator reflected whether exact repetition (verbatim) and
paraphrased repetition (gist) differentially influence perceived truth, as these forms
commonly occur in real-world contexts. We coded whether the statement repeated in the
test phase was a verbatim (u = 350) or a gist (u = 16) of the statement presented in the
exposure phase. When no information was provided, we assumed that the statements were
verbatim repetitions.

Modality of presentation. We included the modality of presentation to
understand how the presentation channel affects the illusory truth effect. This moderator
accounts for variability in how content is encountered across studies and reflects real-
world differences in media consumption. We coded whether the statements were
presented visually (u = 257) (i.e., written) or verbally (u = 62) (i.e., read aloud). We coded
the modality of presentation as missing data when the modality of the statement
presentation differed between the exposure and the test phase (e.g., verbally in the
exposure phase and visually in the test phase, u = 25) or when statements were presented
both verbally and visually (u = 17).

Presentation time during exposure. This moderator reflected whether the
duration of initial exposure affects the illusory truth effect. Exposure time is a key
methodological factor that may affect encoding depth and fluency. This moderator also
reflects real-world variability in how long individuals attend to repeated information,
making it relevant for interpreting the robustness of the effect in ecological settings. We
coded the presentation time of the statement presentation in the exposure phase. When
the presentation time was not specified and the statements were presented visually, we
assumed that presentation time was participant- paced. We coded the presentation time
as missing data when the statements were presented verbally (u = 5). To ensure a balanced
distribution of effect sizes across categories, we grouped the effect sizes based on
presentation time: 5 seconds or less (u = 77), more than 5 seconds (u = 92), and
participant-paced (u = 179).

Presentation time during test. To examine whether the amount of time available
for truth judgments moderates the illusory truth effect, we examined the presentation time
during the test phase. Varying test durations may influence the extent to which
participants rely on quick, fluency-based heuristics versus more deliberative evaluation.
We coded the extent to which the presentation time of the statements was the same
between the exposure and the test phase. When not specified, we assumed that the
presentation time was participant-paced. There was u = 43 effect sizes with a presentation
time during test of 5s or less, u = 54 of more than 5s, and u = 265 of participant-paced.

Response scale. We coded whether the response scale was a Likert scale (u =
269), a binary scale (u = 91) (e.g., yes vs. no), or a slider from 0 to 100 (u = 6) to examine
whether the precision of the response format used to evaluate truth judgments influenced
the effect size. Additionally, we distinguished response scales based on whether they had
an odd number of points (u = 119) or an even number of points (u = 241). The goal was
to explore the moderating role of a neutral or midpoint option (e.g., 3 on a 5-point scale),
versus even-numbered scales that force participants to express a choice that leans in one
direction or another (i.e., there is no true midpoint).

Proportion of true statements. We included the proportion of true statements to
evaluate whether the overall truth base rate within a study influences participants’
sensitivity to repetition. This moderator captures variation in the informational context
(e.g., all-true, all-false, or mixed item sets), which may affect the baseline likelihood of
endorsing repeated items as true. To capture design variability across all‑true, all‑false
and mixed item sets, we created a continuous moderator (range 0-1) that records the
proportion of factually true statements in each study’s stimulus pool (e.g., 0 = all false;
0.50 = 50 % true/50 % false; 1 = all true).

Veracity. We investigated whether repetition increases perceived truth for true
vs. false statements equally which relates to the illusory truth effect in the misinformation
context. Effects sizes obtained using factually true (u = 83) or false (u = 81) statements
were coded accordingly. In case where the statement could not be true or false (e.g.,
opinion-based statements), the effect size was recoded as none (u = 12). We coded the
veracity as missing data when the factual veracity of a statement was not indicated or
when the statements were a mix of true and false statements (u = 190).

Testing environment. We examined the effect of testing environment to assess
whether the data collection setting (online vs. face-to-face) introduces variability in effect
sizes. This is especially relevant considering the increasing use of online platforms in the
illusory truth effect research. It also helps evaluate the generalizability of laboratory
findings to digital contexts where repeated misinformation is most encountered. We
coded whether data were collected online (u = 169) or in face-to-face (u = 196).

Missing Data in Moderating Variables

When data on the moderating variables considered in this meta-analysis were not
directly available, the reviewers examined open data and supplementary materials when
available. Missing data were then imputed using multivariate imputation by chained
equations with “mice” package 47 in R. This method allowed us to preserve the
relationships between variables while avoiding data losses associated with deletion
methods. During the imputation process, we generated 20 datasets ensuring the
robustness of the imputation. This approach allows to overcome the risks of producing
inaccurate results when running the meta-regression due to the number of missing data
for moderating variables 77.

Effect Size Calculation and Missing Outcome of Interest

The outcome of interest was the standardized mean difference g 78 of the truth
judgment in the test phase of the new statements and of the ones already presented in the
exposure phase. To compute g, we first computed the standardized mean difference d 79
by dividing the mean difference in a given study by its standard deviation 80. For missing
effect sizes, we followed the general guidelines of the Cochrane handbook for systematic
reviews of interventions 81. When the effect size was not reported, we estimated d from
the mean and the standard deviation reported in the study. The standard error of the effect
size was computed based on the sample size of each study to assign a weight to each of
them. When the exact number of participants in each group in a between-subject design
was missing, or could not be estimated (e.g., from open data or df), we assumed that the
two groups included the same number of participants. Missing effect sizes were thus
computed as follows 80:

(1)
𝑑 = (𝑌1 − 𝑌2) / 𝑆𝐷𝑤𝑖𝑡ℎ𝑖𝑛

with standard deviation within groups computed as follows:

(2)
𝑆𝐷𝑤𝑖𝑡ℎ𝑖𝑛 = 𝑆𝐷𝑑𝑖𝑓𝑓 / √2(1−𝑟)

the standard deviation of the difference as follows 81:

(3)
𝑆𝐷𝑑𝑖𝑓𝑓 = √𝑆𝐷1^2 + 𝑆𝐷2^2 − 2×𝑟×𝑆𝐷1×𝑆𝐷2

and the standard error of the effect size as follows:

(4)
𝑆𝐸𝑑 = √𝑉 = √(1/𝑛 + 𝑑^2/2𝑛) × 2(1−𝑟)

When the standard deviation of each group was not provided, we estimated one based on
the median of the truth judgment for the new and repeated statements in the test phase in
the other included studies using a similar scale. Given that the standard mean error d tends
to overestimate the effect size of small samples, we computed the Hedge’s g 78, an
unbiased estimate of d. We applied the following correction using the correction factor J
80:

(5)
𝐽 = 1 − 3 / (4(𝑛−1)−1)

We obtained g as follows:

(6)
𝑔 = 𝐽 × 𝑑

And we computed the standard error as follows:

(7)
𝑆𝐸𝑔 = √𝑉 = √𝐽^2 × 𝑉𝑑

For studies adopting a between-subject design to evaluate the illusory truth effect (i.e., in
which truth judgment was compared between a group exposed to statements repeated
from the exposure phase and a control group exposed to new statements), we used the
formula proposed by Borenstein et al. 80 to measure the standardized effect size.

We also conducted a sensitivity analysis using Becker’s formula to compute the
standardized mean difference, which only requires standard deviations from the first
assessment and therefore avoids the need to impute correlations between repeated
measures 82. This approach yielded effect sizes close to those from Borenstein’s formula
but with slightly wider confidence intervals, reflecting greater uncertainty (see
Supplementary Table 2). We selected Borenstein’s method for the main analyses because
it yielded more stable estimates across studies, which facilitates interpretation and
comparability of effect sizes in the synthesis. However, we acknowledge that its greater
precision is contingent on the imputation of missing correlations, which may lead to
potentially overconfident uncertainty estimates.

Missing Outcomes of Interest and Sensitivity Analyses

Considering that: (1) calculating a standardized mean difference in a repeated
measure study design requires the correlation (r coefficient) between matched groups
(i.e., repeated and new statements) 80, (2) none of the included publication reported the
correlation coefficient in the full-text article, and (3) some of the included studies that did
not report the effect size also did not report the standard deviation of both repeated and
new statements, we computed missing values (i.e., standard deviations and correlation
coefficients) from previous studies and conducted sensitivity analyses to measure a range
of uncertainty.

We estimated missing standard deviations with the median of the standard
deviations reported in other studies using the same measuring scale for truth judgment in
the test phase (e.g., binary scale, 4-point Likert scale…). Missing correlation coefficients
were computed in a similar way: we computed the coefficient of correlation between
repeated statements and new statements when data were available. Otherwise, we
imputed the median of such coefficients of correlation.

Sensitivity analyses were performed to determine whether our results would be
affected if, instead of using the median, we used the minimum or maximum of the
standard deviations or correlation coefficients of other studies to impute missing data.

Statistical Analyses

We applied a random-effect approach, in light of the between-study heterogeneity
reported in the previous meta-analysis 2. We used a three-level meta-analysis model 40,41
to control for the dependence between the effect sizes reported on the same sample in
studies manipulating several potential moderating factors. This method appropriately
handles the clustering of effect sizes within individual studies and allows for estimation
of between-study and within-study variance.

In a three-level meta-analysis model, the variance within each study is adjusted
from the number of reported effect sizes. There are three different sources of variance:
the between-study level of variance (level 3), the variance between effect sizes extracted
from a same study sample (cluster) (level 2), and the variance in the sampling error for
each study (level 1). We used the restricted maximum-likelihood (REML) random model
to estimate the model parameters. The Knapp-Hartung-correction was applied; thus, a
two-sided t-test was used for testing our individual regression coefficients rather than a
Z-test 83. Meta-analyses and meta-regressions were performed in R using the “rma.mv”
function of the metafor package at a 5% significance level. In the meta-regression
analysis, the between-study (τ²) and within-study (σ²) variance components were
estimated from the complete set of effect sizes and kept constant across moderator
levels80. All statistical tests reported in this study were two-tailed, and all confidence
intervals are two-sided.

We additionally quantified the amount of between-study heterogeneity explained
by the moderator set with the pseudo-R² statistic 84:

(8)
Pseudo R2 = (τ²RE - τ²ME) / τ²RE

Where τ² is the level-3 variance from the baseline random-effects model and τ² is the
RE ME
residual level-3 variance from the mixed-effects model that includes all moderators. The
statistic reflects the proportion of between-study variance accounted for by the
moderators.

Risk of Bias

We used a version of the revised risk of bias tool for randomized trials (RoB 2) 43
which was adapted to the illusory truth effect experimental design for each study in five
areas: 1) risk of bias arising from the randomization process, 2) risk of bias due to
deviations from the intended interventions (effect of assignment to intervention),
3) missing outcome data, 4) risk of bias in outcome measurement, 5) risk of bias in selection
of the reported results. An overall risk of bias was then computed for each study. This
overall risk of bias was coded as low if all RoB 2 domains were low. If up to three RoB
2 domains were of concern, the overall risk of bias was coded as some concerns. It was
coded as high if one of the RoB 2 domains was high, or if four out of 5 domains were of
concern. Two reviewers (i.e., S.Y. & M.G.) undertook the task of coding independently
a random set of 10 included articles. The inter-reviewer agreement for the overall risk of
bias measure was strong (Kappa = .83). All disagreements between reviewers were
discussed until consensus was reached. The remaining articles were coded by S.Y.

Inclusion and Ethics

This study is a meta-analysis of previously published experimental studies and did
not involve new data collection or interactions with human participants. Inclusion of
studies was based solely on predefined eligibility criteria, without regard to the
geographic origin of the research. Ethical approval was not applicable to this study, as it
involved only the analysis of existing data. Informed consent and participant
compensation were obtained in the original studies, as reported in the respective
publications.

Data Availability

The data generated in this study is available in the Open Science Framework
(OSF) repository under accession85 DOI: https://doi.org/10.17605/OSF.IO/2DB8S. No
raw individual-level participant data were generated in this study. The processed data
underlying all analyses, including extracted effect sizes, moderator coding, and imputed
datasets, are available in the OSF repository. No data are subject to ethical, legal, or
commercial restrictions.

Code Availability

All analysis scripts used to perform the meta-analyses and generate the figures in
this study are available in the OSF repository under accession DOI:
https://doi.org/10.17605/OSF.IO/2DB8S.

