WORKING PAPER · NO. 2020-73

Justifying Dissent

Leonardo Bursztyn, Georgy Egorov, Ingar Haaland, Aakaash Rao, and Christopher RothJANUARY 2022

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Justifying Dissent∗
Leonardo Bursztyn†

Georgy Egorov‡

Ingar Haaland§

Aakaash Rao¶

Christopher Rothk
January 2022
Abstract
Dissent plays an important role in any society, but dissenters are often silenced through social sanctions. Beyond their persuasive effects, rationales providing arguments supporting dissenters’ causes
can increase the public expression of dissent by providing a “social cover” for voicing otherwisestigmatized positions. Motivated by a simple theoretical framework, we experimentally show thatliberals are more willing to post a Tweet opposing the movement to defund the police, are seen as
less prejudiced, and face lower social sanctions when their Tweet implies they had first read scientific evidence supporting their position. Analogous experiments with conservatives demonstratethat the same mechanisms facilitate anti-immigrant expression. Our findings highlight both thepower of rationales and their limitations in enabling dissent and shed light on phenomena such associal movements, political correctness, propaganda, and anti-minority behavior.
Keywords: Dissent; social image; rationales; social media
JEL Classification: D83, D91, P16, J15∗
This paper supersedes an earlier draft circulated under the title “Disguising Prejudice: Popular Rationales as
Excuses for Intolerant Expression.” We thank Ben Enke, Davide Cantoni, Ed Glaeser, Daniel Gottlieb, Emir Kamenica, Ro’ee Levy, Ross Mattheis, Nathan Nunn, Pietro Ortoleva, Peter Schwardmann, Marco Tabellini, Joel Van
der Weele, David Yang, Noam Yuchtman, Florian Zimmermann, and numerous seminar participants for very helpful
suggestions. We thank Danil Fedchenko, Takuma Habu, Hrishikesh Iyengar, Melisa Kurtis, and Alison Zhao for outstanding research assistance. We gratefully acknowledge financial support from the Pearson Institute for the Studyand Resolution of Global Conflicts and the UChicago Social Sciences Research Center. Roth acknowledges funding from the Deutsche Forschungsgemeinschaft (DFG, German Research Foundation) under Germany’s Excellence
Strategy EXC 2126/1-390838866. The research described in this article was approved by the University of Chicago
Social and Behavioral Sciences Institutional Review Board and the Humanities and Social Sciences Research Ethics
Committee at the University of Warwick.
†
University of Chicago and NBER, bursztyn@uchicago.edu‡
Kellogg School of Management and NBER, g-egorov@kellogg.northwestern.edu§
University of Bergen and CESifo, ingar.haaland@uib.no¶
Harvard University, arao@g.harvard.eduk
University of Cologne and CEPR, roth@wiso.uni-koeln.de1Introduction

From speaking out against injustice to victimizing protected groups, dissent can be a force foror against social change and therefore plays a consequential role in any society. Fundamental todissent are rationales — narratives disseminated by political entrepreneurs, social movements, andmedia outlets — that provide arguments supporting dissenters’ causes. Some rationales spur dissent
through persuasion: they change people’s views and, as a result, their public behavior. Yet dissent
is often limited not because few people hold dissenting opinions, but rather because these people fear
speaking their mind. Indeed, 62 percent of Americans agree that “The political climate these days
prevents me from saying things I believe because others might find them offensive” (Ekins, 2020).
Consider Democrats who oppose the movement to defund the police. In many settings, publicly
expressing this opposition generates social costs: opposition to police defunding may be seen as asignal of racial intolerance either by a majority or by a small but vocal minority. Suppose thata credible study is publicized suggesting that defunding the police would increase violent crime.
This new study might increase an individual’s willingness to publicly oppose police defunding even
if the study does not change her convictions, as long as she is able to attribute her views to thestudy. The key point is that the availability of this rationale opens up explanations other than
racial intolerance for her position, reducing the social costs incurred by voicing it publicly and thus
making her more willing to dissent.
In this paper, we present experiments exploring the power and potential limitations of rationales
in facilitating the expression of dissent. Across the political spectrum, dissent is often expressed— and suppressed — on social media, where rationales from both mainstream and fringe sources
proliferate and where people often face large social costs from expressing controversial opinions.
Motivated by a simple theoretical framework, we experimentally examine the expression and interpretation of dissent on social media in two contentious and policy-relevant domains: liberals’
opposition to defunding the police and conservatives’ support for deporting illegal immigrants.
We begin by studying opposition to police reform among liberals. In a first experiment, respondents read a Washington Post article written by a Princeton criminologist arguing that “Oneof the most robust, most uncomfortable findings in criminology is that putting more officers on
the street leads to less violent crime”.1 Respondents then choose whether to join a campaign opposing the movement to defund the police and, conditional on doing so, decide whether to post a
Tweet promoting the campaign. The experimental manipulation subtly varies the availability of a1

See “Why do we need the police?” Sharkey, Patrick. The Washington Post, June 12, 2020.

1

social cover in the Tweet while holding fixed other potential motives to post. In particular, in the
Cover condition, respondents’ Tweets indicate that they were shown the article before joining the
campaign, while in the No Cover condition, respondents’ Tweets indicate that they were shown
to the rationale after joining the campaign.2 The implied timing in the Cover condition provides
these respondents with a social cover — the (implicit) justification that they joined the campaign
because they were persuaded by the article’s claims — while the timing implied by the No Covercondition eliminates this social cover. Differences in the “willingness to Tweet” thus cannot be
explained by the persuasiveness of the rationale — all respondents in both groups read the article— or by respondents’ expectations that the rationale will persuade their followers — both versionsof the Tweet contain an identical description of and link to the article.
The availability of a social cover strongly affects posting behavior: respondents are 12 percentage points more likely to post the Tweet in the Cover condition than in the No Cover condition.
In a placebo experiment with an identical design, but with a Tweet expressing support for anon-stigmatized cause, we find no difference between posting rates in the Cover and No Coverconditions, suggesting effects are indeed driven by (anticipated) changes in the stigma associatedwith dissenting expression rather than some other independent effect of the treatment. An additional experiment in which respondents describe the considerations on their mind when posting
potentially controversial content corroborates the importance of the cover effect of rationales.
We conduct a second experiment, again with liberal respondents, to examine how social covershifts an audience’s inferences about the motives underlying dissent and the resulting sanctions
levied upon dissenters. Respondents are matched with a participant who posted the Tweet fromthe previous experiment — either a previous participant assigned to the No Cover condition or to
the Cover condition — and are shown the anti-defunding Tweet their matched participant choseto post. They choose whether to deny a bonus to their matched participant, a measure of social
sanctions. We also elicit respondents’ inferences about their matched participant’s underlying
prejudice: respondents guess whether or not the participant authorized a donation to a pro-Black
organization.
The results confirm that the availability of social cover shifts inference and resulting social
sanctions. Respondents matched with a participant in the Cover condition are 7 percentage points
more likely to think that their matched participant authorized the pro-Black donation (relative
to a No Cover mean of 31 percent) and are 7 percentage points less likely to deny their matched
2

Both Tweets are factually correct, as respondents in both conditions were shown the article both before andafter joining the campaign.

