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Metacognitive experiences in judgments of truth and risk

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Metacognitive experiences in judgments of truth and risk

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Content Copyright 2021 Madeline Jalbert
Metacognitive Experiences in Judgments of Truth and Risk
by
Madeline Jalbert
A Dissertation Presented to the
Faculty of the USC Graduate School
University of Southern California
In Partial Fulfillment of the Requirements for the Degree
Doctor of Philosophy
(Psychology)
August 2021

ii
Acknowledgements
First, I would like to thank my advisor, Norbert Schwarz. I have learned more than I
thought possible during my graduate career and I am endlessly grateful for the doors he helped
open. I truly could not have asked for a better mentor to guide me through my PhD.
I would also like to thank Eryn Newman, who took me under her wing as a new graduate
student. She has been an excellent role model for how to succeed in academia while being an
incredibly kind and caring person.
Additionally, I would like to thank my lab group, which has provided me with endless
support and friendship over the years. I can’t say enough about how lucky I feel to have been
part of such an interesting, intelligent, friendly, and funny group of people. We also always had
the best snacks.
Next, I would like to thank Daphna Oyserman, Richard John, and Dan Simon for serving
on my dissertation committee and providing helpful feedback on my projects as I developed my
dissertation.
Finally, I’d like to give a shoutout to my undergraduate advisor Ira Hyman. He gave me
my first opportunity to join a research lab, connected me to the cognitive psychology committee,
and guided me through the process of applying for graduate school when I had no idea what I
was doing. Even though I completed my degree long ago, he has continued to provide excellent
mentorship and useful advice that I am always grateful for. I am honored to continue his legacy
of paying it forward with my future mentees.

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Table of Contents
Acknowledgements..........................................................................................................................ii

Abstract......................................................................................................................................iv

Introduction......................................................................................................................................1

Chapter I: Only Half of What I’ll Tell You is True: Expecting to Encounter Falsehoods Reduces
Illusory Truth......................................................................................................................4

Chapter II: Individual Differences in Elaborative Processing and the Illusory Truth Effect:
What Helps Now Hurts Later?...........................................................................................31

Chapter III: A Lemon in Yellow, a Lemon in Blue: Color Congruence and Truth Judgment......50

Chapter IV: If It’s Relatively Difficult to Pronounce, It Might be Risky: Risk Perception Depends
on Processing Experience in Context.................................................................63

General Discussion........................................................................................................................84

References......................................................................................................................................86

Appendices...................................................................................................................................102
Appendix A: Chapter I Figures........................................................................................102
Appendix B: Chapter I Supplementary Materials............................................................106
Appendix C: Chapter II Figures.......................................................................................133
Appendix D: Chapter III Supplementary Materials.........................................................136
Appendix E: Chapter IV Tables.......................................................................................142
Appendix F: Chapter IV Supplementary Materials.........................................................150

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Abstract
Understanding how people make judgments of truth and risk is a key component in developing
effective misinformation prevention and correction strategies. When deciding whether something
is true or risky, people often rely on their metacognitive experience of how easy the information
feels to process. Processing ease can serve as a valid cue for making these judgments, but can
also arise due to factors unrelated to the judgment at hand. Importantly, these metacognitive
experiences also interact with the context of judgment. In this dissertation, I explore the role of
several contextual factors in metacognitive evaluations of truth and risk. In Chapter I, I examine
the impact of common experimental warnings on belief in repeated information. In Chapter II, I
look at the influence of individual differences in elaboration on the truth effect. In Chapter III, I
consider the potential influence of multimodal associations in knowledge networks on truth
perception by exploring the role of color congruence – a novel variable. Finally, for Chapter IV,
I investigate how absolute and relative variation in fluency – manipulated through
pronounceability – influences judgments of risk. Across these four papers, I elucidate several
factors that should be considered when evaluating effective methods for correcting
misinformation and communicating potential risks to the general public. These findings have a
number of implications for how to better conduct and apply laboratory research to address real-
world problems.

1
Introduction
In a world of social media use and heightened political polarization, it has become
increasingly important to develop new strategies to prevent the spread of false information and
foster belief in the truth. Recent events regarding the COVID-19 pandemic have added new
urgency to this need. Throughout this pandemic, the public has been exposed to contradictory
claims regarding the spread of the virus, which preventative measures and treatments are safe
and effective, and the safety and efficacy of vaccination.
For example, national headlines have continued to be filled with concern about the safety
of vaccinations following reports of rare blood clots resulting from the Oxford-AstraZeneca
vaccine. Yet, an investigation conducted by the European Medicine Agency (EMA) failed to find
a link between the Oxford-AstraZeneca vaccine and an overall increase in blood clot events
(European Medicines Agency, 2021) – possibly because the risk of blood clots following
COVID-19 infections is much higher than the risk of blood clots following administration of the
vaccine (Mahse, 2021). These investigations have led the EMA and World Health Organization
to agree that the benefits of receiving the vaccine outweigh the risks and to advise continued
vaccination. Yet public concern over blood clot risks continues to hinder vaccination efforts. For
example, weeks after the EMA’s investigation finding the AstraZeneca vaccine to be safe and
effective, Chinese citizens remain hesitant to receive their doses, leading Malaysia to pause
access to the vaccine at public vaccination centers despite an alarming spike in cases and only
4% of its population currently vaccinated (Power & Goh, 2021).
What are the best ways to improve public understanding of the current state of expert
knowledge about vaccines? How can we properly communicate the relative risks associated with
contracting COVID-19 compared to those of vaccinations? Questions such as these are difficult

2
to answer given the extensive variation in the content and context of information individuals are
exposed to. Thus, sweeping recommendations for how to correct false beliefs are unlikely to be
effective. Rather, more work must be done to understand which strategies may be maximally
effective for the context at hand.
How do people evaluate whether information is true or whether something is risky?
People may carefully analyze the content of the information given to them, an effortful analytic
strategy. On the other hand, people may rely on how easy the information feels to process when
making these decisions, a less effortful intuitive process that occurs quickly. Processing fluency
plays a powerful role in making judgments of risk and truth, leading people to draw different
conclusions than they would reach solely through careful analysis (for reviews, see Newman,
Jalbert, & Feigenson, 2019; Schwarz & Jalbert, 2020; Schwarz, Jalbert, Noah, & Zhang, 2021).
Sometimes, processing ease can serve as a valid cue for making these judgments. For
example, a statement may feel difficult to process because it is incoherent and does not fit
together logically, and is thus unlikely to be true. However, people are often more sensitive to
their processing experience than to the source of this experience (Schwarz, 2012). Thus, they are
also likely to misread fluent processing due to incidental influences as bearing on the truth of a
statement or the risk of a situation. Indeed, numerous variables that affect processing fluency
have been found to influence judgments of truth and risk, from mere repetition (Hasher,
Goldstein, and Toppino (1977); Dechêne, Stahl, Hansen, & Wänke, 2010) to print font and color
contrast (e.g., Garcia-Marques, Silva, & Mello, 2016; Parks & Toth, 2006; Reber & Schwarz,
1999; Silva, Garcia-Marques, & Mello, 2016) to accent and audio quality (Lev-Ari & Keysar;
Newman & Schwarz, 2016), to the ease of pronouncing the information or the information’s
source (Newman et al., 2014; Song & Schwarz, 2009; Zürn & Topolinki, 2017).

3
However, the influence of metacognitive experiences of fluency on judgments of truth
and risk does not occur independently from the context in which these judgments occur. The
implications of overlooking this fact are wide-reaching when attempting to offer widespread
recommendations on real-world policy based on the results of isolated lab studies. Manipulations
that appear fruitful for correcting false beliefs in the lab may not generalize to other contexts, as
commonplace experimental practices are often uncommon outside the lab. For example, lab
studies may routinely provide participants with information or instructions to guide their thinking
in ways that do not occur in the real world. They may only investigate the effectiveness of
interventions or corrections with short, one-session studies and not consider how corrections may
influence judgments over time. Finally, they may focus on judgments in isolation instead of
considering how they are situated as part of a broader associative knowledge network or may be
made in the context of other judgments.
Overview of dissertation
In this dissertation, I explore how contextual factors such as these may influence
metacognitive evaluations of truth and risk. I present four connected sets of studies, three
focused on judgments of truth (Chapters one through three) and one focused on judgments of
risk (Chapter four). In Chapter I, I examine the role of common experimental warnings on belief
in repeated information (Jalbert, Newman, & Schwarz, 2020). In Chapter II, I look at the
influence of individual differences in elaboration on the truth effect (Newman, Jalbert, Schwarz,
& Ly, 2020; Experiments 3 & 4). In Chapter III, I consider the potential influence of multimodal
associations in knowledge networks on truth perception by exploring the role of color
congruence – a novel variable. Finally, for Chapter IV, I investigate how absolute and relative
variation in fluency – manipulated through pronounceability – influences judgments of risk.

4
Chapter I: Only Half of What I’ll Tell You is True: Expecting to Encounter Falsehoods
Reduces Illusory Truth
1

For millennia, demagogues believed that repetition can turn lies into truth. Experimental
research confirmed their intuitions. Four decades ago, Hasher, Goldstein, and Toppino (1977)
reported that the mere repetition of a statement increased its acceptance as true. This so-called
illusory truth effect proved robust and easily replicable, with a meta-analysis of seventy effect
sizes reporting an average between-items effect size of d = 0.50 (95% CI [0.43, 0.57]) for the
difference in truth ratings between new and repeated items (Dechêne, Stahl, Hansen, & Wänke,
2010). Current concerns about the prevalence of fake news and their repetition on social media
have renewed interest in the issue. Unfortunately, the standard procedures of truth effect
experiments may not be a good approximation of the conditions of message repetition in natural
contexts. Most commonly used experimental procedures create exposure conditions that draw
attention to the fact that some of the information one will see is false. Such pre-exposure
warnings may systematically decrease the impact of repetition compared to natural conditions,
where false information does not come with a warning label. We test this possibility by
investigating the size of illusory truth effects under conditions that do or do not include common
pre-exposure warnings.
Judgment and persuasion research suggests that people draw on a limited set of criteria to
determine whether a claim is likely to be true (Schwarz, 2015): Is the claim compatible with
other things they believe? Is it internally consistent? Does it come from a credible source? Do

1
This chapter is based on:
Jalbert, M., Newman, E., & Schwarz, N. (2020). Only half of what I’ll tell you is true: Expecting
to encounter falsehoods reduces illusory truth. Journal of Applied Research in Cognition and
Memory, 9, 602-613. https://doi.org/10.1016/j.jarmac.2020.08.010

5
others believe it? Is there supporting evidence? Each of these truth criteria can be assessed by
careful attention to the claim and reliance on applicable knowledge (for reviews, see Brashier &
Marsh, 2020; Schwarz, 2015; Unkelbach et al., 2019). They can also be assessed by drawing on
one’s metacognitive experiences as a proxy. In each case, the attribute that provides an
affirmative answer to the criterion is correlated with fluent processing. For example, when
information is compatible with other things one believes (Unkelbach & Rom, 2017; Winkielman,
Huber, Kavanagh, & Schwarz, 2012), internally coherent (Johnson-Laird, 2012), or familiar
from previous exposures (Jacoby, 1983), it is processed more fluently than when it is not.
Moreover, familiar sources are more credible (Petty & Cacioppo, 1986) and supporting evidence
is assumed to be more plentiful when some comes to mind easily (Schwarz, 1998; Tversky &
Kahneman, 1973). This makes the metacognitive experience of processing fluency a heuristically
informative input into judgments of truth, independent of whether people assess the claim’s
compatibility with their own knowledge, its coherence, social consensus, source credibility, or
the likely amount of supporting evidence. Indeed, fluent processing can override one’s own
knowledge; when information feels true and no alternative accounts easily come to mind, people
may accept it without performing the more effortful analysis that would lead them to find it false
(Brashier, Eliseev, & Marsh, 2020, for a review see Brashier & Marsh, 2020).
That processing fluency is correlated with substantive attributes relevant to judging truth
implies that it provides valid information. Unfortunately, people are more sensitive to their
processing experience itself than to the source of this experience (Schwarz, 2012) and sometimes
misread fluent processing due to incidental influences as bearing on the truth of a statement.
Indeed, numerous incidental variables that affect processing fluency have been found to
influence judgments of truth, from print font and color contrast (e.g., Garcia-Marques, Silva, &

6
Mello, 2016; Parks & Toth, 2006; Reber & Schwarz, 1999; Silva, Garcia-Marques, & Mello,
2016) to accent (Lev-Ari & Keysar, 2010) and audio quality (Newman & Schwarz, 2016), to the
ease of pronouncing the information’s source (Newman et al., 2014). Such fluency effects are
incidental and unrelated to the semantic content of the claim.
Repetition of a claim can influence judgments of truth through several pathways, namely
increased perceptual and conceptual fluency, increased accessibility of applicable knowledge,
and recollection of source information. Accordingly, variants of recollective and fluency-based
process accounts have been offered since Hasher and colleagues’ (1977) experiments.
Empirically, knowledge gleaned from recalling the context of prior exposure as well as
processing experience contribute to repetition effects (Unkelbach & Stahl, 2009). Additionally,
the impact of repetition often exceeds that of perceptual fluency manipulations, such as print font
(e.g., Parks & Toth, 2006), and strategies that are effective in attenuating the influence of
perceptual fluency, such as stressing the need to be accurate when assessing truth, are less
effective in correcting repetition-based truth effects (e.g., Garcia-Marques et al., 2016; Silva et
al., 2016).
Pre-exposure and Pre-test Warnings
A typical investigation of repetition-based truth effects begins with an exposure phase,
where participants view a series of ambiguous claims. Usually, half of these claims are true and
half are false. Following a delay (ranging from a few minutes to several days), there is a test
phase, where participants view claims they saw during the exposure phase along with new claims
and rate the truth of each claim.
Studies vary in the extent to which they draw participants’ attention to the truth of the
claims at initial exposure. In the majority of studies, researchers alert participants to the presence

7
of potential falsehoods at exposure in at least one of two ways: by stating in the instructions that
claims vary in truth value (e.g., Begg, Anas, & Farinacci, 1992; Hasher et al., 1977) and/or by
asking participants to make a truth judgment for each claim as it is presented (e.g., Brown & Nix,
1996; Hasher et al., 1977). Occasionally, claims are explicitly labeled as true or false as they are
presented (e.g., Skurnik, Yoon, Park, & Schwarz, 2005). In a small number of studies,
participants are not alerted to the presence of potential falsehoods at exposure. Instead,
participants may be asked about attributes other than truth (e.g., Brashier et al. 2020; Hawkins &
Hoch, 1992) or simply view the claims for a later memory test (Mitchell, Sullivan, Schacter, &
Budson, 2006).
At the time of testing, all truth effect studies draw participants’ attention to the truth of
the claims simply by asking participants to judge their truth. At this stage, some studies
additionally provide participants with explicit instructional information alerting them that
“some” or “half” of the claims are false (e.g., Begg, et al., 1992; Brashier et al., 2020).
How might drawing attention to the presence of falsehoods at the time of encoding, either
by asking participants to make truth judgments or through instructional details, influence the size
of the truth effect? Previous research showed that making truth judgments during initial exposure
reduces the impact of repetition (e.g., Hawkins & Hoch, 1992). More recent research focusing on
false claims indicates that this protective influence may only occur for false claims for which
participants have knowledge that allows them to arrive at the correct answer (Brashier et al.,
2020). In a meta-analysis, Dechêne et al. (2010) obtained an effect size of d = 0.45 (95% CI
[0.37, 0.54]) for studies that included truth judgments at exposure as compared to d = 0.62 (95%
CI [0.49, 0.75]) for studies that asked for other judgments or no judgments at all. Dechêne and
colleagues (2010) attributed this observation to differences in level of processing, but it is worth

8
noting that asking for an assessment of truth amounts to acknowledging that truth cannot be
taken for granted. From this perspective, the meta-analysis suggests that drawing attention to
truth at encoding by requesting explicit judgments for each claim can reduce the size of the truth
effect.
However, it is unclear whether merely informing participants that some statements will
be false through standard experimental instructions can do the same thing. This question is
difficult to answer meta-analytically because most of the available studies (51 out of 70 effect
sizes included in Dechêne et al., 2010) include truth judgments at exposure, making the impact
of instructional warnings difficult to isolate. Additionally, the methods sections of some reports
lack the procedural details that would be necessary to determine if instructional warnings were
given at the exposure stage.
Research on the encoding and correction of misinformation suggests that instructional
warnings can influence later belief in false information (for a review, see Lewandowsky, Ecker,
Seifert, Schwarz, & Cook, 2012). In general, people are better able to protect themselves from
misinformation if a warning makes them skeptical of the accuracy of that information during
encoding. Increased skepticism promotes more critical processing and reduces the acceptance of
new information as true (e.g., Fein, McCloskey, & Tomlinson, 1997; Greene, Flynn, & Loftus,
1982; Lewandowsky, Stritzke, Oberauer, & Morales, 2005; Schul, 1993). Pre-exposure warnings
that some statements are false may similarly elicit more critical processing at encoding, reducing
the impact of repetition in truth effect experiments. These findings suggest that without
instructional warnings at exposure, the truth effect may be larger than previously thought. Hence,
the most frequently used experimental procedures may underestimate the impact of repetition
under natural conditions.

9
It is less clear how instructional warnings at the time of test may influence the size of the
truth effect. Being asked to make a truth judgment already entails that the claims are likely to
vary in veracity. Hence, additional information that merely warns recipients that some of the
claims are false may have little impact. Consistent with this assumption, Nadarevic and Aßfalg
(2017) reported that only a detailed explanation of the truth effect and specific instructions for
how to prevent it prior to test reduced the impact of repetition, whereas more general warnings
did not. We similarly expect to find little impact of warnings presented at the time of testing, in
contrast to warnings presented at the time of exposure.
Present Research
We investigated how the presence, timing, and content of instructional warnings
influence the size of the truth effect. In Experiment 1.1, we manipulated the presence of pre-
exposure warnings: participants either did or did not receive a warning that half of the claims are
false before they were exposed to the claims. In Experiment 1.2, we tested the impact of pre-
exposure and pre-test warnings: participants received a warning prior to exposure and test, a
warning prior to test only, or no warning at all. This allowed us to determine whether
instructional warnings at the time of testing have a protective value either by themselves or in
combination with pre-test warnings. In Experiment 1.3, we varied the warnings by telling
participants either that “some” or “half” of the statements would be false.
Experiment 1.1
The purpose of Experiment 1.1 was to investigate how the presence of standard
instructional warnings prior to the initial exposure influences the size of the truth effect. Based
on the observation that pre-exposure warnings reduce the impact of misleading information in
other paradigms (e.g., Fein et al., 1997; Greene et al., 1981; Lewandowsky et al., 2005; Schul,

10
1993) we predicted that the impact of repetition is smaller when participants are aware, prior to
exposure, that some information they are about to see may be false. We included a delay of three
to six days between initial exposure and test to approximate the often long delays between
exposure and re-exposure under natural conditions. We predicted that, compared to a no warning
condition, pre-exposure warnings would attenuate the impact of repetition on rated truth even
after a multi-day delay. All stimuli, instructions, recruitment and attrition information, data,
syntax, and additional analysis are included in the supplemental materials and are available at
https://doi.org/10.3886/E115141V2.
Method
Design. We used a 2 (warning: before exposure only vs. no warning) x 2 (repetition:
trivia claim repeated vs. new) mixed design, manipulating warning between subjects and
repetition within subjects. The delay between exposure and test was 72 to 144 hours (three to six
days).
Participants. Students from the University of Southern California psychology subject
pool completed the survey for course credit. Data collection took place in two waves. Based on
the between-items effects size of d = 0.50 (95% CI [0.43, 0.57]) reported by Dechêne et al.
(2010), a sample size of 54 would be required to detect the truth effect in a repeated measures
design, with α = .05, power (1-β) = .95, and two-tailed, according to G*Power (Faul, Erdfelder,
Lang, & Buchner, 2007). We chose to overpower our study and recruit up to 200 participants,
100 per between-subjects condition. However, we ended data collection when the subject pool
closed and included all participants that had completed the experiment at that point.
Unfortunately, by the time the subject pool closed, we had only recruited approximately one

11
third of our desired number of participants. We therefore collected additional data in a second
wave the following year, where we again opened the study up to 200 participants.
We include all participants in the analyses below, except those who did not complete part
one (n = 13) within 24 hours of when they began the survey or part two (n = 5) within 48 hours
after the email invitation for that part; both exclusions are necessary to ensure the desired delay
period of three to six days. Three additional participants were excluded due to procedural errors
(two participants received access to and completed part 2 early and one participant completed
part 1 twice). Overall, 220 participants (58 male; Mage = 20.51, SD = 2.63, one not reporting)
completed both parts of the experiment: 55 in the first wave and 165 in the second wave. Adding
time of data collection as a factor to the analysis reveals neither a significant main effect, F (1,
216) = 0.15, p = .703, partial eta
2
< .01, nor a significant interaction with warning condition, F
(1, 216) = 0.51, p = .475, partial eta
2
< .01, repetition, F (1, 216) = 1.03, p = .312, partial eta
2

= .01, or three-way interaction, F (1, 216) = 2.05, p = .154, partial eta
2
= .01. Moreover,
analyzing both waves of data collection separately reveals the same pattern of significant main
and interaction effects for each wave. Hence, we collapsed analysis across the two waves,
resulting in 113 participants in the no warning condition and 107 participants in the pre-exposure
warning condition.
Materials. We selected trivia claims from a larger set of previously normed claims
(Jalbert, Newman, & Schwarz, 2019). The trivia claims covered a variety of topics (sports,
geography, food, animals, and science) and were selected to be ambiguous – only those rated as
true between 35% and 65% of the time were included. Examples of true claims are “Walruses
use their tusks primarily for mating” and “Kava is a beverage made from the root of the pepper
plant”. Examples of false claims are “The mouth of a sea urchin is on its top” and “Biking is the

12
first event in a triathlon”. During norming, false claims had been created by taking a true claim
(e.g., “The mouth of a sea urchin is on its bottom” and “Swimming is the first event in a
triathlon”) and altering one word to an incorrect but plausible sounding alternative. We only
chose either the true or false version of a claim so that participants would never see both.
Participants saw 36 trivia claims during the initial exposure. In the test phase, participants
saw the same 36 claims as well as 36 new claims, for a total of 72 claims. Each claim was
presented for five seconds in random order during each session. Half of the trivia claims were
true and half were false, both during exposure and testing phases.
The trivia claims were counterbalanced such that half of the participants saw one set of
36 claims repeated, and half of the participants saw the other set of 36 claims repeated. Based on
the norming data, both true and false claims were rated as true approximately the same
proportion of the time (both M = 0.52, SD = 0.08).
Procedure. The procedures for all experiments reported in this paper were approved by
the University of Southern California’s Institutional Review Board (IRB). When participants
signed up, they agreed to complete both parts of a two-part online survey.
Exposure Phase. Immediately after completing a consent form, participants were told that
they would see a series of trivia claims for approximately three minutes. In the pre-exposure
warning condition, participants were additionally given a warning “half the statements are true,
and half the statements are false”. Participants in the no warning condition were not told this. All
participants were then told that the trivia statements would be presented automatically and that
there was no need to press any buttons. They were asked to read the trivia statements carefully as
they were presented, but to not do anything else. The claims were then presented.