Peer review rounds
[{"round": 1, "reviewer_comments": {"reviewer_1": "At the outset, we note that we have limited expertise in the statistical procedures of meta-analysis; we trust other reviewers will address the technical aspects. Turning to the psychological issues, this manuscript makes useful contributions to the illusion-of-truth (ITE) literature. Our comments draw attention to aspects that should be addressed in a revision. Introduction LL27-32 - These lines (which describe a correction strategy for fake news and the possibility of corrections to backfire) seems tangential to the current focus of the paper. Additionally, the cited paper (Pennycook et al., 2018) doesn’t investigate the effects of repeating fake news in the process of debunking it as the sentence seems to imply. I would recommend the authors stick to the focus on the effects of information exposure here (where the Pennycook et al., 2018 would still be relevant). LL33-34 - regarding “The illusory truth effect or repetition-induced truth effect is not restricted to fake news: any repeated statement tends to be judged truer than novel statements” - given there have been some exceptions noted (e.g., highly implausible/ plausible claims - Pennycook et al., 2018; Fazio, Rand, & Pennycook; 2019; headlines in the form of questions, Calvillo & Harris, 2022), we would tone down this claim a bit from “any repeated statement” LL64-68 - These lines suggest that inferring truth from processing fluency is always a misattribution. That is not the case. Fluency is a valid correlate of all major truth criteria from coherence to compatibility with one’s knowledge, social consensus, and so on. The problem is that people are insensitive to the source of the fluency experience and misread incidental fluency (e.g., from the readability of a print font) as indicative of coherence, consensus, and so on (Schwarz & Jalbert, 2020, in Greifeneder et al., Fake news, Routledge). LL70-76. – Empirically, manipulations of color contrast have a smaller effect than manipulations of repetition. However, it does not follow from this observation that “conceptual fluency” beats “perceptual fluency.” The latter conclusion about types of fluency (rather than specific singular manipulations) requires a calibration of the implementations of color contrast and repetition, ensuring equal subjective experiences of ease of processing. Without this calibration, all conclusions are limited to the manipulation and general inferences about types of fluency are unwarranted (although offered in the papers you cite). Methods LL159 following. – What is the rationale for excluding statements that were “not ambiguous” (common knowledge facts) and opinions? It would be worthwhile to include comparisons across these types of statements along with the present results. Piecemeal publication of these aspects in separate papers is not desirable. In addition, how were “common knowledge facts” defined in making these exclusions? Was a full study excluded if participants judged a mix of “common knowledge facts” and ambiguous information? Studies may just report the mean truth of the selected claims from pretesting with a mix of better-known and more ambiguous information. In addition, studies may not have norming data collected in the sample the study was conducted in, making the determination of whether or not they include claims that are “common knowledge facts” in that population impossible to assess. Finally, it is unclear why only ambiguous information is of interest, given the explicit goal of discussing practical implications regarding the current misinformation crises. Does repeating unambiguously false information nevertheless increase acceptance? LL161-171 - Can you clarify whether all data from a study were excluded if some (but not all) conditions met the exclusion criteria or if only the condition that met the exclusion criteria was excluded while the others were maintained? It currently sounds as if all conditions were excluded which suggests a loss of relevant data. LL256-262 - The impact of warnings depends on whether the warning occurs at exposure or test. For example, Jalbert et al., (2020) found that warnings only moderate the effect of repetition when they occur at exposure and have no effect when presented only at test (probably because asking for a truth judgment itself acts as a type of warning). There are important theoretical reasons to suspect that the timing of this warning is critical and that warnings at exposure and test should be analyzed separately rather than pooled into the same category. The ms also flags that many earlier truth effect papers do not contain sufficient information to determine whether or not a study included a warning as part of the standard instructions. Assuming that participants did not receive a warning when the paper doesn’t include information regarding these instructions may miscategorize the studies. It would be good to add an analysis that only includes studies with vs. without warnings at exposure to assess the effect of warnings. . LL229 - The size of the illusory truth effect depends on whether a within-ss or between-ss design is used. The effect is larger when participants judge a mix of repeated and new claims than when they judge only repeated claims (Dechêne et al., 2009 and related studies). It is therefore surprising that this meta-analysis apparently includes within-ss and between-ss studies without consistently differentiating between them. Within vs. between designs should be treated as an important additional moderating variable. LL301-302 - Why was the response scale coded by odd vs. even? Explaining the reason would be useful. LL304-305 - Why was data containing a mix of true and false claims excluded from the veracity comparison? This represents a large portion of the data and comparing true vs. false vs. mixed could provide useful insights. LL379 - We may have overlooked this, but we didn’t see whether or not effect sizes were fixed across subgroups? We would expect them to be fixed given recommendations by Borenstein et al. (2009) when the number of subgroups is small. Results Overall, the substantive results are useful and make a valuable contribution to the literature. Some details: LL450 following. – This paragraph is uninformative. We cannot meaningfully relate this material to specific variables, even with the help of the supplementary material. All p-values should be reported to the same level of specificity (some have 2 decimal places and some have three). It would also be useful to provide degrees of freedom and corresponding estimates of ds for each subgroup in the main text (or the difference between ds) Discussion We appreciate the comparisons of the present results with the earlier meta-analysis by Dechene et al. and are largely in agreement with the interpretations offered. LL550-551 - Jalbert et al. (2020) discuss ways in which making an initial truth evaluation at exposure (similar to a warning) may decrease the size of the illusory truth effect goes beyond the depth of processing account offered here. Asking people for a truth judgment necessarily entails that some of the claims may not be true. LL590-597 - The studies included in this paper do not include multiple truth judgments (i.e. an initial one and a later one) but the explanation provided is specific to this scenario. What about when participants do not complete multiple test phases? LL639-653 – When the fluency experience is (correctly or incorrectly) attributed to an incidental variable (e.g., repetition), the informational value of fluency is undermined. Awareness of the influence is more likely after very short delays (for a discussion, see Schwarz, Jalbert, et al., 2021). LL692-695 - Several recent papers report that debunking messages that include a repetition of false information do not always result in backfire effects (e.g., Ecker et al., 2020, Briony Swire-Thompson et al., 2020). These issues can be addressed in a revision that would further increase the contribution of this manuscript.", "reviewer_2": "I co-reviewed this manuscript with one of the reviewers who provided the listed reports. This is part of the Nature Communications initiative to facilitate training in peer review and to provide appropriate recognition for Early Career Researchers who co-review manuscripts.", "reviewer_3": "This is an extremely relevant article for those who approach the field of truth illusions. As a participant in the field, I appreciate the updated meta-analytic review work relative to the 2010 work by Dechene and colleagues, and the systematic map created by Henderson et al. in 2022. However, despite claiming its relevance, I believe the article has room for improvement, and I would like to see these revisions made before recommending its publication. My first point refers to the objectives of conducting this meta-analysis (p. 6). These should focus more on the gains it brings rather than on the deficits that previous approaches might present. While gains and deficits are related, I would recommend placing greater emphasis on what is gained. The argument that the advantage comes from greater rigor in estimates, enabled by the developments in the meta-analytic approach, is weak on its own. The studies are now more numerous, with greater variability in conditions, allowing for more consistent estimation of moderators’ roles and the inclusion of new moderators that were previously unexplored, among other benefits. These are all relevant arguments in favor of a new meta-analytic study. However, it is precisely in this area where the paper loses some strength—it adds very little to what we already know. There is no reason for this. Since 2010, many other questions have been raised about the effect, and these can be tested in a meta-analytic context. By framing the paper solely around emphasizing the rigor of effect estimation, an opportunity is being missed here. In my reading I would have liked to find not only evidence that corroborates or challenges Dechene’s conclusions but new evidence. For example, Dechene discusses the difference in effect size when the contrast is within-subjects versus between-subjects, highlighting that the fluency/familiarity experience may be relative. Since 2010, some studies have directly addressed this issue, providing data that could be included in this new meta-analysis. With this approach, the present paper would add secure knowledge to the previous paper adding content and not only more rigor in the estimation methods. There are also references in the original paper to differences in effect magnitude between repetition and fluency manipulations, and since then, more studies have been published that use both types of manipulations. I do not see familiarity being contrasted with fluency in this analysis. Another very relevant aspect that could not have been addressed 14 years ago is the nature of the information. When identifying the effect, the statements made were ambiguous. Today, many studies not only present factually false information but also add warnings, etc. These data are not addressed here. Essentially, what I think diminishes the relevance of this paper is that the moderation analyses are neither directly contrasted with the status quo provided by previous analyses nor clearly theoretically oriented. The analyses would gain relevance if they directly or indirectly answered theoretically significant questions (which would also facilitate and better integrate the data discussion). For instance, more than the instructions and the time spent reading the sentences at the first moment, it is the question of whether these factors may influence the explicit use of memory as information about the validity of a statement. If the effect is smaller when the instructions make it explicit that memory is not informative (with ½ true sentences and ½ false sentences presented at the start) than when nothing is stated, and this happens especially when there is encoding time, such a test could examine whether the effect depends on explicit versus implicit memory. Such kind of questions would induce to test the interaction between moderators and not only their main effects. In the same line of thought, I believe that the analysis contrasting the magnitude of effects between online and in-person conditions is presented without contextualizing its relevance (pragmatically to alert that the conditions do not allow the effect to be detected, or theoretically because we know the level of motivation of the respondents is different?). Therefore, it lacks a true discussion of the results. Personally, I find some conclusions drawn from the analysis of studies with very different methodologies concerning. For example, what happens when the authors conclude that the most relevant phase for deep processing is encoding, with retrieval not being relevant. In the retrieval phase, the time of sentence presentation is considered independently of whether they are presented immediately or one month after the study phase. In neither of these contexts does the exposure time influence retrieval conditions. One reason is that the information is still accessible in working memory or almost so, and in the other case, explicit accessibility does not improve with sentence presentation time. I believe that the text would benefit from better readability if the results of the moderation analyses were presented in Figure 4 within a table, and if on that table they were contrasted with previous meta-analyses, highlighting what differs and what is new. Please clarify, because I see no reason why the statistics are not presented in a more complete way, with their respective degrees of freedom and effect sizes. I would like to point out that when t<1, the p-value calculation is unstable and unreliable, so it does not need to be presented (see, for example, Voelkle et al., 2007). Finally, when I finished reading the discussion, I realized that the article could gain more consistency if it were to adopt a theoretical or pragmatic objective instead of an unbalanced mixture of both. When I read it, my interest was theoretical, and I wanted to understand the cognitive mechanisms underpinning the effect. But the article might aim for a pragmatic framework. In that sense, it is important to understand that misinformation goes beyond the truth illusion effect and should not be conflated. But if this is the main concern, it would be important to understand what the moderators say about the possibility of spreading fake news or how we can prevent it. I also have two small details that could assist in the more detailed revision of the presented text: Line 37: “after a certain delay” should be changed to “In most studies after a certain…” Line 39: “… and new statements previously unseen in a random order”", "reviewer_4": "General Assessment This meta-analysis presents a comprehensive and updated synthesis of the illusory truth effect, incorporating 108 studies and 195 effect sizes—a significant expansion compared to the previous meta-analysis by Dechêne et al. (2010). The authors employ a three-level meta-analysis framework to account for dependencies among effect sizes within studies, use meta-regression to explore sources of heterogeneity, and conduct sensitivity analyses with multiple imputation to address missing data under the MAR assumption. These methodological advancements strengthen the reliability of the findings. From my perspective as a statistical reviewer, the study implements several best practices in meta-analysis. However, there are specific aspects related to effect size calculation, heterogeneity, and small-study effects that could benefit from further refinement and discussion. Points of Critique 1. Standardized Mean Differences and Imputation of Missing Data The authors rely on standardized mean differences (Hedges’ g) as their primary effect size metric. While group means are often available, the standard deviations and correlations needed for standardizing within-group designs are frequently missing. To address this, the authors use imputation from external sources. However, an alternative approach that might reduce uncertainty in the pooled estimates is the method proposed by Becker, which only requires standard deviations from the first assessment occasion (see Morris & DeShon, 2002). This would eliminate the need for imputed correlations and likely yield more less uncertain effect size estimates. 2. Heterogeneity and Potential Multiplicity in Analytical Methods High heterogeneity is common in psychological meta-analyses, particularly those involving RCTs. Beyond variation in population, intervention, and outcome characteristics, one likely source of heterogeneity is the diversity of analytical methods used in the original studies to derive effect size estimates. The authors report substantial within- and between-study heterogeneity (I² ≈ 71%-81%), which raises interpretational concerns about the aggregated effect size. Additionally, reliance on standardized mean differences may further contribute to heterogeneity, as prior research has suggested (e.g., https://psycharchives.org/en/item/1b670ec4-fec9-43d8-b72c-ecb85b27d0e5). I recommend including a critical reflection on how potential hidden multiplicity and standardization might inflate heterogeneity in the discussion section. With regard to the impact of standardization, meta-regression on the coefficient of variation might be considered as another worthwhile sensitivity analysis. 