2

participant the $1 bonus (relative to a No Cover mean of 47 percent). In an additional inference
experiment, we show that slightly lowering the credibility of the rationale by removing mention of
the academic background of the article’s author largely eliminates the treatment effects, highlighting
the limits of rationales in shaping inference.
We next study the effects of rationales among a different sample, conservatives, and in a different
policy context, anti-immigrant policies. Here, supporting the immediate deportation of all illegal
immigrants from Mexico is a stigmatized opinion that people may be reluctant to publicly express,
but a similar rationale as studied in the previous experiments — concerns about crime — may
be effective in shifting inference about motives and thus decreasing social sanctions. In addition
to speaking to the robustness of our previous findings and examining the use of rationales by adifferent population (conservative rather than liberal respondents), these experiments allow us to
examine how rationales can generate social cover vis-a-vis different types of audience. In particular,
opposition to police defunding is primarily stigmatized by liberals’ in-group (fellow liberals) rather
than their out-group (conservative); in contrast, support for deportation is primarily stigmatizedby conservatives’ out-group (liberals) rather than their in-group (fellow conservatives).
The experimental manipulation follows the logic in our first experiment: in the Cover condition,
respondents’ Tweets indicate that they were exposed to the rationale — a clip of Fox News anchor
Tucker Carlson arguing that illegal immigrants commit violent crimes at vastly higher rates thancitizens — before joining the campaign, while in the No Cover condition, respondents’ Tweets indicate that they were exposed to the rationale after joining the campaign. Our findings corroborate
the importance of rationales in facilitating the expression of dissent: respondents are 17 percentage points more likely to post the Tweet in the Cover condition than the No Cover condition,
relative to a No Cover mean of 56 percent. A further experiment shows that this rationale once
again has strong effects on inference: respondents matched with a participant who chose to post
the Cover Tweet are 5 percentage points more likely to believe that this participant authorized
the pro-immigrant donation (relative to a No Cover mean of 11 percent) and are 7 percentage
points less likely to deny their matched participant the bonus (relative to a No Cover mean of 80
percent). Additional experiments with large and representative samples in a somewhat more stylized setting confirm that the availability of rationales increases respondents’ willingness to publicly
express anti-immigrant sentiments (by donating to an anti-immigration organization) and shapes
an audience’s inference about underlying motives.
Taken together, our evidence highlights the importance of rationales in facilitating dissent on

3

both sides of the political spectrum, and it sheds light on the mechanisms by which individuals
and institutions can influence public behavior by shaping the supply of rationales and perceptionsof their social acceptability. Our findings have important implications for how the expression ofdissent responds to the availability of new narratives. First, rationales are only effective to theextent to which observers believe that they genuinely change the dissenter’s beliefs: an obscure or
non-credible rationale may fail to shift inference, and may even backfire, if it signals the dissenter’s
underlying type. For example, if only intolerant people tend to read a particular source, citing
a novel rationale provided by this source will fail to generate social cover. This implies thatthe endorsement of rationales by prominent figures such as politicians or celebrities may generateparticularly large “social amplifiers”: such figures may not only be more credible and directly
persuade more people, but also more able to generate common knowledge such that dissenters canclaim they were exposed to the rationale without seeking it out directly from stigmatized sources.
Conversely, groups seeking to suppress dissent have strong incentives to silence or marginalize
potential sources of rationales (for example, disinviting campus speakers or branding certain news
sources as fringe), because these tactics reduce the perceived probability that people will be exposed
to rationales “by chance.” If successful, these groups can create and sustain a “political correctness”
culture — for better or for worse — in which certain rationales are ineffective because citing thestigmatized source undermines social cover. By challenging the credibility of rationales or explicitly
linking them to stigmatized positions, a vocal group, even a vocal minority, can silence a majority— even when the “silent majority” knows they are a majority.
Related literature Our paper builds on a theoretical literature on the effects of social image
concerns on economic and moral decision-making. Most closely related to our work is Bénabou
et al. (2020), which presents a model of the production and circulation of arguments justifying
actions on the basis of morality. We also build on a growing empirical literature studying theeffect of social image concerns on political and economic outcomes.3 Relative to existing work, thekey contribution of this paper is to characterize, both theoretically and empirically, how rationales
shape the expression of dissent by providing a “social cover,” thus lowering the social costs ofexpression. Our paper is thus related to laboratory evidence on strategic communication used to
3
These outcomes include moral behavior, as in Ariely et al. 2009; Lacetera and Macis 2010; Ewers and Zimmermann 2015; voting, as in DellaVigna et al. 2017; tax evasion, as in Perez-Truglia and Troiano 2018; Besley et al. 2019;
identity choice, as in Jia and Persson 2019; campaign donations, as in Perez-Truglia and Cruces 2017; educational
investments, as in Bursztyn and Jensen 2015; and labor market choices, as in Bursztyn et al. 2017.