13
After viewing the claims, participants were asked a few general questions to provide a
rationale for presenting the claims, including “How many statements do you think you read?”
and “How many minutes do you think it took you to read the statements?”.
Delay Phase. After a three-day delay, participants received a link to part 2 of the survey
and were given 48 hours to complete it. Thus, the total time between exposure and test was 72 to
144 hours.
Test Phase. In the test phase, participants were shown another series of trivia claims. All
participants were correctly told that half of the statements were ones that they had seen before
and half of the statements were new. None of the participants were given any warning about the
truth of the statements. For each claim, all participants answered the question “Is this statement
true or false?” on an unnumbered six-point scale from “definitively true” (coded as 6) to
“definitely false” (coded as 1).
Demographics. Following the truth ratings, participants completed individual difference
measures, unrelated to the present hypotheses. The results of one of these measures, an 18 item
Need for Cognition Scale, are reported in Experiment 3 of Newman, Jalbert, Schwarz, and Ly
(2020) as a reanalysis of this existing data set. Finally, participants answered demographic
questions, including gender and age.
Results
We performed a 2 (warning: before exposure vs. no warning) x 2 (repetition: trivia claim
repeated vs. new) mixed model ANOVA. All reported means are estimated marginal means; the
raw means show the same pattern and are included in the supplemental materials. Replicating the
standard truth effect, repeated claims were rated as more true (M = 4.10, 95% CI [4.02, 4.19])
than new claims (M = 3.51, 95% CI [3.46, 3.57]), mean difference = 0.59 (95% CI [0.51, 0.67]),

14
F (1, 218) = 192.62, p < .001, partial eta
2
= .47, for the main effect. More important, participants
who received a warning prior to exposure rated claims as less true (M = 3.66, 95% CI [3.57,
3.74]) than participants who did not receive a warning (M = 3.96, 95% CI [3.88, 4.05]), mean
difference = 0.30 (95% CI [0.18, 0.42]), F (1, 218) = 24.58, p < .001, partial eta
2
= .10, for the
main effect. These main effects are qualified by an interaction of warning and repetition, F (1,
218) = 26.88, p < .001, partial eta
2
= .11.
To diagnose this interaction, we computed simple effects using a Bonferroni correction
for multiple comparisons. For this analysis and later analyses using a Bonferroni correction, we
report a p-value adjusted for these multiple comparisons that can be compared to the standard
alpha level of .05. Repeated measures d effect sizes were calculated using Comprehensive Meta-
Analysis Software (Version 3.0) from mean differences and standard deviations of the
differences, taking into account the correlation between repeated and new claims and corrected
for small sample size. This analysis revealed significant truth effects in both conditions (Figure
1.1). However, the truth effect was considerably larger without a pre-exposure warning, F (1,
218) = 186.80, p < .001, partial eta
2
= .46, d = 1.31 (95% CI [1.02, 1.60]), than with a pre-
exposure warning, F (1, 218) = 36.79, p < .001, partial eta
2
= .14, d = 0.70 (95% CI [0.48, 0.91]).
The difference is driven by participants’ truth ratings of repeated claims, which are higher in the
absence of a warning (M = 4.37, 95% [4.24, 4.49]) than after a pre-exposure warning (M = 3.84,
95% CI [3.72, 3.97]), mean difference = 0.52 (95% CI [0.35, 0.70]), F (1, 218) = 33.69, p < .001,
partial eta
2
= .13. Participants’ truth judgments for new statements did not differ across
conditions, F (1, 218) = 2.33, p = .128, partial eta
2
= .01.
The applied importance of these findings is more apparent when one considers how
frequently repetition of a claim can shift people’s judgments from false to true. We can assess

15
this by analyzing how many claims are rated on the “false” vs. “true” side of our six point scale.
Recall that the claims were normed to be judged true about half of the time. Consistent with this
norming, participants rated new claims to be true about half the time, independent of whether
they received no warning (M = 51.18%, SD = 14.50%) or a pre-exposure warning (M = 51.28%,
SD = 15.14%). For repeated claims, acceptance as true increased to 70.11% (SD = 16.83%)
without a warning but only to 60.23% (SD = 16.77%) with a pre-exposure warning. This reflects
a robust illusory truth effect of almost 20 percentage points without a warning that is cut in half
with a pre-exposure warning.
In sum, replicating earlier studies, prior exposure to a statement increased its perception
as true, even three to six days later. However, alerting participants at the time of exposure that
some of the statements they are about to see are false was sufficient to significantly reduce the
size of this truth effect. Pre-exposure warnings did not shift participants’ ratings of new claims-
rather, the reduction in the size of the truth effect was driven by reducing the perceived truth of
the repeated claims. A signal detection analysis of response bias (c) parallels these findings
across all experiments. These findings are reported in our supplemental materials.
Experiment 1.2
In the real world, people are rarely alerted to the presence of falsehoods before they are
exposed to them. However, it is often possible to alert people to falsehoods after exposure.
Empirically, post-exposure warnings are usually less effective in correcting the influence of
misinformation than pre-exposure warnings (for a review, see Lewandowsky et al., 2012).
Experiment 1.2 tests whether this holds as well for the influence of repetition. Truth effect
experiments often include information prior to test that some or half of the claims are false (i.e.,
Begg et al., 1992; Brashier et al., 2020; Nadarevic & Erdfelder, 2014; Schwartz, 1982; Silva et

16
al., 2016). In Experiment 1.2 (preregistered at http://aspredicted.org/blind.php?x=8yz2q5), we
tested the influence of warnings at the time of test using three conditions: a pre-exposure and
pre-test warning condition, a pre-test warning only condition, and a no warning condition. We
expected that a pre-test warning alone would have little effect for two reasons. First, if
participants are only warned prior to test, it will be difficult to correct for claims that were
already encoded as true during the initial exposure. Second, making a truth rating at test is
already drawing attention to truth independent of the warning, so an additional warning that
some claims are false will provide little new information. These predictions are consistent with
findings by Nadarevic and Aßfalg (2017) that extensive, but not simple, pre-test warnings may
reduce the size of the truth effect.
Method
Design. We used a 3 (warning timing: before exposure and before test, only before test,
or no warning) x 2 (repetition: trivia claim repeated vs. new) mixed design, manipulating
warning timing between subjects and repetition within subjects.
Participants. We aimed to recruit 300 Mechanical Turk (MTurk) workers, located in the
United States, with a HIT approval rate of at least 95% to complete the experiment using the
online survey platform Qualtrics. We again chose to overpower our study and aimed to recruit
100 participants for each of the three between-subjects conditions. Participants were told the
experiment would take approximately 30 - 45 minutes and were paid $1.20.
A total of 297 participants completed the study. The actual number of participants varies
slightly from the posted MTurk HITs because of interactions between Qualtrics and MTurk
procedures. However, due to an error in recruitment, 15 participants had taken a past truth effect
survey with the same materials, and these participants were excluded, resulting in a remaining

17
sample of 282 participants (127 male; Mage = 37.18, SD = 12.13; n = 96 in the pre-exposure and
pre-test warning condition, n = 97 in the pre-test warning only condition, n = 89 in the no
warning condition).
Procedure. The procedure was similar to the procedure of Experiment 1.1, except that all
parts took place in one experimental session.
Exposure Phase. Participants were told that they would see a series of trivia claims for
approximately three minutes. Participants in the warning before exposure and before test
condition were told that “Half of these trivia statements are true, and half of these trivia
statements are false.” Participants in the other conditions were not given this warning. After
exposure, participants were not asked any general questions, but instead moved immediately to
the delay phase.
Delay Phase. A twenty-minute delay followed the initial exposure. During that time,
participants answered multiple-choice questions about articles unrelated to the trivia claims.
Test Phase. The test phase was identical to the test phase of Experiment 1.1, except for
the introduction of a warning prior to test for some participants. All participants were correctly
told that half of the statements were ones that they had seen before and half of the statements
were new. Following this information, participants in the warning before exposure and before
test condition and the warning before test only conditions were given a pre-test warning that half
of the statements were true and half of the statements were false. Participants in the no warning
condition did not receive this warning.
Demographics. Finally, participants answered demographic questions.
Results

18
We performed a 3 (warning timing: before exposure and before test, only before test, or
no warning) x 2 (repetition: trivia claim repeated vs. new) mixed model ANOVA. Replicating
the standard truth effect, participants rated repeated claims (M = 4.56, 95% CI [4.46, 4.66]) as
more true than new claims (M = 3.48, 95% CI [3.41, 3.54]), mean difference = 1.09 (95% CI
[0.97, 1.20]), F (1, 279) = 327.93, p < .001, partial eta
2
= .54, for the main effect of repetition.
Moreover, a main effect of warning, F (2, 279) = 11.92, p < .001, partial eta
2
= .08, reflected that
participants who received a warning prior to exposure and prior to test found the statements less
true (M = 3.81, 95% CI [3.70, 3.91]), whereas those who only received a warning prior to test (M
= 4.15, 95% CI [4.05, 4.26]) reported similar truth judgments as participants who received no
warning (M = 4.10, 95% CI [3.99, 4.21]). However, these main effects were qualified by an
interaction of warning and repetition, F (2, 279) = 29.39, p < .001, partial eta
2
= .17.
We followed up the interaction with simple effects analyses using a Bonferroni correction
for multiple comparisons. As shown in Figure 1.2, and replicating the findings of Experiment
1.1, the interaction was driven by a change in truth ratings for repeated claims. Repeated claims
received significantly higher truth ratings when participants received no warning or a pre-test
only warning than when they were warned before exposure (both p < .001). The truth ratings for
repeated claims in the no warning and pre-test warning only conditions did not differ
significantly (p = 1.00). Finally, participants’ truth ratings of new claims were unaffected by
warnings, F (2, 279) = 2.44, p = .089, partial eta
2
= .02.
A comparison of new and repeated claims showed a significant truth effect in all three
conditions. More importantly, this effect was smaller when participants received a pre-exposure
and pre-test warning, F (1, 279) = 18.78, p < .001, partial eta
2
= .06, d = 0.72 (95% CI [0.45,
0.98]), than when they received only a pre-test warning, F (1, 279) = 206.35, p < .001, partial

19
eta
2
= .43, d = 1.85 (95% CI [1.37, 2.32]) or no warning at all, F (1, 279) = 159.01, p < .001,
partial eta
2
= .36, d = 1.70 (95% CI [1.24, 2.15]). In sum, warning participants prior to exposure
was critical in reducing the truth effect by more than half, from d > 1.70 to d = 0.72. Including
only a warning prior to test had no effect.
As noted in Experiment 1.1, the practical size of these effects is particularly apparent
when we consider the proportion of statements rated on the “true” vs. “false” side of our 6-point
rating scale. Across warning conditions, participants rated similar proportions of new claims as
true (no warning: M = 47.85, SD = 18.01%, pre-test warning only: M = 45.93%, SD = 20.75,
pre-exposure and pre-test warning: M = 52.86%, SD = 17.52%). These proportions increased for
repeated statements, reflecting sizable illusory truth effects. Without any warning, participants
accepted 78.46% (SD = 19.86%) of the statements as true and a pre-test only warning did not
affect this proportion (80.41%; SD = 17.27%). In contrast, the combination of a pre-exposure and
pretest warning reduced the proportion to 65.09% (SD = 17.84), again cutting the size of the
illusory truth effect by about half.
Experiment 1.3
The experimental literature has used two main variations of instructional warnings. In
some studies, participants are given information about the specific proportion of true and false
claims, usually that “half” of the statements are false (e.g., Begg et al., 1992; Garcia-Marques et
al., 2015; Silva et al., 2016). In other studies, participants are merely alerted that “some”
statements are false (Brown & Nix, 1996: Brashier et al., 2020, Schwartz; 1982) or that
statements could be true or false (e.g., Gigerenzer, 1984; Hasher et al., 1977; Mutter et al., 1977)
without any rate information. In Experiment 1.3 (preregistered at:
https://aspredicted.org/ir6fa.pdf) we explored whether these variations make a difference by

20
comparing both types of warnings (“half” vs. “some”) when administered only prior to test or
prior to exposure and prior to test.
Method
Design. We used a 2 (warning timing: before test vs. before exposure and before test) x 2
(warning content: “half” vs. “some”) x 2 (repetition: trivia claim repeated vs. new) mixed design,
manipulating warning timing and warning content between subjects and repetition within
subjects.
Participants. As in the previous experiments, we recruited 100 participants for each of
four between-subjects conditions from MTurk. Participants were told the experiment would take
approximately 30 - 45 minutes and were paid $1.20. In total, 405 participants completed the
study (154 male; Mage = 37.48, SD = 11.55). One participant was excluded because they reported
their age to be less than 18 years old. This left 206 participants in the “some” warning condition
(n = 106 in the pre-test warning only condition; n = 100 in pre-exposure and pre-test warning
condition) and 198 participants in the “half” warning condition (n = 97 in pre-test warning only;
n = 101 in pre-exposure and pre-test warning).
Procedure. This study was an exact replication of Experiment 1.2, with two exceptions.
First, we only included two warning conditions, namely a warning prior to exposure and test vs.
a warning prior to test only. Second, we added a variation in the specific content of the warning,
with half of participants receiving the warning that half of the claims true and half of the claims
were false and the remaining participants receiving the warning that some of the claims were true
and some of the claims were false.
Results

21
We performed a 2 (warning timing: before test vs. before exposure and before test) x 2
warning content: “half” or “some”) x 2 (repetition: trivia claim repeated vs. new) mixed model
ANOVA. Whether participants were told that “half” or “some” of the claims were false made no
difference, with F (1, 400) = 0.01, p = .933, partial eta
2
< .01 for the main effect, F (1, 400) =
0.01, p = .935, partial eta
2
< .01 for the interaction with warning timing, F (1, 400) = 1.32, p
= .251, partial eta
2
< .01 for the interaction with claim repetition, and F (1, 400) = 0.03, p = .611,
partial eta
2
< .01 for the three-way interaction. Thus, this variable is not further discussed.
Replicating the illusory truth effect, participants rated repeated claims (M = 4.29, 95%
CI [4.20, 4.37]) as significantly more true than new claims (M = 3.50, 95% CI [3.45, 3.55]),
mean difference = 0.79, (95% CI [0.71, 0.88]), F (1, 400) = 335.25, p < .001, partial eta
2
= 0.46,
for the main effect of repetition. As in Experiment 1.2, participants who were warned prior to
exposure and prior to test rated claims as less true (M = 3.70, 95% CI [3.63, 3.78]) than
participants who were warned prior to test only (M = 4.08, 95% CI [4.00, 4.16]), mean difference
= 0.38 (95% CI [0.27, 0.48]), F (1, 400) = 46.88, p <.001, partial eta
2
= .11, for the main effect
of warning time. These main effects were again qualified by a significant interaction between
warning timing and claim repetition, F (1, 400) = 88.99, p < .001, partial eta
2
= .18.
As shown in Figure 1.3, simple effects analyses using a Bonferroni correction for
multiple comparisons revealed a significant truth effect when a warning was presented only prior
to test, F (1, 400) = 39.24, p < .001, partial eta
2
= .09, d = 1.47 (95% CI [1.23, 1.70]), and when
a warning was presented prior to exposure and repeated prior to test, F (1, 400) = 386.38, p
< .001, partial eta
2
= .49, d = 0.64 (95% CI [0.45, 0.84]). As in Experiment 1.2, the truth effect
was significantly smaller in the latter condition. This difference was again driven by how
participants rated repeated claims: these claims were judged as less true when participants

22
received a warning prior to exposure and prior to test (M = 3.90, 95% [3.78, 4.01]) than when
they received a warning only prior to test (M = 4.68, 95% [4.56, 4.80]), mean difference = 0.78
(95% CI [0.62, 0.95]), F (1, 400) = 85.94, p < .001, partial eta
2
= .18. Participants’ ratings of
new claims were unaffected by the warnings, F (1, 400) = 0.42, p = .517, partial eta
2
< .01.
To assess the practical size of these effects, we again consider the proportion of claims
rated on the “true” vs. “false side of the rating scale. Consistent with the norming of the
ambiguous claims, participants accepted new claims as true about half the time across
conditions (pre-test warning only: M = 48.91%, SD = 18.20%; pre-exposure and pre-test
warning: M = 50.25%, SD = 15.48%). For repeated claims, acceptance as true increased to
75.86% (SD = 21.19%) in the pre-test warning only condition, while adding a pre-exposure
warning reduced the proportion to 60.97% (SD = 18.14%).
In sum, these findings are consistent with Experiments 1.1 and 1.2. Warning participants
about the presence of falsehoods prior to exposure reduced the size of the truth effect by more
than half, even when all participants were given a warning prior to test. There was no difference
between a warning that “some” of the claims were false and a warning that “half” of claims were
false.
Effect Size Analyses
Figure 1.4 shows a forest plot of all effect size estimates for each warning timing and
warning type condition. Analysis was performed using Comprehensive Meta-Analysis Software
(Version 3.0). Due to the small number of studies, tau-squared was pooled across studies,
following recommendations by Borenstein, Hedges, Higgins, and Rothstein (2009). A random
effects model was used and effect sizes were fixed across subgroups. Effect sizes were corrected
for small sample biases (Borenstein et al., 2009). The effects were grouped into three subgroups:

23
conditions where no warnings were given, conditions where warnings were only given at the
time of test, and conditions where warnings were given at the time of exposure (both with and
without repetition of the warning at the time of test). Each effect fit into exactly one of these
three subgroups, so no effects were double-counted.
The total effect size across all conditions was d = 1.00, 95% CI [0.90, 1.10]. There was
evidence of a significant difference among warning conditions, Q (2) = 58.61, p < .001. Follow-
up analyses using a Bonferroni correction for multiple comparisons confirmed that the truth
effect was significantly smaller in the pre-exposure warning condition (d = 0.68, 95% CI [0.55,
0.81]) than in both the pre-test warning only condition (d = 1.55, 95% CI [1.33, 1.76]) and the no
warning condition (d = 1.42, 95% CI [1.18, 1.67]); both Q (1) > 28, p < .001. The pre-test
warning only and no warning conditions were not significantly different, Q (1) = 0.27, p = 1.000.
Additional Analyses
What accounts for the robust observation that pre-exposure warnings reliably reduce the
size of the truth effect? One possibility is that pre-exposure warnings increase participants’
ability to accurately discriminate between true and false repeated claims at test. To test this
possibility, we performed a signal detection analysis (Stanislaw & Todorov, 1999) using
discrimination (d’) to investigate whether participants who received pre-exposure warnings were
more accurate at discriminating between true and false claims. Following earlier research (e.g.,
Begg et al., 1992; Garcia-Marques et al., 2016; Mitchell et al., 2006), we converted the
unnumbered six-point scale used in the experiments (ranging from “definitely true”, coded as 6,
to “definitely false”, coded as 1) to a binary measure, with values from 1 to 3 treated as “false”
and values from 4 to 6 treated as “true”. Across all three studies, there was no consistent
influence of warning timing on participants’ ability to discriminate between true and false

24
claims. In Experiments 1.1 and 1.2, there was no significant main effect of warning timing;
Experiment 1.1: F (1, 218) = 2.64, p = .105, partial eta
2
= .01; Experiment 1.2: F (2, 279) = 0.26,
p = .774, partial eta
2
< .01. Additionally, neither experiment had a significant interaction of
warning timing and repetition, both Fs < 0.99, ps > .373. In Experiment 1.3, no main effect of
warning timing emerged, F (1, 400) = 0.04, p = .850, partial eta
2
< .01, but one significant
interaction with warnings did: the three way interaction of repetition, warning timing, and
warning content, F (1, 400) = 5.60, p = .018, partial eta
2
= .01. However, simple effects analysis
using Bonferroni correction for multiple comparisons revealed that pre-exposure warnings did
not significantly increase overall accuracy in either the condition using a “some” warning or the
condition using a “half” warning (both Fs < 0.84, ps > .512), nor did they significantly increase
accuracy for any specific claim type (new or repeated) within those conditions. In fact, the only
single significant effect when looking at new and repeated claims alone was in the opposite
direction, with pre-exposure warnings decreasing accuracy for repeated claims in the “half”
warning condition relative to a pre-test warning only condition (pre-test warning only M = 0.22,
95% CI [0.13, 0.33], pre-test and pre-exposure warning M = 0.07, 95% CI [-0.03, 0.17]; raw
mean difference = -0.15, 95% CI [-0.29, 0.00], F (1, 400) = 3.96, p = .047, partial eta
2
= .01; all
Fs < 1.91, ps > .170 in other conditions). In short, we found no evidence that pre-exposure
warnings reduce the size of the truth effect by improving participant’s ability to accurately
discriminate between true and false claims.
Another possibility is that warnings at exposure allow participants to catch
inconsistencies in false claims that they may otherwise not notice, protecting participants from
accepting the claim at test. This would be consistent with Brashier and colleagues’ (2020)
finding that asking participants to fact check information at exposure reduces the size of the truth

25
effect for false claims, provided they have the relevant knowledge to draw on. If so, only
factually false claims should show a smaller truth effect in the pre-exposure warning conditions.
This prediction entails a three-way interaction of actual truth value of the claim, repetition, and
warning.
To test this possibility, we ran additional analyses with the actual truth value of the
claims added as a within-subjects factor. Despite norming that aimed to equalize the perceived
truth of true and false claims, we found a main effect of actual truth value in each experiment.
Participants consistently rated true claims as more true than false claims (Experiment 1.1: F (1,
218) = 72.13, p < .001, partial eta
2
= .25; Experiment 1.2: F (1, 279) = 51.83, p < .001, partial
eta
2
= .16; Experiment 1.3: F (1, 400) = 51.65, p < .001, partial eta
2
= .11), although this effect
was relatively small (raw mean difference on a six point scale: Experiment 1.1: 0.26, 95% CI
[0.20, 0.32]); Experiment 1.2: 0.21, 95% CI [0.15, 0.27]; Experiment 1.3: 0.18, 95% CI [0.13,
0.23]). More importantly, the three-way interaction of truth value, warning timing, and repetition
was F < 1 in each of the experiments (Experiment 1.1: F (1, 400) = 0.09, p = .771, partial eta
2

< .01; Experiment 1.2: F (2, 279) = 0.77, p = .464, partial eta
2
< .01; Experiment 1.3: F (1, 218)
= 0.15, p = .703, partial eta
2
< .01). The consistent lack of three-way interactions indicates that
the impact of warning timing on the size of the truth effect was not moderated by the actual truth
value of the claims. See the supplemental materials for a detailed report of this analysis.
Discussion
Across three experiments, a remarkably consistent pattern emerged: pre-exposure
warnings that alerted participants that some of the claims they were about to see would be false
significantly reduced the size of the truth effect compared to all other conditions. In contrast,
warnings given only prior to test exerted no influence and failed to reduce the truth effect

26
compared to a condition without any warning – likely because asking participants to rate truth at
test already draws attention to the truth value of the claim. The protective effect of pre-exposure
warnings was observed both when people were told that “half” or “some” of the statements were
false. Given that warnings at exposure are a common feature of truth effect studies, this robust
finding implies that the bulk of this literature underestimates the influence of repetition under
conditions in which falsehoods do not come with a warning label.
Based on a meta-analysis of seventy effect sizes, Dechêne et al. (2010) reported an
average between-items truth effect size of d = 0.50 (95% CI [0.43, 0.57]). The confidence
interval of their estimate overlaps with the confidence interval of the effect sizes of all conditions
that included a pre-exposure warning in the present experiments (d = 0.68; 95% CI [0.55, 0.81]).
This is consistent with the observation that most prior truth effect studies warned participants
about truth at initial exposure, either by asking participants to rate the truth of each claim (51 out
of 70 effect sizes included in Dechêne et al., 2010) or by explicitly informing them that some of
the claims they will see are false. However, the present three experiments converge on much
higher effect size estimates when participants received no warning at all, d = 1.55, 95% CI [1.33,
1.76] or were only warned prior to test, d = 1.42, 95% CI [1.18, 1.67]. These effect sizes are two
to three times the size otherwise reported, suggesting that the experimental procedures
commonly used in truth effect studies are likely to underestimate the impact of message
repetition on later judgments of truth under natural conditions.
While results strongly support this conclusion of applied relevance, they also allow us to
consider possible underlying mechanisms. One is that alerting people prior to exposure that not
all of the statements are true makes them more careful at test - a criterion shift. If so, one would
expect participants to be less likely to rate any claim as true at test. Our results make this

27
unlikely: pre-exposure warnings influenced participants’ responses to repeated claims, but not
new claims. If warnings made people more careful overall, we should have seen a reduction in
true responses for both new and repeated claims. Instead, only repeated claims were rated less
true after pre-exposure warnings. Signal detection analyses with response bias (c) align with
these findings. Moreover, an identical warning given only immediately before test had no
influence. Another possibility is that pre-exposure warnings allow participants to identify false
claims during the exposure phase, which they would otherwise not have noticed. When these
false claims are seen again at test, they may be more likely to be correctly identified as false. If
so, pre-exposure warnings should protect participants from believing factually false claims, but
should do little to reduce belief in factually true claims. Our results do not support this account
either - the influence of warnings on the size of the truth effect was not modified by the actual
truth value of claims. Additionally, warnings had no influence on participant’s ability to
accurately discriminate between factually true and factually false claims at test.
An additional possibility is that participants use the recollection that they saw the claim
during the exposure phase in evaluating the credibility of the source: when they were warned that
some of the presented claims are false the source is less credible than without such a warning.
Supporting this possibility, several studies found that recollection can reduce acceptance of a
claim under such conditions (e.g., Begg et al., 1992; Brown & Nix, 1996; Unkelbach & Stahl,
2009), although this is not always the case (Henkel & Mattson, 2011). Because recollection
becomes less likely as time passes, this account predicts that a pre-exposure warning should be
more effective when the delay between exposure and test is short. In contrast, we observed a
similar influence of pre-exposure warnings for delays of 20 minutes (Experiments 1.2 and 1.3)
and delays of 3 to 5 days (Experiment 1.1), which renders this account less likely.