3. Small-Study Effects and Publication Bias The study acknowledges the presence of small-study effects, which the authors attribute to publication bias. However, while the presence of small-study effects is noted, no corrective methods (e.g., PET-PEESE, selection models) are applied. Given the substantial heterogeneity, publication bias is a serious concern, and the lack of adjustment likely means that the reported effect size estimates are inflated. Based on the evaluation of small-study effect corrections by Carter, Schönbrodt, Gervais, and Hilgard (2019), I recommend implementing the PEESE method. The authors claim in the discussion section, that such methods cannot be implemented with multi-level meta-analyses. I do not agree, because the PEESE approach is essentially an ad-hoc meta-regression on sample precision. As such it is supposed to provide a pragmatic and conservative correction under conditions of questionable research practices and high heterogeneity. Additionally, I suggest using this adjusted model as a baseline before adding substantive moderators. This would allow for a clearer interpretation of the impact of study characteristics on the illusory truth effect, free from confounding small-study biases. 4. Reporting of Meta-Regression Results While the authors conduct a meta-regression to account for moderator effects, there are two areas where reporting could be improved: - Moderator Impact on Effect Size Scale: Regression coefficients should be explicitly reported in the main text (rather than supplementary materials) with confidence intervals to provide readers with a clearer understanding of how each moderator influences the standardized mean difference. A modification of Figure 4 to include these coefficients would be particularly useful. - Proportion of Heterogeneity Explained: The proportion of between-study variance accounted for by the meta-regression should be reported (e.g., pseudo R²). This would provide insight into the extent to which the included moderators successfully explain the observed heterogeneity. 5. Visualization of Effect Heterogeneity The authors include a funnel plot for assessing publication bias, that could be improved with regard to the contour enhancement proposed by Peters, Sutton, Jones, Abrams and Rushton (2008). Specifically, the contours are currently constructed around the naïve pooled effect estimate (that is unadjusted for small study bias). Instead, they should be constructed around to H0: g = 0 effect scenario, to facilitate the identification of those studies, that reported effect estimates just below the conventional 0.05% level. Precision-adjusted or naïve pooled effect estimates (and their CI regions) could then simply be added as a top-layer of figure elements. Additional visualization of the data would further improve interpretability: - Forest Plots Stratified by Key Moderators: Presenting supplementary forest plots ordered by major moderators (e.g., exposure task and delay, truth warning) would allow readers to see how effect sizes vary within each subgroup. Conclusion Overall, this meta-analysis provides a rigorous and updated synthesis of the illusory truth effect. The authors should be commended for their methodological choices, particularly in their use of three-level modeling and sensitivity analyses. However, I encourage further methodological refinement in the areas of effect size calculation, heterogeneity interpretation, and small-study effect adjustments. Addressing these points would enhance the robustness and interpretability of the findings. Recommendations for Revision 1. Consider Becker’s method for standardizing mean differences in within-group designs to reduce imputation uncertainty. 2. Reflect on the impact of standardization and hidden multiplicity on effect size heterogeneity in the discussion. 3. Implement small-study effect corrections, particularly the PEESE method, to provide more conservative effect size estimates. 4. Report regression coefficients and the proportion of heterogeneity explained by meta-regression in the main text. 5. Modify funnel plot and provide supplementary forest plots stratified by moderators. My own brief screening using PubMed and the search term from the paper returned several new primary studies on the illusory truth effect that have been published since Sep 2022. Although I dont assume, that those new studies will contribute substanially more information than currently compiled by the authors, an update of the meta-analysis would definitely be worthwhile. By integrating these refinements, this paper will provide an even stronger contribution to the literature on the illusory truth effect."}, "author_response": "Systematic review and meta-analysis of the evidence for an illusory truth effect and its determinants Response to Reviewers We thank the Reviewers for their constructive comments. All modifications in the manuscript were highlighted in yellow color. In the revised manuscript, we implemented the following changes to address the different issues: 1. Expanded our dataset to 366 effect sizes across 182 studies, including studies published up to February 2025. 2. Broadened inclusion criteria, by including opinion-based and non-ambiguous items. 3. Added several new moderators to capture methodological and contextual factors more precisely: - Item type: statements, headlines, or claims. - Veracity cues: positive, negative, balanced, or none. - Truth warning: we separated the coding for exposure and test phases. - Proportion of true statements in stimulus pool. - Study design: within vs. between-participant repetition manipulation. 4. Clarified our eligibility criteria and inclusion/exclusion of effect sizes drawn from studies with different methodologies based on the available data breakdown. 5. Updated our analytic strategy: - Applied small-study effect correction (PEESE) in the main meta-analytic model and subsequent models as a baseline. 6. Clarified our theoretical vs. practical scope by revising the Introduction and Discussion sections to better articulate the rationale and the aims of our meta-analysis. 7. Improved reporting transparency: - Standardized the reporting of p-values. - Included degrees of freedom, regression coefficients, and subgroup effect size estimates along with their 95% confidence intervals in the main text. - Created a summary table comparing moderator results with the previous meta-analysis (Dechêne et al., 2010). 8. Updated our tables and figures: - Added a systematic contrast of our findings with Dechêne et al. (2010) (Table 2) - Modified the funnel plot (Figure 1) to construct the contour around h = 0 with precision-adjusted and naïve pooled effect estimates as layers. - Modified the visualization of the meta-regression (Figure 3) to describe regression coefficients rather than standardized Z values. 9. Updated the Supplementary Information with: - A table describing studies by the five RoB2 domains - A sensitivity analysis of effect size computation method between Borenstein and Becker’s formula - Forest plots stratified by key moderators 10. Incorporated clarifications requested by the Reviewers. 11. Reorganized sections and subsections according to Nature Communications’ formatting guidelines. Detailed responses to each point raised by Reviewers are provided below. Reviewer 1 & Reviewer 2 Comments • Overall Comment: At the outset, we note that we have limited expertise in the statistical procedures of meta-analysis; we trust other reviewers will address the technical aspects. Turning to the psychological issues, this manuscript makes useful contributions to the illusion-of-truth (ITE) literature. Our comments draw attention to aspects that should be addressed in a revision. […]. Overall, the substantive results are useful and make a valuable contribution to the literature. […]. We appreciate the comparisons of the present results with the earlier meta-analysis by Dechene et al. and are largely in agreement with the interpretations offered. Response: We thank the Reviewers for their comments and the suggestions for improving our manuscript. Introduction 1. Comment: LL27-32 - These lines (which describe a correction strategy for fake news and the possibility of corrections to backfire) seems tangential to the current focus of the paper. Additionally, the cited paper (Pennycook et al., 2018) doesn’t investigate the effects of repeating fake news in the process of debunking it as the sentence seems to imply. I would recommend the authors stick to the focus on the effects of information exposure here (where the Pennycook et al., 2018 would still be relevant). Response: We very much agree with the Reviewers’ comment that the correction strategies are tangential to the main aim of the meta-analysis. Accordingly, we have revised the Introduction section and now focus only on the relevant aspect of repeated exposure increasing perceived truthfulness of fake news, i.e., namely the illusory truth effect. We no longer discuss the correction strategies and refer to Pennycook et al. (2018) to introduce the illusory truth effect as follows: - Lines (22-24): “Repeated exposure to fake news can increase individuals’ perception of its accuracy 6, a phenomenon known as the ‘illusory truth effect’” 2. Comment: LL33-34 - regarding “The illusory truth effect or repetition-induced truth effect is not restricted to fake news: any repeated statement tends to be judged truer than novel statements” - given there have been some exceptions noted (e.g., highly implausible/ plausible claims - Pennycook et al., 2018; Fazio, Rand, & Pennycook; 2019; headlines in the form of questions, Calvillo & Harris, 2022), we would tone down this claim a bit from “any repeated statement” Response: Initially, we formulated the sentence broadly because previous literature demonstrates that repetition can increase perceived truthfulness of statements in many forms, depending on the study design (e.g., Garcia-Marques et al., 2015; Lacassagne et al., 2022). Nevertheless, we fully agree that the phrase “any repeated statements” might be overclaimed. We have now toned down the claim as follows: - Lines (25-26): “The illusory truth effect or repetition-induced truth effect is not restricted to fake news: repeated statement tends to be judged truer than novel statements.” - Lines (45-46): “However, repetition does not always increase perceived truth for extremely implausible statements6,11, or headlines in form of questions27.” 3. Comment: LL64-68 - These lines suggest that inferring truth from processing fluency is always a misattribution. That is not the case. Fluency is a valid correlate of all major truth criteria from coherence to compatibility with one’s knowledge, social consensus, and so on. The problem is that people are insensitive to the source of the fluency experience and misread incidental fluency (e.g., from the readability of a print font) as indicative of coherence, consensus, and so on (Schwarz & Jalbert, 2020, in Greifeneder et al., Fake news, Routledge). Response: We fully agree that using processing fluency is not always indicative of misattribution and can often serve as a valid heuristic for judging truth (e.g., Brashier & Marsh, 2020). Specifically, the illusory truth effect arises when individuals incorrectly attribute increases in fluency (e.g., due to repetition alone) to truthfulness. We have thus revised the manuscript accordingly to clarify this sentence as follows: - Lines (51-53): “While fluency can be a legitimate indicator of truth when it aligns with valid cues30,31 , the illusory truth effect arises when people misattribute incidental increases in fluency from mere repetition or font as evidence of truth.” 4. Comment: LL70-76. – Empirically, manipulations of color contrast have a smaller effect than manipulations of repetition. However, it does not follow from this observation that “conceptual fluency” beats “perceptual fluency.” The latter conclusion about types of fluency (rather than specific singular manipulations) requires a calibration of the implementations of color contrast and repetition, ensuring equal subjective experiences of ease of processing. Without this calibration, all conclusions are limited to the manipulation and general inferences about types of fluency are unwarranted (although offered in the papers you cite). Response: The Reviewers rightly note that concluding a direct difference between \"conceptual\" and \"perceptual\" fluency based solely on these manipulations might be premature. We have revised the sentence to more accurately reflect the complexity of such comparison by acknowledging that conclusions regarding different types of fluency are limited by the absence of direct empirical comparisons controlling for equivalence in fluency magnitude as follows: - Lines (55-57): “[…], with studies indicating that manipulation of color contrasts often yield a smaller illusory truth effect than repetition 33,34.” - Lines (60-63): “However, differences in effect size may reflect how strongly each manipulation induces subjective ease of processing, rather than a fundamental disparity between fluency types. Thus, inferences about which type of fluency is more influential remain limited to the specific context studied. Methods 5. Comment: LL159 following. – What is the rationale for excluding statements that were “not ambiguous” (common knowledge facts) and opinions? It would be worthwhile to include comparisons across these types of statements along with the present results. Piecemeal publication of these aspects in separate papers is not desirable. Response: The primary aim of our meta-analysis was to estimate the illusory truth effect in its most prototypical form (i.e., the influence of repetition on subjective truth judgments when the factual status of a statement is not readily known). We initially excluded certain types of statements for two main reasons: 1. Non-factual items (Exclusion Criterion 1): We excluded statements whose veracity cannot be objectively verified (e.g., opinions, rumors, or beliefs). Including items whose “truth” depends on personal preference or social consensus would introduce additional variability (e.g., personal attitudes, cultural norms) and confound the standard illusory truth paradigm. 2. Non-ambiguous items (Exclusion Criterion 2): We excluded statements that were cued to be either clearly true or clearly false. Such statements offer explicit veracity cues thereby potentially lowering the overall effect size. Including them could have obscured the underlying processes of interest in the standard paradigm. After careful consideration of your recommendation, we agree that it would be valuable to investigate whether repetition shapes perceived truth for well-known facts, opinions, or other statement categories with readily verified truth status. Therefore, exclusion criteria 1 was removed, and exclusion criteria 2 was modified to exclude only studies providing veracity cues during the test phase. Specifically, we revisited the effect sizes previously excluded under Criteria 1 or 2 and re-considered them for inclusion into our database. As a result, we retrieved 97 new effect sizes from 20 manuscripts, 11 of which had been fully excluded before. To accommodate these newly included data, we introduced two new moderators. First, an “item type” moderator distinguishes among standard fact-based statements, news headlines, and opinion-based statements. Second, a “cue” moderator captures whether veracity cues were provided (e.g., tags or explicit feedback) during the task. We also revised our “veracity” coding so that, in addition to “true” or “false,” we can track statements with no clearly established factual basis such as rumors or opinion statements (with the coding option “none”). This broader inclusion and expanded coding now allow us to provide a more comprehensive assessment of how repetition affects perceived truth across a vaster range of statement types and contexts. We have revised the following parts of our manuscript as follows: See in the Method section: - Lines (542-543): “We excluded studies that involved (1) veracity cues during truth judgment in the test phase, […]” - Lines (639-646): “Item type. We included item type (e.g., trivia, headlines, opinions) to examine whether the illusory truth effect generalizes across common real-world formats, especially given the prominence of news headlines and unverifiable claims in online misinformation. We coded the item type used in each study to examine differences in effect sizes across three categories: “standard statements” (u = 309), defined as any declarative sentences; “headlines” (u = 43), defined as items formatted as social media news headlines, and “claims” (u = 12) included unverifiable assertions (e.g., any kind of opinions or marketing claims).” - Lines (683-690): “Veracity cues. We included veracity cues as a moderator to examine the impact of explicit truth indicators (e.g., labels or