4

justify public charitable donations (Foerster and van der Weele, 2021).4
Our work also relates to a small literature on political correctness (Morris, 2001; Golman,2020) and to work examining how social norms govern public behavior more generally (Bénabou
and Tirole, 2006, 2011b; Ali and Lin, 2013; Kuran, 1997). Braghieri (2022) shows that publicly
expressed views, which may be affected by political correctness norms, are less informative thanprivate views. Like some of this previous work (Bursztyn et al., 2020a,b), our paper examines
how previously-stigmatized public behavior can become socially acceptable, but it differs bothconceptually and in its implications for equilibrium expression. Conceptually, we isolate the social
cover effect of rationales, which shapes the audience’s beliefs about a dissenter’s motives, from thepersuasive effects of the rationale either on the dissenter or the audience. We show that the social
cover provided by rationales increases the public expression of dissent by lowering its social cost, as
rationales make public actions less informative about dissenters’ underlying type. Practically, themechanism allows even views that are privately unpopular — such as conspiracy theories or extreme
statements about certain minorities — to be publicly expressed in equilibrium. At the same time,
it can enable a minority to silence majority positions, even in the absence of misperceptions about
people’s views.
More generally, our work connects to a vast literature on the effects of media and propaganda
on political and cultural behavior, such as anti-minority violence (e.g. Yanagizawa-Drott 2014;
Enikolopov and Petrova 2015; Adena et al. 2015). This literature, examining persuasion in fieldsettings, often finds substantial effects (e.g. Caprettini et al. 2022) — in contrast to the relatively
small effects of persuasion documented in survey experiments in which stated views are private(see, for example, Haaland et al. 2021). While there are a number of plausible explanations for thisdiscrepancy, our paper proposes one possible mechanism: widespread propaganda creates common
knowledge of rationales and thus a “social amplifier” that magnifies rationales’ effect on public
4

Several laboratory studies show that “moral wiggle room” can have substantial effects on behavior: see, forexample, Dana et al. (2007); Golman et al. (2017); Saccardo and Serra-Garcia (2020); Golman et al. (2016); Lazear
et al. (2012); Hamman et al. (2010); Exley (2016); Cunningham and de Quidt (2016). Because decisions in thesesettings are anonymous, these findings can be understood through a behavioral model of self-signaling, as in Bénabou
and Tirole (2011a). Our work holds this channel constant by exposing respondents to the same private information
set, and we instead examine signaling vis-a-vis others, developing a revealed-preference approach that allows us to
study image concerns associated with a natural form of expression — posting on social media — before a naturalaudience — people’s actual social media followers. Theoretically, our argument follows the tradition of signal jamming(Holmstrom, 1982; Fudenberg and Tirole, 1986), where individual’s action (the use of rationale in our case) makes
the individual’s characteristics more difficult to infer. Our work is also related to work on “excuses” in psychology,
such as Langer et al. (1978), which finds that subjects are more likely to comply with a request (to jump a line to
make Xerox copies) justified by a reason. Our paper probes the mechanisms by which some rationales shift social
inference about underlying motives — and others fail to do so — and thus sheds light on how rationales can enable
dissent.

5

behavior by generating social cover. Thus, our work also connects to a literature on populist
political movements (e.g. Acemoglu et al. 2013; Guriev and Papaioannou 2020; Patir et al. 2021):
authoritarian populists are often highly skilled at generating social cover for exclusionary policies
targeting minority groups.
The remainder of this paper proceeds as follows. In Section 2, we present a simple model ofthe use and interpretation of rationales facilitating dissenting expression. In Section 3, we present
experiments studying how the availability of a social cover shapes liberal respondents’ willingness topublicly oppose the movement to defund the police, and how this social cover shifts their audience’s
beliefs about and behavior toward them. In Section 4, we present similar experiments focusing onconservative respondents in the context of anti-immigrant expression. Section 5 discusses implications of our findings and concludes.

2

Theoretical Framework

To organize these ideas and guide the experimental design, we start with a theoretical framework.
All formal proofs are provided in Appendix A.

2.1

Setup

The society A consists of a continuum of citizens facing a binary policy decision between the statusquo (Q) and change (C). There is some objective measure of social welfare from decision C, andwe denote this value w. The welfare under the status quo Q is normalized to zero. From the
2 . This social welfare may
citizens’ perspective, this value is distributed normally: w ∼ N w0 , σw
incorporate the expected economic payoff to each citizen from enacting decision C, but it may also
include externalities to people outside the society or other factors inasmuch as citizens care about
them.
Apart from the objective economic consequences captured by w, citizens have idiosyncratic
tastes. Specifically, citizen i gets additional utility ti if policy C, as opposed to Q, is enacted; werefer to ti as i’s type. We assume that ti is distributed with c.d.f. H (·) and p.d.f. h (·), and that ith(x)is increasing in x, which is satisfied, e.g., forsatisfies the monotone hazard rate property ( 1−H(x)the normal and uniform distributions). To avoid corner cases, we assume that ti has full support
on the real line.
A citizen i ∈ A is given a chance to publicly state support for change (decision di = 1) before6

an audience. Doing so results in expressive benefit B but social cost S, so Ui (di = 1) = B − S. We
assume thatB = β (E (w | ∗) + ti ) ;in other words, the benefit is proportional to the sum of citizen i’s posterior belief about w using
all available information and i’s own type. The social cost S is borne because action di = 1 may berevealing about i’s type ti , and having a high type is stigmatized by the audience. For simplicity,
we assume that stigma is linear in the audience’s posterior about citizen i’s type:
S = γE−i (ti | di = 1, ∗) .
Lastly, the utility from inaction (di = 0) is normalized to 0: Ui (di = 0) = 0.5

2.2

Analysis

In the absence of new information, the posterior of citizen i about w equals the prior w0 , and thus
the benefit of action di = 1 is B = β (w0 + ti ). Citizen i makes the decision holding his social cost
S fixed. Therefore, he chooses di = 1 if and only ifti ≥1
S − w0 .
β

Thus, any equilibrium takes the threshold form, with the threshold τ satisfying the conditionτ=γ
E (ti | ti > τ ) − w0 .
β(1)Generally speaking, the threshold need not be unique due to strategic complementarity: if not only
extreme right but also moderate types choose action di = 1, the social cost is lower, which increases
citizens’ propensity to choose di = 1. However, if the distribution of ti satisfies the monotone hazard
rate property, the equilibrium is unique.
Proposition 1. Suppose that γ < β. Then there is a unique equilibrium that takes the form of athreshold: individuals with ti > τ choose di = 1 and those with ti < τ choose di = 0.
5
We implicitly assume that the audience does not observe that i had a chance to make the action, and thus if hechooses di = 0 he is pooled with a continuum of citizens who are passive in this model. If the audience observes thatinaction is by choice, there may be social consequences in this case as well. Nevertheless, all the results go throughas stated.

7In other words, the equilibrium is unique provided that the citizen’s choice is not driven solely
by social image concerns and that the expressive benefit from their choice is sufficiently high.