28
Instead, we propose that variables that alert participants to the potential presence of
falsehoods at the time of exposure are effective because they disrupt the tacit assumptions
underlying communication in daily life. As observed in many studies of conversational
pragmatics, people generally assume that communicated information is truthful, unless
contextual cues or other knowledge indicate that the communicator may not be cooperative
(Grice, 1975; Sperber & Wilson, 1986; for reviews, see Schwarz, 1994, 1996). When contextual
cues elicit distrust, recipients consider how things might differ from what is claimed (for a
review, see Mayo, 2015), resulting in a higher accessibility of incongruent associations (Schul,
Mayo, & Burnstein, 2004) and more counterfactuals and alternative accounts (Kleiman, Sher,
Elster, & Mayo, 2015; Schul, 1993). For example, people who are warned that information may
be false prior to reading the false claim “Biking is the first event in a triathlon” may be more
likely to think about whether people actually start a triathlon by running or swimming. When
later assessing the claim’s truth, these contradictory possibilities would more easily come to
mind as plausible alternatives, reducing the impact of repetition on truth.
This possibility is consistent with Unkelbach and Rom’s (2017) observation that bringing
associations to mind that are incongruent with a given claim attenuates the otherwise observed
truth effect, which may reflect an influence of the accessible declarative information (Brashier &
Marsh, 2020; Unkelbach et al., 2019) and/or the reduced fluency experienced when processing
contradictory information (Winkielman et al., 2012). Paralleling these observations, distrust at
the time of encoding has also been found to protect people against the continued influence of
misinformation after it is retracted (Fein et al., 1997; Lewandowsky et al., 2005, 2012). From
this perspective, any manipulation that fosters distrustful elaboration at encoding may counteract
the influence of repetition-based familiarity.

29
Finally, a methodological point is worth noting. How people process information they
encounter in an experiment depends on what they consider their task to be. As discussed in the
introduction, most illusory truth experiments draw attention to the truth value of the claims at an
early stage, either through instructional warnings or early requests to evaluate the truth of the
claim. As seen, such tasks can decrease the size of illusory truth effects. Other processing tasks,
like rating how interesting or easy to understand a statement is, are likely to draw attention away
from truth. This may increase the size of illusory truth effects when they prompt detailed
encoding of the statement without attention to its veracity, thus facilitating more fluent
processing at test. Examining the impact of different initial exposure conditions on the size of the
illusory truth effect provides a fruitful area for future research with important theoretical and
applied implications.
Applied implications
The present findings indicate that the experimental literature on illusory truth effects has
most likely underestimated the truth-creating power of repetition in everyday life. This is the
case because widely used experimental procedures alert participants that some of the claims are
false. In our experiments, the impact of repetition was two to three times larger when these pre-
exposure warnings were removed. This is consistent with the finding that warnings can provide
protection against the acceptance of misinformation in different domains (Lewandowsky et al.,
2012). Given that false information rarely comes with warning labels in the real world, the latter
effect size estimates are probably closer to what may be observed under natural conditions,
provided that the communicator is not perceived as untrustworthy. Additionally, truth effect
experiments are typically limited to a single repetition, as were the present studies. In contrast,

30
social media and the 24-hour cable news cycle ensure a much larger number of repetitions,
which may further enhance the size of truth effects (cf., Hasher et al., 1977).
On a more optimistic note, our findings suggest that simple reminders that not all
information is true can protect people from believing false information when they encounter it
again. Including such reminders in contexts where false information is likely to be present, such
as at the top of social media feeds or articles that have not been fact checked, may provide an
opportunity to curb later belief in false information in contexts where more extensive
interventions may be impossible.
As this discussion indicates, much remains to be learned about the applied implications of
the robust illusory truth effects documented in dozens of laboratory studies since Hasher and
colleagues’ (1977) pioneering work. Hopefully, future research that more closely mirrors how
people encounter information in daily life will fill these gaps, providing a fuller understanding of
the role of repetition in the creation and maintenance of beliefs.

31
Chapter II: Individual differences in elaborative processing and the Illusory Truth Effect:
What helps now hurts later?
2

When considering the validity of a claim, people may draw on general knowledge or
other external sources to decide whether it is true. In addition to this declarative knowledge,
people also rely on how easy it is to process a claim or idea to establish whether it is true (Fazio,
Brashier, Payne, & Marsh, 2015; Unkelbach & Greifeneder, 2018). When information feels easy
to process, people are more likely to believe it, especially in the absence of more probative
information (for reviews, see Schwarz, 2015; Schwarz & Jalbert, 2020). Across a wide variety of
studies, manipulations that increase the ease of perceiving, understanding, or recalling an idea --
such as repetition, the addition of photographs, changes in color contrast, and semantic primes—
bias people to believe information is truth (Cardwell, Henkel, Garry, Newman, & Foster, 2016;
Hansen & Wänke, 2010; Jalbert, Newman, & Schwarz, 2020; Newman, Garry, Bernstein,
Kantner, & Lindsay, 2012; Newman, Jalbert, & Schwarz, 2020; Reber & Schwarz, 1999).
Indeed, fluency due to incidental variables increases belief in information even in the
presence of more informative declarative inputs such as general knowledge or available source
information (Brashier, Umanath, Cabeza, & Marsh, 2017; Fazio et al., 2015; Unkelbach &
Greifeneder, 2018). Both contextual variables and individual differences in processing styles
may influence relative reliance on declarative and experiential information. For instance, when
people judge claims for which they have relevant knowledge (e.g., “The White House is in
Washington, DC”) the influence of incidental fluency manipulations is diminished (Newman et

2
This chapter is based on:
Experiment 3 and 4 from: Newman, E. J., Jalbert, M., Schwarz, N., & Ly, D. (2020). Need for
Cognition: Individual differences in truthiness and illusory truth. Consciousness & Cognition,
78, 102866. https://doi.org/10.1016/j.concog.2019.102866

32
al., 2012; Parks & Toth, 2006; Unkelbach, 2007). People are also less likely to rely on
experiential information when the judgment is important to them and when they have the time
and motivation to search for, and elaborate on, declarative inputs (for reviews, see Greifeneder,
Bless, & Pham, 2011; Greifeneder & Schwarz, 2014). These observations parallel lessons from
decades of persuasion research into the conditions that foster thoughtful processing of a
persuasive message (for a review, see Wegener, Clark, & Petty, 2019). Persuasion research has
also identified individual differences that influence the extent to which message recipients think
about the content of a message or rely on heuristic cues, such as the communicator’s status or
affiliation, to evaluate the arguments (for a review, see Briñol & Petty, 2019). One of the most
impactful of these variables is Cacioppo and Petty’s (1982) Need for Cognition (NFC), a
measure of an individual’s tendency to spontaneously engage in elaborative processing, which
we will return to later.
Because elaboration on declarative inputs may reduce reliance on incidental influences of
fluency such as repetition or print font, it may be tempting to believe that interventions aimed at
increasing elaborative thought would be effective in protecting people from fluency-based biases
in truth judgments. Indeed, strategies aimed at promoting better decision-making and preventing
the spread of misinformation often ask people to slow down and think more carefully about what
they’re reading. For example, current tips by the News Literacy Project include waiting twenty
seconds before sharing information and thinking hard as a way to spot conspiracy theories (News
Literacy Project, 2021). Research also supports that slowing down and deliberating more can be
a successful strategy when evaluating the truth of information. For example, encouraging a
careful and accurate analysis or explicitly warning people about the influence of repetition on
judgments of truth at the time of judgment can reduce the impact of fluency (e.g., Garcia-

33
Marques, Silva, & Mello, 2016; Nadarevic & Aßfalg, 2017). This processing may also help
people more accurately discriminate between true and false information. For example,
participants who were given more time to make their assessment were less likely to believe fake
(but not true) headlines (Bago, Rand, & Pennycook, 2020), and asking participants to pause and
consider whether information is true or false before sharing on social media decreased the
sharing false - but not true - headlines (Fazio, 2020).
Role of elaboration in truth judgments
This work suggests that encouraging elaboration may protect people from the illusory
truth effect – the finding that the mere repetition of information can systematically bias people to
believe that information is true (Bacon, 1979; Begg, Anas, & Farinacci, 1992; Hasher, Goldstein,
& Toppino, 1977; for a review see Dechêne, Stahl, Hansen, & Wänke, 2010). In a typical
illusory truth effect study, people see some claims at time 1, the exposure phase. After a delay
(ranging from minutes to weeks), at time 2, the test phase, people assess the truth of another
series of claims. Some of these claims they have already seen at time 1, and some are new.
The key finding, first reported by Hasher et al. (1977), is that people are biased to rate old
claims as true, compared to new claims they have never seen before. A growing literature shows
that this repetition-based illusory truth effect is robust, holding across a variety of domains and
despite having general knowledge about a claim, and occurring even when other more probative
information is available (for a meta-analysis, see Dechêne et al., 2010). Repetition is thought to
increase truth via an increase in processing fluency, consistent with the observation that many
other variables that increase fluency also increase truth (Reber & Schwarz, 1999; for a review,
see Schwarz, 2015). Indeed, there is work that suggests that encouraging a careful and accurate
analysis or explicitly warning people about the influence of repetition on judgments of truth at

34
the time of judgment can reduce the size of the illusory truth effect (e.g., Garcia-Marques et al.,
2016; Nadarevic & Aßfalg, 2017). However, the role of elaborative processing more broadly –
not just at the time of judgment – is less clear.
Additionally, studies often ask participants to consider information in the context of
making judgments of truth. For example, participants in truth effect studies are typically warned
that they will be seeing false information and/or are explicitly asked to consider whether or not
information is false. However, in the real world, people are rarely alerted before they are exposed
to false information. Considering whether or not elaboration is occurring in the context of
considering information truth is important, as the presence of these warnings at the time of
exposure has been shown to reduce the susceptibility to the truth effect (Jalbert et al., 2020;
Nadarevic & Aßfalg, 2017). Thus, the impact of elaboration on truth may depend on whether or
not people are considering that information may be false.
In our studies, we investigate the impact of individual differences in elaborative
processing on susceptibility to the truth effect both when warnings of falsehoods are and are not
present at exposure. We use NFC as our measure of elaborative processing, as reviewed below.
Need for Cognition
Cacioppo and Petty’s (1982) Need for Cognition (NFC) scale measures how much people
enjoy thinking and engage in it. Example items are, “I prefer my life to be filled with puzzles that
I must solve” and “I like to have the responsibility of handling a situation that requires a lot of
thinking.” Those who score high on NFC are more likely to consider the quality of an argument
and the consistency of the evidence presented, and are therefore persuaded by strong arguments
more than weak arguments (for reviews, see Briñol & Petty, 2019; Cacioppo, Petty, Feinstein, &
Jarvis, 1996). In contrast, those who score low on NFC attend less to the substance of the

35
arguments and are often equally persuaded by strong and weak arguments. Moreover, those low
on NFC are more likely to be influenced by attributes of a message that are not diagnostic of its
accuracy but make its content easy to process, such as anecdotes, heuristically useful cues (e.g., a
message with more arguments is better), easy to read fonts, and semantic primes (e.g., Bornstein,
2004; Cho & Schwarz, 2006; Petty, DeMarree, Briñol, Horcajo, & Strathman, 2008). These
observations suggest that those high on NFC may also be less susceptible to the biasing effects of
incidental fluency in assessments of truth.
NFC and illusory truth
Assuming that those who are high on NFC draw more on the content of the message and
less on accompanying experiential inputs, those individuals may be less sensitive to feelings of
fluency when they judge truth at time 2. If this is the case, we would expect individuals who are
high in NFC to be less influenced by repetition when judging truth. But it is also possible that
being high on NFC backfires due to the influence of high NFC on the encoding
of claims at time 1. Research shows that those who score high on NFC elaborate more on the
content of a message and have better recall for its details than those who score low on NFC
(Cacioppo, Petty, & Morris, 1983; LaTour, LaTour, & Brainerd, 2014; Wootan & Leding, 2015).
This may protect high NFC individuals from being influenced by experiences of incidental
fluency on immediate tests. But in the illusory truth effect paradigm, engaging in elaboration at
time 1 may result in higher fluency and familiarity when high NFC individuals encounter
previously seen statements at time 2 (see, for example, Unkelbach & Rom, 2017). There is some
evidence for this possibility in the false memory literature—those who are high on NFC are more
susceptible to illusory recognition due to increased semantic elaboration at encoding (Graham,
2007; LaTour et al., 2014; Leding, 2011; Wootan & Leding, 2015). In this case, we would expect

36
those who are high in NFC to be more likely to believe repeated information. Additionally, the
context in which elaboration occurs (e.g., with or without a warning that information may be
false) may moderate this effect.
In two experiments, we examine whether high NFC reduces or enhances the illusory truth
effect under conditions in which participants are warned or not warned about the presence of
falsehoods at the time of initial exposure. In Experiment 2.1, we used an existing dataset (Jalbert
et al., 2020) to examine whether high NFC protects people from the illusory truth effect via an
increase in elaboration at time 1. Participants first viewed a series of trivia claims (time 1). Half
of the participants were warned that some of the claims were false, while half of the participants
did not receive this warning. Following a delay of three to six days, they were asked to rate the
truth of another series of trivia claims, some of which they had seen at time 1 and some of which
were new. Finally, participants completed the NFC scale. Compared to participants who scored
low on NFC, those who scored high on NFC showed a larger illusory truth effect under
conditions in which they were not warned of falsehoods at exposure. Experiment 2.2 replicated
this no warning pattern, but the effect of NFC did not reach significance. Taken together we find
that when people are not warned they may be exposed to false information, NFC moderates
illusory truth, with a tendency to engage in elaborative processing increasing susceptibility to
illusory truth.
Experiment 2.1
Examining the influence of NFC on the truth effect, Experiment 2.1 is a reanalysis of an
existing dataset that allows us to explore the influence of NFC on the size of the illusory truth
effect. Here we consider the possibility that thinking more about the content of a claim at time 1
(being high on NFC) may ironically, make the claim easier to process after a delay, potentially

37
resulting in an increased illusory truth effect. We examine the influence of NFC on illusory truth
by reanalyzing a previously reported experiment (Jalbert et al., 2020; Exp. 1) with NFC as a
continuous variable. NFC was not part of the original report, which focused on the effect of
warnings. Next, we summarize the methods of Jalbert et al., 2020, Exp. 1) and describe the
inclusion of NFC as a factor in our analysis of susceptibility to the illusory truth effect. We focus
on methodological details and procedures that are most relevant for the present analysis. For a
full report please see Jalbert et al., 2020, Exp. 1).
Method
Participants. We exclude one participant included in the original Jalbert et al., 2020
report in our analysis because they did not complete the full NFC scale. Overall, 219 participants
(58 male; Mage = 20.51, SD = 2.64, one not reporting) completed both parts of the experiment: 54
in the first wave of data collection and 165 in the second wave. As described in Jalbert et al.,
2020, we collapsed our analysis across the two waves. There were 112 participants in the no
warning condition and 107 participants in the pre-exposure warning condition.
Materials. Ambiguous true and false trivia claims were selected on a variety of topics
(sports, geography, food, animals, and science) from a larger set of previously normed claims
(Jalbert, Newman, & Schwarz, 2019). During the initial exposure phase, participants were
presented with 36 of these trivia claims. Half of the trivia claims were true and half were false. In
the final test phase, participants saw these same 36 claims as well as 36 new claims (also half
true and half false), for a total of 72 claims. In each session, claims were presented in a random
order for five seconds each. The trivia claims were counterbalanced such that half of the
participants saw one set of 36 claims repeated, and half of the participants saw the other set of 36
claims repeated.

38
Procedure. When participants signed up for the study, they agreed to complete both parts
of a two-part online survey. In part 1 of the study, the exposure phase, participants simply read
36 trivia claims. In the pre-exposure warning condition, participants received the warning “half
the statements are true and half the statements are false” prior to reading the claims. In the no
warning condition, participants did not receive any warning. We included a few general
questions at the end of part 1 to provide a rationale for presenting the claims, including “How
many statements do you think you read?” and “How many minutes do you think it took you to
read the statements?”
After a three day delay, participants received a link to part 2 of the survey and were given
48 hours to complete it. In part 2 of the experiment, the test phase, participants were shown
another series of trivia claims. All participants were correctly told that half of the statements
were ones that they had seen before and half of the statements were new. None of the
participants were told anything about the truth of the claims. For each claim, all participants
answered the question “Is this statement true or false?” on an unnumbered six-point scale from
“definitively true” (coded as 6) to “definitely false” (coded as 1).
Individual differences. Following the truth ratings in part 2, participants completed the
18-item NFC scale. In the second wave of data collection, this NFC scale was followed with a
few additional individual difference measures for exploratory purposes. As described earlier,
NFC was always collected in position 1 and the primary individual difference measure.
Demographics. Finally, participants answered demographic questions, including gender
and age.
Results and discussion

39
As reported by Jalbert et al., 2020, people rated repeated claims as more true than new
claims, and this pattern was most pronounced in the no warning condition. Of interest is whether
high NFC participants show a larger illusory truth effect, or whether being high on NFC protects
people from this bias. Participants’ mean NFC score (Cronbach’s α = 0.891) was M = 7.97, SD =
11.87. As shown in Figure 2.1, our reanalysis reveals that being high on NFC led to a larger
illusory truth effect.
Statistical design. We reanalyzed these data using the full design from Jalbert et al.,
2020. Thus the design was a 2 (Warning: warning, no warning) x 2 (Claim type: repeated, new)
mixed model design and including NFC analyzed both as a continuous between-subjects
variable, and, in a separate analysis, as a categorical between-subjects variable (NFC: high, low).
Illusory truth effect and NFC. Our reanalysis with NFC as the added individual
difference variable showed a main effect of NFC on truth judgments, with increasing NFC
associated with an increase in truth ratings, F (1, 215) = 11.95, p = .001, partial eta
2
= 0.05.
There was also a significant interaction of NFC and repetition, F (1, 215) = 4.31, p = .039, partial
eta
2
= 0.02. When we conducted a further spotlight analysis to examine the interaction, we found
that the size of truth effect one SD above the mean of NFC was, F (1, 215) = 130.57, p < .001,
partial eta
2
= 0.38, raw mean difference = 0.68, 95% CI [0.57, 0.80], and one SD below the mean
was, F (1, 215) = 71.97, p < .001, partial eta
2
= 0.25, raw mean difference = 0.51, 95% CI [0.39,
0.63]. There was no significant interaction of warning and NFC, F (1, 215) = 0.17, p = .684,
partial eta
2
< 0.01, nor a significant three-way interaction of warning, NFC, and repetition, F (1,
215) = 1.47, p = .226, partial eta
2
= 0.01.
We also further investigated whether the influence of NFC on the size of the truth effect
held up in each warning condition when analyzed separately. Thus, we conducted a 2 (Claim

40
type: repeated, new) mixed model analyses adding NFC as a continuous variable in each warning
condition alone. In the no warning condition, a significant interaction remained, F (1, 110) =
4.32, p = .040, partial eta
2
= 0.04. However, the influence of NFC on the truth effect did not hold
up in the warning condition alone, F (1, 105) = 0.50, p = .481, partial eta
2
= 0.01. This indicates
that NFC has a more robust influence with no warning, mirroring our analysis with NFC as a
categorical variable and results of our mini-meta analysis.
We then replicated these analyses using a categorical median split NFC classification. In
order to examine the effects of high and low levels of NFC, we split our participants into “high”
and “low” NFC groups using a median split approach. A total of 10 participants had NFC scale
scores exactly the same as the median (Mdn = 7) and so were not included in the following
analysis. We performed a 2 (Warning: warning, no warning) x 2 (NFC: high, low) x 2 (Claim
type: repeated, new) mixed model ANOVA. Replicating Jalbert et al. (2020), there were
significant main effects of warning and claim type, with a significant interaction such that a
larger truth effect emerged in the no warning condition than in the warning condition.
Additionally, there was a main effect of NFC, F (1, 205) = 8.69, p = .004, partial eta
2
= 0.04,
with high NFC participants rating claims more true than low NFC participants. However, these
effects were modified by a three-way interaction of warning, NFC, and repetition, F (1, 204) =
4.78, p = .030, partial eta
2
= 0.02. We followed up this three-way interaction with simple effects
analysis corrected for multiple comparisons with a Bonferroni correction. As shown in Figure
2.1, there was the expected effect of NFC on the truth effect in the no warning condition, with
high NFC participants showing a larger truth effect, mean difference between repeated and new
claims = 1.04, 95% CI [0.87, 1.20] than for low NFC participants, mean difference between
repeated and new claims = 0.61, 95% CI [0.45, 0.78]. However, when given a warning, there was

41
no difference in the size of the truth effect between low and high NFC participants, high NFC
mean difference = 0.39, 95% CI [0.23, 0.56]), low NFC mean difference = 0.35, 95% CI [0.17,
0.52].
Taken together, our reanalysis of Experiment 3 of Jalbert et al., 2020 suggests that
susceptibility to the illusory truth effect does indeed vary across individuals; being high on NFC
ironically makes people more vulnerable to this cognitive bias. This is consistent with the
assumption that being high on NFC elicits more elaborative processing at time 1, which
increases the fluency with which previously seen claims can be processed at time 2. In
Experiment 2.2, we aim to replicate these findings.
Experiment 2.2
Method
Participants. Students from the University of Southern California psychology participant
pool completed the study for course credit. Jalbert et al., 2020 attempted to recruit up to 100
participants. Replicating Jalbert et al., we included all participants who had completed both parts
of the study, except for two participants who did not complete part two within the 48-hour
window after the email invitation. One additional participant was excluded because they
completed part 1 twice prior to part 2. Overall, 89 participants (28 male; Mage = 20.52, SD = 2.07,
one not reporting) completed both parts of the experiment and were included in the analysis.
Design. The design was a 2 (Claim type: repeated, new) condition repeated measures
design with NFC analyzed as a continuous between-subjects variable, and, in a separate analysis,
as a categorical between-subjects variable (NFC: high, low). We also had a between-subjects
variable, cultural fluency (high or low) intended to prime careful processing under conditions of
low cultural fluency, but, as discussed below, this manipulation had no effect on susceptibility to

42
the illusory truth effect and did not interact with other variables, so we collapsed across this
factor in our subsequent analyses.
Materials and procedure. The materials and procedure were an exact replication of the
no-warning condition of Experiment 2.1 with two exceptions: First, at the end of the test phase
(time 2), a 12 item Faith in Intuition scale was added to the NFC scale. Second, the order of these
scales was randomized. No additional individual difference measures were assessed.
Results and discussion
As in Experiment 2.1, we calculated the mean truth rating for repeated and new claims
and then calculated a NFC score for each participant (Cronbach’s α = 0.858; M = 6.45, SD =
10.74). As Figure 2.2 shows, we replicated the key patterns from Experiment 2.1: participant
were more likely to believe claims that were repeated, and this pattern appeared to be more
pronounced for high NFC participants. However, the moderating effect of NFC did not reach
significance.
Cultural fluency manipulation. A cultural fluency manipulation (adapted from Lin,
Arieli, & Oyserman, 2019; Exp. 4) was implemented prior to the initial exposure phase. The
purpose of this manipulation was to put people in a state of cultural disfluency, which should
alert them to pay attention to their environment, or cultural fluency, where they would assume all
was right with the world (Oyserman, 2011). Theoretically, the culturally fluent condition would
be analogous to be exposed to claims in a familiar environment, while the disfluent condition
would be analogous to being exposed to information in an unfamiliar environment. For this
purpose, participants were shown photos of a wedding that were either consistent with cultural
expectations (e.g., a bride in a white wedding dress, a white wedding cake) or inconsistent with
cultural expectations (e.g., a bride in a black wedding dress, a black wedding cake) and asked to

43
rate the quality of each photo (1 = extremely poor quality, 7 = extremely good quality). A 2
(Claim type: repeated, new) x 2 (Cultural fluency manipulation: fluent photos, disfluent photos)
mixed model ANOVA with NFC as a continuous variable and cultural fluency as a between
participants factor showed no influence of cultural fluency, with the main effect of cultural
fluency and all interactions having Fs < 0.841 and ps > 0.361. The same results were found when
NFC was included in this same analysis as a categorical, rather than continuous, variable, with
the main effect of cultural fluency and all interactions having Fs < 0.471 and ps > 0.494.
Because this manipulation had no effect on susceptibility to the illusory truth effect and did not
interact with other variables, we report the remaining analysis collapsed across this factor.
Illusory truth effect and NFC. In a 2 (Claim type: repeated, new) mixed model
ANOVA with NFC as a continuous variable, we once again replicated the classic illusory truth
effect, F (1, 87) = 59.95, p < .001, partial eta
2
= 0.41, with repeated claims rated more true (M =
4.18, SD = 0.66) than new claims (M = 3.44, SD = 0.39). Unlike Experiment 2.1, there was no
main effect of NFC on truth ratings, F (1, 87) = 0.43, p =.513, partial eta
2
= 0.01, and the
interaction of NFC and repetition did not reach significance, F (1, 87) = 0.97, p = .327, partial
eta
2
= 0.01.
We replicated these analyses using a categorical median split NFC classification. A total
of 5 participants had NFC scale scores exactly the same as the median (Mdn = 7), and so were
not included in the following analysis. We performed a 2 (NFC: high, low) x 2 (Claim type:
repeated, new) mixed model ANOVA. There was a significant illusory truth effect, F (1, 82) =
84.33, p < .001, partial eta
2
= 0.51, with repeated claims rated more true than new statements. As
shown on Figure 2.2, the interaction of NFC and repetition was, F (1, 82) = 3.76, p = .056,
partial eta
2
= 0.04, with high NFC participants showing a truth effect, F (1, 82) = 59.04, p < .001,

44
partial eta
2
= 0.42 (raw mean difference = 0.86, 95% CI [0.64, 1.09]), than low NFC participants
showing a truth effect, F (1, 82) = 27.55, p < .001, partial eta
2
= 0.25 (raw mean difference =
0.56, p < .001, 95% CI [0.35, 0.78]). There was no main effect of NFC, F (1, 82) = 1.29, p
= .260, partial eta
2
= 0.02.