statements like “this is false”) commonly used in misinformation interventions such as fact-checking. We coded each effect size that involved any indication of a statement’s factual status during the exposure phase. These cues could be embedded directly in the statements (e.g., “most people know that,” “certain,” “impossible”), provided as feedback after exposure, or presented as explicit tags labeling statements as true or false. We classified veracity cues into four subgroups: positive cues (n = 32), negative cues (n = 41), balanced cues (n = 6), or uncued (n = 287).” - Lines (757-758): “In case where the statement could not be true or false (e.g., opinion-based statements), the effect size was recoded as “none” (u = 12).” See in the Results section: - Lines (228-233): “Item type. The illusory truth effect was significantly larger in studies using statements (g = 0.41, 95% CI [0.33, 0.48]) compared to news headlines (g = 0.17, 95% CI [0.01, 0.34]), b = 0.25, 95% CI [0.02, 0.47], t(162) = 2.16, p = .033, but not compared to opinion-based claims (g = 0.47, 95% CI [0.20, 0.73], t(117) < 1. Effect sizes did not significantly differ between news headlines and opinion-based claims, t(127) = 1.10, p = .275.” - Lines (252-262): “Veracity cues. Veracity cues significantly moderated the illusory truth effect. Explicitly labelling statements as false at the exposure phase (g = -0.18, 95% CI [-0.33, -0.03]) decreased the effect compared to no veracity indication (g = 0.43, 95% CI [0.37, 0.50]), b = -0.63, 95% CI [-0.81, -0.15], t(164) = 6.87, p < .001, a balanced mix of true or false cues (g = 0.28, 95% CI [-0.08, 0.64]), b = -0.55, 95% CI [-0.97, -0.12], t(298) = 2.55, p = .011, and explicitly labelling statements as true (g = 0.70, 95% CI [0.51, 0.88]), b = -0.90, 95% CI [-1.10, -0.70], t(170) = 8.79, p < .001). Additionally, explicitly labelling statements as true yielded a larger illusory truth effect compared to no veracity indication, b = 0.27, 95% CI [0.03, 0.50], t(116) = 2.25, p = .027. However, this was not robust with sensitivity analysis using maximum estimates of missing values, t(117) = 1.25, p = .215. No other moderating effects were found.” - Lines (300-307): “Statements’ veracity. The size of the illusory truth effect was not modulated the factual truth of the exposed statements. Repetition of true statements (g = 0.46, 95% CI [0.36, 0.56]) yielded similar effect sizes compared to false statements (g = 0.33, 95% CI [0.23, 0.42]), t(66) < 1, or non-verifiable statements (e.g., opinions, meaningless statements) (g = 0.31, 95% CI [0.12, 0.49]), t(47) = 1.37, p = .175.” See in the Discussion section: - Lines (397-412): “Crucially, our findings suggest that explicit cues about the truth status of a statement significantly reduced the illusory truth effect. Statements labeled as false yielded substantially smaller effects compared to uncued ones. This finding provides additional support for the value of debunking interventions. Explicit markers of whether information is true or false may significantly reduce the illusory truth effect. While findings from primary studies are mixed, our results align with some studies showing that veracity cues diminish the illusory truth effect 56,57. Others have reported that such cues attenuate but do not eliminate the effect 6,58, and some found no influence at all 59,60. Stanley et al. noted 60 that even when participants remember the cue, they may not use it during the truth judgment phase, suggesting that individuals rely more on fluency than retrieved knowledge. However, variability in the type of veracity cue (e.g., warning labels, post-rating feedback, or epistemic qualifiers) likely contributes to the inconsistent findings, especially given the substantial between-study heterogeneity observed in our analysis. Understanding these mechanisms is crucial for developing effective interventions to mitigate the spread of misinformation 61. Future studies should investigate how different types of veracity cues influence the illusory truth effect.” - Lines (413-426): “We found no significant moderating effect of the factual veracity of statements on the illusory truth effect, which aligns with findings from most primary studies6,62 . The illusory truth effect also appeared robust across different types of repeated items (e.g., statements, headlines, or opinions), their factual veracity, and independently of the proportion of true or false statements in the stimuli pool, confirming its relevance to the current misinformation landscape. Interestingly, studies using news headlines yielded smaller effect sizes than those using standard trivia statements. One possible explanation is that many headline-based studies assessed the illusory truth effect in the context of social media misinformation, where items were not systematically chosen for ambiguity. Moreover, a recent meta-analysis 63 showed that participants are generally able to distinguish real from fake news, suggesting that false information in headline formats may be easier to identify than ambiguous trivia items. As such, news headlines may function as an implicit warning cue, attenuating the illusory truth effect in these contexts.” 6. Comment: In addition, how were “common knowledge facts” defined in making these exclusions? Response: Our objective was to focus on genuinely ambiguous statements, which allow us to isolate and measure the illusory truth effect without the confounding influence of firmly established factual knowledge. For this reason, we excluded effect sizes using non-ambiguous statements (e.g., widely known facts, highly implausible claims, procedures involving cues or feedback regarding the actual truth status) if the study’s explicit primary goal was to investigate the effect of these types of statements on reducing the illusory truth effect. The term “common knowledge facts” was referring to statements which may be used in studies with the goal of measuring the illusory truth effect on unambiguously true statements. However, as noted in the previous comment, references to common knowledge facts have been removed from the revised manuscript. 7. Comment: Was a full study excluded if participants judged a mix of “common knowledge facts” and ambiguous information? Response: Our approach was to retain data only from the ambiguous items whenever possible. Specifically, if a study included both ambiguous and non-ambiguous statements but reported them separately (or if the authors’ raw data allowed us to separate them ourselves), we coded only the ambiguous subset. However, if the study provided only a single, combined measure (i.e., mixing ambiguous and non-ambiguous items) and we could not isolate the ambiguous data, we excluded the study entirely. This principle applied across all our exclusion criteria: we always aimed to code valid effect sizes from eligible subsets but excluded studies in which we could not separate the relevant data. We have revised the manuscript to clarify how we addressed situations in which a part of an eligible study (but not all the study) met an exclusion criteria as follows: - Lines (605-611): “When a study included multiple conditions such that only some conditions met our inclusion criteria, we extracted data exclusively from those qualifying conditions. Specifically, if a study provided distinct outcome metrics for each condition or made raw data available, we retained only the eligible subsets that satisfied our criteria and excluded the ineligible ones. In instances where outcomes for eligible and ineligible conditions were reported only as combined results, making it impossible to isolate appropriate data, we excluded the entire study to maintain methodological consistency.” 8. Comment: In addition, studies may not have norming data collected in the sample the study was conducted in, making the determination of whether or not they include claims that are “common knowledge facts” in that population impossible to assess. Response: We agree that, in the absence of norming data for the specific sample, it can be difficult to identify “common knowledge facts.” However, our exclusion of effect sizes did not depend on the presence of such norming data. Instead, we relied on the authors’ own designations. If the authors explicitly labeled certain items as “known facts” or “highly implausible statements,” we previously excluded those items according to our criteria. Conversely, when the authors referred to their items simply as “general” or “trivia” statements without specifying any pretesting or norming, we included those data in our meta-analysis. However, we now include all types of statements, as specified in the response to comment 5. 9. Comment: Finally, it is unclear why only ambiguous information is of interest, given the explicit goal of discussing practical implications regarding the current misinformation crises. Does repeating unambiguously false information nevertheless increase acceptance? Response: Initially, we focused on ambiguous statements to examine how repetition alone shapes subjective truth in the absence of firm knowledge, yielding a “pure” measure of the illusory truth effect. However, we acknowledge that examining unambiguously false information is directly relevant to addressing real-world misinformation concerns. With our broadened inclusion criteria, we now incorporate studies presenting unambiguous information. In the revised manuscript, we now include the “veracity cue” moderator which allows us to investigate whether repetition increases truth judgment in unambiguously information (cf. response to comment 5), and discuss the implications of our findings as follows: - Lines (397-412): “Crucially, our findings suggest that explicit cues about the truth status of a statement significantly reduced the illusory truth effect. Statements labeled as false yielded substantially smaller effects compared to uncued ones. This finding provides additional support for the value of debunking interventions. Explicit markers of whether information is true or false may significantly reduce the illusory truth effect. While findings from primary studies are mixed, our results align with some studies showing that veracity cues diminish the illusory truth effect 56,57. Others have reported that such cues attenuate but do not eliminate the effect 6,58, and some found no influence at all 59,60. Stanley et al. noted 60 that even when participants remember the cue, they may not apply it during the truth judgment phase, suggesting that individuals rely more on fluency than retrieved knowledge. However, variability in the type of veracity cue (e.g., warning labels, post-rating feedback, or epistemic qualifiers) likely contributes to the inconsistent findings, especially given the substantial between-study heterogeneity observed in our analysis. Understanding these mechanisms is crucial for developing effective interventions to mitigate the spread of misinformation 61. Future studies should investigate how different types of veracity cues influence the illusory truth effect.” 10. Comment: LL161-171 - Can you clarify whether all data from a study were excluded if some (but not all) conditions met the exclusion criteria or if only the condition that met the exclusion criteria was excluded while the others were maintained? It currently sounds as if all conditions were excluded which suggests a loss of relevant data Response: When studies included multiple conditions, only some of which met our exclusion criteria (e.g., combining non-ambiguous and ambiguous statements in a within-subject design), we excluded just those ineligible conditions while retaining any that satisfied our criteria. If a study reported separate results for each condition (e.g., means, standard deviations, sample sizes) or provided raw data that let us isolate eligible conditions, we used only those eligible subsets. However, if a study presented only aggregate data that combined eligible and ineligible subsets with no separate data, we had to exclude the entire study to preserve methodological consistency. We followed the same procedure when a study reported separate effect sizes for different conditions (e.g., true vs. false statements). Specifically, we extracted each effect size that met our inclusion criteria. Because multiple effect sizes from the same sample introduce dependency, we employed a multi-level meta-analysis to correctly handle clustered effect sizes from a single study sample. We have revised the manuscript to clarify this point as follows: - Lines (605-611): “When a study included multiple conditions such that only some conditions met our inclusion criteria, we extracted data exclusively from those qualifying conditions. Specifically, if a study provided distinct outcome metrics for each condition or made raw data available, we retained only the eligible subsets that satisfied our criteria and excluded the ineligible ones. In instances where outcomes for eligible and ineligible conditions were reported only as combined results, making it impossible to isolate appropriate data, we excluded the entire study to maintain methodological consistency.” 11. Comment: LL256-262 - The impact of warnings depends on whether the warning occurs at exposure or test. For example, Jalbert et al., (2020) found that warnings only moderate the effect of repetition when they occur at exposure and have no effect when presented only at test (probably because asking for a truth judgment itself acts as a type of warning). There are important theoretical reasons to suspect that the timing of this warning is critical and that warnings at exposure and test should be analyzed separately rather than pooled into the same category. The ms also flags that many earlier truth effect papers do not contain sufficient information to determine whether or not a study included a warning as part of the standard instructions. Assuming that participants did not receive a warning when the paper doesn’t include information regarding these instructions may miscategorize the studies. It would be good to add an analysis that only includes studies with vs. without warnings at exposure to assess the effect of warnings. Response: We agree with the Reviewers that the timing of the warning, whether at exposure or test, can significantly affect how it moderates the illusory truth effect. For instance, Jalbert et al. (2020) demonstrated that warnings at exposure effectively reduce illusory truth, whereas warnings introduced only at test appear to have little influence. Initially, we primarily focused on warnings delivered at the exposure phase as many studies did not explicitly state whether there was a warning or not (we supposed that any warnings would be specified in the procedure), and sometimes did not clearly differentiate whether they reiterated the warning at test, making it difficult to cleanly separate “exposure-only” vs. “test-only” warnings. However, we acknowledge that this procedure presents the risk to miscategorize studies. Therefore, we: 1. Separated the coding of the warning during the exposure and the test phase to explore the differences in timing. 2. Conducted an additional sensitivity analysis running a meta-regression comparing studies with no warning vs. warning vs. unspecified warning status to investigate any differences in results. 