2.3

Persuasive Rationales

Suppose that citizen i, prior to making the decision, received an informative signal s = w +ε, whereε ∼ N 0, σε2 . His posterior expectation about w is then equal tow1 = E (w | s) = w0

2
σε2
σw
+
s
,
2 + σ22 + σ2σw
σw
εεwhich exceeds w0 if and only if s > w0 . Now, if indeed the signal is positive (s > w0 ), then fora fixed social cost S, this would prompt more citizens to choose di = 1 (specifically, all citizens
with ti ≥ β1 S − w1 would do so). This corresponds to a persuasion mechanism. Now that more
moderate people choose di = 1, the social cost of doing so is lower: intuitively, publicly supporting
C is no longer a sign of extremism. Of course, a decrease in S will prompt even more people tochoose di = 1 (a “social amplifier”). In the end, we have the following characterization of the new
equilibrium.
Proposition 2. Suppose that citizen i makes his decision after receiving informative signal s > w0 .
This citizen then has a higher posterior about w than the prior, and the ex ante probability thatcitizen i chooses di = 1 is higher. The equilibrium social cost S is lower with signal s than without.

2.4

Polarizing Rationales

In reality, individuals are often presented with the same evidence, but the evidence is interpreted
differently. This may be due to differences in background knowledge, cognitive limitations, or
behavioral biases, among other factors. For example, different individuals may pick up different
arguments from a long article. Alternatively, some credulous individuals may take the text at
face value, while others know the bias of a particular journalist or the news outlet and update
accordingly.
To study this possibility, we assume that share µ of citizens get a high signal sh > w0 (with thecorresponding posterior wh > w0 ) and share 1 − µ get a low signal sl < w0 (and their posterior iswl < w0 ). We prove the following result.

8

Proposition 3. Suppose thatµ (H (τ ) − H (τ − (wh − w0 ))) ≥ (1 − µ) (H (τ + (w0 − wl )) − H (τ )) ,(2)

where τ is the equilibrium threshold in the basic model (Proposition 1). Then the ex ante probability
that citizen i chooses di = 1 is higher than in the basic model, and the equilibrium social cost islower.
In other words, if the mass of people who are persuaded to choose di = 1 by high signal sh(holding the social cost fixed) is at least as large as the mass of people who are dissuaded fromdoing so by low signal sl , then the social cost of choosing di = 1 will go down in equilibrium, andmore people will do so in equilibrium. Intuitively, the audience now faces the inference problem:
citizen i may have chosen di = 1 either because ti is high, or because he got a high signal sh . Moreprecisely, the set of citizens who would choose to support S now contains some types with ti < τ(moderates who got a high signal sh ) and lacks some types with ti > τ (extremists who got a low
signal sl ). As long as share of the former is not too small, the posterior of ti conditional on choosing
di = 1 goes down. As a result, more citizens will choose di = 1 and face a lower social cost for doing
so. This result is not knife-edge, and would apply even if somewhat more people are dissuaded.
Taken together, Propositions 2 and 3 imply that while informative and persuasive evidence canreduce the social cost of a stigmatized public action and lead to more people doing it, evidence that
dissuades as many people as it persuades can also be effective at that, due to the social inference
problem that such evidence creates. Put differently, for a rationale to be effective it does not haveto be persuasive, as long as it hinders inference about the motives for a public action.

3

Opposition to Defunding the Police

The primary experiments in this paper examine the expression of dissent on social media, which weview as an ideal setting for several reasons. First, expression on social media is of direct interest:
over 70 percent of Americans report using social media daily, many politicians and other prominent
figures have turned to social media as a primary channel of communication with the public, andsocial media has been linked to a number of important real-world outcomes: protests (Enikolopov
et al., 2020), hate crimes (Müller and Schwarz, 2018; Bursztyn et al., 2019), and social movements(Levy and Mattsson, 2021). Second, expressing dissent on social media — like doing so in realworld offline settings, and unlike doing so in more artificial lab settings — may have real social
9costs vis-a-vis a natural population about whose opinions respondents care — family members,
friends, acquaintances, and current and/or future employers. Indeed, a substantial majority ofhiring managers report using social media accounts as a screening tool (O’Brien, 2018).
Our first two experiments examine the use and interpretation of rationales for opposing the
movement to defund the police. The slogan “defund the police” rose to national prominence after
the murder of George Floyd in May 2020; advocates seek to decrease funding for police departments, and many favor restricting the responsibilities of law enforcement primarily to violent crime,
redirecting resources to specialized response teams such as social workers and conflict-resolution
specialists to deliver other services (Thompson, 2020). Popular opposition to police defunding isrelatively high: as of an October 2021 Pew Research survey, only 15 percent of adults, 25 percent
of Democrats, and 23 percent of Blacks support reducing spending on policing in their area (Parker
and Hurst, 2021). Nonetheless, because the movement is closely linked to concerns about racial
injustice — most advocates claim that the American law enforcement system is fundamentally
racist and requires radical reform (or abolition) — it seems a priori plausible that many liberals
would feel uncomfortable publicly voicing opposition to defunding. This is particularly true giventhat liberal Twitter users are more interested in social justice causes and are more likely to call out
perceived injustice than liberals at large (Cohn and Quealy, 2019).

3.1
3.1.1

Experiment 1: Rationales and Anti-Defunding Expression
Motivation for experimental design

Experiment 1 studies how the social cover provided by rationales affects respondents’ willingness
to post a Tweet on their account opposing the movement to defund the police. Identifying thiseffect is challenging from both a design and ethical perspective. From a design perspective, weneed to manipulate the availability of a social cover, ruling out other possible reasons for why arationale might change posting behavior. For example, the rationale may affect posting behavior
by changing respondents’ private beliefs (persuasion), or respondents might cite the rationale topersuade others (anticipated persuasion). Identifying the cover effect requires us to hold these otherchannels fixed across experimental conditions. At the same time, we wish to avoid a complicatedor heavy-handed intervention in order to maximize the extent to which our results can speak tothe expression of dissent in real-world contexts. From an ethical perspective, while we want toexamine the most natural possible outcome — respondents’ willingness to Tweet — we prefer toavoid leading respondents to actually post political content on Twitter (a particular concern in10

our similarly-structured Experiment 3, which studies willingness to publicly support a campaign todeport all illegal Mexican immigrants). A related and conflicting goal is to avoid explicitly deceiving
respondents. We address these design and ethical difficulties with an experiment that (1) holds the
persuasion and anticipated persuasion effects constant while varying only the availability of a social
cover; (2) measures respondents’ revealed-preference willingness to express dissent on their Twitter
account; (3) avoids respondents actually posting these Tweets; and (4) avoids explicit deception.
We discuss the ethical considerations underlying all experimental designs in Appendix D.
3.1.2