Effect Size Analysis
We conducted a mini meta-analysis of Experiments 2.1 and 2.2 to more precisely
estimate the influence of NFC on the illusory truth effect. Figure 2.2 shows a forest plot of all
effect size estimates for high and low NFC across the two experiments reported here. Analysis
was performed using Comprehensive Meta-Analysis Software (Version 3.0). Due to the small
number of studies, tau-squared was pooled across studies, following recommendations by
Borenstein, Hedges, Higgins, and Rothstein (2009). A random effects model was used and effect
sizes were corrected for small sample biases (Borenstein et al., 2009). The total illusory truth
effect across all conditions was d = 1.09, 95% CI [0.71, 1.47]. The illusory truth effect for
participants with high NFC was, d = 1.40, 95% CI [0.84, 1.95] and for participants with low
NFC, d = 0.82, 95% CI [0.30, 1.34], but this difference did not reach significance in the overall
analysis, Q (1) = 2.25, p = .134, d = 0.58, 95% CI [−0.18, 1.32].
In an additional analysis, we considered the possibility that warnings may mitigate the
effects of high NFC. Indeed, being warned prior to exposure may reduce the reliance on positive
hypothesis testing, leading high NFC participants to elaborate on both the possibility that claims
are true and the alternative, that they may indeed be false. To this end, we conducted separate
analyses for the warning and no warning conditions to examine under what conditions the
influence of NFC was most pronounced. In the warning condition, high NFC participants had an
illusory truth effect of d = 0.74, 95% CI [0.45, 1.02], compared to low NFC participants, d =

45
0.63, 95% CI [0.29, 0.96], but this difference did not reach significance, Q (1) = 0.25, p = .619, d
= 0.11, 95% CI [−0.33, 0.56]. In contrast, in the no warning condition, high NFC participants
had a significantly larger illusory truth effect, d = 1.86, 95% CI [1.43, 2.30], compared to low
NFC participants, d = 0.91, 95% CI [0.66, 1.17], Q (1) = 13.55, p < .001, d = 0.95, 95% CI [0.44,
1.45]. Taken together, these data suggest that there is little evidence that NFC moderates the
illusory truth effect with standard experimental instructions. However, without a warning that
one may encounter false information, NFC did indeed moderate the illusory truth effect. These
results are of course preliminary and further investigation into the conditions by which NFC may
moderate illusory truth is warranted, given the effect of NFC without warnings.
Discussion
Across two experiments, we replicated the basic illusory truth effect in all conditions.
Additionally, we found evidence that that being high on NFC - an individual difference measure
of people’s disposition to enjoy effortful thinking and to spontaneously engage in it (Cacioppo &
Petty, 1982) - may lead people to be more susceptible to illusory truth when no warnings of
falsehoods are present. These findings suggest that a proclivity to think more extensively is not
uniformly protective against fluency-based biases in truth judgments. In fact, it may increase
susceptibility to these biases under conditions in which truth is not considered during initial
elaboration. Thus, understanding the influence of elaborative processing on susceptibility to
incidental influence of fluency requires attention to the context of judgment, such as the presence
of warnings and whether or not a judgment is delayed.
Our replication of the basic illusory truth effect across levels of NFC is unsurprising
given the illusory truth effect is robust to a variety of conditions that typically attenuate
experiential inputs: high knowledge, warnings, and source variations at the time of judgment

46
reduce but do not reverse or eliminate the effect of repetition (Fazio et al., 2015; Jalbert et al.,
2020; Unkelbach & Greifeneder, 2018). When variation in fluency is apparent, it may be a
particularly potent input in assessments of truth, in part because ease of processing serves as
evidence for several truth-related criteria (e.g., Schwarz, 2015). Information that is easy to
process is rated as more coherent, credible, compatible with our own general knowledge, more
likely to have high social consensus, and better supported by evidence (Schwarz, 2015; see also
Unkelbach, Koch, Silva, & Garcia-Marques, 2019).
However, despite the large body of literature examining the illusory truth effect, to our
knowledge, very few studies have considered possible moderators to individual differences and
experimental influences of processing style on illusory truth. Brashier et al. (2017) examined the
moderating role of claim difficulty in the emergence of age differences in susceptibility to
illusory truth (see also, Parks & Toth, 2006). This moderator was critical in detecting effects of
age on illusory truth; while they found no effects of age with difficult claims, older adults were
less susceptible to the illusory truth effect for better-known claims—perhaps due to better
knowledge application at the time of test (Brashier et al., 2017). It is possible that any effect of
NFC may also emerge more robustly for better-known claims. Additionally, the influence of
increased elaboration for high NFC may be greater for topics where they have more developed
knowledge networks, leading to a larger illusory truth effect (e.g., Boehm, 1994).
Our findings suggest another important moderator — incidental instructional warnings —
may reduce the possibility that differences in elaborative processing are detected. We are only
aware of one other paper that considered NFC and truth. In that study, instead of simply reading
the statements at encoding, participants judged whether or not each statement was true, a kind of
incidental warning that would alert participants that some claims are false in the first phase.

47
Boehm (1994) observed no effect of NFC. This finding is consistent with our reanalysis of the
warning condition of Jalbert et al.’s (2020, Experiment 1) data, which failed to find an effect of
NFC in a condition without warning. In our experiments, the NFC effect only emerged when
people were not alerted to think about truth during the encoding phase, a critical methodological
difference to the Boehm experiment (see Jalbert et al., 2020, on the effect of instructional
warnings). This is also a critical methodological difference studies conducted by
Dekeersmaecker et al. (2020) studies, which detected no reliable effect of individual difference
variables.
There are several reasons to suspect that this standard methodological feature may reduce
the possibility of detecting individual differences and other experimental manipulations,
especially in the context of NFC. Consistent with the persuasion literature, we assume that high
NFC individuals think more about the claims at the time of initial exposure (Briñol & Petty,
2019; Cacioppo et al., 1996). This, in turn, makes the claims more familiar and easier to process
when they are encountered again at time 2, especially in comparison to the novel claims
presented at the same time (see Unkelbach & Rom, 2017). The claims presented in illusory truth
experiments are usually ambiguous and testing their truth value is likely to involve positive
hypothesis testing—e.g., do I know of any evidence that supports this claim? This positive
testing is less likely when participants are warned that half of the claims are false, which may
increase the likelihood of negative hypothesis testing, as observed under other conditions of
induced distrust (Mayo, 2017; Mayo, Alfasi, & Schwarz, 2014). As a result, standard
experimental warnings and other distrust eliciting variables at the time of initial exposure may
curb the otherwise observed increase in illusory truth under high NFC or in a context that fosters
increased elaboration. While preliminary, this finding suggests that understanding individual

48
differences in truth biases requires attention to context and other situational variables that may
moderate any effect of individual difference measures.
The persuasion literature identifies several moderators that influence the extent to which
high and low NFC individuals differ in their evaluation of presented content. Some variables
work to increase differences between high and low NFC on outcome measures. For example,
people with high NFC are more convinced by strong, rather than weak arguments, a variable that
is rarely manipulated in truth paradigms and may affect the extent to which high NFC
individuals draw on positive, rather than negative, testing of truth (e.g., Cacioppo, Petty, &
Morris, 1983). Other variables work to reduce differences between high and low NFC. For
example, high uncertainty and high self-relevance are sufficient to motivate elaborative thinking
even among low NFC individuals, which reduces differences between high and low NFC
participants (Smith & Petty, 1996; Ziegler, Diehl, & Ruther, 2002). Conversely, those with high
NFC behave more like low NFC participants when they are led to believe they are considering a
message intended for those who typically do not engage in effortful thought (Wheeler, Petty, &
Bizer, 2005; see also See, Petty, & Evans, 2009). Considering potential moderators across
materials, instructions and context will enhance understanding of the role of individual
differences, but also provide converging evidence for theory in these paradigms.
Summary
Overall, we find evidence that a tendency to engage in elaborative processing (as
measured by NFC) increases the size of the illusory truth effect under conditions in which people
are not warned about potential falsehoods. We found no evidence that NFC moderates the size of
the illusory truth effect when warnings of falsehoods were present. Thus, we conclude that
elaboration is unlikely to universally protect against susceptibility to fluency-based biases in

49
truth assessment. Rather, the results reported here suggest that strategies aimed at correcting
belief in false information through more elaborative processing should consider judgment
context and the influence of this processing on judgments across time.

50
Chapter III: A Lemon in Yellow, a Lemon in Blue: Color Congruence and Truth
Judgment
3

Information that feels easier to process is also judged to be more true. In some cases –
like when information has been made easy to process due to repeated exposure from a credible
source – processing ease can be a valid cue for truth. However, processing ease can also result
from incidental factors unrelated to truth. Researchers have identified several mechanisms that
facilitate processing ease (for reviews, see Newman, Jalbert, & Feigenson, 2019; Schwarz &
Jalbert, 2020; Schwarz, Jalbert, Noah, & Zhang, 2021). One mechanism is perceptual fluency –
that is, the ease of perceiving and identifying information. For example, claims are judged to be
more true when they are in a print font that is easier to read (Song & Schwarz, 2008) or when
they are presented with a photo that makes it easier to imagine what the claim is about (Newman
et al., 2012, 2015; for a review see Newman & Zhang, 2021). Other examples of perceptual
manipulations that influence truth perception include audio quality (Newman & Schwarz, 2018),
pronounceability (Newman et al., 2014; Silva, Chrobot, Newman, Schwarz, & Topolinski,
2017), and handwriting (Greifeneder et al., 2010).
Information can also feel easier to process through conceptual fluency - the ease of
extracting meaning and understanding information. For example, claims seem more true when
they are written in concrete language compared to abstract language (Hansen & Wänke, 2010) or
when the topic of a claim has just been made familiar through earlier exposure (Begg, Armour,
& Kerr, 1985). Additionally, information may feel easier or more difficult to process through

3
This chapter is based on:
Jalbert, M., Li, S., & Schwarz, N. (2021, February). A lemon in yellow, a lemon in blue: Color
congruence and truth judgment. Poster presented at the annual meeting of the Society for
Personality and Social Psychology.

51
bodily cues of effort, like using one’s non-dominant hand (Briñol & Petty, 2003) or furrowing
one’s brow (Strack & Neumann, 2000).
Repetition and fluency
The mere repetition of information is a particularly strong influence on perceived truth as
it may act through perceptual and conceptual fluency, making claims both perceptually easier to
read when seen again and easier to understand through the increased accessibility of applicable
knowledge (e.g., Hasher, Goldstein, & Toppino, 1977; Jalbert, Newman, & Schwarz, 2020; for a
meta-analysis, see Dechêne, Stahl, Hansen, & Wänke, 2010; for a discussion of mechanisms, see
Unkelbach, Koch, Silva, & Garcia-Marques, 2019). Indeed, the impact of repetition is typically
much larger than that of perceptual fluency manipulations (e.g., Parks & Toth, 2006) and its
influence is much more difficult to correct for (e.g., Garcia-Marques, Silva, & Mello, 2016;
Silva, Garcia-Marques, & Mello, 2016).
Additionally, exact repetition is not necessary for this effect to occur. Rather, prior
exposure to partial content or related information may facilitate the perceived truth of a novel
claim. For example, as mentioned previously, information about a familiar topic is perceived to
be more true than information about an unfamiliar topic (Begg et al., 1985; see Unkelbach &
Rom, 2017 for a related discussion). In this case, consistency with conceptual associations
contained in an associative knowledge network may facilitate the processing of information.
Consistent semantic associations also have a similar effect. For example, Zhang and Schwarz
(2020) found that claims containing word combinations that appear more frequently in the
corpus of language are judged to be more true than claims that contain word combinations that
appear less frequently.
Multimodal associations and color congruency

52
In combination, this work suggests that the match between current context and prior
associations developed through daily experiences gives rise to experiences of processing fluency
that guide evaluative judgment. One extension of this work is to investigate whether the physical
attributes of objects represented in knowledge networks may influence the evaluation of
semantic content. This may be thought of as a type of multimodal processing facilitation, with
prior associations in one modality (e.g., sight, taste, sound, touch, smell) influencing a relevant
judgment in a different modality (e.g., semantic content).
We investigate the possibility of multimodal processing facilitation by asking participants
to assess the truth of information presented in colors congruent or incongruent with the subject of
the claim. Color is a variable that can have visual, conceptual, and semantic associations (Naor-
Raz, Tarr, & Kersten, 2003). We suspect that these visual associations may facilitate perceived
truth in a similar way as conceptual and semantic associations. Indeed, there is already robust
evidence that the visual presentation color can facilitate or disrupt the processing of color or
color-related words. Take the classic Stroop effect, in which participants have more difficulty
and take longer to read a color word (like “blue”) when it is written in a congruent color (blue)
than when it is written in an incongruent color (red; Stroop, 1935). This effect has been
replicated numerous times since, and further research has found that this effect can carry over to
words with strong color associations (e.g., sky in blue; Klein, 1964).
Present research
In two studies, we test the hypothesis that information presented in a color congruent
with the subject of the claim (e.g,. a claim about lemons in yellow) is perceived to be more true
than information presented in a color incongruent with the subject of the claim (e.g., a claim
about lemons in blue). In Experiment 3.1, participants are asked to rate the truth of a series of

53
claims about fruits and vegetables in colors congruent or incongruent with the subject of the
claim. We replicate this basic methodology in an online sample in Experiment 3.2. The
implications of multimodal associations like color congruence moderating processing fluency are
discussed in the context of relevant literature.
Experiment 3.1
Method
Participants. Based on a within-items effect size of d = 0.2 (a small effect similar to the
size of truth effects obtained across two studies with a similar paradigm, d = 0.226, 95% CI
[.151, .301]; Newman, Jalbert, Schwarz, & Ly, 2020), a sample of 199 participations would be
required to detect the effect in a repeated measures design with α = .05, power (1-β) = .80, and
two-tailed according to G*Power (Faul, Erdfelder, Lang, & Buchner, 2007). Thus, we decided to
recruit 200 participants. Participants could only sign up for the experiment if they did not have
any form of colorblindness. Two participants were excluded because they did not complete the
full survey, and 2 participants were excluded because they had learned about the nature of the
study prior to completing it. This left us with data from 196 participants (67 Male; MAge = 19.81,
SDAge = 1.52) for analysis.
Design. We manipulated color congruence (congruent or incongruent) within-subject.
Claim truth was also manipulated within-subject. In a between-subjects condition, participants
were randomly assigned to one of two claim color counterbalance conditions.
Materials. We first compiled true and false trivia claims about fruits and vegetables. We
chose fruits and vegetables with the following colors: red, orange, yellow, green, purple, and
brown. False claims were created by taking true claims (e.g., “Pumpkins can be grown in
Alaska”) and changing one word to alter the meaning of the claim (e.g., Pumpkins cannot be

54
grown in Alaska). We then normed the claims for truth using 78 participants in the USC subject
pool claims (28 Male; MAge = 19.89, SDAge = 1.37). Participants were asked whether each claim
was true or false and made their answer on an unnumbered six-point scale from definitely true
(coded as 6) to definitely false (coded as 1). Participants only rated either the true or false version
of a claim, but not both.
Based on the norming data, we selected 24 claims of ambiguous truth rating, with mean
truth ratings between 3.10 and 4.18 on the six-point scale. We wanted to choose claims that
participants did not immediately recognize as true or false to allow for more movement in belief.
Claims were counterbalanced such that half of the participants saw 12 congruent claims (i.e., the
color of the claim matches the subject of the claim) and 12 incongruent claims (i.e., the color of
the claim does not match the subject of the claim). Each participant saw one of two sets of claims
– set A or set B. While each set had the same 24 claims, the 12 claims that were in a congruent
color in one set were swapped to be the claims that were in the incongruent claims in the other
set. Both item sets contained 12 true claims and 12 false claims, with each of the six colors
appearing four times. Based on the norming data, each set of 12 claims that were presented as
congruent or incongruent had similar truth ratings. True and false claims also had similar truth
ratings within each item set.
Claims were presented in a bolded 18-point Verdana font using standard Microsoft Word
colors. To make sure lower contrast colors like yellow were easy to read, all words were outlined
with a 0.25 point black line. Images of example claims and a full list of claims used in each
counterbalance be found in the supplementary materials.
Procedure. As a cover story to prevent participants from guessing the goal of the study,
participants were informed that the study they were completing involved memory for incidental

55
color exposure. Participants were then told that they would be shown a series of trivia statements
presented in a variety of colors and be asked to evaluate them. Then they would complete
another task and then be asked about their memory for the colors they had seen.
Participants were presented with the 24 trivia claims from set A or set B. For each, they
answered the question “Is this statement true or false” on an unnumbered six-point scale from
definitely true (coded as 6) to definitely false (coded as 1). The order in which the claims were
presented was randomized.
Participants then completed an 18-item Need for Cognition Scale (Cacioppo, Petty, &
Feng Kao, 1984) for exploratory purposes unrelated to our primary hypothesis. Next, participants
answered a few memory questions about how many claims were presented in each color to stay
consistent with the cover story. We then included an additional colorblindness question to ensure
only participants with normal color vision were included in the study. Finally, participants
answered a few questions for an unrelated study and completed demographic questions on their
gender, age, and nationality.
Results
In order to assess whether claims presented in a congruent (vs. incongruent) color were
perceived to be more true, we conducted a paired-samples t-test comparing the mean truth
ratings of the congruent and incongruent claims. This analysis yielded a marginally significant
effect consistent with our hypothesis, with color congruent claims (M = 3.58, 95% CI [3.50,
3.66]) perceived to be more true than color incongruent claims (3.49, 95% CI [3.43, 3.56]; t
(195) = 1.904, p = .058, d = 0.168.
Experiment 3.2

56
In Experiment 3.2, we aimed to replicate the general findings of Experiment 3.1. We
made just a few modifications to our method in this replication. The main change was adjusting
how we assigned incongruent colors. In Experiment 3.1, we had assigned incongruent colors to
claims such that the frequency of colors used for congruent colors matched the frequency of
colors used for incongruent claims. This kept color variation constant across claim type but also
meant we were limited as which claims we could assign incongruent colors to. This left us with
some color-claim pairings in which the incongruent colors may not be perceived to be
incongruent. For example, the incongruent claim about figs was in green, and the incongruent
claim about bananas was in brown, which are colors these items sometimes appear in. To address
this concern, we now basing our incongruent color choices on stimuli used in prior research on
Stroop-like effects (Nao-Raz et al., 2003).
Method
Participants. In this study, we recruited participants from Prolific who were located in
the United States and had a 95%+ approval rating. Once again, we conducted a power analysis
based on a within-items effect size of d = 0.2, which gave us a necessary sample of 199
participants required to detect the effect in a repeated measures design with α = .05, power (1-β)
= .80 (Faul et al., 2007). Due to the setup of Prolific, we were not able set normal color vision as
a prerequisite for this study. Instead, we allowed all participants to sign up and complete the
study regardless of color vision, but only participants who indicated they had normal color vision
in a question at the end of the study were included in data analysis. To account for potential
exclusions, we overrecruited and collected data for 220 participants to ensure an adequate
number following exclusions. Overall, 217 participants finished the study. All participants
reported having normal color vision. One participant was excluded because they reported their

57
age to be less than 18 years old. This left us with 216 participants for analysis (113 male, 99
female, 4 not reporting; Mage = 33.16).
Design. We again used a repeated measures design, manipulating color congruence
(congruent or incongruent) within-subjects. We also manipulated truth within-subject and
randomly assigned participants to one of two claim sets between-subjects as a counterbalance
condition.
Materials. We once again chose fruit and vegetable claims from the norming described
in Experiment 3.1, with chosen claims having truth ratings between 3.05 and 4.00 (1 = definitely
false, 6 = definitely true).
This time, we only used fruits and vegetable claims with subjects that had been used as
object-color pairs in work by Naor-Raz et al. (2003) on Stroop-like effects. This was done to
ensure our incongruent colors were actually incongruent. We then created two sets of eight
claims, each half true and half false. Based on the norming data, each set of 8 claims that were
presented as congruent or incongruent had similar truth ratings (M = 3.58, SD = 3.58 for set A,
M = 3.59, SD = 3.74 for set B). True and false claims also had similar truth ratings within each
item set.
Claims were created in PowerPoint using 44-point Verdana, 0.25 point black outline, and
exported to 1440x324 PNG images. Exactly color information and full lists of claim
counterbalances and colors can be found in the supplementary materials.
Method. The method for Experiment 3.2 was similar to Experiment 3.1. Participants
were given the same cover study as in Experiment 3.1. Participants were then presented with the
8 trivia claims (four randomly chosen to be in a congruent color, the other four in an incongruent
color) from set A or set B in a randomized order. Again, they answered the question “Is this

58
statement true or false” on an unnumbered six-point scale from definitely true (coded as 6) to
definitely false (coded as 1). The order in which the claims were presented was randomized.
Finally, participants answered a few memory questions about how many claims were presented
in each color to stay consistent with the cover story. They also reported whether they had any
form of colorblindness and answered demographics questions on their gender, age, and
nationality.
Results
Once again, we conducted a paired-samples t-test to see if claims presented in a
congruent (vs. incongruent) color were perceived to be more true. This time we failed to find a
significant effect of color congruence, t (215) = 0.857, p = .392, d = 0.077, with congruent
claims (M = 3.61, 95% CI [3.51, 3.72]) not rated to be significantly more true than incongruent
claims (M = 3.55, 95% CI [3.43, 3.66]).
Effect Size Analysis
In order to better estimate the effect of color congruent on perceived truth, we performed
a mini meta-analysis combining effect sizes across our two studies. Analysis was performed
using Comprehensive Meta-Analysis Software (Version 3.0). Tau-squared was pooled across
studies due to small study size (Borenstein, Hedges, Higgins, & Rothstein, 2009) and the effect
size was corrected for small sample biases (Borenstein et al., 2009). This analysis revealed a
marginally significant effect of color congruence on truth across both studies, with an effect size
of d = 0.123, 95% CI [-0.001, 0.247], p = .052. There no evidence that effect size differed
between the two studies, Q (1) = 0.52, p = 0.471, I
2
< .001
Discussion

59
Overall, we found initial suggestive evidence for our hypothesis that presenting
information in a color congruent (vs. incongruent) with the subject of the claim would increase
perceived truth. In two studies, participants rated the truth of true and false claims about fruits
and vegetables presenting in colors that matched or did not match the subject of the claim.
Combining across both studies, there was a marginally significant effect of color congruence on
perceived truth, d = 0.123, 95% CI [-.001, 0.247], p = .052. While further research is necessary
to establish the extent to which color congruence may influence truth perception, in this
discussion we consider the potential implications of this finding and its relationship to existing
literature.
Potential mechanisms
First, we consider the mechanism through which color congruence may influence
perceived truth. Color congruence is unlikely to act solely by enhancing the perceptual
processing of the claim. While related research on truth perception has demonstrated that
variation in color contrast between a claim and its background can influence truth by making the
information feel more or less easy to read (Reber & Schwarz, 1999), we ensured all of our colors
were similarly easy to read by including a black outline around each claim and presenting them
on white backgrounds. Additionally, we controlled for color variation in Experiment 3.1 by
creating the item sets such that congruent and incongruent sets of claims each contained the same
colors appearing at the same frequency. Thus, differences in processing fluency resulting from
the ease of perceiving different colors should wash out across item sets.
Similarly, it is also unlikely the color congruence would facilitate processing fluency
purely through enhancing conceptual fluency. At a surface level, manipulating whether a claim is
presented in a color that is congruent or incongruent with the subject of the claims seems to share

60
similarities with the finding that adding a non-probative photo depicting the subject of a claim
can increase the perceived truth of a statement (Newman et al., 2012, 2015). These photos are
theorized to boost perceived truth by increasing the ease of imagining the claim and retrieving
related details (Zhang et al., 2020; for a review, see Newman & Zhang, 2021). Perhaps color
congruence operates through a similar mechanism, helping participants imagine the subject and
more readily bringing related information to mind. However, this work also finds that there are
limits to the conditions in which photos are helpful. Critically, photos only increase perceived
truth when the subject would otherwise be difficult to imagine and not when the subject is
already easy to imagine (Zhang, Newman, & Schwarz, 2020). This is also consistent with
findings that photos of unfamiliar subjects facilitate perceived truth more than those of familiar
subjects (Abed, Fenn, & Pezdek, 2017; Newman et al., 2012). As we only included claims about
familiar fruits and vegetables that should be easy to imagine, it seems unlikely that color
congruence would be enough to significantly increase processing fluency via the same
conceptual mechanisms underlying photo effects.
Rather, the mechanism through which color congruence may operate to influence
processing fluency is more consistent with a different body of work that considers the impact of
associative knowledge networks on processing experience. For example, we can consider
research on conceptual metaphors, which people use to represent abstract concepts using more
concrete elements (Lakoff and Johnson 1999; Landau, Meier, & Keefer 2010). For example,
people typically represent the abstract concepts of rationality and emotion physically, with
rationality situated up and in the head and emotion situated down and in the heart. Cian, Krishna,
& Schwarz (2015) investigated whether presenting product advertisements in a visual format that
matched these metaphorical representations influenced evaluations and preference for the

61
product. Indeed, they found that participants preferred products paired with claims that appealed
to rationality when those claims were presented at the top of the page, while they preferred
products paired with claims that appealed more to emotion when those claims were presented at
the bottom of the page. This work provides convincing evidence that a match between concepts
associated in memory (e.g., rationality and up) can influence the processing experience of novel
information containing those elements.
Research that uses a culture-as-situated-cognition approach is similarly relevant. This
approach assumes that previous experience gives rise to culturally-rooted associative knowledge
networks that guide expectations and how information is processed (for reviews, see Oyserman
2011; Oyserman & Yan, 2018). A key assumption of this approach is that people hold many of
these associative knowledge networks that are differentially activated depending on the context
at hand. Situations consistent with expectations arising from the activated knowledge network
(e.g., an American seeing a bride wear a white dress at a wedding) are met with feelings of
fluency and a sense that all is right with the world. Alternatively, situations that violate
expectations (e.g., seeing a bride wear a black dress at a wedding) are met with experiences of
cognitive disfluency. These feelings of fluency and disfluency lead to downstream cognitive and
behavioral consequences (e.g., Mourey, Lam, & Oyserman, 2015; Lin, Arieli, & Oyserman,
2019).
Taking a broad perceptive, this body of work provides a framework for conceptualizing
how experiences of processing fluency arise from the consistency of incoming information with
prior knowledge and experience (for a related discussion, see Unkelbach & Rom, 2017). In this
case, our color-subject pairings may be consistent or inconsistent with existing associative
knowledge about the colors of fruits and vegetables. A match or mismatch of these color pairings

62
with these existing associations may then give rise to experiences of fluency or disfluency.
Interestingly, our studies hint that these processes occur across modalities that are not typically
paired together in everyday life (e.g., visual and semantic representations of color). Additionally,
just as the accessibility of culturally-rooted associated knowledge networks may depend on the
context at hand, multimodal associations may be thought of as similarly contextually situated.
Although preliminary, our findings open the door to a number of theoretical questions and future
experimental investigations. While we chose to examine the influence of color congruence on
perceived truth, future work may utilize other multimodal representations, such as those
involving taste, sound, touch, or smell. The possible questions to be asked here are endless. For
example, are people more compelled by claims about women they hear them in a woman’s
voice? Do claims about the ocean seem more true when they come with a whiff of salty brine?
Are you more likely to believe claims about children when you hear children playing outside
your window?
Overall, we find that color congruence may be a novel variable that influences perceived
truth. This finding indicates that the commonly discussed mechanisms (e.g., perceptual fluency,
conceptual fluency, bodily cues of effort) are not the only ones underlying experiences of
processing fluency. Rather, a more comprehensive framework for understanding how people
judge truth should also consider how a match (or mismatch) between current context and
associative knowledge networks may guide processing experience.