3. Instead of recoding the absence of information about warning as a study containing no warning, we left those as missing data which is addressed by multiple imputations by chained equations (MICE) to preserve relationship between moderators and the outcome without data losses, while preventing any study to be miscategorized. We now specify this new coding scheme in our revised manuscript as follows: See in Methods: - Lines (667-675): “Truth warning at the exposure phase. This moderator reflected whether explicitly alerting participants to potential falsehoods prior to exposure modulates the illusory truth effect. We coded whether participants were explicitly instructed that “some” or “half” of the statements were true or false in the exposure phase, including the presence of cues (u = 163), or did not provide any explicit warning (u = 41). To prevent any risk of miscategorization, we coded studies that did not specify whether participants were warned about the statement’s veracity or did not provide the full verbatim of the instructions to participants as missing data (u = 162). Instructions to rate the truth of statements were not coded as explicit warnings.” - Lines (676-682): “Truth warning at the test phase. As warnings at test and exposure are likely to influence truth judgments through distinct cognitive mechanisms and serve different theoretical functions 18, we coded truth warnings at the exposure and test phases as separate moderators. We followed the same procedure as for the warning during the exposure phase, coding studies in which participants were warned (u = 66) or not (u = 41) that statements could be false in the test phase. Similarly, we coded missing data (u = 259) if the warning status is not specified (or respecified for the test phase).” See in Results: - Lines (246-251): “Providing a truth warning did not moderate the illusory truth effect at either phase of the experiment. During the exposure phase, the effect did not differ significantly with a truth warning (g = 0.34, 95% CI [0.25, 0.43]) or without one (g = 0.44, 95% CI [0.32, 0.57]), after controlling for other moderating variables, t(61) < 1. Similarly, the illusory truth effect with a warning (g = 0.38, 95% CI [0.27, 0.48] did not differ compared to no warning (g = 0.37, 95% CI [0.26, 0.49] in the test phase, t(30) < 1.” In the additional analysis the Reviewers suggested on the updated data set, we found no significant difference in the effect size between any warning (e.g., “some” of the statements are false, “half” of the statements are false, or the presence of cues) and no warning whether at the exposure phase or test phase (ps > .12).Similarly, effect sizes did not differ comparing studies with unspecified warning (e.g., which were previously coded as “no warning”) and studies clearly stating that they did not warn participants, whether at the exposure (t(236) < 1) or the test phase (t(330) <1). However, using our new coding scheme (i.e., leaving unspecified warnings as missing data), we surprisingly found no difference between studies with or without warning (neither at the exposure phase or test phase), which is contrary to both our previous analysis and Jalbert et al.’s (2020) findings. We have thus conducted an additional analysis using the new data set with our previous coding scheme (i.e., recoding unspecified warning as no warning) to examine if the incongruency in our results emerges from modifications in our updated data set (e.g., addition of new studies) and analytical model (e.g., new moderators, and bias-correction) or in our coding scheme. This analysis is consistent with our main analysis, which found no effect of warning during the exposure phase, t(195) < 1, or the test phase, t(263) = 1.62, p = .106, suggesting that the lack of effect was robust to the modification of our coding scheme. Thus, we have revised the interpretation of this finding in the Discussion section as follows: - Lines (359-367): “Asking participants to make an initial truth judgment may serve as an implicit warning that not all statements are true 18. However, our meta-regression found no overall effect of explicit warnings, whether provided during the exposure or test phase. This contrasts with Jalbert et al.’s findings 18, which showed that explicit warnings reduced the illusory truth effect, but only when given during exposure alongside reading instructions. A plausible explanation is that implicit and explicit warnings may function overlap: once participants are instructed to evaluate veracity, an additional instructional warning may provide little new information, which makes its impact difficult to detect at the aggregate level.” 12. Comment: LL229 - The size of the illusory truth effect depends on whether a within-ss or between-ss design is used. The effect is larger when participants judge a mix of repeated and new claims than when they judge only repeated claims (Dechêne et al., 2009 and related studies). It is therefore surprising that this meta-analysis apparently includes within-ss and between-ss studies without consistently differentiating between them. Within vs. between designs should be treated as an important additional moderating variable. Response: We agree that systematically differentiating between within- and between-participants designs is crucial, particularly in light of findings indicating the illusory truth effect can vary by design (e.g., Dechêne et al., 2009). Thus, we included the repetition design as a moderator analysis in our revised manuscript. However, it is worth noting that only 5 out of our 366 effect sizes use a between-participants design, limiting our statistical power to detect meaningful differences. Nevertheless, we highlighted this limitation and discussed implications for interpreting the results given the small number of between-participants studies. We have revised the manuscript accordingly as follows: - Lines (234-236): “The illusory truth effect did not significantly differ whether repetition was manipulated within-participants (g = 0.38, 95% CI [0.30, 0.45]) or between participants (g = 0.17, 95%CI [-0.28, 0.61]), t(262) < 1.” - Lines (426-432): “Contrary to earlier primary studies suggesting that the illusory truth effect is smaller in between-participant designs 64–66, our meta-regression did not detect a significant difference. However, this result should be interpreted considering the imbalance between the number of effect sizes drawn from within-participants design (u = 361) and between-participants design (u = 5). This disparity substantially limits statistical power, suggesting that any true difference in effect sizes may simply be too small to detect considering the current data set.” - Lines (647-652): “Repetition study design. To evaluate whether the illusory truth effect varies based on repetition format, we examined whether participants were exposed to repeated and new statements within the same condition or in isolation. We coded whether the effect size was extracted from a within-participant (u = 361) or a between-participant (u = 5) manipulation of the repetition. In between-participant designs, two groups of participants evaluated either all-repeated or all-new statements during the test phase.” 13. Comment: LL301-302 - Why was the response scale coded by odd vs. even? Explaining the reason would be useful. Response: We distinguished odd-numbered response scales (which have a “neutral” option) from even-numbered scales (which do not) because having or lacking a midpoint could impact how participants make their truth judgments. An odd-numbered scale allows individuals to select a neutral middle point, whereas an even-numbered scale forces participants to choose one side of the scale or the other. We therefore coded scales as odd or even to capture this potentially meaningful difference in how participants use the rating scale. We have included this justification in the manuscript as follows: - Lines (741-745): “We distinguished response scales based on whether they had an odd number of points (u = 119) or an even number of points (u = 241). The goal was to explore the moderating role of a “neutral” or midpoint option (e.g., 3 on a 5-point scale), versus even-numbered scales that force participants to express a choice that leans in one direction or another (i.e., there is no true midpoint).” 14. Comment: LL304-305 - Why was data containing a mix of true and false claims excluded from the veracity comparison? This represents a large portion of the data and comparing true vs. false vs. mixed could provide useful insights. Response: We did not exclude data containing a mix of true and false statements from the analyses. Instead, whenever a study did not clearly distinguish between which items were true or false (or did not provide raw data for us to differentiate them), we coded veracity as “missing” and used multiple imputation via MICE to address these missing values. This approach preserves the relationships among variables and mitigates data loss. Our comparison specifically aimed to see whether the illusory truth effect differs for true versus false statements. Including studies where items are “mixed” (i.e., contain both true and false statements) makes it impossible to isolate a single effect size for true items and another for false items. With our current methodology, we have the advantage of extracting two effect sizes (one for true statements and one for false statements) from a single study using mixed veracity items. Conversely, if we separated all-true, all-false, and mixed designs, we could not identify how much of the overall truth effect arises from each veracity type. Because our analysis requires two clear-cut effect sizes (i.e., one for true statements and one for false statements), mixed designs prevent that distinction and thus cannot serve the purpose of a direct true–false comparison. Nevertheless, we agree that comparing illusory truth effects across purely true, purely false, and mixed statements could offer valuable insights. To capture this variance, we introduced a new moderator, “proportion of true statements,” which codes the proportion of statements in each study that were factually true. This would provide a comparison of designs using all-true vs. all-false vs. mixed items, while maintaining a direct comparison of the illusory truth effect for factually true and false statements. We have modified the manuscript accordingly as follows: - Lines (304-307): “Similarly, the proportion of true or false statements showed no influence on the effect size (t(245) < 1), indicating that the illusory truth effect is comparable in studies that employ mixed, all-true, or all-false item pools.” - Lines (414-418): “The illusory truth effect also appeared robust across different types of repeated items (e.g., statements, headlines, or opinions), their factual veracity, and independently of the proportion of true or false statements in the stimuli pool, confirming its relevance to the current misinformation landscape.” - Lines (633-637): “When a study included effect sizes potentially matching multiple categories of a moderator, we extracted each effect size individually whenever the data (e.g., distinct outcomes or open datasets) permitted clear separation. In instances where effect sizes were reported in a combined form and could not be disentangled by moderator category, we coded the moderator as missing.” - Lines (746-753): “Proportion of true statements. We included the proportion of true statements to evaluate whether the overall truth base rate within a study influences participants’ sensitivity to repetition. This moderator captures variation in the informational context (e.g., all-true, all-false, or mixed item sets), which may affect the baseline likelihood of endorsing repeated items as true. To capture design variability across all‑true, all‑false and mixed item sets, we created a continuous moderator (range 0-1) that records the proportion of factually true statements in each study’s stimulus pool (e.g., 0 = all false; 0.50 = 50 % true/50 % false; 1 = all true).” - Lines (772-774): “This method allowed us to preserve the relationships between variables while avoiding data losses associated with deletion methods.” To clarify the usefulness of the three-level meta-regression model, we also have added an additional explanation: - Lines (846-848): “This method appropriately handles the clustering of effect sizes within individual studies and allows for estimation of between-study and within-study variance.” 15. Comment: LL379 - We may have overlooked this, but we didn’t see whether or not effect sizes were fixed across subgroups? We would expect them to be fixed given recommendations by Borenstein et al. (2009) when the number of subgroups is small. Response: We thank the Reviewers for raising this point. Borenstein et al. (2009) in Chapter 19 recommended pooling the between-study variance (τ²) across subgroups when each subgroup contains only a few studies (≈ ≤ 5), because separate τ² estimates would be unstable. In our three-level random-effects model (rma.mv, metafor package), the level-3 between-study variance (τ²) and the level-2 within-study variance (σ²) were estimated once from the complete dataset and held constant for every moderator and subgroup analysis, which follows the approach recommended by Borenstein et al. (2009). We clarified this point in the revised manuscript as follows : - Lines (857-860): “In the meta-regression analysis, the between-study (τ²) and within-study (σ²) variance components were estimated from the complete set of effect sizes and kept constant across moderator levels 83.” Results 16. Comment: LL450 following. – This paragraph is uninformative. We cannot meaningfully relate this material to specific variables, even with the help of the supplementary material. Response: We appreciate the request for greater clarity. The revised manuscript now describes more clearly our analyses and provides an interpretation of our findings as follows: - Lines (195-205): “Using the RoB-2 framework, 43 of the 182 studies were judged at low overall risk, while the remaining 139 raised some concerns. Among the five RoB-2 domains, deviation from intended intervention (Domain 2) raised concerns in 86 studies and selection of the reported results (Domain 5) in 138 studies, primarily resulting from lack of pre-registration processes. Supplementary Table 1 describes every study by the five RoB-2 domains. Figure 2 provides a weighted summary. A three-level meta-regression using overall RoB grade as a moderator showed no significant difference between effect sizes from studies at low risk of bias and those with some concerns, b = 0.12, 95% CI [-0.02, 0.26], t(363) = 1.63, p = .104. Thus, the risk-of-bias analyses suggested that the pooled illusory truth effect remained stable after controlling for study-level biases.” 17. Comment: All p-values should be reported to the same level of specificity (some have 2 decimal places and some have three). Response: We thank the Reviewers for their suggestion. We have now standardized the precision of all p-values throughout the manuscript to 3 decimals. 18. Comment: It would also be useful to provide degrees of freedom and corresponding estimates of ds for each subgroup in the main text (or the difference between ds) Response: We thank the Reviewers for this helpful suggestion. We now report the degrees of freedom and the estimates of Hedge’s g and its corresponding 95% confidence intervals for every subgroup comparison in the main text of the revised manuscript as follows: - Lines (216-221): “To provide an overview of effect sizes within each subgroup, we also report the estimates. Because these values are not adjusted for the other moderators, they are not directly comparable to the coefficients from the multivariate meta-regression.” Please see for an instance of the revision implemented in the Results section as follows: - Lines (237-245): “A significant moderating effect was found for the content of the task used during the exposure phase. When participants were asked for a truth judgment during the exposure phase (g = 0.10, 95% CI [-0.03, 0.23]), the illusory truth effect was consistently reduced compared to irrelevant tasks (g = 0.42, 95% CI [0.34, 0.50]), b = -0.35, 95% CI [-0.50, -0.20], t(303) = 4.62, p < .001, or passive processing (g = 0.47, 95% CI [0.34, 0.60]), b = -0.47, 95% CI [-0.70, -0.23], t(221) = 3.94, p < .001. However, the illusory truth effect did not significantly vary when the exposure task only instructed participants to read the statements compared to performing an irrelevant task, t(218) = 1.32, p = .190. Discussion 19. Comment: LL550-551 - Jalbert et al. (2020) discuss ways in which making an initial truth evaluation at exposure (similar to a warning) may decrease the size of the illusory truth effect goes beyond the depth of processing account offered here. Asking people for a truth judgment necessarily entails that some of the claims may not be true. Response: We agree that asking participants for an initial truth judgment can operate in ways that go beyond a simple depth-of-processing account. As the Reviewers noted, requesting a truth evaluation at exposure could implicitly warn participants that some statements may be false. In other words, truth judgments during the exposure phase might function in part like a “warning” by prompting participants to treat the task as one involving potential falsehoods rather than simply rating interestingness or familiarity. However, we did not find an effect of warning neither during the exposure phase or test phase in our updated analysis. We have thus revised the Discussion section accordingly as follows: - Lines (359-367): “Asking participants to make an initial truth judgment may serve as an implicit warning that not all statements are true 18. However, our meta-regression found no overall effect of explicit warnings, whether provided during the exposure or test phase. This contrasts with Jalbert et al.’s findings 18, which showed that explicit warnings reduced the illusory truth effect, but only when given during exposure alongside reading instructions. A plausible explanation is that implicit and explicit warnings may function overlap: once participants are instructed to evaluate veracity, an additional instructional warning may provide only few additional information, which makes its impact difficult to detect at the aggregate level. 