Sample and experimental design

Sample composition

We conducted our pre-registered Experiment 1 in October 2021 with asample of 1,122 Democrats and Independents.6 As explained below, this resulted in a final sample
for analysis of 529 respondents. Given the need for respondents to (1) have an active Twitter
account and (2) be willing to log into the survey using their Twitter account, as described below,
recruiting respondents to participate in this experiment was more difficult than we anticipated.
To reach our pre-registered minimum of 500 complete responses, we recruited respondents fromboth Luc.id and CloudResearch, two survey providers widely used in the social sciences (Woodand Porter, 2019; Litman et al., 2017).7 Our final sample is well-balanced on observables acrosstreatment arms (Appendix Table B2).
Twitter login Figure 1 outlines the structure of Experiment 1. After completing a short attention check, we ask respondents to log in to our survey using their Twitter account through“Tweetability,” a Twitter application we created using Twitter’s Application Programming Interface (API) that allows us to schedule Tweets to be posted on the users’ accounts at a future date.
To an observer, these Tweets look as though they were posted by the respondent him or herself.
We automatically capture respondents’ Twitter handles after they log in. Respondents are assured
that we will never use this application to access any private information from accounts, that alldata will be securely stored until its deletion by no later than December 1, 2021, and that we will
never schedule posts on their accounts without their explicit permission. Respondents then respondto a set of basic demographic and other background questions.
6
Our experiment was pre-registered in the AEA RCT registry under ID AEARCTR-0008432. The full set ofexperimental instructions is included in Appendix E.1.
7
Our final analysis sample consists of 382 respondents from Lucid and 147 respondents from CloudResearch. The
two estimates using the samples individually are very similar in size (12.6 p.p. on CloudResearch vs 11.3 p.p. on
Luc.id) and statistically indistinguishable.

11

Information provision and campaign support

We then present respondents with an op-ed

written in the Washington Post by Patrick Sharkey, a professor of public affairs and criminology
at Princeton University.8 In the article, Sharkey argues that a vast body of evidence shows that
increasing policing decreases violent crime, that defunding the police is thus likely to increase
violence, and that other solutions (e.g. granting communities more resources to maintain safety)
will likely be more effective. After reading the article, respondents are asked if they would liketo join a campaign to oppose the movement to defund the police. The survey terminates forrespondents who do not join, leaving us with 529 remaining respondents. These respondents arepresented with the article again and informed that they can spend as long as they wish reading it.
Twitter post Once they continue, we inform respondents that the campaign involves circulatinga petition on Twitter opposing the movement to defund the police. We show them a screenshotof the Tweet and ask if they are willing to schedule the Tweet to be posted on their account. We
inform respondents that the Tweets of all respondents will be posted if and when we have surveyed
people in all US counties (a strategy which, as we explain to respondents, is often used in social
media campaigns to make certain topics “trend” on users’ timelines). In practice, because we target
fewer respondents than the number of counties in the US, we ensure Tweets will never be posted.
Respondents in the Cover condition are asked whether they would like to schedule the following
Tweet:
I have joined a campaign to oppose defunding the police: [LINK]. Before joining, I wasshown this article written by a Princeton professor on the strong scientific evidence thatdefunding the police would increase violent crime: [LINK]The Tweet is identical for respondents in the No Cover condition, with one exception: the second
sentence begins “After I joined the campaign. . . ”. Both Tweets are factually correct (all respondents were in fact shown the article both before and after joining the campaign), but this difference
in wording suggests to potential readers of the Tweet that respondents in the Cover condition had
been exposed to the scientific evidence against defunding the police before joining the campaign— and thus had a strong rationale for doing so. In contrast, the No Cover Tweet suggests that
respondents had only been exposed to the evidence after joining, and thus that the evidence could
not have led them to join the campaign. This design therefore isolates the cover effect of rationales
8The
articleisavailable
defund-police-violent-crime/.

athttps://www.washingtonpost.com/outlook/2020/06/12/

12

while fixing the persuasion channel (all respondents are exposed to the same information) and theanticipated persuasion channel (all respondents know their Tweet’s readers will be exposed to thearticle, since it is linked in the Tweet) across conditions. By employing a one-word manipulation,
we also hold other potential confounds, such as the length of the Tweet, fixed across conditions.
3.1.3

Results

Figure 2 displays the results, which we also show in regression table form in Table 1. 57% of
respondents authorize the Tweet in the No Cover condition compared to 70% of respondents in
the Cover condition (p < 0.01). These effects are stable to the inclusion of demographic andpartisan controls; the effect size corresponds to 0.25 standard deviations, comparable to or larger
than the effects on persuasion generally documented in information provision experiments (Haaland
et al., 2021) and the effects of image concerns generally documented in experiments varying theobservability of decisions (Bursztyn and Jensen, 2015).9 This relatively large effect underscores theimportance of the cover effect in driving the expression of dissent.
3.1.4

Ruling out alternative explanations

Placebo

One potential concern is that respondents are more willing to schedule the Cover Tweet(“Before I joined the campaign. . . ”) than the No Cover Tweet (“After I joined the campaign. . . ”)
for reasons unrelated to the availability of the social cover. For example, respondents might thinkthe “before” wording in the Cover Tweet sounds more natural than the “after” wording in the No
Cover Tweet.
To address this concern, we run a placebo experiment (Auxiliary Experiment 2)10 with thesame design and manipulation, but in a different, non-stigmatized context — conservation of the
Amazon rainforest — and with a different rationale — an article reporting a new study whichfinds that over 10,000 species are at risk due to deforestation in the Amazon. Panel A of Figure 3
and Appendix Table B5 show no significant difference between posting rates in the Cover and No
Cover conditions. The difference in effect sizes between the defunding experiment and the placebo
experiment is large in magnitude and significant at the 1% level, suggesting effects are indeed drivenby (anticipated) changes in the stigma associated with dissenting expression rather than some other9
Indeed, in our pre-registered Auxiliary Experiment 1 with the same rationale, we estimate a persuasion effecton private attitudes of 0.12 standard deviations (p=0.059). See Appendix B.2 for details and Appendix E.5 forexperimental instructions.
10
See Appendix B.3 for details and Appendix E.6 for experimental instructions.