Copyright 2021 Madeline Jalbert

Chapter IV: If It’s Relatively Difficult to Pronounce, It Might be Risky: Risk Perception
Depends on Processing Experience in Context
4

In many domains of life, people judge familiar things to be less risky than new things.
For example, in the investment world, people believe that assets with familiar names are less
risky than assets with unfamiliar names (Weber, Siebenmorgen, & Weber, 2005). People living
close to a nuclear power plant believe it is less risky than those who live far from it (Richardson,
Sorensen, & Soderstrom, 1987).
Indeed, because the unknown comes with uncertainty, familiarity may serve as a valid
cue for safety when it comes with the absence of any negative associations (Zajonc, 1980; 1998;
for a review, see Herzog & Hertwig, 2015). However, the role of mere familiarity on judgments
of risk is difficult to isolate in the real world due to the presence of other confounding variables.
For example, as one becomes more familiar with a potential risk, one is also likely to pick up
more knowledge about that risk. Those who are more familiar with a risk may have self-selected
to engage with it. On the other hand, people may have to engage with the risk out of necessity,
leading to a denial or downplaying of the risk as a form of dissonance reduction. Factors such as
these make it difficult to isolate the role of familiarity in the real world.
One way to avoid these confounds is to experimentally manipulate perceived
familiarity while keeping substantive information bearing on that risk constant. This can be
accomplished by taking advantage of naïve theories of familiarity and processing fluency. In

4
This chapter is based on:
Jalbert, M., Newman, E., & Schwarz, N. (2019, February). If it’s relatively difficult to
pronounce, it must be risky: Risk perception depends on processing experience in context. Poster
presented at the annual meeting of the Society for Personality and Social Psychology. Portland,
OR.

64
general, prior exposure to stimuli increases the ease of processing that stimuli when it is
encountered again. This makes processing ease a potentially valid source of information that
people rely on when judging familiarity, especially in the absence of more probative
information (for reviews, see Alter & Oppenheimer, 2009; Schwarz, 2004; Schwarz, Jalbert,
Noah, & Zhang, 2021). However, this fluency-familiarity link results in misattributions as
ease of processing resulting from tangential variables, such as presentation format, as bearing
on familiarity. For example, when words were made easier to process by increasing the visual
clarity with which they were presented, participants were more likely to believe that they had
previously encountered those words (Whittlesea et al., 1990).
Song and Schwarz (2009)
In an initial series of studies, Song and Schwarz (2009, henceforth SS) manipulated
processing fluency through pronounceability in order to test the link between familiarity and risk.
Participants were asked to make risk judgments about easy and difficult to pronounce stimuli in a
variety of domains. Across these studies, SS found that difficult to pronounce stimuli were
consistently judged to be more risky than easy to pronounce stimuli, and the influence of fluency
on perceived risk was mediated by perceived familiarity.
Following this work, other researchers have replicated this effect of pronunciation-
fluency on perceived risk using stimuli from the original SS studies (e.g., Dohle & Siegrist,
2014; Topolinksi & Strack 2010). Investigations with different stimuli in different domains have
also mirrored these findings. For example, fabricated stocks with easy to pronounce named
names were predicted to have higher returns than those with difficult to pronounce names (Alter
& Oppenheimer, 2006, Exp. 1). Water with an easier to pronounce brand name was perceived to
be more pure than water with a difficult to pronounce brand name (Cho, 2019). People are more

65
likely to trust eBay sellers (Silva, Chrobot, Newman, Schwarz, & Topolinski, 2017) and alleged
partners in an economic trust game (Zürn & Topolinki, 2017) when they have easier to
pronounce names or usernames.
Adding broader support to the theoretical account that pronounceability influences risk
judgments through processing fluency are parallel findings with other manipulations of
processing fluency. For example, both Silva et al. (2017) and Zürn & Topolinki (2017) find that
increasing name length leads to decreased perceived trust independent of variation in
pronounceability. Additionally, making a face easier to process through prior exposure makes
that person seem more honest and trustworthy when viewed again (Brown, Brown, & Zoccoli,
2002), and using better audio quality to play research talks leads to better evaluations of the
research quality and the competence of the researcher (Newman & Schwarz, 2018).
Bahník and Vranka (2017)
However, recent work by Bahník and Vranka (2017, henceforth BV) has called the
validity of this pronounceability and risk link into question, specifically focusing on the
results of the original SS studies. They base their concerns on the idea that psychological
experiments are conducted with limited participant populations and a small set of materials,
making it wise to explicitly acknowledge “constraints on generality” (Simons, Shoda, &
Lindsay, 2017).
Apparently identifying such a constraint, BV compared the relationship between
pronounceability and risk in three studies using stimuli from SS as well as newly created
stimuli. After reproducing the pronounceability effect using SS stimuli in two out of three
studies, and with their own stimuli in only one out of three studies, they concluded that “the
effect of pronounceability on judgment of riskiness may be much weaker than originally

66
thought or even nonexistent” (p. 8).
This conclusion is surprising given that pronunciation effects have been demonstrated
with varied stimuli by different labs. As already noted, in addition to pronounceability effect
with SS stimuli (Dohle & Siegrist, 2014; Topolinksi & Strack 2010), others have replicated these
effects with novel stimuli and in varied domains (e.g., Alter & Oppenheimer, 2009; Silva et al.,
2017).
Additionally, manipulating processing fluency through ease of pronunciation has been
found to similarly influence related judgments of liking and truth. Just as familiarity is associated
with safety, it is also associated with liking and truth, with familiar things liked more and
familiar information judged to be more true (for a review, see Schwarz, Jalbert, Noah, & Zhang,
2020). For example, studies have found that people like companies, stocks, and eBay names
more when they are easier to pronounce (Fetcherin, Diamantopoulos, Chan, & Abbott, 2015),
and information that comes from someone with an easier to pronounce name is more likely to be
judged true (Newman et al., 2014).
Discrepant results
In order to further our understanding of the underlying processing driving the
pronounceability and risk link, we examine several aspects which may have led to the
discrepant results between BV and the existing literature of familiarity and risk, including
stimuli selection, stimuli presentation, and data analysis methods. First, key differences exist
between the stimuli utilized by SS and BV. Because SS wished to study the impact of
familiarity on risk without changing the substantive information provided, SS items were
created to be as context-free as possible and were not based on pre-existing stimuli from that
category. However, BV items were created based on real items. For example, in BV’s Exp. 5,

67
participants were asked to rate the hazardous of original SS food additive stimuli and newly
created BV stimuli, the items from SS (2009) had been completely made up to be food
additives, while the stimuli of BV (2017) were derived from the names of existing
medications by “randomly changing one letter in the names, and then removing names that
sounded too similar to well-known substances (e.g., Tedtosterone)” (p. 3). Such real medicine
names with a single typo may be perceived as typical for the target category and contain
suffixes and prefixes that come with prior associations. Similarly, in BV’s Exp 6., Czech
participants asked to rate the perceived hazardless of food additives using original SS food
additive items (made up and normed for a US population) to new stimuli created from real
medicine names that were modified to have suffixes based on the suffixes of real Czech food
additives.
These differences in stimuli are important to note because multiple characteristics of
stimuli may be expected to influence perceived risk. For example, medicine names that have
qualities about them that bring to mind prior associations are likely to influence perceived risk
irrespective of pronounceability. In one study on the effects of drug names on risk judgments,
Tasso, Gavaruzzi, & Lotto (2014) kept the pronounceability of drug names constant but
manipulated whether parts of their names were functional (related to the condition it was
treating), persuasive (related to the outcome of treatment), or control names that not contain any
information (e.g., a meaningless string of numbers). All words were similarly easy to pronounce.
However, the drug names of both functional and persuasive names were rated to be more
meaningful than control names, and drugs with persuasive names were rated to be less risky than
the others.
These findings demonstrate that there are many inputs to judgments of risk, including

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whether or not participants have any pre-existing associations with the item and what
information those associations might provide. Typicality is itself a reliable fluency manipulation
and affects judgment in ways that parallel other fluency manipulations (Alter & Oppenheimer,
2009; Winkielman, Halberstadt, Fazendeiro, & Catty, 2006). This predicts that BV’s items will
be judged as more typical and less harmful than SS’s items at comparable levels of
pronounceability.
In a related vein, the pronounceability of words is only one factor that may make them
easier or more difficult to process. BV draws attention to this in their conclusion by positing that
the word length of specific stimuli may explain the pronounceability risk link observed by SS.
That this may be the case is not a novel proposal. As noted earlier, word length is another
variable that influences processing fluency, and studies have demonstrated independent
influences of pronounceability and world length on trust (Silva et al., 2017; Zürn & Topolinki,
2017).
We instead point out that pronounceability is just one input of many that may make
information easy or difficult to process. Expecting there to be a “pronounceability” effect that
occurs independently of inputs, like word length or item typicality, misses the theoretical
explanation underlying the fluency effect. Depending on the strength of the manipulation,
variations in one input may override (or decrease) the effects of variation of another input. For
example, if an item has prior associations, the role of these factors may reasonably be expected
to override fluency effects due to pronounceability.
To address concerns that pronounceability effect observed by Song and Schwarz (2009)
with original stimuli are due to specific stimuli or the confounding effects of word length, we
conduct new investigations using items created by BV, and also include two studies in which

69
word length is held constant while only pronounceability is manipulated.
Stimuli Presentation
SS’s participants judged 10 items, of which 5 were easy and 5 difficult to pronounce.
This produces marked shifts in the subjective fluency experience from item to item. On the other
hand, BV’s participants judged 10 stimuli randomly drawn from a pool that also included
moderately difficult items, resulting in less variation from item to item. While randomly
sampling stimuli may allow research to generalize more broadly, this type of stimuli sampling
may be problematic when a phenomenon relies on a specific type of variation between stimuli.
BV’s random stimuli sampling inherently led to smaller changes in pronunciation than when
sampling from just high and low pronunciation words. Yet, fluency effects depend on
participants experiencing changes in fluency. This has been demonstrated across an array of
judgments driven by processing fluency, from truth (e.g., Dechêne, Stahl, Hansen, & Wänke;
2009; Hansen, Dechêne, & Wänke, 2008) to confidence in performance on multi-step tasks
(Stevenson & Carlson, 2018). Additionally, Zürn and Topolinki (2017) found pronounceability
effects on trust in four within-subject studies where participants experienced variation in
pronounceability across items, but did not find a significant effect in a between-subjects design
where only one judgment was made. By focusing only on absolute pronunciation, Bahník and
Vranka (2017) miss the theoretical point made by Song and Schwarz (2009): the study is an
investigation of fluency effects in context, not on absolute pronunciation.
Stimuli presentation and data analysis
Finally, in their initial experiments (Exp. 1 - 4), BV noted that they were more likely to
find significant fluency effects when they treated stimuli as a fixed factor and that effects were
no longer significant when “correctly” treating item as a random effect, underscoring the

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importance of including item as a random factor. This led them to a new method of random
stimuli sampling used in Exp. 5-7, where they compare the fluency effects obtained with their
new items to those obtained with SS items. However, this change in methodology does more
than just increase the variety of items used; it also changes the context in which each judgment is
being made.
Present investigations
In light of the mixed results of BV, the main goal of the present studies is to test the
robustness of pronounceability effects on risk judgment using stimuli developed by BV. We
address concerns that the pronounceability effect observed by past researchers may have resulted
from the following factors: 1) specific stimuli, 2) word length, and 3) treating stimuli as fixed,
rather than as a random factor, and demonstrate that the influence of pronounceability on
perceived risk can generalize more broadly. Additionally, we test whether BV may not be
reliably observing pronounceability effects because their method of presentation results in
reduced item-to-item changes in fluency.
In Experiment 4.1, we first use BV items with comparable changes in fluency to the
original SS words to show that the influence of fluency is not limited just to these specific
stimuli. In Experiment 4.2, we investigate whether the size of pronounceability effects is driven
by the item to item variations in fluency by presenting the same set of items in three different
presentation orders that either minimize or maximize item to item variations in pronounceability.
Across all three presentation orders, significant fluency effects emerged but the size of these
effects did not vary by presentation order. However, we also noticed evidence of idiosyncratic
effects of specific stimuli. In order to reduce these effects and address BV’s concern about word
length driving observed effects rather than pronounceability, in Experiments 4.3 and 4.4, we use

71
a new set of randomly generated stimuli of constant word length in presentation orders that
minimize or maximize item to item variations in fluency. Finally, to address data analysis
concerns, we include complimentary analysis in all studies where stimuli and participants are
treated as random factors. This results obtained using this approach parallel those reported in this
chapter and are reported in full in the supplementary materials.
Experiment 4.1
In Experiment 4.1 (preregistered at http://aspredicted.org/blind.php?x=hd6br4), we
investigated whether BV items with the same variability in pronunciation as items in the original
SS study demonstrated a fluency effect. We also measured the typicality of items to see if BV
items seem more typical of medicine names than SS items.
Method
Design. Of interest are discrepant results between two specific sets of words, namely
items of comparable difficulty used by BV and SS. Hence, we used a 2 (pronounceability: easy
vs. difficult) x 2 (item source: SS vs. BV) repeated measures design with pronounceability and
item source as within-participant factors. Participants were presented with one of two sets of
items to control for item effects.
Participants. One hundred Mechanical Turk (MTurk) workers located in the United
States with a HIT approval rate of at least 95% completed the experiment using the online survey
platform Qualtrics. The mean age was 36.89 (SD = 12.62), with 41% male and 59% female. The
study was expected to take about 5 minutes and participants were paid $0.30 for completing it.
Materials. Using BV’s difficulty ratings, we selected the 10 items from BV’s pool that
were closest in difficulty to each of the 10 original SS items (MBV = 3.48, SDBV = 0.66; MSS =
3.51, SDSS = 0.68; 1 = easy to pronounce, 5 = hard to pronounce). With these items, we generated

72
a list that alternated between SS and BV items and mirrored the alternation between easy and
difficult items in the original SS study (see Table 4.1 for matched items, Table 4.2 for
presentation order).
Procedure. We used BV’s medicine scenario and asked participants to imagine they
were part of a team of scientists searching through the archives of a laboratory that used to
research medicines. During the search, they found a number of medicines. Participants were
given a list of all 20 medicine names and asked to answer “Is this a typical name for a
medicine?” (1 = no, not typical; 7 = yes, very typical) for each item. On a different screen, they
were then given the same list of 20 medicines and asked to answer “How potentially harmful
would you think this medicine is?” (1 = very safe; 7 = very harmful) for each item. We
counterbalanced between participants whether they made typicality or harm ratings first.
Results
We first looked whether our results were influenced by whether participants making
typicality ratings first or harm ratings first. To investigate this potential influence, we conducted
a 2 (pronounceability: easy vs. difficult) x 2 (item source: SS vs. BV) x 2 (rating order: typicality
ratings first vs. hard ratings first) mixed model ANOVA, with pronounceability and item source
as within-subjects variables and rating order as a between-subjects variable for both typicality
ratings and harm ratings. For typicality ratings, there was no main effect of rating order, F (1, 98)
= 0.91, p = .343, partial eta
2
= .009, no interaction of rating order and pronounceability, F (1, 98)
= 0.09, p = .771, partial eta
2
= 001, no interaction of rating order and item source, F (1, 98) =
0.26, p = .615, partial eta
2
= 003, and no significant three-way interaction, F (1, 98) = 0.66, p
= .419, partial eta
2
= 007.

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For harm ratings, there was also no main effect of rating order, F (1, 98) = 0.54, p = .466,
partial eta
2
= .005, no interaction of rating order and pronounceability, F (1, 98) = 0.52, p = .472,
partial eta
2
= 005, no interaction of rating order and item source, F (1, 98) = 1.31, p = .255,
partial eta
2
= 013, and no significant three-way interaction, F (1, 98) = 0.20, p = .659, partial eta
2

= 002. Because whether or not participants made typicality or harm ratings first did not influence
the results, thus we report the remaining results collapsed across these counterbalance conditions.
Typicality Ratings. We conducted a 2 (pronounceability: easy vs. difficult) x 2 (item
source: SS vs. BV) repeated measures ANOVA. All reported means are estimated marginal
means; the raw means show the same pattern and are included in the supplementary materials for
all studies. BV’s items were rated as more typical of medicine names (M = 3.69, 95% CI [3.47,
3.90]) than SS’s items (M = 3.20, 95% CI [2.98, 3.42]); mean difference = 0.49, (95% CI [0.36,
0.61], F (1, 99) = 56.65, p < .001, partial eta
2
= .364). Additionally, easy to pronounce words
were rated as more typical of medicine names (M = 4.19, 95% CI [3.95, 4.43]) than difficult to
pronounce words (M = 2.70, 95% CI [2.45, 2.95]); mean difference = 1.49, (95% CI [1.22, 1.76],
F (1, 99) = 120.85, p < .001, partial eta
2
= .550). These main effects were qualified by an
interaction, F (1, 99) = 4.05, p = .047, partial eta
2
= .039. Simple effect analyses showed that the
real versus fictitious nature of the names exerted more influence on typicality when the words
were difficult to pronounce, mean difference = 0.61 (95% CI [0.43, 0.80], F (1, 99) = 43.31, p
< .001, partial eta
2
= .304), rather than easy to pronounce, mean difference = 0.36 (95% CI [0.18,
0.53], F (1, 99) = 16.21, p < .001, partial eta
2
= .141).
Harmfulness Ratings. Replicating SS, fictitious medicines were rated as more harmful
when their names were difficult (M = 4.43, 95% CI [4.23, 4.64]) rather than easy to pronounce
(M = 3.91, 95% CI [3.71, 4.12]); mean difference = 0.52, 95% CI [0.34, 0.70], F (1, 99) = 32.48,

74
p < .001, partial eta
2
= .247. In addition, BV’s misspelled real medicines were rated as less
harmful (MBV = 4.10, 95% CI [3.90, 4.30]) than SS’s fictitious medicines (MSS = 4.24, 95% CI
[4.06, 4.43]); mean difference = -0.14 (95% CI [-0.24, -0.04], F (1, 99) = 7.66, p = .007, partial
eta
2
= .072). These main effects were qualified by a nonsignificant interaction, F (1, 99) = 3.40,
p = .068, partial eta
2
= .033. Simple effect analyses confirmed that the influence of
pronounceability holds for BV’s stimuli, mean difference = 0.41 (95% CI [0.23, 0.60], F (1, 99)
= 18.83, p < .001, partial eta
2
= .160), and SS’s stimuli, mean difference = 0.62 (95% CI [0.39,
0.85], F (1, 99) = 28.26, p < .001, partial eta
2
= .222).
Experiment 4.2
In Experiment 4.1, we found that SS items and BV items matched for variation in
pronounceability demonstrated significant fluency effects. In Experiment 4.2 (preregistered at
http://aspredicted.org/blind.php?x=zw7m5m), we investigated whether the size of the fluency
effect depends on item to item variability in fluency. We presented items from Experiment 4.1 in
an order that either maximized or minimized item-to-item variation in pronounceability while
keeping variation across the set as a whole constant.
Method
Design. We used a 2 (pronounceability: three most easy to pronounce items vs. three
most difficult to pronounce items) by 3 (item order: easy to hard, hard to easy, or mixed list
order) mixed design, with pronounceability as a within-subjects factor and item order as a
between-subjects factor. Participants saw one of the two sets of items to control for item effects.
We preregistered the key analysis of comparing the means of the three most easy to pronounce
and three most difficult to pronounce items to allow us to directly compare the size of the
fluency effect for the same items when they appeared in different locations in the list – either in

75
the locations minimizing variation in pronunciation from one item to the next (by presenting
items in an order slowly increasing or decrease in pronounceability) or in locations that
maximized variation in pronounceability from one item to the next (in the mixed list where the
easiest and most difficult to pronounce items were interspersed with each other).
Participants. Of primary interest is a predicted interaction of item pronounceability,
manipulated within participants, and item order, manipulated between participants. We
conducted a power analysis using G*power software, aiming for 80% power for this interaction,
assuming a small effect size (f = .10) and a 0.5 correlation between repeated measurements (Faul,
Erdfelder, Lang, & Buchner, 2007). Based on this analysis we recruited 246 MTurk users
necessary to achieve this power. One participant was excluded because they reported an age
below 18, leaving us with a total N = 245 (list order: easy to hard N = 81, hard to easy N = 82,
mixed N = 82), Mage = 37.06, SDage = 13.11, 49.0% male, 51.0% female. The study was expected
to take 3 - 5 minutes and participants were paid $0.36 for completing it.
Materials. We chose our words from the fifty words created by Bahník and Vranka’s
(2017) study 5, which had been normed for pronounceability in an MTurk population (1 = easy
to pronounce, 5 = hard to pronounce). After ordering the words from easiest to pronounce to
most difficult to pronounce, we created two lists by taking every fifth word starting with the first
word (item set A) or by taking every fifth word starting with the second word (item set B). These
ten items were then presented to participants in one of three orders: an up ladder going from
easiest to most difficult to pronounce words, a down ladder from most difficult to easiest to
pronounce words, or in a mixed order in which words largely alternated between easy and
difficult to pronounce words (4, 10, 3, 8, 1, 9, 2, 7, 6, 5, with 1 = easiest to pronounce, 10 = most

76
difficult to pronounce). Full lists of these items and their orders in each condition can be found in
Table 4.3.
Procedure. Participants were given the same medicine scenario as in Experiment 4.1.
However, we dropped the typicality ratings and only asked participants to assess the harmfulness
of each medicine with the question, “How potentially harmful would you think this medicine
is?” (1 = very safe; 7 = very harmful). Unlike Experiment 4.1, where participants saw a list of all
items at the same time, here participants only saw one medicine name appear on each screen at a
time and had to rate it before viewing the next item.
Results
We ran a 2 (pronounceability: three most easy to pronounce items vs. three most difficult
to pronounce items) by 3 (item order: easy to hard, hard to easy, or mixed) mixed model
ANOVA, with pronounceability as a within-subjects factor and item order as a between-subjects
factor. The risk ratings serve as the dependent variable.
We replicated the typical fluency effects on risk rates; the three easiest to pronounce
medicines were rated as less harmful (M = 4.23, 95% CI [4.10, 4.36]) than the three most
difficult to pronounce medicines (M = 4.69, 95% CI [4.57, 4.82], raw mean difference = -0.46,
95% CI [-0.61, -0.31], F (1, 242) = 37.37, p < .001, partial eta
2
= .134). There was no main effect
of item order on risk ratings, F (2, 242) = 0.30, p = .740, partial eta
2
= .002, partial eta
2
= .001,
nor did item order qualify the main effect of ease of pronunciation, F (2, 242) = 0.09, p = .910,
for the interaction.
Adding item set as a between subjects factor revealed an unexpected main effect of item
set, indicating that item set A (M = 4.63, 95% CI [4.49, 4.78]) was perceived as more risky than
item set B (M = 4.30, 95% CI [4.15, 4.44], mean difference = 0.34, 95% CI [0.13, 0.54], F (1,

77
239) = 10.50, p = .001, partial eta
2
= .042. Moreover, a significant interaction of
pronounceability and item set emerged, F (1, 239) = 16.12, p < .001, partial eta
2
= .063.
Following this up with simple effects analysis using a Bonferroni adjustment for multiple
comparisons showed a significant fluency effect with item set 1, mean difference = 0.75, 95% CI
[0.55, 0.96], F (1, 239) = 53.15, p < .001, partial eta
2
= .182, but not with item set 2, mean
difference = 0.17, 95% CI [-0.04, 0.37]), F (1, 239) = 2.66, p = .104, partial eta
2
= .011. There
was no significant interaction of item set with list order, F (2, 239) = 1.21, p = .327, partial eta
2

= .009, and no significant three-way interaction, F (1, 239) = 1.09, p = .337, partial eta
2
= .009.
To explore why only one set of items showed a significant truth effect, we examined the
means of individual items to investigate whether there were any obvious item effects. This
seemed to be the case. For example, the difficult to pronounce item “Radiogvrdase” in item set A
achieved a risk rating of 5.29 (SD = 1.40) compared to only 4.44 (SD = 1.3) to the item
Azathioprpne matched for pronounceability in item set B. Similarly, the item “Memhsuximide”
in item set B was given a risk rating of 5.21 (SD = 1.42) in item set A compared to the matched
item of “Imiglucrrase” in item set B (M = 4.08, SD =1.44). A full report of by-item harm ratings
can be found in Table 4.4. Because these words were taken from real medicine names, it seems
plausible that some parts of these words are already associated with danger or safety. So an item
starting with “radio” may seem dangerous because of past associations (e.g., “radioactive), while
an item with “gluc” in it (e.g., “imiglucrrase” may seem less dangerous because of past
associations (e.g., “glucose”) – even though both are difficult to pronounce. We tried to correct
for this potential confound in Experiments 4.3 – 4.4 by using randomly generated stimuli that
would be less likely to be confounded by potentially meaningful past associations than the
misspelled medicine names used by BV.