20. Comment: LL590-597 - The studies included in this paper do not include multiple truth judgments (i.e. an initial one and a later one) but the explanation provided is specific to this scenario. What about when participants do not complete multiple test phases? Response: In our meta-regression, effect sizes emerging from multiple truth judgment (i.e., an initial one and a later one) was included in the subgroup “truth judgment” of the “exposure task” moderator. In this subgroup, participants were asked to rate the truth of statements in the exposure phase, which half were generally repeated in the test phase. However, there might be a confusion from our exclusion criteria (currently criteria #2), which focused on eliminating studies in which the same items were repeated more than once before the final truth judgment, including multiple test phases that were used to re-test the same set of items more than once. The objective of this exclusion criteria was to control the number of times participants were exposed to a statement, focusing on the illusory truth effect emerging from only one exposure. We did, however, include studies in which participants made an initial truth judgment with a single test phase, or multiple test phases in which repeated statements were only presented once. For instance, while Nadarevic et al.’s (2014) first experiment implemented an exposure phase (with an initial truth judgment) followed by two test phases (one after 10 minutes and another after one week). Participants did not re-judge the same items in both test phases (i.e., half of the initially exposed statements were repeated in the first test phase, and the other half were judged only in the second test phase). Therefore, each item was effectively repeated just once, which satisfied our inclusion criteria; accordingly, we included such studies and coded their effect sizes separately. In the paragraph the Reviewers referenced, we highlighted that Nadarevic et al. (2014) found an initial truth judgment appeared to suppress the illusory truth effect when the retention interval was short (10 minutes), but that the effect reemerged with a one-week retention interval, leading us to conclude that “over time, the influence of initial truth judgment may decrease, allowing fluency processes to take over”. However, to strengthen the validity of this statement, we now also refer to Brashier et al. (2020)’s study that reports similar findings in four different experiments. The manuscript was revised as follows: - Lines (367-373): “Importantly, evidence indicates that an initial truth judgment decreases illusory truth effect only when the delay between the exposure and the test phase is short. After a delay of two days, the effect of the initial truth judgment disappeared 23,51. This effect was robust after controlling for participants’ memory of the statements, suggesting that the initial truth judgment may engage different cognitive processes that override fluency or coherence effect. Over time, the initial truth judgment may have a smaller impact, allowing fluency processes to take over.” Furthermore, we have clarified our exclusion criteria 2 as follows: - Lines (543-545): “(2) multiple exposure to a statement before evaluation (e.g., participants are exposed to a same statement twice or more before test phase)” 21. Comment: LL639-653 – When the fluency experience is (correctly or incorrectly) attributed to an incidental variable (e.g., repetition), the informational value of fluency is undermined. Awareness of the influence is more likely after very short delays (for a discussion, see Schwarz, Jalbert, et al., 2021). Response: We appreciate the Reviewers drawing attention to the role of attributions in shaping the impact of fluency on truth judgments. With our revised analysis plan and expanded dataset, we no longer observe a clear effect of delay on the effect size. However, we have integrated this explanation in the Discussion section as follows: - Lines (383-396): “We also observed a relatively smaller truth effect when the test phase followed exposure within the same day versus within the same week, although sensitivity analyses were inconsistent. Primary studies have also reported inconsistent findings. Some suggest that a longer delay was associated with a larger illusory truth effect 19, possibly because individuals attribute their ease of processing to recent repetition and thus discount fluency as a cue for truth. In contrast, with a longer delay, the source of fluency may be forgotten, which makes fluency more likely to be misattributed to truthfulness 31. Other studies found that a smaller effect was associated with a longer delay 53,54, which is consistent with both the fluency account and the referential theory, which predict that fluency or coherence in memory would be reduced over time. However, the moderating effect of delay may interact with other variables influencing the illusory truth effect during the exposure phase, such as the type of task 19 or the type of repetition 55. Given the critical role of the exposure phase, the interaction between delay and exposure conditions may provide key insights into the underlying mechanisms of the illusory truth effect.” 22. Comment: LL692-695 - Several recent papers report that debunking messages that include a repetition of false information do not always result in backfire effects (e.g., Ecker et al., 2020, Briony Swire-Thompson et al., 2020). Response: We thank the Reviewers for drawing our attention to this literature. We fully agree that the interplay between re-exposure to misinformation and backfire effects seems more nuanced than initially stated. We have revised the Discussion of the illusory truth effect in the context of misinformation to provide a more nuances account of the backfire effects as follows: - Lines (510-514): “Metacognitive interventions 69, encouraging reflection with accuracy prompts 70 or debunking strategies 71 may effectively counteract the illusory truth effect. Moreover, the concern that repeating false claims during debunking might backfire appears less warranted than previously feared; current evidence suggests that corrective interventions can be effective without amplifying beliefs in the exposed claims 72,73.” Reviewer 3 Comments Overall Comment: This is an extremely relevant article for those who approach the field of truth illusions. As a participant in the field, I appreciate the updated meta-analytic review work relative to the 2010 work by Dechene and colleagues, and the systematic map created by Henderson et al. in 2022. However, despite claiming its relevance, I believe the article has room for improvement, and I would like to see these revisions made before recommending its publication. Response: We thank the Reviewer for his/her comment and suggestions for improving our manuscript. 1. Comment: My first point refers to the objectives of conducting this meta-analysis (p. 6). These should focus more on the gains it brings rather than on the deficits that previous approaches might present. While gains and deficits are related, I would recommend placing greater emphasis on what is gained. The argument that the advantage comes from greater rigor in estimates, enabled by the developments in the meta-analytic approach, is weak on its own. The studies are now more numerous, with greater variability in conditions, allowing for more consistent estimation of moderators’ roles and the inclusion of new moderators that were previously unexplored, among other benefits. These are all relevant arguments in favor of a new meta-analytic study. However, it is precisely in this area where the paper loses some strength—it adds very little to what we already know. There is no reason for this. Since 2010, many other questions have been raised about the effect, and these can be tested in a meta-analytic context. By framing the paper solely around emphasizing the rigor of effect estimation, an opportunity is being missed here. Response: We agree that clearly articulating the added value of our new meta-analysis beyond methodological rigor is critical. Indeed, framing the objectives mainly around methodological improvements may overshadow other significant contributions made possible by our updated meta-analysis. As the Reviewer pointed out, since the previous meta-analysis by Dechêne et al. (2010), the literature on the illusory truth effect has grown substantially, offering not only an increased quantity of data but also greater methodological diversity and new theoretical questions. We have now revised the introduction and the discussion sections the added value of this new meta-analysis as follows: - Lines (102-120): “In the present study, we conducted an updated meta-analysis of the illusory truth effect that synthesizes 182 studies and 366 effect sizes published from 1977 to 2025. Our goals were twofold. First, we aimed to provide a more accurate estimate of the overall effect size by using a three-level random-effects model 39,40, which accounts for the non-independence of multiple estimates derived from the same sample. This model was complemented by (a) study-level quality appraisal using the Risk of Bias 2 tool 41, (b) tests for publication bias, and (c) extensive sensitivity analyses using multiple imputation strategies for missing data. Second, we substantially expanded the set of moderators, including item type, presence of veracity cues or truth warnings, statement’s veracity, and proportion of true items. The inclusion of these moderators enhances the practical relevance of our findings by identifying contextual features of information exposure that amplify or attenuate the illusory truth effect, offering direct implications for the design of interventions aimed at countering misinformation. These moderators were analyzed simultaneously in a multiple meta-regression to isolate the contribution of each moderator independently of the others. While our selection of moderators was primarily guided by pragmatic and applied considerations, some of them also align with key theoretical distinctions in the literature, offering insight into mechanisms such as fluency-based processing, referential coherence and memory-based correction mechanisms assumed to be at the root of the illusory truth effect.” - Lines (318-329): “This systematic review and three-level meta-analysis provides robust evidence that repetition increases the perceived truth of information, with growing relevance in today’s media landscape. Recent studies suggested that repeated exposure not only increases the perceived accuracy of misinformation but also increases individuals’ tendency to share it 48. This highlights the importance of mitigating the illusory truth effect in the context of the current misinformation crisis. Synthesizing 182 studies (366 effect sizes; N = 31,184), we found a small illusory truth (g = 0.37, 95% CI [0.30, 0.44]), after correcting for publication bias. Comparing to the previous meta-analysis 38, our analyses incorporated an expanded set of moderators, many of which have direct practical implications. Together, these moderators accounted for 28% of the between-study variance on average, indicating that their relative importance in moderating the illusory truth effect.” 2. Comment: In my reading I would have liked to find not only evidence that corroborates or challenges Dechene’s conclusions but new evidence. For example, Dechene discusses the difference in effect size when the contrast is within-subjects versus between-subjects, highlighting that the fluency/familiarity experience may be relative. Since 2010, some studies have directly addressed this issue, providing data that could be included in this new meta-analysis. With this approach, the present paper would add secure knowledge to the previous paper adding content and not only more rigor in the estimation methods. Response: We thank the Reviewer for pointing this out and fully agree that the between-participant or within-participant manipulation of the repetition in study design can modulate the illusory truth effect as described in some studies (i.e., Dechêne et al., 2009, Garcia-Marques et al., 2016; 2019). As noted in our response to Reviewer 1 and 2 (comment 12), we have now added the “repetition study design” moderator in our three-level meta-regression. However, only 5 out of 366 effect sizes use a between-participants design, limiting our statistical power to detect meaningful differences. In the revised manuscript, we now describe the new moderator and note in the discussion that the evidence is not definitive due to lack of power, see our response to Reviewer 1 and 2 for the changes implemented in the revised manuscript. 3. Comment: There are also references in the original paper to differences in effect magnitude between repetition and fluency manipulations, and since then, more studies have been published that use both types of manipulations. I do not see familiarity being contrasted with fluency in this analysis. We thank the Reviewer for raising this issue. In the literature on the illusory truth effect, the subjective sense of familiarity linked with repetition is generally framed as a manifestation of conceptual fluency (e.g., Silva et al., 2016; Unkelbach et al., 2019). Because our goal was to derive a clean estimate of the repetition-induced truth effect, our eligibility criteria restricted the intervention to verbatim or gist repetition and explicitly excluded studies in which fluency was manipulated independently of repetition (e.g., font clarity, perceptual priming). We agree that systematically contrasting repetition with other fluency routes is theoretically important (Silva et al., 2016, 2017; Unkelbach et al., 2019), but this problematic is outside of the focus of the present meta-analysis. 4. Comment: Another very relevant aspect that could not have been addressed 14 years ago is the nature of the information. When identifying the effect, the statements made were ambiguous. Today, many studies not only present factually false information but also add warnings, etc. These data are not addressed here. Response: We fully agree that the informational context including the nature of information and potential cues to address the issue of misinformation is increasingly relevant. In addition to the factual veracity of the presented information and the presence of warnings in the instructions (during the exposure or the test phase), we now examine the role of the type of item (e.g., statements, news headlines, opinions) and veracity cues (e.g., uncued, positive cues, negative cues, or balanced cues) in moderating the illusory truth effect on our new analysis. For more details on the changes proposed to the manuscript, see our responses to Reviewer 1 and 2’s comments (comments 5, 9 and 11). 5. Comment: Essentially, what I think diminishes the relevance of this paper is that the moderation analyses are neither directly contrasted with the status quo provided by previous analyses nor clearly theoretically oriented. The analyses would gain relevance if they directly or indirectly answered theoretically significant questions (which would also facilitate and better integrate the data discussion). For instance, more than the instructions and the time spent reading the sentences at the first moment, it is the question of whether these factors may influence the explicit use of memory as information about the validity of a statement. If the effect is smaller when the instructions make it explicit that memory is not informative (with ½ true sentences and ½ false sentences presented at the start) than when nothing is stated, and this happens especially when there is encoding time, such a test could examine whether the effect depends on explicit versus implicit memory. Such kind of questions would induce to test the interaction between moderators and not only their main effects. Response: We appreciate the reviewer’s comment that the value of moderation analyses is increased when they test theoretically significant questions. While our primary rationale for moderator selection was pragmatic (e.g., we aimed to assess which contextual and methodological features reliably amplify or reduce the illusory truth effect) with an eye toward real-world implications (e.g., misinformation correction, truth judgments in digital environments), several of the moderators we included also provide information on theoretical accounts of the effect. However, testing these theoretical implications is limited by our data presenting substantial heterogeneity and uneven distributions of effect sizes across moderator combinations, thereby limiting the power and interpretability of interaction effects. The Reviewer specifically proposed investigating whether longer encoding time affects the illusory truth effect differently depending on whether participants are explicitly told that memory may not be a reliable source of truth (e.g., when warned that “half” of the statements are false). We agree that such analysis would shed light on the role of memory on the illusory truth effect. In line with this suggestion, we conducted an exploratory analysis including an interaction term between warning and presentation time during exposure in our meta-regression model. However, neither the interaction nor the main effects reached statistical significance. A key limitation to this analysis is the sparse and imbalanced cell structure, as shown below: Warning/Time <= 5 sec > 5 sec Participant-paced Unspecified Presence of cues 4 8 3 11 “Half” true/false 5 5 2 2 “Some” true/false 33 11 69 1 No warning 4 4 33 2 Unspecified 30 64 72 2 As this table illustrates, many theoretically meaningful interaction cells contain too few effect sizes for reliable estimation. We therefore see the identification and testing of such interactions as an important direction for future experimental research, where moderators can be systematically