13independent effect of the before/after wording.
The placebo results also deliver additional insight into the effect sizes documented in the main
experiment. The difference in the fraction of respondents authorizing the post in the No Covertreatment, conditional on privately joining the campaign — 83% in the placebo experiment, compared to 57% in the main experiment — constitutes suggestive evidence for the existence of (perceived) social sanctions for opposing police defunding and suggests that credible rationales may
significantly reduce the extent to which these sanctions prevent the public expression of dissent.
Anticipated persuasion While implausible, it remains possible that respondents anticipate
that the Cover Tweet will be more persuasive to followers than the No Cover Tweet, and that
this difference drives our estimated treatment effects. To directly address this concern, we run anauxiliary experiment (Auxiliary Experiment 3) in which we present Democratic and Independent
Twitter users with either the Cover or No Cover Tweet and then ask them to estimate the shareof their followers who would join the campaign after seeing their Tweet.11 Panel B of Figure 3 andAppendix Table B6 show a small and insignificant 1.9 percentage point difference, suggesting thatdifferences in posting rates are not driven by differences in the anticipated persuasiveness of the
Tweets.
3.1.5

Direct evidence on social cover mechanism

Finally, we provide direct evidence that our manipulation varies the perceived availability of social cover, and that this availability is an important consideration on respondents’ minds when
considering the expression of dissent.
Experimental design We conducted Auxiliary Experiment 4 with a sample of 400 Democratswith Twitter accounts recruited from Prolific. Respondents begin by reading the article presented
in Experiment 1 describing the evidence that defunding the police would increase violent crime.
We ask them to imagine that at this stage, they joined a campaign to oppose defunding the police.
As in the main experiment, all respondents are then given the chance to read the article again.12
Then, respondents randomized into the Cover condition are asked which of two Tweets they would
hypothetically prefer to post: the Tweet from the Cover condition in Experiment 1, or a Control
Tweet omitting any reference to a rationale:
11
12

See Appendix B.4 for details and Appendix E.7 for experimental instructions.
See Appendix E.8 for experimental instructions.

14

I have joined a campaign to oppose defunding the police: [LINK].
Respondents randomized into the No Cover condition are instead asked about their hypotheticalpreference between posting the Tweet from the No Cover condition in Experiment 1 or the Control
Tweet above. After respondents choose their preferred Tweet, we ask them to “Please explain why
you chose this Tweet rather than the other Tweet.” Our main object of interest is the difference
in respondents’ explanations between conditions.
A few comments about the experimental design are in order. First, we separately study preferences for the Cover Tweet over the Control Tweet and for the No Cover Tweet over the Control
Tweet, rather than directly estimating preferences for the Cover Tweet over the No Cover Tweet.
Our design thus avoids making the “Before/After” distinction between the Tweets salient, better capturing behavior both in our main experiment and in real-world settings and reducing thescope for experimenter demand effects. Similarly, our use of open-ended text to elicit motives,
rather than structured questions, avoids priming respondents on particular motivations and better
captures what naturally comes to mind when making their choice.
We hand-code open-ended responses across three categories.13(i) “Social cover” responses mention that the respondent’s preferred Tweet indicates to followersthat the article affected the respondent’s choice to join the campaign. For example, one
respondent writes: “I think the evidence provided in the article is an important catalyst in
why i would have joined the campaign and without any context that first tweet could be
misconstrued, or even cause me to be publicly shamed.”(ii) “Anticipated persuasion” responses mention that the article might persuade others. For
instance, one respondent writes: “The tweet is meant to not only inform people of yourdecision, but to also advertise others to do the same. Having supporting evidence for yourcause will increase the chance of other to side and agree with you. Tweet B does this, Tweet
A doesn’t.”(iii) “Information” responses mention that the article is informative or credible, or that it provides
an explanation for why people might want to join the campaign, but do not explicitly relate
the information to the respondent’s own views or other people’s views. For example, one
13

Our categories themselves are mutually exclusive, but a response might fall under multiple categories if the
respondent mentions multiple reasons for their choice. We hand-coded the responses in a team of two people blindly
to the treatment status.

15

respondent writes: “I would want others to see this article and know that I have someevidence to back my tweet.”As evidenced by the “Information” example above, many respondents classified as “Information”
may have had the “Social cover” or “Anticipated persuasion” mechanisms in mind, but wrote
responses that we could not unambiguously classify into either category. We chose a conservativecoding scheme for “social cover” and “anticipated persuasion” in order to provide a plausible lower
bound.
Results

We begin by analyzing respondents’ preferences over which Tweet to post. 83% of re-

spondents in the No Cover condition prefer the Tweet linking to the evidence over the Control
Tweet without the evidence, compared to 87% of respondents in the Cover condition. The treatment effect is not comparable with the effect estimated in Experiment 1: for example, we mightobserve zero treatment effect in this experiment and a strong treatment effect in Experiment 1
if most respondents prefer the Cover Tweet to the No Cover Tweet, but strongly prefer either
Tweet to the Control Tweet (while a minority of respondents exhibit strong preferences for the
shorter Control Tweet). Nonetheless, it is reassuring that the treatment effect is positive (thoughstatistically insignificant, p = 0.311). More importantly, the high fraction choosing the Tweet withthe rationale (whether the Cover or the No Cover version) over the Control Tweet suggests a
widespread preference for citing evidence when engaging in dissenting expression.
We next turn to the open-ended text. As shown in Panel C of Figure 3, a relatively large
fraction of respondents (20 percent) explicitly mention the social cover mechanism, three times thenumber who mention the anticipated persuasion mechanism (7 percent). The majority of responses(54 percent) fall into the “Information” category. However, given the considerations above, thesefigures likely substantially underestimate the number of respondents who meant to convey concerns
relating to social cover.
Focusing on treatment effects across conditions, the one-word manipulation indeed induces substantially more respondents to mention social cover (a 9 percentage point difference, or a 55 percent
effect relative to the No Cover mean). Consistent with our previous experiment measuring anticipated persuasion, the manipulation appears to have no effect on the probability that respondents
mention that their followers will find the article persuasive. Finally, the Cover treatment decreases
the share of responses in the “Information” category by 6 percentage points (though this difference
is not statistically significant). This presumably reflects the fact that some respondents would have16