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Experiments 4.3 - 4.4
In Experiments 4.3 (preregistered at http://aspredicted.org/blind.php?x=7y9wi3) and
Experiment 4.4 (preregistered at http://aspredicted.org/blind.php?x=vm6g78), we replicated the
methods of Experiments 4.2 with different stimuli: two sets of 10 alleged eBay usernames. We
investigated whether participants with easier to pronounce usernames would seem more
trustworthy than participants with difficult to pronounce usernames. Experiment 4.3 was
conducted with participants on MTurk and Experiment 4.4 was conducted in the University of
Southern California (USC) subject pool.
Method
Design. Matching Experiment 4.2, each experiment used a 2 (pronounceability: three
most easy to pronounce items vs. three most difficult to pronounce items) by 3 (item order: easy
to hard, hard to easy, or mixed) mixed model design, with pronounceability as a within-subject
factor and item order as a between-subject factor.
Participants. In Experiment 4.3, we again aimed to recruit 246 MTurk participants, and
ended up with 247 total (list order: easy to hard N = 81, hard to easy N = 83, mixed N = 83), Mage
= 36.42, SDage = 11.34, 57.5% male, 42.5% female. The study was expected to take 3 - 5 minutes
and participants were paid $.36 for completing it.
In Experiment 4.4, we recruited 246 participants. One response was excluded because the
participant had already previously completed the survey, leaving us with 245 responses (item
order: easy to hard N = 81, hard to easy N = 82, mixed N = 82), Mage = 20.26, SDage = 2.28 (two
not reporting); 25.7% male, 73.9% female, 1 participant not reporting. Participants took part in
the study in exchange for course credit.

79
Materials. In Experiments 4.3 and 4.4, we used 10 letter pseudowords created by Bahník
(2017) as our stimuli. These stimuli were created using a Python program and were not based on
any existing usernames. Participants were told these items were eBay usernames (similar to Silva
et al., 2017). Our goal was to create a set of items that spanned the range from the easiest to the
most difficult to pronounce names to allow for as much variation in pronounceability as possible.
To do this, we first ran a new norming of the pronounceability of a subset of 50 of the 120
original pseudowords in an MTurk sample from the United States to more closely match the
population with which we could be conducting the study. Each participant saw a random
selection of 25 pseudowords. For each of the words presented, we asked participants to rate how
easy or difficult it was for them to pronounce that word on an unnumbered 7 point scale with
endpoints of “easy to pronounce” (coded as 1) and “difficult to pronounce” (coded as 7). We
looked at the ratings for the easiest to pronounce word and the rating for the most difficult to
pronounce word. We then divided this range by 10 and picked the items with the ratings closest
to these values to create two sets of 10 words that spanned the full range of pronunciation ratings
as evenly as possible. For a full list of these items and their pronunciation ratings, see Table 4.5,
and for a list of item orders, see Table 4.6.
Procedure. Participants were asked to imagine they are buying an item on eBay and see
several sellers. They were shown the usernames of ten sellers and, for each username, answered
the question, “How trustworthy do you think this seller is?” on a 7 point scale (1 = not at all
trustworthy, 7 = very trustworthy).
In Experiment 4.4, we followed the same procedures with a modification aimed to
address concerns that participants may not be fully reading the usernames before making their
ratings. First, prior to introducing participants to the task, participants were asked to ensure they

80
had no interruptions for the next three minutes so they could complete the task in one sitting.
Second, participants were told they would see each username for several seconds and to read
each username carefully as it appeared. During the task itself, each username appeared alone on
the screen underneath the question “How trustworthy do you think this username is?” for four
seconds before the rating scale appeared for participants to make their judgment.
Results
Following our preregistered analysis protocol, we compare the trustworthiness ratings of
the three most easy and three most difficult to pronounce names as a function of experimental
conditions.
Experiment 4.3. A main effect of pronunciation, F (1, 244) = 121.65, p < .001, partial
eta
2
= .333, reflects that eBay sellers with easier to pronounce usernames were rated as more
trustworthy (M = 4.03, 95% CI [3.87, 4.18]) than eBay sellers with difficult to pronounce
usernames (M = 3.21, 95% CI [3.03, 3.40]). There was no main effect of list order, F (2, 244)
= .03, p = .969, partial eta
2
< .001, or interaction of item pronunciation and list order, F (2, 244)
= 2.12, p = .122, partial eta
2
= .017.
Since there were two sets of items, we also added in item set as a between-subjects
variable to this analysis. There was no significant main effect of item set, F (1, 241) = 1.15, p
= .284, partial eta
2
= .005, interaction with list order F (2, 241) = 2.04, p = .132, partial eta
2

= .017, or three-way interactions F (2, 241) = 2.15, p = .119, partial eta
2
= .018, but there was a
significant interaction with pronunciation F (1, 241) = 9.81, p = .002, partial eta
2
= .039, such
that there was a larger fluency effect with item set 2, mean difference = 1.05, 95% CI [0.84,
1.25] than with item set 1, mean difference = 0.59, 95% CI [0.39, 0.79].

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Experiment 4.4. Again, a main effect of pronunciation on trustworthiness ratings, F (1,
242) = 299.59, p < .001, partial eta
2
= .553, indicates that eBay sellers with easier to pronounce
usernames were rated as more trustworthy (M = 3.66, 95% CI [3.52, 3.80]) than eBay sellers
with difficult to pronounce usernames (M = 2.46, 95% CI [2.33, 2.59]). There was no main effect
of list order, F (2, 242) = 2.78, p = .064, partial eta
2
= .022, and no significant interaction of item
pronunciation and list order, F (2, 242) = 0.54, p = .518, partial eta
2
= .004.
Adding in item set as a between-subjects factor, there was no significant main effect of
item set, F (1, 239) = 0.36, p = .548, partial eta
2
= .002, interaction with list order, F (2, 239) =
0.67, p = .513, partial eta
2
= .006, or three way interaction, F (2, 239) = 1.45, p = .238, partial
eta
2
= .012, but there was a significant interaction with pronunciation, F (1, 239) = 17.25, p
< .001, partial eta
2
= .067, such that there was a larger fluency effect with item set 2, mean
difference = 1.48, 95% CI [1.29, 1.66] than item set 1, mean difference = 0.92, 95% CI [0.73,
1.11].
Discussion
Overall, we found robust fluency effects on risk perception using variation in
pronounceability as our fluency manipulations. These effects were not “limited only to the
original items used by Song and Schwarz” (BV, p. 430) but also obtained with BV’s original
stimuli in Experiment 4.1 and 4.2 and stimuli borrowed from Bahník (2017) in Experiments 4.3
and 4.4. Pronounceability effects were also obtained when holding the word length of stimuli
constant and only manipulating pronounceability (Exp. 4.3-4.4), ruling out the possibility that
only word length – and not changes in pronounceability – influences risk judgments of specific
stimuli. These effects also held up across studies using both fixed and mixed effects analysis
approaches, with full mixed effects analysis results reported in the supplementary materials.

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Importantly, fluency effects on risk perception are robust but are not solely driven by
pronunciation, which is consistent with theory. Other influences on processing fluency, like
word length, past exposure, or print font, would be expected to have similar effects. And
indeed, some inputs may result in larger fluency changes than others. For example, word
length may result in significantly larger fluency changes than pronounceability, reducing the
relative impact of pronounceability on fluency and limiting its impact. But while the relative
contributions of fluency manipulations like word length may be isolated and experimentally
manipulated, these factors bear similarly on the basic question of, "Are familiar things
perceived as less risky?"
Additionally, it is also important to draw attention to the fact that processing fluency is
not the only possible input into risk judgments: substantive information derived from the stimuli
and the context is also used (e.g., Tasso, et al. 2014 for a relevant example with medication
names). In this case, BV stimuli were created in such a way as to more closely resemble real
medications, which made them seem more typical of the class of items being judged. This
typicality may be used as an input to risk assessment, leading these items to generally seem less
safe and reduce the relative impact of changes in pronounceability. Indeed, we found higher
typicality ratings and a smaller impact of pronounceability for BV items in our Experiment 4.1.
Second, due to the similarity of BV items to real items, there was more substantive information
that could be derived from the item’s familiar suffixes and prefixes that could be brought to bear
on these judgments. For example, we found the BV item “Radiogvrdase” being judged to be
riskier than other similarly difficult to pronounce items in Experiment 4.2, likely due to
containing the “radio” which is a prefix associated with risk (e.g., radioactive). The perceived

83
typicality and item idiosyncrasies of BV items may explain why fluency effects could be easier
to obtain with SS items.
Interestingly, item to item variation in fluency was less relevant than expected based on
fluency findings in other domains (e.g., truth, Dechêne et al. 2009). Across Experiments 4.2-4.4,
we found little evidence that presenting items in a way that maximized item to item changes in
fluency increased the impact of pronounceability on judgments of risk. Future research may seek
to establish the conditions which moderate the impact of item to item variations in fluency. In
our case, perhaps since participants saw a smaller number of items that spanned a large range of
pronounceability, the order in which items were presented had less of an impact than if
participants were viewing more items that had less variation.
If it's difficult to pronounce, it might be risky. But pronunciation does not work in
isolation; if it's unfamiliar, lengthy, and atypical for the judgment at hand, it might also be risky.
We find evidence that manipulating pronounceability in isolation influences perceived risk (Exp.
4.3-4.4). But more broadly, whether or not pronounceability is manipulated in isolation, the role
of other inputs – whether bear on processing fluency or more substantive aspects of the target
judgment - should not be ignored.

84
General Discussion
Across four chapters, I investigated how a wide array of contextual factors influence
metacognitive experiences of truth and risk. I consistently find that these influences do not act in
isolation, but rather interact with a wide array of variables such as the presence of warnings,
individual differences in processing style, and other features of the target of judgment.
Understanding this interplay between processing experience and context is key for providing
effective recommendations for misinformation correction in real-world settings. The
investigations presented in this dissertation have a number of implications for future research
addressing this issue, a few of which I highlight below.
First, researchers should pay careful attention to how the conditions present in laboratory
investigations differ from the conditions present in the real world. For example, while
researchers often warn participants about the presence of falsehoods during truth studies, false
information in the real world rarely comes with a warning label. The presence of this common
experimental feature has likely led to an underestimation of the impact of repetition on belief in
the real world for decades (Chapter I).
Second, researchers should consider the role of elaborative processing in how judgments
are made across time. While thinking more may be effective in preventing false beliefs in the
short term, elaborating more about information now also means that it will feel more familiar -
and potentially more true - when encountered again in the future (Chapter II). Along the same
lines, researchers should take into account how expectations and associations people have
formed about the world through past experiences match the current context. Consistency of
associative knowledge and context may lead to experiences of fluency, while inconsistency may

85
lead to disfluency. These experiences may then be brought to bear on the judgment at hand
(Chapter III).
Finally, researchers should pay close attention to what other inputs are present at the time
of judgment as people are more sensitive to changes in processing experience than to its absolute
level. For example, a claim presented on a well-designed website may seem more true after
viewing a poorly designed website, and an unfamiliar medication may seem less safe when
viewed along with familiar ones (Chapter IV).
Final word
When deciding what is true and what to trust, people are often influenced by
metacognitive experiences of processing ease or difficulty resulting from factors that are
irrelevant to the judgment at hand. The biasing effects of these feelings can occur even in the
presence of more substantive information that bears on truth. Given the current state of social
media and political polarization, it is more important than ever to develop effective
misinformation prevention and correction strategies. Unfortunately, no one recommendation is
likely to be universally effective; in fact, what is effective in one context may have little impact
or even backfire in another. Instead, interventions should carefully consider how judgments are
formed in the real world and carefully tailor recommendations to match the context at hand.

86
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102
Appendix A: Chapter I Figures

Figure 1.1. Mean truth ratings across warning conditions for new and repeated claims after a
three to six day delay in Experiment 1.1. Participants either received a warning that half of the
claims were false prior to exposure only or no warning. Truth ratings were made on an
unnumbered six-point scale from “definitively true” (coded as 6) to “definitely false” (coded as
1). Error bars are 95% confidence intervals.
3.0
3.5
4.0
4.5
5.0
5.5
No Warning Pre-Exposure Warning Only
Truth Rating
1 = definitely false, 6 = definitely true
Warning Condition
New claims
Repeated claims

103

Figure 1.2. Mean truth ratings across warning conditions for new and repeated claims in
Experiment 1.2. Participants either received a warning that half of the claims were false prior to
exposure and test, prior to test only, or did not receive a warning. Truth ratings were made on an
unnumbered six-point scale from “definitively true” (coded as 6) to “definitely false” (coded as
1). Error bars are 95% confidence intervals.
3.0
3.5
4.0
4.5
5.0
5.5
No Warning Pre-Test Warning Only Pre-Exposure + Pre-Test
Warning
Truth Rating
1 = definitely false, 6 = definitely true
Warning Condition
New claims
Repeated claims

104

Figure 1.3. Mean truth ratings for repeated and new claims across warning timing conditions in
Experiment 1.3. Participants received a warning that “some” or “half” of claims were true and
“some” or “half” of claims were false. In the pre-exposure and pre-test warning condition,
participants received a warning prior to initial exposure to trivia claims and prior to test. In the
pre-test warning only condition, participants received a warning prior to test only. Truth ratings
were made on an unnumbered six-point scale from “definitively true” (coded as 6) to “definitely
false” (coded as 1). Error bars are 95% confidence intervals.

3.0
3.5
4.0
4.5
5.0
5.5
Pre-Test Warning Only Pre-Exposure + Pre-Test Warning
Truth Rating
1 = definitely false, 6 = definitely true
Warning Condition
New claims
Repeated claims

105

Figure 1.4. Effect sizes (d unbiased) for the truth effect across all experiments and warning
timing conditions. These effects represent 95% confidence intervals.
All conditions overall
No warnings overall
Experiment 1.3
Experiment 1.1
Pre-test warning only overall
Experiment 1.3
Experiment 1.2
Pre-exposure warning overall
Experiment 1.3
Experiment 1.2
Experiment 1.1
-1.5 -1 -0.5 0 0.5 1 1.5 2 2.5 3
Cohen's d (unbiased) and 95% CI
Pre-exposure warning
Pre-test warning only
No warnings

106
Appendix B: Chapter I Supplementary Materials
Trivia claims
Trivia Claims Counterbalance 1
Claim
number
Category Claim
True
or
False
Proportion
of people
who said
true
1 Sports Volleyball was originally called mintonette True 0.35
2 Animals Walruses use their tusks primarily for mating True 0.4
3 Geography Greenland is a part of the Kingdom of Denmark True 0.41
4 Sports The stationary ball in lawn bowls is called a jack True 0.44
5 Science
In almost all human populations of newborns, there
is a slight excess of males
True 0.46
6 Animals Domesticated goats are descended from the pasang True 0.49
7 Food
Kava is a beverage made from the root of the
pepper plant
True 0.49
8 Geography
Lake Baikal is the world's largest freshwater lake
by volume
True 0.52
9 Animals
Female turkeys generally weigh half as much as
males
True 0.52
10 Food The lima bean is also known as the sieva bean True 0.54
11 Food Halvah is a confection made of sesame seeds True 0.54
12 Science Normal color vision is known as trichromacy True 0.56
13 Sports Dart boards are commonly made of sisal True 0.57
14 Animals Snakes lack movable eyelids True 0.58
15 Food Couscous is a dish from Africa True 0.58
16 Science
The sun constitutes more than 99 percent of the
entire mass of the solar system
True 0.6
17 Sports
The stones used in curling are concave on the
bottom
True 0.6
18 Sports Rugby is played with an oval ball True 0.65
19 Food The grape plant is a large herb False 0.35
20 Sports
The Chicago Marathon is the world’s oldest annual
marathon
False 0.42
21 Food
Kvass is an alcoholic beverage fermented from
honey
False 0.42
22 Animals Sheep are a type of tylopod mammal False 0.44
23 Science
Levels of the metal iridium are lower in meteorites
than on Earth
False 0.45
24 Geography The monetary unit in Afghanistan is the rupee False 0.48

107
25 Geography
Europe has the highest average elevation of the
continents
False 0.49
26 Food Spain produces most of the world's almonds False 0.5
27 Geography The Nile river flows southward False 0.51
28 Sports Competitive badminton is usually played outdoors False 0.52
29 Food Dough is boiled in the process of making croissants False 0.52
30 Geography The highest waterfall in the world is in Argentina False 0.54
31 Sports Biking is the first event in a triathlon False 0.56
32 Animals The mouth of a sea urchin is on its top False 0.58
33 Geography
The Swazi are the single largest ethnic group in
South Africa
False 0.59
34 Sports
Candlepins is the most widely played variation of
bowling
False 0.63
35 Sports Tennis has been traced back to the baths of Rome False 0.63
36 Science Endothermic reactions release chemical energy False 0.65

108
Trivia Claims Counterbalance 2
Claim
number
Category Claim
True
or
False
Proportion
of people
who said
true
1 Sports Bandy is a game similar to ice hockey True 0.37
2 Animals Moose may dive underwater while feeding True 0.39
3 Animals Most sea turtles are carnivorous True 0.41
4 Food The Colchester is a popular type of oyster True 0.41
5 Animals Both sexes of lions are polygamous True 0.46
6 Geography Taboga Island is in Panama True 0.46
7 Sports In foxhunting, the hunter usually wears a red shirt True 0.52
8 Science Pluto is part of the Kuiper belt True 0.52
9 Food Cabbages are in the mustard family True 0.54
10 Animals Guinea pigs belong to the cavy family True 0.54
11 Science Sublimation refers to a substance changing states
from solid to vapor
True 0.55
12 Animals The flamingo's pink color comes from carotenoid
pigments in its food
True 0.56
13 Science Xylem is the water-transporting tissue in plants True 0.57
14 Sports Fly-fishing is the oldest method of recreational
fishing
True 0.58
15 Geography Vesuvius is an active volcano in Italy True 0.59
16 Science Glia cells function primarily to support neurons. True 0.59
17 Geography Canada is the second largest country in the world
in area
True 0.61
18 Food Most limes have more acid than lemons True 0.63
19 Science Orbital velocity is the steady speed achieved by an
object freely falling
False 0.39
20 Sports The longbow was invented after the crossbow False 0.39
21 Food Corn was first domesticated by native peoples in
Argentina
False 0.42
22 Animals The otter belongs to the squirrel family False 0.43
23 Geography Finland is the least densely forested country in
Europe
False 0.45
24 Food Sticky toffee pudding is a classic Polish dessert False 0.45
25 Science The electron is the heaviest charged particle found
in nature
False 0.5
26 Science None of the genes in baker's yeast are also present
in humans
False 0.5
27 Animals Giraffes have terrible eyesight False 0.51

109
28 Geography The Carpathian Mountains form a high wall
between France and Spain
False 0.52
29 Sports Snowboarding is believed to have originated in
Europe
False 0.53
30 Science Night blindness is a symptom of vitamin D
deficiency
False 0.54
31 Sports The heptathlon, in athletics, is a footrace over an
obstacle course
False 0.58
32 Sports Slalom skiing is the navigation of large bumps on
the ski slope
False 0.58
33 Science In chemistry, a mass spectrometer is used to
separate substances into its constituent parts
according to color
False 0.63
34 Geography The Caspian Sea is the lowest body of water on the
surface of Earth
False 0.63
35 Food Mayonnaise is usually made with raw egg whites False 0.63
36 Food Sherbert has less sugar than ice cream False 0.63

110
Recruiting and Attrition Information

Experiments 2 and 3 had a relatively large number of MTurk participants who started the studies
without completing them. Most of these dropouts occurred when participants hit the delay task
about 5 minutes in, which was relatively tedious and boring. While it is common to have drop-
outs in online experiments, we checked that the drop-out rate did not vary by warning condition
to ensure that there was no differential attrition.

Experiment 1.1
Performed before exclusions
Number of people who opened survey: 280
Number of people assignment a warning condition and completed part 1: 276
Number of people who completed both parts of study: 243

Pre-test warning only
Pre-exposure and pre-test
warning
Total: 138
Finished: 125
Dropped out: 13
Total: 138
Finished: 118
Dropped out: 20

Finish: Got to the point where they saw the completion code
Dropped out: Did not get to the point where they saw the completion code

Chi-squared test
No differential attrition, X
2
= (1, N = 276) = 1.69, p = .194

Experiment 1.2
Performed before exclusions
Number of people who started study: 524
Number of people who got past consent: 486

Warning pre-exposure and pre-
test
Warning pre-test only No warning
Total: 174
Finished: 101
Dropped out: 73
Total: 162
Finished: 98
Dropped out: 64
Total: 150
Finished: 98
Dropped out: 52

No differential attrition, X
2
= (2, N = 486) =1.839, p = .399

Experiment 1.3
Performed before exclusions
Number of people who started study: 696
Number of people who got past consent and were assigned a warning condition: 649

111

Pre-test warning only
Pre-exposure and pre-test
warning
“Some” warning
Total: 176
Finished: 106
Dropped out: 70
Total: 174
Finished: 100
Dropped out: 74
“Half” warning
Total: 150
Finished: 98
Dropped out: 52
Total: 149
Finished: 101
Dropped out: 48

Some condition: pre-test warning only or pre-exposure and pre-test warning, finished or did not
finish, X
2
= (1, N = 350) = .274, p = .600 -> no differential attrition,

Half condition: pre-test warning only or pre-exposure and pre-test warning, finished or did not
finish: X
2
= (1, N = 299) = .202, p = .653 -> no differential attrition,

Overall conditions
Pre-test warning only or pre-exposure and pre-test warning: X
2
= (1, N = 649) = .008, p = .927 ->
no differential attrition,

Some or half condition, X
2
= (1, N = 649) = 4.73, p = .044 -> more likely to drop out overall in
the “some” warning condition than in the “half” warning condition.