manipulated under controlled conditions. Nevertheless, we agree with the Reviewer that contrasting our results with the previous meta-analysis would be valuable. Thus, we have revised the manuscript to clarify how our moderator choices relate to both practical application and theoretical models, and we now include Table 2 to contrast our findings with Dechêne et al.’s to contextualize our findings within prior meta-analytic work as follows: - Lines (116-120): “While our selection of moderators was primarily guided by pragmatic and applied considerations, some of them also align with key theoretical distinctions in the literature, offering insight into mechanisms such as fluency-based processing, referential coherence and memory-based correction mechanisms assumed to be at the root of the illusory truth effect 28.” - Lines (219-220): “Table 2 summarizes the subgroup analyses contrasted with Dechêne et al.’s meta-analysis.” - Lines (624-630): “Our selection of moderators was primarily guided by pragmatic considerations, with the aim of identifying factors that inform how, when, and for whom the illusory truth effect is most likely to occur. These included features commonly encountered in online misinformation contexts such as headline formats, exposure duration, or the presence of accuracy cues. At the same time, several moderators also align with key theoretical distinctions in the literature, including fluency-based processing, referential coherence, and memory-based correction mechanisms 28.” We have also included an additional justification for each moderator in the Methods section as follows: - Lines (639-642): “We included item type (e.g., trivia, headlines, opinions) to examine whether the illusory truth effect generalizes across common real-world formats, especially given the prominence of news headlines and unverifiable claims in online misinformation.” - Lines (647-649): “To evaluate whether the illusory truth effect varies based on repetition format, we examined whether participants were exposed to repeated and new statements within the same condition or in isolation.” - Lines (653-655): “We examined the moderating effect of participants’ task during the initial exposure to determine how different levels of cognitive engagement during encoding influence susceptibility to the illusory truth effect.” - Lines (667-669): “This moderator reflected whether explicitly alerting participants to potential falsehoods prior to exposure modulates the illusory truth effect.” - Lines (676-679): “As warnings at test and exposure are likely to influence truth judgments through distinct cognitive mechanisms and serve different theoretical functions 18, we coded truth warnings at the exposure and test phases as separate moderators.” - Lines (683-685): “We included veracity cues as a moderator to examine the impact of explicit truth indicators (e.g., labels or statements like “this is false”) commonly used in misinformation interventions such as fact-checking.” - Lines (691-693): “We examined the influence of delay between exposure and test to assess the temporal durability of the illusory truth effect. This moderator helps understanding the long-term influence of repeated information in both experimental and applied settings.” - Lines (702-704): “This moderator reflected whether exact repetition (verbatim) and paraphrased repetition (gist) differentially influence perceived truth, as these forms commonly occur in real-world contexts.” - Lines (708-711): “We included the modality of presentation to understand how the presentation channel affects the illusory truth effect. This moderator accounts for variability in how content is encountered across studies and reflects real-world differences in media consumption.” - Lines (717-721): “This moderator reflected whether the duration of initial exposure affects the illusory truth effect. Exposure time is a key methodological factor that may affect encoding depth and fluency. This moderator also reflects real-world variability in how long individuals attend to repeated information, making it relevant for interpreting the robustness of the effect in ecological settings.” - Lines (729-732): “To examine whether the amount of time available for truth judgments moderates the illusory truth effect, we examined the presentation time during the test phase. Varying test durations may influence the extent to which participants rely on quick, fluency-based heuristics versus more deliberative evaluation.” - Lines (738-745): “We coded whether the response scale was a Likert scale (u = 269), a binary scale (u = 91) (e.g., yes vs. no), or a slider from 0 to 100 (u = 6) to examine whether the precision of the response format used to evaluate truth judgments influenced the effect size. Additionally, we distinguished response scales based on whether they had an odd number of points (u = 119) or an even number of points (u = 241). The goal was to explore the moderating role of a “neutral” or midpoint option (e.g., 3 on a 5-point scale), versus even-numbered scales that force participants to express a choice that leans in one direction or another (i.e., there is no true midpoint).” - Lines (746-750): “We included the proportion of true statements to evaluate whether the overall truth base rate within a study influences participants’ sensitivity to repetition. This moderator captures variation in the informational context (e.g., all-true, all-false, or mixed item sets), which may affect the baseline likelihood of endorsing repeated items as true.” - Lines (754-756): “We investigated whether repetition increases perceived truth for true vs. false statements equally which relates to the illusory truth effect in the misinformation context.” - Lines (761-765): “We examined the effect of testing environment to assess whether the data collection setting (online vs. face-to-face) introduces variability in effect sizes. This is especially relevant considering the increasing use of online platforms in the illusory truth effect research. It also helps evaluate the generalizability of laboratory findings to digital contexts where repeated misinformation is most encountered.” 6. Comment: In the same line of thought, I believe that the analysis contrasting the magnitude of effects between online and in-person conditions is presented without contextualizing its relevance (pragmatically to alert that the conditions do not allow the effect to be detected, or theoretically because we know the level of motivation of the respondents is different?). Therefore, it lacks a true discussion of the results. Response: We appreciate the Reviewer’s comment and agree that the difference in effect sizes between online and in-person studies requires deeper contextualization. The choice of this moderator was clearly pragmatical. With the growing reliance on online platforms for data collection it is important to assess whether study format introduces systematic variability in effect sizes. We included this moderator for its implications for the generalizability of findings to real-world settings (e.g., online misinformation exposure). In the original manuscript, we reported that in-person studies tended to show larger illusory truth effects compared to online studies. However, following modifications to our analysis (i.e., inclusion of new studies, additional moderators, and a small-study effect corrections), the difference between online and in-person studies did not reach statistical significance. This suggests that the previously observed difference may not be robust (as suggested by the inconsistent findings in the sensitivity analysis) and could reflect variability unrelated to the testing environment. We believe this absence of a significant effect is still worth highlighting, as it suggests that the illusory truth effect may be robust across testing environments. Thus, we have revised our manuscript accordingly as follows: - Lines (761-765): “We examined the effect of testing environment to assess whether the data collection setting (online vs. face-to-face) introduces variability in effect sizes. This is especially relevant considering the increasing use of online platforms in the illusory truth effect research. It also helps evaluate the generalizability of laboratory findings to digital contexts where repeated misinformation is most encountered.” - Lines (445-451): “The illusory truth effect seems to operate similarly whether participants complete the experiment online or in laboratory settings. This finding suggests that factors such as experimenter presence, environmental control, or potential distractions in online settings do not substantially influence cognitive processes involved in the illusory truth effect. Considering the increasing reliance on online data collection in psychological research, this consistency supports the generalization of such findings in real-world settings” 7. Comment: Personally, I find some conclusions drawn from the analysis of studies with very different methodologies concerning. For example, what happens when the authors conclude that the most relevant phase for deep processing is encoding, with retrieval not being relevant. In the retrieval phase, the time of sentence presentation is considered independently of whether they are presented immediately or one month after the study phase. In neither of these contexts does the exposure time influence retrieval conditions. One reason is that the information is still accessible in working memory or almost so, and in the other case, explicit accessibility does not improve with sentence presentation time. Response: We thank the Reviewer for highlighting this important methodological point. In our primary three-level meta-regression, we analyzed the main effect of each moderator because cells in crossed designs would contain too few effect sizes to support a reliable interaction test. We agree that this approach has limitations, particularly regarding the detection of potential interaction effects (e.g., between delay and test-phase presentation time). The Reviewer rightfully notes that the presentation time has theoretically a limited impact on retrieval conditions when the test phase follows immediately, or after a too long period the exposure phase. To address this specific concern, we performed an exploratory analysis of simple effects, excluding effect sizes drawn from studies with no delay and with a delay superior to a week. In this restricted data set, longer presentation time during the test phase still did not reliably modulate the illusory-truth effect compared with participant-paced presentation, t(101) = 1.72, p = .088, or shorter presentation time, t(117) = 1.71, p = .070. Within the moderator set and power constraints of our meta-analysis, two exposure phase moderators (i.e., exposure task, presentation time) robustly predicted effect size, whereas no test phase moderators reached conventional significance. While these findings highlight the relative salience of the exposure phase in our data, we acknowledge that it cannot rule out possible contribution of retrieval processes in specific study designs. In the revised manuscript, we modified statements on the importance of retrieval and discussed these limitations as follows: - Lines (476-483): “Another key limitation of the current meta-analysis is the substantial methodological diversity across the included studies. Procedures varied in initial rating tasks, delay intervals, presentation timing, and other moderators. While our three-level meta-regression is appropriate for estimating overall trends and accounting for clustered data, it lacks power to detect interaction effects given the uneven distribution of study designs across moderator combinations. Thus, moderator effects should be interpreted as indicators of relative salience rather than definitive estimates, as potential interactions may remain undetected in aggregate-level analyses” 8. Comment: I believe that the text would benefit from better readability if the results of the moderation analyses were presented in Figure 4 within a table, and if on that table they were contrasted with previous meta-analyses, highlighting what differs and what is new. Response: We thank the Reviewer for his/her suggestion. In our revised manuscript, the results of moderation analyses with the regression coefficient and their confidence intervals are reported in the main text. Additionally, the results are now contrasted with the results of Dechêne et al.’s (2010) meta-analysis in Table 2 presented below. A quick visual summary of the moderators’ effect is still provided in Figure 3, see: - Lines (219-221): “Table 2 summarizes the subgroup analyses contrasted with Dechêne et al.’s meta-analysis.” Table 2. Regression analysis results contrasted with Dechêne et al. (2010). All effect sizes and 95% confidence intervals are from bivariate random-effects subgroup analyses based on the between-item criterion. The current results reflect bias-corrected estimates using the PEESE method and account for missing data via multivariate imputation by chained equations, in contrast to the listwise deletion approach used by Dechêne et al. (2010). Current moderator analysis Dechêne et al. (2010) Coding u g 95% CI P-value Coding k d 95% CI P-value Item type Statement 309 0.41 [0.33, 0.48] < .001 / / / / / Headline 43 0.17 [0.01, 0.34] .048 / / / / / Claim 12 0.47 [0.20, 0.73] < .001 / / / / / Repetition Within- 361 0.38 [0.30, 0.45] < .001 Heterogeneous 65 0.51 [0.44, 0.58] < .001 manipulation participants Between- 5 0.17 [-0.28, 0.61] .464 Homogeneous 1 -0.09 [-0.76, 0.55) n.s. participants Exposure task Truth judgment 78 0.10 [-0.03, 0.23] .137 High level of 51 0.45 [0.37, 0.54] < .001 processing Irrelevant task 213 0.42 [0.34, 0.50] < .001 Low level of 19 0.62 [0.49, 0.75] < .001 Passive processing 73 0.47 [0.34, 0.60] < .001 processing Truth warning Warning 163 0.34 [0.25, 0.43] < .001 / / / / / at exposure No warning 41 0.44 [0.32, 0.57] < .001 / / / / / Truth warning Warning 66 0.38 [0.27, 0.48] < .001 / / / / / at test No warning 41 0.37 [0.26, 0.49] < .001 / / / / / Veracity cues No cue 287 0.43 [0.37, 0.50] < .001 / / / / / Balanced cues 6 0.28 [-0.08, 0.64] .130 / / / / / Positive cue 32 0.70 [0.51, 0.88] < .001 / / / / / Negative cue 41 -0.18 [-0.33, -0.03] .020 / / / / / Delay No delay 135 0.46 [0.35, 0.56] < .001 / / / / / between the Within day 138 0.33 [0.23, 0.43] < .001 Within day 25 0.49 [0.37, 0.62] < .001 exposure and Within week 47 0.36 [0.21, 0.50] < .001 Within week 14 0.44 [0.29, 0.59] < .001 test phases Over a week 41 0.25 [0.06, 0.44] .008 Longer delay 12 0.49 [0.32, 0.65] < .001 Repetition Verbatim 350 0.36 [0.29, 0.44] < .001 Verbatim 64 0.53 [0.46, 0.60] < .001 type Gist 16 0.63 [0.35, 0.91] < .001 Gist 6 0.22 [-0.02, 0.46] < .10 Presentation Visual 257 0.38 [0.31, 0.46] < .001 Visual 38 0.52 [0.42, 0.61] < .001 mode Verbal 62 0.30 [0.12, 0.48] < .001 Auditory 24 0.52 [0.39, 0.64] < .001 Both 17 0.32 [0.02, 0.62] .071 Mixed 4 0.67 [0.38, 0.95] < .001 Participant-paced 179 0.34 [0.26, 0.43] < .001 Participant-paced 16 0.41 [0.24, 0.58] < .001 5 seconds or less 77 0.39 [0.26, 0.52] < .001 Presentation More than 5 92 0.48 [0.33, 0.63] < .001 8 seconds or less 5 0.51 [0.21, 0.82] < .01 time at seconds exposure* Presentation Participant-paced 265 0.38 [0.31, 0.46] < .001 time at test* 5 seconds or less 43 0.31 [0.12, 0.49] < .001 More than 8 27 0.53 [0.41, 0.65] < .001 More than 5 54 0.36 [0.16, 0.56] < .001 seconds seconds Response / / / / / 1-7 (false-true) 40 0.41 [0.32, 0.49] < .001 scale (1) / / / / / 1-7 (true-false) 12 0.65 [0.49, 0.79] < .001 Likert scale 269 0.36 [0.29, 0.44] < .001 1-6 (false-true) 6 0.65 [0.43, 0.88] < .001 100-point slider 6 0.23 [-0.17, 0.62] .256 16cm (false-true) 5 0.65 [0.42, 0.89] < .001 Binary scale 91 0.43 [0.30, 0.56] < .001 Dichotomous 7 0.53 [0.27, 0.79] < .01 Response Odd 119 0.30 [0.18, 0.43] < .001 Odd 52 0.47 [0.38, 0.55] < .001 scale (2) Even 241 0.40 [0.32, 0.17] < .001 Even 13 0.60 [0.42, 0.78] < .001 Veracity True 83 0.46 [0.36, 0.56] < .001 / / / / / False 81 0.33 [0.23, 0.42] < .001 / / / / / None 12 0.31 [0.12, 0.49] < .001 / / / / / Face-to-face 196 0.31 [0.20, 0.43] < .001 Paper and pencil 42 0.59 [0.51, 0.69] < .001 Testing Online 169 0.40 [0.32, 0.48] < .001 Computer 14 0.33 [0.16, 0.50] < .01 environment *In Dechêne et al. (2010), the exposure time was not differentiated between the exposure phase and the test phase. 