written an “Information” response if assigned to the No Cover treatment (e.g. “The article provides
context for my decision”) but instead wrote a “Social cover” response when assigned to the Covertreatment (e.g. “The article explains why I made the decision”).
The perceived social costs of dissent in this setting are evidenced by the substantial numberof Tweets mentioning some form of social sanction — for example, “The second tweet contains
more information and explanation regarding my choice. Rather than being thrown off by misunderstanding the notion that I want to not defund the police, a direct explanation as to why would
make people feel less angry, more understanding, and more interested.” Importantly, zero responses
mention concerns about the “before” or “after” wording being misleading, and only two respondents (both in the Cover treatment) write that the Tweet with the rationale sounds strange or
unnatural. Alternative interpretations of the treatment effects — for example, respondents feelingthat perceived pressure by the experimenter (rather than the article itself) will serve as a social
cover, or respondents differentially desiring to signal their support of the article’s message — arenot supported by the open-ended responses. The small fraction of respondents who choose theControl Tweet without a rationale generally cite its shorter length as the reason for doing so (forexample, “Because it’s short and makes the point. I don’t think a lot of people would be interested
in clicking and reading the article.”). Given that the one-word manipulation in Experiment 1 holds
the length of the Tweet fixed, preferences for shorter Tweets will not affect our results.
Together, the placebo experiment, the anticipated persuasion experiment, and this experimenteliciting participant’s reasoning establish that the treatment effects documented in Experiment 1
are indeed driven by differences in the availability of a social cover.

3.2

Experiment 2: Interpretation of Anti-Defunding Rationale

Our theoretical framework implies that rationales lower the social cost of dissent by making theaction less informative about type. We now examine empirically how the availability of rationales
affects inference about the dissenter’s motives and the social sanctions levied upon the dissenter.
3.2.1

Sample and experimental design

Sample composition We conducted our pre-registered Experiment 2 in November 2021 witha sample of Democrats and Independents recruited from Prolific.14 Our final sample of 1,040
14

Our experiment was pre-registered in the AEA RCT registry under ID AEARCTR-0005462. The full set ofexperimental instructions is included in Appendix E.2.

17

Democrats and Independents is mostly balanced on observables across treatment arms (Appendix
Table B7).
Information about matched respondent Figure 4 outlines the structure of Experiment 2. After completing a battery of demographic and other background questions, respondents are informedthat they have been matched with a previous survey participant who joined a campaign to oppose
the movement to defund the police. They are then randomized into a Cover and a No Cover condition: respondents in the Cover condition are told that their matched participant authorized the
Tweet corresponding to the Cover condition of Experiment 1 (“Before I joined the campaign. . . ”)
whereas respondents in the No Cover condition are told that their matched participant authorized
the No Cover Tweet (“After I joined the campaign. . . ”).
Inference and sanctions We begin by asking respondents to respond to the following openended question: “Why do you think your matched participant chose to donate to the campaign?”
This approach avoids priming respondents to think about particular dimensions and instead directly
elicits “what comes to mind” (Gennaioli and Shleifer, 2010). As a more direct measure of inference about their matched participant’s prejudice, we subsequently tell them that their matched
participant had the opportunity to authorize a $5 donation to the National Association for the
Advancement of Colored People (NAACP) and ask them to guess whether or not the participant
donated. Finally, we also give respondents the opportunity to authorize a $1 bonus to their matched
respondent (at no cost to themselves): declining to do so is our measure of social sanction.
3.2.2

Results

We estimate statistically and economically significant treatment effects on all three measures oftype inference. Panel A of Figure 5 displays the fraction of participants in the Cover and No
Cover condition who believe their matched participant donated to the NAACP (results reported
in regression table form in Panel A, Columns 1–3 of Table 2). 27% of respondents in the No Covercondition believe their matched participant donated, compared to 35% of respondents in the Covercondition (p = 0.012). Similarly, Panel B of Figure 5 displays the fraction of participants who deny
their matched participant a bonus (results reported in regression table form in Panel B, Columns
1–3 of Table 2). 47% of respondents in the No Cover condition deny their matched participant abonus, compared to 40% of respondents in the Cover condition (p = 0.016). As shown in Table 2,these estimates are stable to the inclusion of demographic and partisan controls. As implied by our18

framework, even respondents who privately agree with their matched participant’s opposition to
defunding the police may choose to levy social sanctions if they believe that the only people who
would be comfortable publicly expressing such an opinion are prejudiced.
To analyze the open-ended text, we look for the words or phrases of up to three words that are
most characteristic of each condition. More precisely, we follow Gentzkow and Shapiro (2010) to
calculate Pearson’s χ2 statistic for each phrase p:
χ2p =


NR
NR R 2nRp n∼p − np n∼p,NRRR
N R + nN R )(nR + nN R )(nR
p + np )(np + n∼p )(np
∼p
∼p
∼p

N R are the number of times p appears across all responses in the Cover condition
where nRp , npand No Cover condition, respectively, and ni∼p is the total number of times a phrase that is not p
appears in condition i. This statistic will be higher when the use of p is more asymmetric acrosstreatment conditions and lower for phrases that are used rarely across both conditions. Appendix
Figure B1 plots the top 100 phrases by χ2 (where the χ2 statistics corresponding to phrases morecharacteristic of the No Cover condition have been multiplied by −1 to facilitate visualization).
Consistent with our framework and the treatment effects on the structured measures of inference,
we find that respondents in the Cover condition are more likely to use phrases related to the article
or the associated evidence — for example, “read an article,” “convincing,” “increase violent crime,”“study” — while respondents in the No Cover instead use phrases such as “Republican,” “racist,”and “probably white”.15
3.2.3

Exploring the role of credibility

How credible must rationales be in order to be effective? Insufficiently credible rationales may
fail to shift social inference and thus social sanctions: a dissenter’s audience may not believe thedissenter was persuaded by the rationale, and thus the rationale may not provide the dissenter social
cover. A society that sets this “credibility bar” too high may stifle the expression of legitimate
perspectives on issues where strong evidence does not exist. Indeed, if the credibility bar varies
between groups — for example, if conservatives are seen as more easily persuaded by fake news
than liberals — then groups held to a lower credibility bar can use a wider variety of rationales
15
These open-ended responses also allow us to mitigate concerns about other potential explanations for our findings:
for example, that respondents in the Cover condition believed that their matched participant felt pressured by theexperimenter to donate and this pressure led them to do so. No respondents mention this explanation, and inspectionof the phrases most characteristic of each condition suggest that this explanation does not drive the treatment effects.