112
Truth Effect Warnings Instructions from Exposure and Test Phases

Experiment 1.1
[Part 1]

Welcome

Page Break

This is a two part online study. This part of the study takes 5 minutes and Part 2 takes 10
minutes. Part 2 will be emailed to you three days after you complete this study and must be
finished within 48 hours. You will receive credit after you complete Part 2.

Page Break

[Information sheet]

Page Break

For approximately the next three minutes, you will see a series of trivia statements.

[Pre-exposure warning condition only:] Half of these trivia statements are true, and half of
these trivia statements are false.

The trivia statements will be presented automatically - there is no need to press any buttons.
Please read the trivia statements carefully as they are presented, but do not do anything else. You
will not be able to pause the study, so make sure you have no distractions.

Press the next button to begin.

Page Break

[Claim presentation here]

Page Break

How long did the task of reading the trivia statements feel?

113

Went by
quickly

Lasted
forever

()

Page Break

How interesting were the trivia statements?

Not interesting
at all

Extremely
interesting

()

Page Break

Without looking at the clock, please answer the following questions

How many minutes did it take to complete the whole study up to this point?
________________________________________________________________

Just thinking about reading the trivia statements, how many minutes do you think it took you to
read the statements?
________________________________________________________________

[Part 1 wrap up]

[Part 2]

Welcome

Page Break

114
This is Part 2 of a two part study on trivia claims. This part of the experiment is expected to take
around 10 minutes and you will receive .5 credits once the study is completed.

Please click continue to indicate you have read the information above and are ready to start the
experiment:

• Continue

Page Break

You will now see a series of trivia statements appear on the screen.

Half of these statements are the same ones that you saw in Part 1 of the study, and half are new.

You will be asked to assess whether each claim is true or false. When you see each statement
appear on the screen, please read it carefully and answer the following question:

Is this statement true or false?

You will be asked to answer this question on a scale from definitely true to definitely false.

Page Break

It is important that you respond as quickly as possible, but not so quickly that you start making
errors.

Page Break

Please do not search the answers online while you are completing the study;
if you are unsure of an answer please just make your best guess.

Page Break

Now, you will see a series of trivia statements.

As a reminder, for each trivia statement you will be answering the following question:

Is this statement true or false?

Please go on to the next page to begin.

115
Page Break

[Trivia claim truth judgments here]

Page Break

[Demographics/ wrap-up]
Experiment 1.2

Welcome

Page Break

[Information sheet]

Page Break

For approximately the next three minutes, you will see a series of trivia statements.

[Pre-exposure + pre-test warning condition only:] Half of these trivia statements are true, and
half of these trivia statements are false.

The trivia statements will be presented automatically - there is no need to press any buttons.
Please read the trivia statements carefully as they are presented, but do not do anything else.

Press the next button to begin.

Page Break

[Claim presentation here]

Page Break

[Delay task]

Page Break

You will now see another series of trivia statements appear on the screen.

116
Half of these statements are ones that you have already seen, and half are new. [Pre-test
warning only and Pre-exposure + pre-test warning conditions]: Half of these statements are
true, and half are false.

You will be asked to assess whether each claim is true or false. When you see each statement
appear on the screen, please read it carefully and answer the following question:

Is this statement true or false?

You will be asked to answer this question on a scale from definitely true to definitely false.

Page Break

It is important that you respond as quickly as possible, but not so quickly that you start making
errors.

Page Break

Please do not search the answers online while you are completing the study;
if you are unsure of an answer please just make your best guess.

Page Break

Now, you will see a series of trivia statements.
As a reminder, for each trivia statement you will be answering the following question:

Is this statement true or false?

Please go on to the next page to begin.

Page Break

[Trivia claim truth judgments here]

Page Break

[Demographics/ wrap-up]
Experiment 1.3

Welcome

117

Page Break

[Information sheet]

Page Break

For approximately the next three minutes, you will see a series of trivia statements.

[Pre-exposure + pre-test warning condition only:] Half (some) of these trivia statements are
true, and half (some) of these trivia claims are false.

The trivia statements will be presented automatically - there is no need to press any buttons.
Please read the trivia statements carefully as they are presented, but do not do anything else.

Press the next button to begin.

Page Break

For approximately the next three minutes, you will see a series of trivia statements.

The trivia statements will be presented automatically - there is no need to press any buttons.
Please read the trivia statements carefully as they are presented, but do not do anything else.

Press the next button to begin.

Page Break

[Claim presentation here]

Page Break

[Delay task]

Page Break

You will now see another series of trivia statements appear on the screen.

Half of these statements are ones that you have already seen, and half are new. Half (some) of
these statements are true, and half (some) are false.

118
You will be asked to assess whether each claim is true or false. When you see each statement
appear on the screen, please read it carefully and answer the following question:

Is this statement true or false?

You will be asked to answer this question on a scale from definitely true to definitely false.

Page Break

It is important that you respond as quickly as possible, but not so quickly that you start making
errors.

Page Break

Please do not search the answers online while you are completing the study;
if you are unsure of an answer please just make your best guess.

Page Break

Now, you will see a series of trivia statements.

As a reminder, for each trivia statement you will be answering the following question:

Is this statement true or false?

Please go on to the next page to begin.

Page Break

[Trivia claim truth judgments here]

Page Break

[Demographics/ wrap-up]

119

Raw means and standard deviations for truth judgments

Experiment Repetition Warning condition

Pre-exposure
and pre-test
warning
Pre-exposure
warning only
Pre-test
warning only
No warning Overall
M SD M SD M SD M SD M SD
Experiment
1.1
New claims 3.47 0.38 3.56 0.42 3.52 0.40

Repeated
claims
3.84 0.60 4.37 0.73 4.11 0.72
Overall 3.66 0.43 3.96 0.48 3.81 0.48
Experiment
1.2
New claims 3.58 0.49 3.42 0.67 3.43 0.56 3.48 0.58

Repeated
claims
4.03 0.71 4.89 0.89 4.77 0.96 4.56 0.94
Overall 3.80 0.49 4.15 0.54 4.10 0.56
4.01
7
0.55
Experiment
1.3
New claims 3.51 0.45

3.48 0.57

3.49 0.51

Repeated
claims
3.90 0.70

4.68 0.97

4.29 0.93

Overall 3.70 0.45

4.08 0.63

3.89 0.58

120
Supplementary data analysis
We give a detailed report for the additional analysis summarized in the primary chapter.
Experiment 1.1
Discrimination and response bias
We investigated whether pre-exposure and pre-test warnings influenced participants’
ability to accurately discriminate between true and false claims using a signal detection approach
(Stanislaw & Todorov, 1999) in each of our three experiments. We also looked at whether these
warnings impacted response bias to say a claim was true. To do his, we first converted the
unnumbered six-point scale used in the experiments (ranging from “definitely true”, coded as 6,
to “definitely false”, coded as 1) to a binary measure, with values from 1 to 3 treated as “false”
and values from 4 to 6 treated as “true”.
We report discrimination (d’) and response bias (c) as our outcome measures following
the produce described by Stanislaw and Todorov (1999). We report means and standard
deviations for d’, c, hit rates, and false alarm rates by warning timing condition in Table 1.1. We
used a common approach for dealing with extreme values, replacing hit and false rates of 0
with .5/n and hit and false alarm rates of 1 with (n-.5)/n, where n is the number of signal or noise
trials (Macmillan & Kaplan, 1985).
We performed a 2 (warning: before exposure only vs. no warning) x 2 (repetition: trivia
claim repeated vs. new) mixed model ANOVA for both d’ and c, with warning timing between
subjects and repetition within subjects. Overall, none of our manipulations influenced
discrimination. There was no main effect of repetition, F (1, 218) = 0.13, p = .721, partial eta
2

= .001, no main effect of warning, F (1, 218) = 2.64, p = .105, partial eta
2
= .012, and no
interaction of warning and repetition: F (1, 218) = 0.06, p = .805, partial eta
2
< .001.

121
Turning to response bias, we found a main effect of repetition, F (1, 218) = 101.46, p
< .001, partial eta
2
= .318, with participants more likely to say repeated claims were true (M = -
0.73, 95% CI [-0.84, -0.62]) than new claims (M = 0.09, 95% CI [0.01, 0.18], raw mean
difference = 0.82, 95% CI [0.66, 0.99]). There was also a main effect of warning, F (1, 218) =
16.96, p < .001, partial eta
2
= .072, with participants more likely to say claims were true with no
warnings (M = -0.43, 95% CI [-0.51, -0.46]), than when a pre-exposure warning was added (M =
-0.21, 95% CI [-0.28, -0.13], raw mean difference = -0.23, 95% CI [-0.34, 0.12]).
Importantly, there was a significant interaction of warning and repetition: F (1, 218) =
6.45, p = .012, partial eta
2
= .029. With no warning, participants were more biased to rate
repeated claims as true (M = -0.95, 95% CI [-1.10, 0.80]) than to rate new claims as true (M =
0.08, 95% CI [-0.04, 0.20]; raw mean difference = 1.03, 95% CI [.81, 1.26]). This bias was
attenuated with the additional of a pre-exposure warning (mean c repeated claims = -0.51, 95%
CI [-0.67, -0.36]; mean c new claims = 0.10, 95% CI [-0.02, 0.23]; raw mean difference: 0.62,
95% CI [0.39, 0.85]), and was driven by ratings of repeated claims. New claims did not differ
between warning conditions (raw mean difference = -0.02, 95% CI [-0.19, 0.15], F (1, 218) =
0.05, p = .818, partial eta
2
< .001). However, participants were more biased to rate repeated
claims as true when there was no warning than when there was a pre-exposure warning (raw
mean difference = -0.44, 95% CI [-0.65, -0.22]; F (1, 218) = 15.95, p < .001, partial eta
2
= .068).
This is consistent with the analysis of the continuous scale reported in the main manuscript.
Participants in both conditions were more likely to respond true to repeated claims than new
claims. However, pre-exposure warnings reduced this effect by making participants less likely to
judge repeated claims as true while leaving judgements of new claims the same.
Actual truth

122
We investigated whether warnings influenced claims that were factually true vs. factually
false differently by adding in the actual truth value of claims as a factor in our analysis. Thus, we
conducted a 2 (warning timing: before exposure only vs. no warning) x 2 (repetition: trivia claim
repeated vs. new) x 2 (truth value: true or false) mixed model ANOVA, manipulating warning
timing between subjects and repetition and truth value within subjects, with mean truth rating (1
= definitely false, 6 = definitely true) as the dependent measure.
Despite having previously normed the claims to have equivalent truth ratings for true and
false claims, there was a main effect of truth value, F (1, 218) = 72.13, p < .001, partial eta
2

= .249, with true claims (M = 3.94, 95% CI [3.87, 4.00]) rated significantly more true than false
claims (M = 3.68, 95% CI [3.61, 3.75]; raw mean difference = 0.26, 95% CI [0.20, 0.32]). There
was a significant interaction of truth value and warning condition, F (1, 218) = 4.36, p = .038,
partial eta
2
= .020, although this interaction did not replicate in Experiment 1.2 or 1.3, Fs < 0.34,
ps > .70. The difference between truth ratings of true and false claims was larger in the warning
condition (mean truth rating false claims = 3.50, 95% CI [3.40, 3.60]; mean truth rating true
claims = 3.82, 95% CI [3.72, 3.91]); raw mean difference = 0.32, 95% CI [0.23, 0.41]) than in
the no warning condition (mean truth rating false claims = 3.86, 95% CI [3.77, 3.96]; mean truth
rating true claims = 4.06, 95% CI [3.97, 4.15]); raw mean difference = 0.19, 95% [0.11, 0.28]).
The interaction of truth value and repetition did not meet significance, F (1, 218) = 0.18, p
= .669, partial eta
2
< .001, nor did the interaction of truth value, repetition, and warning, F (1,
218) = 0.15, p = .703, partial eta
2
= .001
Replicating our main results, there was a significant truth effect, F (1, 218) = 192.61, p
< .001, partial eta
2
= .469 and significant main effect of warning condition, F (1, 218) = 24.59, p

123
< .001, partial eta
2
= .101, with a significant interaction between repetition and warning, F (1,
218) = 26.87, p < .001, partial eta
2
= .110.
Experiment 1.2
Discrimination and response bias
We performed a 3 (warning timing: no warning, warning pre-test only, warning pre-
exposure and pre-test) x 2 (repetition: trivia claim repeated vs. new) mixed model ANOVA,
manipulating warning timing between subjects and repetition within subjects, for both d’ and c.
Means and standard deviations for d’, c, hit rate, and false alarms can be seen in Table 2.
Once again, none of our manipulations influenced discrimination. There was no main
effect of repetition: F (1, 279) = 0.78, p = .379, partial eta
2
= .003, no main effect of warning: F
(2, 279) = 0.26, p = .774, partial eta
2
= .002, and no interaction of warning and repetition, F (2,
279) = 0.99, p = .372, partial eta
2
= .007.
Looking at response bias, there was again a main effect of repetition, F (1, 279) = 229.79,
p < .001, partial eta
2
= .452, and warning, F (2, 279) = 229.79, p < .001, partial eta
2
= .452. The
interaction of warning and repetition was also significant, F (2, 279) = 5.43, p = .005, partial eta
2

= .037. People were more biased to respond true to repeated claims than to new claims across
warning conditions, but this effect was larger with no warning (raw mean difference = 1.41, 95%
CI [1.13, 1.70]; F (1, 279) = 95.39, p < .001, partial eta
2
= .255) or with a pre-test warning only
(raw mean difference = 1.43, 95% CI [1.16, 1.70]; F (1, 279) = 106.39, p < .001, partial eta
2
= .276) than with a pre-exposure and pre-test warning (raw mean difference = 0.86, 95% CI
[0.58, 1.13]; F (1, 279) = 37.81, p < .001, partial eta
2
= .119). While response bias for new
claims did not significantly differ across conditions, F (2, 279) = 2.67, p = .071, partial eta
2
= .019, people were more biased to judge repeated claims as true with no warning (M = -1.50,

124
95% CI [-1.70, -1.29]) or a pre-test warning only (M = -1.59, 95% CI [-1.79, -1.40]) when
compared to a pre-test and pre-exposure warning (M = -0.73, 95% CI [-0.93, -0.54]; both ps
< .001). There was no difference in response bias between the no warning and pre-test warning
conditions (p = .001). In sum, adding a pre-exposure warning resulted in participants being less
biased to judge repeated claims as true, but did not impact the ratings of new claims. Pre-test
warnings alone did not have this effect.
Actual truth
We performed a 3 (warning timing: no warning, warning pre-test only, warning pre-
exposure and pre-test) x 2 (repetition: trivia claim repeated vs. new) x 2 (truth value: true or
false) mixed model ANOVA, manipulating warning timing between subjects and repetition and
truth value within subjects, with mean truth rating (1 = definitely false, 6 = definitely true) as the
dependent variable.
We once again found a main effect of truth value, with true claims (M = 4.12, 95% CI
[4.00, 4.19]) rated more true than false claims (M = 3.91, 95% CI [.3.84, 3.99]; raw mean
difference = 0.21, 95% CI [0.15, 0.27]), F (1, 279) = 51.83, p < .001, partial eta
2
= .157. There
were no further interactions of truth value with repetition, F (1, 279) = 0.16, p = .695, partial eta
2

= .001, warning condition, F (2, 279) = 0.33, p = .716, partial eta
2
= .002, or three-way
interaction of truth value, repetition, and warning condition, F (2, 279) = 0.77, p = .464, partial
eta
2
= .005
Replicating our main results, there was a significant truth effect, F (1, 279) = 327.95, p
< .001, partial eta
2
= .540, significant main effect of warning condition, F (2, 279) = 13.40, p
< .001, partial eta
2
= .079, with a significant interaction between repetition and warning, F (2,
279) = 29.39, p < .001, partial eta
2
= .174.

125
Experiment 1.3
Discrimination and response bias
We performed a 2 (warning timing: before test vs. before exposure and before test) x 2
(warning content: “some” or “half”) x 2 (repetition: trivia claim repeated vs. new) mixed model
ANOVA, manipulating warning timing and warning content between subjects and repetition
within subjects for both d’ and c. Means and standard deviations for d’, c, hit rate, and false
alarms by warning timing and warning content conditions are reported in Table 1.3.
This time, we found a main effect of repetition on discrimination, F (1, 400) = 13.99, p
< .001, partial eta
2
= .034, with participants more accurate for repeated claims (M = 0.16, 95%
CI [0.11, 0.21]), than for new claims (M = 0.04, 95% CI [-0.01, 0.09]; raw mean difference =
0.12, 95% CI [0.06, 0.19]). However, the main effect of warning timing, F (1, 400) = 0.04, p
= .850, partial eta
2
< .001, and warning content, F (1, 400) = 1.33, p = .249, partial eta
2
< .001,
still failed to reach significance, as did all of the two-way interactions, all Fs < 1.24, ps > .268.
While a significant three-way interaction of repetition, warning timing, and warning content
emerged, F (1, 400) = 5.60, p = .018, partial eta
2
= .014, follow-up simple effects analysis with a
Bonferroni correction for multiple comparisons revealed this this interaction was driven by a
difference in the influence of warnings in the “some” vs “half” conditions on discrimination for
new vs. repeated claims. In the “some” warning condition, participants were more accurate for
repeated claims relative to new claims in the pre-exposure and pre-test warning condition, F (1,
400) = 7.09, p = .008, partial eta
2
= .017. When a pre-exposure warning was added, accuracy for
repeated and new claims did not significantly differ, F (1, 400) = 0.65, p = .422, partial eta
2

= .002. However, this pattern was reversed in the “half” warning condition, with participants
significantly more accurate for repeated claims relative to new claims without a pre-exposure

126
warning, F (1, 400) = 11.34, p = .001, partial eta
2
= .028, but showing no difference in accuracy
between repeated and new claims when given a pre-exposure and pre-test warning, F (1, 400) =
0.35, p = .556, partial eta
2
= .001.
Of particular relevance, pre-exposure warnings did not significantly increase overall
accuracy in either the “some” warning condition or the “half” warning condition (both Fs < 0.84,
ps > .512), nor did they significantly increase accuracy for any specific claim type (new or
repeated) within those conditions. In fact, the only single significant effect when looking at new
and repeated claims alone was in the opposite direction, with pre-exposure warnings decreasing
accuracy for repeated claims in the “half” warning condition relative to a pre-test warning only
condition (mean discrimination pre-test warning only = 0.22, 95% CI [0.13, 0.33]; mean
discrimination pre-test and pre-exposure warning: 0.07, 95% CI [-0.03, 0.17]; raw mean
difference = -0.15, 95% CI [-0.29, 0.00], F (1, 400) = 3.96, p = .047, partial eta
2
= .010; all Fs <
1.90, ps > .170 for other conditions). These results are consistent with Experiments 1 and 2
findings that pre-exposure warnings did not increase participants’ ability to accurately
discriminate between true and false claims.
Turning to response bias, we first found that there was no main effect of interactions of
the “some” or “half” warning manipulation: main effect: F (1, 400) = 2.81, p = .095, partial eta
2

= .007, interaction with repetition, F (1, 400) = .01, p = .937, partial eta
2
< .001, interaction with
warning condition, F (1, 400) = .05, p = .829, partial eta
2
< .001, three-way interaction, F (1,
400) = .112, p = .738, partial eta
2
< .001. As with the other experiments, there was a significant
main effect of repetition, F (1, 400) = 175.40, p < .001, partial eta
2
= .305, and warning, F (1,
400) = 65.73, p < .001, partial eta
2
= .141. Once again, the significant interaction of warning and
repetition emerged, F (1, 400) = 29.301, p < .001, partial eta
2
=.068. While participants were

127
more biased to say repeated claims were true relative to new claims in both warning conditions,
this bias was greater in the pre-test only warning condition (mean c repeated claims = -1.35, 95%
CI [-1.49, -1.22]; mean c new claims = -0.04, 95% CI [-.15, 0.06]; raw mean difference: 1.31,
95% CI [1.12, 1.51]), than in the pre-exposure and pre-test warning condition (mean c repeated
claims = -0.53, 95% CI [-0.67, -0.40]; mean c new claims = 0.02, 95% CI [-0.09, 0.12]; raw
mean difference: 0.55, 95% CI [0.36, 0.75]). Again, this difference was driven by pre-exposure
warnings reducing true judgments for repeated claims compared to the pre-test only condition,
raw mean difference = -0.82, 95% CI [-1.02, -0.62], F (1, 400) = 67.07, p < .001, partial eta
2

= .144, with no difference in response bias for new claims, raw mean difference = -0.06, 95% CI
[-0.21, 0.09], F (1, 400) = 0.445, p = .445, partial eta
2
= .144. This is consistent with the results
of Experiment 1.1 and 1.2, with pre-exposure warnings reducing the bias to judge repeated
claims as true while leaving ratings of new claims unaffected.
Actual truth
We performed a 2 (warning timing: before test vs. before exposure and before test) x 2
(warning content: “some” or “half”) x 2 (repetition: trivia claim repeated vs. new) x 2 (truth
value: true or false) mixed model ANOVA, manipulating warning timing and warning content
between subjects and repetition within subjects with mean truth rating (1 = definitely false, 6 =
definitely true) as the dependent variable.
There was a main effect of actual truth value, F (1, 400) = 51.65, p < .001, partial eta
2

= .114, with true claims rated more true (M = 3.98, 95% CI [3.92, 4.04]) than false claims (M =
3.80, 95% C [3.74, 3.86]; raw mean difference = 0.18, 95% CI [0.13, 0.23]). There was a
significant interaction of repetition and truth value, F (1, 400) = 4.55, p = .033, partial eta
2

= .011, with true claims showing a larger truth effect (mean new true claims = 3.56, 95% [3.51,

128
3.62]; mean repeated true claims = 4.40, 95% CI [4.31, 4.48]; raw mean difference = 0.83, 95%
CI [0.74, 0.92]) than false claims (mean new false claims = 3.43, 95% [3.37, 3.49]; mean
repeated false claims = 4.18, 95% [4.09, 4.27]; raw mean difference = 0.75, 95% CI [0.66,
0.85]), although this interaction did not reach significance in Experiments 1.1 and 1.2 (both Fs <
0.19, ps > .668). There was no interaction of truth value with warning timing, F (1, 400) = 0.15,
p = .702, partial eta
2
< .001, warning content, F (1, 400) = 0.53, p = .469, partial eta
2
= .001, any
three-way interactions, all Fs < 0.86, ps > .35, or four-way interaction, F (1, 400) = 2.86, p
= .092, partial eta
2
= .007.
Replicating our main results, there was a significant truth effect, F (1, 400) = 335.32, p
< .001, partial eta
2
= .456, significant main effect of warning timing, F (1, 400) = 46.89, p
< .001, partial eta
2
= .105, and a significant interaction between repetition and warning timing, F
(1, 400) = 89.03, p < .001, partial eta
2
= .182. There was no main effect of warning content, F (1,
400) = 0.01, p = .934, partial eta
2
< .001, or further interactions of warning content, Fs < 1.32,
ps > .25.