9. Comment: Please clarify, because I see no reason why the statistics are not presented in a more complete way, with their respective degrees of freedom and effect sizes. Response: We apologize for the lack of clarity. We agree that providing both the regression coefficients and their associated degrees of freedom can clarify our findings. Previously, we were concerned that reporting degrees of freedom in a multivariate imputation context might be confusing, because they do not align with a typical dataset’s interpretation. Specifically, when dealing with missing data via multiple imputation, each imputed dataset is analyzed separately, and the parameter estimates and standard errors are then pooled accounting for within-imputation variance and between-imputation variance. Thus, the resulting pooled degrees of freedom are generally not simply the sample size minus the number of estimated parameters but also account for the variability introduced by multiple imputations (van Buuren, 2018). Similarly, effect sizes in a meta-regression with numerous categorical moderators depend heavily on the chosen baseline. Hence, in our initial draft, we opted to present standardized estimates in a figure. We have clarified this in our manuscript as follows: - Lines (210-215): “We created 20 imputed data sets, each with a maximum of 20 iterations to ensure convergence of the chained equations. We then pooled the resulting coefficients and their variances according to Rubin’s rules to obtain the meta-analytic estimates 46. As a result, the adjusted degrees of freedom associated with t-statistics also account for the variability introduced by multiple imputations 47.” Additionally, in the revised manuscript, we now include the degrees of freedom and the subgroup effect size estimates in the main text and in Table 2. For example, see: - Lines (228-233): “The illusory truth effect was significantly larger in studies using statements (g = 0.41, 95% CI [0.33, 0.48]) compared to news headlines (g = 0.17, 95% CI [0.01, 0.34]), b = 0.25, 95% CI [0.02, 0.47], t(162) = 2.16, p = .033, but not compared to opinion-based claims (g = 0.47, 95% CI [0.20, 0.73]; observed u = 12), t(117) < 1. Effect sizes did not significantly differ between news headlines and opinion-based claims, t(127) = 1.10, p = .275.” 10. Comment: I would like to point out that when t<1, the p-value calculation is unstable and unreliable, so it does not need to be presented (see, for example, Voelkle et al., 2007). Response: We appreciate the Reviewer’s suggestion and have removed the p-values associated with a t-statistic < 1 in our revised manuscript. 11. Comment: Finally, when I finished reading the discussion, I realized that the article could gain more consistency if it were to adopt a theoretical or pragmatic objective instead of an unbalanced mixture of both. When I read it, my interest was theoretical, and I wanted to understand the cognitive mechanisms underpinning the effect. But the article might aim for a pragmatic framework. In that sense, it is important to understand that misinformation goes beyond the truth illusion effect and should not be conflated. But if this is the main concern, it would be important to understand what the moderators say about the possibility of spreading fake news or how we can prevent it. Response: We thank the Reviewer for their suggestion. Based on the Reviewer’s suggestion, we have revised the manuscript to more clearly articulate the aims of the present meta-analysis and how they are integrated. Specifically, we now clarify at the end of the introduction section that the primary goal of this meta-analysis is to investigate the cognitive mechanisms and boundary conditions of the illusory truth effect, while also examining how these mechanisms relate to the spread of misinformation. While we agree that strictly pragmatic focus can improve the coherence of the article, we believe that our meta-regression should also discuss theoretical mechanisms whenever it is possible. Our Discussion section now more explicitly focuses on the practical implications of the meta-analysis. We also have added a sentence to the Discussion section to emphasize that repetition-based fluency is only one of many mechanisms contributing to misinformation belief and spread as follows: - Lines (514-517): “Nevertheless, it is important to note that the illusory truth effect captures only one mechanism (e.g., repetition-based fluency) among many that contribute to the belief and spread of misinformation.” Finally, we wish to note our selection of moderators was guided more by pragmatic considerations than by strict alignment with any one theoretical framework. This is because the moderators that could be reliably extracted across studies do not systematically align with the constructs proposed by existing theoretical models. Moreover, given the current limitations in the number of effect sizes available per moderator combination, we are not able to reliably examine interactions between moderators, which prevents us from explicitly testing the core predictions of theoretical accounts. As a result, while our findings provide theory-relevant insights (e.g., regarding processing depth, fluency-based processes, encoding conditions…), they should not be interpreted as adjudicating between competing cognitive models. We have clarified this limitation in the manuscript: - Lines (483-492): “Moderator selection was primarily guided by pragmatic considerations than by alignment to a specific theoretical framework. Thus, they should not be interpreted as direct tests of cognitive models. In fact, the moderators that could be reliably extracted across studies do not systematically align with key constructs from existing theoretical accounts. Moreover, the limited number of effect sizes per moderator combination prevents us from testing interaction effects that would be necessary to evaluate core theoretical predictions. While our findings provide relevant insights to theory-relevant processes (e.g., fluency, depth of processing, encoding conditions), they should not be interpreted as conclusions about the validity of competing cognitive models.” 12. Comment: I also have two small details that could assist in the more detailed revision of the presented text: Line 37: “after a certain delay” should be changed to “In most studies after a certain…” Line 39: “… and new statements previously unseen in a random order” Response: We thank the Reviewer for his/her suggestions. We have revised the manuscript accordingly. Reviewer 4 Comments Overall Comment: I have reviewed the revised manuscript and the authors' response to my comments. I appreciate the extensive revisions that have been undertaken. The authors have diligently addressed the major methodological concerns, and the manuscript has been improved considerably as a result. In particular, I would like to highlight several key improvements: - The updated literature search (which now includes studies up to early 2025) is a significant addition that enhances the relevance and comprehensiveness of the review. - The implementation of a PEESE correction to address small-study effects and its use as a baseline for moderator analyses has increased the robustness of the reported findings. - The discussion section has been strengthened by the inclusion of a more nuanced reflection on heterogeneity, including potential artifacts from standardization and multiplicity. I have one final suggestion for a minor revision to improve the statistical accuracy of the reporting. It concerns the justification provided for using Borenstein's formula over Becker's for the effect size calculation. The manuscript states that Borenstein's method was chosen because its estimates were \"more conservative\". This is a terminological inaccuracy. Statistically, a wider confidence interval (as produced by Becker's formula in the authors' sensitivity analysis) reflects greater uncertainty and is therefore considered more conservative. A narrower confidence interval is more precise, but can also be considered more liberal if that precision is an artifact of imputation, as may be the case here. The greater precision of the Borenstein estimator is likely a consequence of imputing missing correlations, which may lead to an overconfident (i.e., artificially narrow) estimate of the uncertainty. Recommendation: I suggest revising the justification on lines 820-821 to transparently acknowledge this trade-off and that the greater precision is contingent on the assumptions made during the imputation of missing correlation coefficients. This would clarify the rationale while also transparently acknowledging the potential limitations of the chosen methods. With this adjustment, the manuscript will be a robust and significant contribution to the literature. Hence, I recommend acceptance following this minor revision. Response: We thank the Reviewer for his/her appreciation of our work and the suggestions to improve our methodology. Standardized Mean Differences and Imputation of Missing Data 1. Comment: The manuscript states that Borenstein's method was chosen because its estimates were \"more conservative\". This is a terminological inaccuracy. Statistically, a wider confidence interval (as produced by Becker's formula in the authors' sensitivity analysis) reflects greater uncertainty and is therefore considered more conservative. A narrower confidence interval is more precise, but can also be considered more liberal if that precision is an artifact of imputation, as may be the case here. The greater precision of the Borenstein estimator is likely a consequence of imputing missing correlations, which may lead to an overconfident (i.e., artificially narrow) estimate of the uncertainty. Recommendation: I suggest revising the justification on lines 820-821 to transparently acknowledge this trade-off and that the greater precision is contingent on the assumptions made during the imputation of missing correlation coefficients. This would clarify the rationale while also transparently acknowledging the potential limitations of the chosen methods. Response: We thank the reviewer for this important clarification regarding the use of the term \"conservative\" and the implications of imputing missing correlations. We agree that describing the Borenstein method as “more conservative” was imprecise and have revised the justification to better reflect the statistical trade-off involved. The revised text now acknowledges the limitations and motivates the choice based on interpretability and convergence properties as follows: - Lines (860-869): “We also conducted a sensitivity analysis using Becker’s formula to compute the standardized mean difference 85. The alternative formula could reduce uncertainty in the pooled estimates caused by missing outcomes imputation, as it only requires standard deviations from the first assessment. Computation using Becker’s formula yielded effect sizes close to those from Borenstein’s but with slightly wider confidence intervals, reflecting greater uncertainty (see Supplementary Table 5). We selected Borenstein’s method for the main analyses because it yielded more stable estimates across studies, which facilitates interpretation and comparability of effect sizes in the synthesis. However, we acknowledge that its greater precision is contingent on the imputation of missing correlations, which may lead to potentially overconfident uncertainty estimates.” Systematic review and meta-analysis of the evidence for an illusory truth effect and its determinants Response to Reviewers We thank the Reviewers for their evaluation of our manuscript and for their constructive feedback. All modifications in the manuscript have been highlighted in yellow color. Detailed responses to each point raised by Reviewers are provided below. Reviewer 2 Comments Overall Comment: I was Reviewer 2 on the last round of reviews. The authors have done an excellent job addressing my concerns, and I applaud their attention to detail when making these changes. I have just a few minor points below, but I believe this manuscript is now ready for publication without another full round of review. Congratulations on this work! Response: We thank the Reviewer for their positive and encouraging assessment of our revised manuscript. We are pleased that we were able to address their previous concerns and appreciate their constructive feedback throughout the review process. New veracity cues moderators: 1. Comment: The authors find that the effect size for providing false cues is g = -0.18, 95% CI [-0.33, -0.03]. The exploratory analysis by type of cue also found that most cues had confidence intervals below zero. This means that the illusory truth effect was actually reversed, with repeated claims now being judged as less true than new claims. In discussing these effects, however, this reversal is not mentioned, and rather it is just reported that the size of the truth effect was decreased with false cues (e.g., from the discussion “False cues reduced the impact of repeated exposure on perceived truth while true cues did not affect the illusory truth effect”). This type of wording (the false cues decreased the size of the illusory truth effect) implies to me that there is still an illusory truth effect with false cues. I think it would be important and informative when presenting results like this to clearly communicate that it’s not just that the size of the illusory truth effect is smaller, but also that it’s reversed. Response: We thank the Reviewer for this comment. We agree that our previous wording may underplay the effect reversal observed in the subgroup analysis. While these subgroup estimates are descriptive and not adjusted for the full set of moderators included in the meta-regression, a negative estimate with confidence intervals entirely below zero indeed indicates that repeated statements were judged as less true than new statements on average in studies implementing false cues. We have therefore revised the Discussion to explicitly state that false cues not only reduce but reverse the illusory truth effect at the subgroup level as follows: - Lines (453-460): “In particular, false cues not only attenuated but, on average, reversed the illusory truth effect, such that repeated statements were judged as less true than new statements. In contrast, true cues did not reliably alter the magnitude of the illusory truth effect. This pattern suggests that explicit falsity cues can override the influence of repetition, providing further support for the potential effectiveness of debunking interventions. However, because this reversal is observed in subgroup estimates that are not adjusted for the full set of moderators, it should be interpreted as descriptive of existing study patterns.” 2. Comment: I didn’t check all the observed u that were added, but noticed that for false cues, the authors reported observed u = 40 in the results and observed u = 41 in the methods. Then, if you add up the observed u for the different types of false cues, they only add up to 37. The true cues, on the other hand, are reported as observed u = 33 in the results and observed u = 32 in the methods, but if you add up the true cues from the table, those equal 36. There seem to be either typos or coding issues going on here. Response: We thank the Reviewer for carefully noting these inconsistencies and apologize for the oversight. We would like to clarify that the inconsistency in the Methods section originate from the same coding error in the veracity-cue moderator that we identified and reported during the previous round of peer review. As stated in our earlier response, this coding error was corrected in the dataset and all analyses, and it did not affect the pattern, magnitude, or interpretation of any results. In addition, the Reviewer refers to a discrepancy in the subgroup analysis by cue type reported in the Supplementary Information. This was due to a typographical swap in the counts for epistemic qualifiers (true vs. false cues), which has now been corrected (false cues = 10; true cues = 7). We have now harmonized the reported counts across the Methods, Results, and Supplementary Information. 3. Comment: In the abstract – saying “since 2006” in the abstract without context (that the previous meta looked for effects up to 2006) may be confusing to readers. As a very minor note, but in case it’s not caught in copy editing, the effect size g = .37 is missing a “0” In front of the decimal. Response: We thank the reviewer for noting these points. We have clarified the reference to “since 2006” in the abstract by explicitly indicating that it refers to the publication date of the previous meta-analysis. We have also corrected the effect size notation to include a leading zero (g = 0.37). The revised abstract now reads: - Lines (4-9): “In light of a growing number of studies published since the previous meta-analysis in 2006 and concern of publishing biases, we conduct a meta-analysis on 182 studies and 366 effect sizes (N = 31,184 participants) published from 1977 to 2025. After correcting for small-study effects, we observe a small illusory truth effect (g = 0.37, 95% confidence interval [0.30, 0.44]), with a substantial within and between-study heterogeneity.” 4. Comment: Minor wording suggestion: On p. 5, line 87 the authors write - “In particular, the illusory truth effect seems to be different” – I think saying “smaller” instead of “different” would work better here. Response: We thank the Reviewer for this helpful suggestion. We have replaced “different” with “smaller” to more precisely reflect the quantitative comparison between within-item and between-item effect sizes. Reviewer 4 Comments Overall Comment: I thank the authors for their thorough revision. My queries have been satisfactorily adressed. Response: We thank the Reviewer for their positive assessment and are pleased that our revisions satisfactorily addressed their concerns."}]

Decision letter