129
References
Stanislaw, H. & Todorov, N. (1999). Calculation of signal detection theory measures. Behavior
Research Methods, Instruments & Computers, 31, 137-149.
Macmillan, N., & Kaplan, H. (1985). Detection theory analysis of group data: Estimating
sensitivity from average hit and false-alarm rates. Psychological Bulletin, 98, 185-199

130
Table 1.1

Discrimination (d’), Hit, and False Alarm (FA) Rates for New and Repeated Claims by Warning Timing Conditions
in Experiment 1.1
Warning
Condition
New
Claims
Hit
Repeated
Claims
Hit
New
Claims
FA
Repeated
Claims
FA
New
Claims
d’
Repeated
Claims
d’
New
Claims
c
Repeated
Claims
c
No Warning
N = 113

M .532 .722 .491 .679 .124 .129 .083 -.949
SD .168 .173 .181 .196 .536 .491 .629 .816
Pre-exposure
only
N = 107

M .549 .638 .476 .567 .202 .228 .103 -.513
SD .178 .184 .178 .189 .522 .506 .664 .799
Total
N = 220

M .541 .681 .483 .625 .162 .177 .092 -.737
SD .173 .183 .179 .200 .530 .499 .645 .835

131
Table 1.2

Discrimination (d’), Hit, and False Alarm (FA) Rates for New and Repeated Claims by Warning Timing Conditions
in Experiment 1.2
Warning
Condition
New
Claims
Hit
Repeated
Claims Hit
New Claims
FA
Repeated
Claims FA
New Claims
d’
Repeated
Claims d’
New Claims
c
Repeated
Claims c
No warning
N = 89

M .506 .801 .451 .768 .154 .129 -.083 -1.496
SD .208 .209 .194 .221 .526 .555 .875 1.084
Pre-test only
N = 97

M .485 .830 .434 .778 .146 .165 -.162 -1.591
SD .234 .163 .220 .215 .538 .582 .956 .957
Pre-exposure +
pre-test
N = 96

M .538 .680 .519 .622 .053 .174 .125 -.732
SD .206 .191 .185 .212 .520 .572 .826 .886
Total
N = 282

M .510 .770 .468 .722 .117 .157 -.039 -1.268
SD .217 .198 .203 .227 .529 .568 .893 1.048

132
Table 1.3

Discrimination (d’), Hit, and False Alarm (FA) Rates for New and Repeated Claims by Warning Timing and
Warning Content Conditions in Experiment 1.3
Warning
Condition
New Claims
Hit
Repeated
Claims Hit
New
Claims FA
Repeated
Claims FA
New
Claims d’
Repeated
Claims d’
New Claims
c
Repeated
Claims c
Warning
Timing

Pre-test only
N = 203

M .496 .781 .482 .736 .038 .174 -.044 -1.356
SD .208 .212 .199 .235 .529 .494 .833 1.118
Pre-exposure
+ pre-test
N = 201

M .510 .633 .495 .586 .044 .152 .017 -.534
SD .170 .203 .189 .200 .521 .544 .681 .875
Warning
Content

“Some”
warning
N = 206

M .497 .717 .473 .664 .068 .181 -.056 -1.004
SD .193 .232 .190 .246 .513 .506 .773 1.161
“Half”
warning
N = 198

M .509 .698 .505 .658 .012 .144 .031 -.888
SD .187 .206 .198 .214 .535 .533 .747 .997
Total
N = 404

M .503 .708 .488 .661 .041 .163 -.014 -.947
SD .190 .220 .194 .231 .524 .519 .761 1.084

133
Appendix C: Chapter II Figures

Figure 2.1. Truth ratings by whether people were “High” or “Low” on Need for Cognition
(NFC) using a median split and if claims were repeated or new in Experiment 2.1. Error bars
represent 95% within-subjects confidence intervals (Masson & Loftus, 2003).

3.0
3.5
4.0
4.5
5.0
5.5
Low NFC High NFC Low NFC High NFC
Truth Rating
1 = definitely false, 6 = definitely true
Warning
New claims
Repeated claims
No Warning

134

Figure. 2.2. Truth ratings by whether people were “High” or “Low” on Need for Cognition
(NFC) using a median split and if claims were repeated or new in Experiments 2.2. Error bars
represent 95% within-subjects confidence intervals (Masson & Loftus, 2003).

3.0
3.5
4.0
4.5
5.0
5.5
Low NFC High NFC
Truth Rating
1 = definitely false, 6 = definitely true
New claims
Repeated claims

135

Figure 2.3. Effect sizes (d unbiased) for the illusory truth effect for high and low Need for
Cognition (NFC) across all experiments.

All conditions overall
Low NFC overall
Experiment 2.2
Experiment 2.1 no warning condition
Experiment 2.1 warning condition
High NFC overall
Experiment 2.2
Experiment 2.1 no warning condition
Experiment 2.1 warning condition
-1.5 -1 -0.5 0 0.5 1 1.5 2 2.5 3
Cohen's d (unbiased) and 95% CI
High NFC
Low NFC

136
Appendix D: Chapter III Supplementary Materials

Example claims from Experiment 3.1

137
Full list of claims from Experiment 3.1

Claim Truth Counterbalance 1 Counterbalance 2
Color Congruence Color Congruence
Strawberries raise blood glucose levels slowly. true red congruent yellow incongruent
Cranberries are native to South America. false red congruent green incongruent
Clementines are named after a monk. true orange congruent brown incongruent
Mango is the national fruit of Indonesia. false orange congruent purple incongruent
Lemon peel is rich in pectin. true yellow congruent red incongruent
Bananas sold in supermarkets are mainly of the
Hutchinson variety.
false yellow congruent brown incongruent
Cucumbers can be grown in outer space. true green congruent purple incongruent
Asparagus is not a natural diuretic. false green congruent red incongruent
Plum skin is naturally covered with a layer of wax. true purple congruent green incongruent
Beets grow well in highly acidic soil. false purple congruent orange incongruent
Potatoes are about 80% water by weight. true brown congruent orange incongruent
Coconut is a minor ingredient in Indonesian cuisine. false brown congruent yellow incongruent
Tomatoes are not mentioned in Shakespeare’s plays. true yellow incongruent red congruent
Radishes are slow-growing crops. false green incongruent red congruent
Pumpkins can be grown in Alaska. true brown incongruent orange congruent
Apricots are less nutritious when dried. false purple incongruent orange congruent
Pineapples ripen five to six months after flowering
begins.
true red incongruent yellow congruent
Corn always has an odd number of rows on each ear. false brown incongruent yellow congruent
Zucchini is the only vegetable that starts with the
letter Z.
true purple incongruent green congruent
Peas are a poor source of protein. false red incongruent green congruent
Figs are one of the most perishable fruits. true green incongruent purple congruent
Grapes are incapable of spontaneous fermentation. false orange incongruent purple congruent
Mushrooms that are edible are called sporophores. true orange incongruent brown congruent
Dates are less than 50% sugar by weight. false yellow incongruent brown congruent

138
Colors used for Experiment 3.1 claims

Color RBC Hex
Red 255, 0, 0 FF0000
Orange 255, 153, 0 FF9900
Yellow 255, 255, 0 FFFF00
Green 0, 204, 0 00CC00
Blue 0, 0, 255 0000FF
Purple 153, 0, 204 9900CC

139
Full list of claims from Experiment 3.2

Set A
Claim Truth Color
Congruent Incongruent
Lime discourages the growth of kidney stones. True Green Red
Apricots will not develop more flavor after they are
harvested.
True Orange Purple
Cherries have been crossed to produce a hybrid called
duke cherries.
True Red Yellow
Peas lose their sweetness after harvest quickly. True Green Red
Raspberries are annual plants. False Red Purple
Pumpkin carving evolved from a Mayan tradition. False Orange Red
Grapes are incapable of spontaneous fermentation. False Green Blue
Bananas are seasonal crops. False Yellow Purple
Set B
Lemon peel is rich in pectin. True Yellow Red
Strawberry consumption erodes tooth enamel. True Red Green
Grapes have an alkalizing effect on urine. True Green Blue
Pumpkins can be grown in Alaska. True Orange Red
Peas are a poor source of protein. False Green Red
Corn always has an odd number of rows on each ear. False Yellow Red
Apricots are less nutritious when dried. False Orange Purple
Cherry intake is associated with a higher risk of gout
attacks.
False Red Yellow

140
Supplemental data analysis
We give a detailed report for the additional analysis summarized in the primary chapter.
Experiment 3.1
To investigate whether there was an impact of color congruence on truth ratings, we
conducted a supplementary mixed effect analysis with color congruence as a fixed factor and
item and participant as random factors. We tested random slopes of congruence across item and
participant; this did not improve model fit and was thus not included in the final model. We
found a significant effect of color congruence on perceived truth, t (448.4) = 3.08, p = .037, b =
0.09, 95% CI = [0.01, 0.17], with congruent claims (M = 3.58, 95% CI [ 3.29, 3.69] rated to be
more true than incongruent claims (M = 3.49, 95% CI [3.38, 3.78]).
Experiment 3.2
We once again conducted a mixed effects model with color congruence as a fixed factor
and item and participant as random factors. Random slopes of congruence across item and
participant again did not improve model fit and were not included in the final model. This time,
we failed to find a significant effect of color congruence on perceived truth, t (1523.81) = 0.30, p
= .764, b = 0.02, 95% CI = [-0.11, -0.16], with congruent claims (M = 3.58, 95% CI [3.34, 3.81])
not rated as significantly more true than incongruent claims (M = 3.56, 95% CI [3.32, 3.79]).

141
Appendix E: Chapter IV Tables

Table 4.1

Items and Their Pronunciation Ratings for Experiment 4.1
Song &
Schwarz items
(in original
order)
Pronounceability
1 = easy
5 = hard
Bahnik &
Vranka items
(selected to
match)
Pronounceability
1 = easy
5 = hard
Cytrigmcmium 4.188 Xrifluridine 4.200
Calotropisin 2.713 Fluphenadine 2.738
Nxungzictrop 4.500 Hyjroxyethyl 4.325
Galptratebuz 3.738 Arflrmoterol 3.738
Fastinorbine 2.688 Tevalbuterol 2.675
Magnalroxate 2.900 Pomalidofide 2.913
Hnegripitrom 4.238 Griseofplvin 4.213
Celceniatrop 3.150 Bicalutadide 3.138
Ribozoxtlitp 4.138 Cjocortolone 4.150
Allotoneline 2.875 Morifloxacin 2.850

142
Table 4.2
Item Order and Pronounceability Ratings for Experiment 4.1
Item number Item
Pronounceability
1 = easy
5 = hard
SS1 Cytrigmcmium 4.188
BV2 Fluphenadine 2.738
SS3 Nxungzictrop 4.500
BV4 Arflrmoterol 3.738
SS5 Fastinorbine 2.688
BV6 Pomalidofide 2.913
SS7 Hnegripitrom 4.238
BV8 Bicalutadide 3.138
SS9 Ribozoxtlitp 4.138
BV10 Morifloxacin 2.850
BV1 Xrifluridine 4.200
SS2 Calotropisin 2.713
BV3 Hyjroxyethyl 4.325
SS4 Galptratebuz 3.738
BV5 Tevalbuterol 2.675
SS6 Magnalroxate 2.900
BV7 Griseofplvin 4.213
SS8 Celceniatrop 3.150
BV9 Cjocortolone 4.150
SS10 Allotoneline 2.875

143
Table 4.3
Item Orders for Experiment 4.2
Easy to hard list
Set A Set B
Pronounceability
1 = easiest
10 = hardest
Item
Pronounceability
1 = easy
5 = hard
Item
Pronounceability
1 = easy
5 = hard
1 Phentolamune
2.6625
Tevalbuterol
2.6750
2 Carissprodol 2.8375 Morifloxacin 2.8500
3 Gemiflaxacin
2.9500
Parisalcitol
2.9875
4 Escitatopram 3.3125 Clomipuamine 3.3375
5 Fluvcinolone 3.4125 Fenflurpmine 3.4500
6 Alittetinoin
3.5125
Cefpododmine
3.5500
7 Glucarpiddse
3.7250
Arflrmoterol
3.7375
8 Memhsuximide
3.8625
Imiglucrrase
3.8750
9 Radiogvrdase 4.0125 Azathioprpne 4.0250
10 Cjocortolone
4.1500
Xrifluridine
4.2000
Hard to easy list
10 Cjocortolone
4.1500
Xrifluridine
4.2000
9 Radiogvrdase
4.0125
Azathioprpne
4.0250
8 Memhsuximide
3.8625
Imiglucrrase
3.8750
7 Glucarpiddse
3.7250
Arflrmoterol
3.7375
6 Alittetinoin
3.5125
Cefpododmine
3.5500
5 Fluvcinolone
3.4125
Fenflurpmine
3.4500
4 Escitatopram
3.3125
Clomipuamine
3.3375
3 Gemiflaxacin
2.9500
Parisalcitol
2.9875
2 Carissprodol
2.8375
Morifloxacin
2.8500
1 Phentolamune
2.6625
Tevalbuterol
2.6750
Mixed list
4 Escitatopram
3.3125
Clomipuamine
3.3375
10 Cjocortolone
4.1500
Xrifluridine
4.2000
3 Gemiflaxacin
2.9500
Parisalcitol
2.9875
8 Memhsuximide
3.8625
Imiglucrrase
3.8750
1 Phentolamune
2.6625
Tevalbuterol
2.6750
9 Radiogvrdase
4.0125
Azathioprpne
4.0250
2 Carissprodol
2.8375
Morifloxacin
2.8500
7 Glucarpiddse
3.7250
Arflrmoterol
3.7375
6 Alittetinoin
3.5125
Cefpododmine
3.5500
5 Fluvcinolone
3.4125
Fenflurpmine
3.4500

144
Table 4.4
Item Harm Ratings from Experiment 4.2
Pronounceability
1 = easiest
10 = hardest Item set A
Harm rating
1 = very safe
7 = very harmful Item set B
Harm rating
1 = very safe
7 = very harmful
M SD M SD
1 Phentolamune 4.60 1.55 Tevalbuterol 4.10 1.52
2 Carissprodol 4.19 1.36 Morifloxacin 4.02 1.65
3 Gemiflaxacin 3.98 1.57 Parisalcitol 4.51 1.38
4 Escitatopram 4.12 1.32 Clomipuamine 4.41 1.36
5 Fluvcinolone 4.08 1.58 Fenflurpmine 4.59 1.55
6 Alittetinoin 3.96 1.51 Cefpododmine 4.59 1.63
7 Glucarpiddse 3.54 1.57 Arflrmoterol 4.40 1.59
8 Memhsuximide 5.21 1.42 Imiglucrrase 4.08 1.45
9 Radiogvrdase 5.29 1.40 Azathioprpne 4.44 1.31
10 Cjocortolone 4.52 1.48 Xrifluridine 4.62 1.49

145
Table 4.5
Items Selected for Experiments 4.3 and 4.4
Set A Set B
Item
Pronounceability
1 = easy
7 = difficult Item
Pronounceability
1 = easy
7 = difficult
kondrimia 3.50 bernberreo 3.60
rustdoroki 3.80 antentaina 3.95
kolaapazko 4.04 ideospotii 4.20
irponturok 4.34 manerttzai 4.55
matproarii
1
4.66 aurtanalzi

4.83
rimeametza 4.96 errenkrtaz 5.13
kooustrtai 5.26 azplgungoo 5.43
omdetgabsm 5.53 grikxufiko 5.70
tonbtzaelu 5.80 ngenttzaek 6.08
npuhieuket 6.11 asnskntxzk 6.33
1
Note. the word "spameriptz” would have been chosen for item set 2, but the word "spam" has
potential negative associations in the context of this study so the next closest word ("manerttza’i)
was chosen instead.

146

Table 4.6
Item Orders for Experiments 4.3 and 4.4
Easy to hard list Hard to easy list Mixed list
Order Set A Set B Order Set A Set B Order Set A Set B
1 kondrimia bernberreo 10 npuhieuket asnskntxzk 4 irponturok manerttzai
2 rustdoroki antentaina 9 tonbtzaelu ngenttzaek 10 npuhieuket asnskntxzk
3 kolaapazko ideospotii 8 omdetgabsm grikxufiko 3 kolaapazko ideospotii
4 irponturok manerttzai 7 kooustrtai azplgungoo 8 omdetgabsm grikxufiko
5 matproarii aurtanalzi 6 rimeametza errenkrtaz 1 kondrimia bernberreo
6 rimeametza errenkrtaz 5 matproarii aurtanalzi 9 tonbtzaelu ngenttzaek
7 kooustrtai azplgungoo 4 irponturok manerttzai 2 rustdoroki antentaina
8 omdetgabsm grikxufiko 3 kolaapazko ideospotii 7 kooustrtai azplgungoo
9 tonbtzaelu ngenttzaek 2 rustdoroki antentaina 6 rimeametza errenkrtaz
10 npuhieuket asnskntxzk 1 kondrimia bernberreo 5 matproarii aurtanalzi

147
Appendix F: Chapter IV Supplementary Materials

Supplementary data analysis
We give a detailed report for the additional analysis summarized in the primary chapter.
Experiment 4.1
To investigate whether there was an impact of pronounceability on harm ratings for SS
and BV words, we conducted a supplementary mixed effect analysis with pronounceability
(continuous measure from BV norming), item source (SS vs. BV), and rating order (typicality
ratings first vs. hard ratings first) as fixed factors and item and participant as random factors. We
looked at the main effects of pronounceability, item source, and rating order, as well as the
interaction between pronounceability and item source and pronounceability and rating order.
Overall, paralleling our analysis with the ANOVA, there was a significant effect of
pronounceability on harm judgements, with more difficult to pronounce items rated to be more
harmful than easy to pronounce items, t (18.3) = 3.99, p < .001, b = .58 95% CI = [0.29, 0.87].
The impact of pronounceability on harm judgements did not vary based on whether the source of
items was SS or BV, as there was no significant interaction between item source and
pronounceability, t (16.0) = -0.89, p = .39, b = -0.08, 95% CI = [0.26, 0.10]. There was also no
significant effect of whether the item came from SS or BV, t (16.0) = 0.47, p = .65, b = 0.15,
95% CI = [-0.48, 0.78], overall effect of whether participants made typicality or harm ratings
first, t (832.4) = 1.47, p = .14, b =. 51, 95% CI = [-0.17, 1.18], or interaction between item source
and rating order, t (1880.0) -1.28, p = .20, b = -0.11, 95% CI = [-0.27, 0.06].
Although the interaction between pronounceability and item source did not reach
significance, we followed up this same analysis by looking at each item coming from SS and
items coming from BV individually to see if each had significant pronounceability effects alone.

148
paralleling analysis by BV. This was the case, with a significant effect for SS items, t (898.0) =
6.57, p < .001, b = 0.51, 95% CI = [0.36, 0.66], and BV items, t (17.8) = 4.46, p < .001, b = 0.41,
95% CI = [0.23, .59].
We next conducted a similar analysis with typicality ratings as our DV. There was a
significant impact of pronounceability on judgements of typicality, with easier to pronounce
items rated to be more typical of medicines than difficult to pronounce items, t (16.39) = -2.87, p
= .01, b = -1.32, 95% CI = [-2.22, -0.42]. Unlike the fixed effects analysis, we did not find an
effect of item source on typicality ratings; that is, BV items we not rated to be more typical of
medicines than SS items, t (16.0) = 0.23, p = .82, b = 0.24, 95% CI [-1.80, 2.29]. No other effects
reached significance; t (979.9) = 0.07, p = .95, b = 0.03, 95% CI = [-0.76, .82], for the overall
effect of rating order, t (16.0) = 0.21, p = .83, b = 0.06, 95% CI = [-0.51, 0.64] for the interaction
of pronounceability and item source, and t (1880.0) = 0.50, p = .62, b = 0.05, 95% CI = [0.14,
0.24] for the interaction of pronounceability and rating order.
Experiment 4.2
To investigate the impact of item to item variation in pronounceability on the relationship
between pronounceability and harm, we ran a mixed effect model with pronounceability (three
most easy to pronounce items vs. three most difficult to pronounce items), item order (easy to
hard, hard to easy, or mixed), and item set (item set A or B) as fixed factors and item and
participant as random factors. The interactions of pronounceability and item order and
pronounceability and pronounceability and item set were included in the model, with the mixed
level of item order serving as the reference group to compare the easy to hard and hard to easy
levels to.

149
Consistent with Experiment 4.1 and with our primary analysis of Experiment 4.2, there
was a significant effect of pronounceability of risk ratings, with easier to pronounce items rated
to be less harmful than difficult to pronounce items, t (10.4) = -2.72, p = .02, b = -0.77, 95% CI =
[-1.32, -0.21]. The key interaction between pronounceability and list order did not reach
significance when comparing the mixed list or to the easy to hard order, t (1213.0) = -0.10, p
= .92, b = -.02, 95% CI = [-0.35, .32] and the mixed listed to the hard to easy order, t (1213.0) =
0.36, p = .72, b = 0.06, 95% CI = [-0.27, 0.40]. There was a significant overall effect of item set,
t (9.4) = -2.28, p = .05, b = -0.63, 95% CI = [-1.17, -0.09], with items from set B overall rated
less harmful than items from set A. There was no overall significant difference in harm rated
when comparing the mixed list or to the easy to hard order, t (491.5) = .72, p = .47, b = 0.11,
95% CI = [-0.19, 0.41] and the mixed listed to the hard to easy order, t (491.5) = 0.05, p = .96, b
= 0.01, 95% CI = [-0.29, 0.31]. There was also no significant interaction between
pronounceability and item set, t (8.0) = 1.57, p =.16, b = 0.59, 95% CI = [-0.15, 1.32].
Experiment 4.3
Our design for Experiment 4.3 was identical to our Experiment 4.2, so we performed the
same mixed effects analysis to investigate whether item to item variation in fluency moderated
the relationship between pronounceability of eBay usernames and trustworthiness. There was
once again an overall effect of pronounceability, with eBay users with easy to pronounce names
perceived to be more trustworthy that users with difficult to pronounce names, t (8.9) = 3,20, p
=.01, b = .92, 95% CI = [0.36, 1.49]. Here, the key interactions of item order and
pronounceability did reach significance. When items were presented in a mixed list that
maximized item to item chances in pronounceability, there was a larger impact of
pronounceability or perceived trustworthiness compared to the easy to hard condition, t (1223.0)

150
= -2.76, p = .006, b = -0.35, 95% CI = [-0.59, -0.10] and the hard to easy condition, t (1223.0) = -
2.26, p = .02, b = -0.28, 95% CI = [-0.53, -0.04]. Looking at just the effect of pronounceability
within each condition: mixed, t (8.2) = 4.85, p = .001, b = 1.03, 95% CI = [0.61, 1.44]; easy to
hard, t (9.3) = 4.06, p = .003, b = 0.68, 95% CI = [0.35, 1.01], hard to easy: t (9.3) = 4.57, p
= .001, b = .75, 95% CI = [0.43, 1.07]. There was no overall effects of list order on harm ratings
when comparing the easy to hard order to the mixed order, t (297.6) = 0.87, p = .39, b = 0.18,
95% CI = [-0.22, 0.57] or hard to easy to mixed, t (297.6) = 0.48, p =.63, b = 0.10, 95% CI = [-
0.30, 0.49], no effect of item set, t (18.6) = -0.23, p = .82, b = -0.06, 95% CI = [-0.55, 0.43], and
no interaction of pronounceability and item set, t (8.0) = 1.58, p = .15, b = 0.45, 95% CI = [-0.11,
1.01].
Experiment 4.4
Our design was identical to Experiment 4.2 and 4.3 so we conducted the same mixed
effects analysis. Once again, we found a significant effect of pronounceability on harm ratings,
with eBay users with easier to pronounce usernames judged to be more trustworthy than those
with difficult to pronounce usernames, t (8.9) = 3.20, p = .01, b = 0.92, 95% CI = [0.36, 1.49].
The key interactions did not reach significance, with no significant difference in
pronounceability or perceived trustworthiness when comparing the easy to hard condition to the
mixed condition, t (1213.0) = -0.89, p = .37, b = -0.10, 95% CI = [-0.33, -0.12] or the hard to
easy condition to the mixed condition, t (1213.0) = 0.75, p = .46, b = 0.09, 95% CI = [-0.14,
0.31]. Additionally, no other effect reached the standard level of significance, with no overall
effect of list order when comparing easy to hard to mixed, t (318.9) = -1.79, p = .07, b = -0.28 ,
95% CI = [-0.59, 0.03] or hard to easy to mixed, t (318.9) = -.88, p = .38, b = -0.14 , 95% CI = [-
0.45, 0.17], no effect of item set, t (10.6) = -1.16, p = .27, b = -0.35 , 95% CI = [-0.94, 0.24], or

151
interaction of pronounceability and item set, t (8.0) = 1.41, p = .20, b = 0.56 , 95% CI = [-0.22,
1.34].

Abstract (if available)

Abstract Understanding how people make judgments of truth and risk is a key component in developing effective misinformation prevention and correction strategies. When deciding whether something is true or risky, people often rely on their metacognitive experience of how easy the information feels to process. Processing ease can serve as a valid cue for making these judgments, but can also arise due to factors unrelated to the judgment at hand. Importantly, these metacognitive experiences also interact with the context of judgment. In this dissertation, I explore the role of several contextual factors in metacognitive evaluations of truth and risk. In Chapter I, I examine the impact of common experimental warnings on belief in repeated information. In Chapter II, I look at the influence of individual differences in elaboration on the truth effect. In Chapter III, I consider the potential influence of multimodal associations in knowledge networks on truth perception by exploring the role of color congruence?a novel variable. Finally, for Chapter IV, I investigate how absolute and relative variation in fluency?manipulated through pronounceability?influences judgments of risk. Across these four papers, I elucidate several factors that should be considered when evaluating effective methods for correcting misinformation and communicating potential risks to the general public. These findings have a number of implications for how to better conduct and apply laboratory research to address real-world problems.

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Asset Metadata

Creator Jalbert, Madeline (author)

Core Title Metacognitive experiences in judgments of truth and risk

School College of Letters, Arts and Sciences

Degree Doctor of Philosophy

Degree Program Psychology

Degree Conferral Date 2021-08

Publication Date 07/23/2021

Defense Date 05/25/2021

Publisher University of Southern California (original), University of Southern California. Libraries (digital)

Tag fake news,judgment and decision making,metacognition,misinformation,OAI-PMH Harvest,processing fluency,risk judgments,truth effect,truth judgments

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Advisor Schwarz, Norbert (committee chair), John, Richard (committee member), Oyserman, Daphna (committee member), Simon, Dan (committee member)

Creator Email maddyjalbert@gmail.com,mjalbert@uw.edu

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