19and thus may be willing to dissent in a wider variety of contexts.
To investigate the role of credibility, we run a slightly revised version of Experiment 2 (Auxiliary
Experiment 5) with a sample of 506 Democrats and Independents.16 We adjust the Tweet (in both
the Cover and No Cover condition) to remove the reference to Sharkey’s academic credentials andto the scientific evidence underlying the article’s claims. The revised Tweets read:
I have joined a campaign to oppose defunding the police: [LINK]. [Before/After] joining,
I was shown this article arguing that defunding the police would increase violent crime:[LINK]
Importantly, the article — published in the reputable Washington Post — remains constant, as does
every other aspect of the experiment). Qualitatively speaking, then, this change does not represent
a dramatic reduction in credibility. Nonetheless, as shown in Panels C and D of Figure 5 andColumns 4–6 of Table 2, the point estimate of the effect of the rationale on both structured measureof inference remains positive, but is much smaller: 30% of respondents in the No Cover condition
believe their matched partner donated, compared to 33% in the Cover condition (p = 0.58) and 44%
of respondents in the No Cover condition deny their matched partner the donation, compared to
42% in the Cover condition.17 While we are underpowered to conclude that these treatment effects
of around 2 percentage points are statistically significantly smaller than the treatment effects ofaround 7 percentage points estimated using the more credible rationale, the evidence is qualitatively
consistent with this slightly less credible rationale being substantially less effective.
The fact that even an article from a highly credible (liberal-leaning) source might fail to facilitate
liberals’ disagreement with the “politically correct” position illustrates how public dissent can besilenced by a vocal minority: only 25% of Democrats privately support decreasing funding forpolice in their area, compared with 34% of Democrats who privately support increasing funding(Parker and Hurst, 2021). To the extent that this phenomenon generalizes, then, it suggests thatfor politically charged issues, only highly credible rationales may be effective in facilitating liberal
dissent. This may thus stifle dissent on issues for which a strong scientific consensus does not yet
exist. Our revised experiment also speaks to one of the most common complaints surrounding“political correctness” culture: the alleged tendency of people to “take things out of context”.
The article prominently lists both Sharkey’s academic credentials and, in the first few paragraphs,
unequivocally states that “One of the most robust, most uncomfortable findings in criminology is
16
17

See Appendix E.9 for experimental instructions.
As shown in Appendix Table B8, our sample is balanced on observables across treatment arms.

20that putting more officers on the street leads to less violent crime.” Nonetheless, the revised Tweet
appears substantially less effective in shifting inference and reducing social sanctions. Requirements
for dissenters to ensure that no part of their argument can be taken out of context and stripped ofaccompanying rationales may leave limited scope for expressing nuanced arguments.

4

Support for Deporting Illegal Immigrants

Our next set of experiments examine the use and interpretation of rationales among a different
population — conservatives — and to justify a different stigmatized position — support for a
campaign to immediately deport all illegal Mexican immigrants. We examine our mechanism inthis different context for three primary reasons. First, defunding the police is a highly salient
but novel policy proposal, and it is thus unclear whether the power of rationales also extends tomore “traditional” policy questions, for which there may be more common knowledge about agreater body of evidence and partisan talking points. Second, opposition to defunding the police islikely stigmatized by the in-group (Democrats) but not the out-group (Republicans); in contrast,
supporting the immediate deportation of all illegal Mexican immigrants is less stigmatized by thein-group (Republicans), but is highly stigmatized by the out-group (Democrats). This setting thus
allows to examine whether rationales can be used to mitigate social sanctions levied by the outgroup as well as from the in-group. Finally, understanding the drivers of anti-immigrant narratives
on social media is of direct interest.
As in the previous experiment on the expression of dissent, we study the expression of xenophobia on social media. Given the widespread and growing importance of right-wing media as suppliersof anti-immigrant narratives, we examine a different form of rationale: a thirty-second clip fromone of the most popular cable news shows in the US, Tucker Carlson Tonight. In the clip, Carlson
draws upon statistics from the US Sentencing Commission to argue that illegal immigrants commit
violent crimes at substantially higher rates than citizens.18
18

The clip is available at https://www.youtube.com/embed/SDdkkTLCUUQ?autoplay=1&amp;controls=0&amp;end=
166&amp;fs=0&amp;modestbranding=1&amp;start=113&amp;iv_load_policy=3.

21

4.1
4.1.1

Experiment 3: Rationales and Pro-Deportation Expression
Sample and experimental design

Sample composition We conducted our pre-registered Experiment 3 in March 2021 with asample of Republicans and Independents.19 We recruited 1,130 participants through Luc.id. Afterscreening out respondents who did not want to join the campaign (as described below), we are left
with a final sample of 517 respondents. Our sample is balanced on observables across treatment
arms (Appendix Table C1).
Experimental design Our experimental design is broadly similar to that of Experiment 1; weprovide a diagram in Figure 6. As in Experiment 1, respondents log into our survey using their
Twitter account and respond to a set of demographic and other background questions. Respondents
then view the embedded clip from Tucker Carlson Tonight and are randomized into the Covercondition or the No Cover condition. Respondents in the Cover condition, but not in the No
Cover condition, are then provided with the link to the video. We then ask all respondents whether
they would like to join a campaign to immediately deport all illegal Mexican immigrants. The
survey terminates for respondents who do not join the campaign, leaving us with 517 remaining
respondents. Those respondents in the No Cover group who do join the campaign are provided the
URL to the video. In other words, at this point in the survey, the only difference between conditions
is whether respondents are provided with the video URL before (Cover ) or after (No Cover )joining the campaign — though all respondents watch the clip before joining the campaign. As wediscuss below, this difference in timing is key to avoiding explicit deception in our experimental
manipulation.
Respondents who join the campaign are informed that one component of the campaign involves
circulating a petition on Twitter calling for illegal Mexican immigrants to be deported. We show
them a screenshot of the Tweet and ask them if they are willing to schedule it to be posted on theiraccount. As in Experiment 1, we inform respondents that all Tweets will be posted all at once if
and when we have surveyed people in all US counties, that this is a common tactic used to makecampaigns trend on Twitter, and that we will delete all identifying information by no later thanAugust 1, 2021. Again as in Experiment 1, because we target fewer respondents than the numberof US counties, we ensure that Tweets will never be posted. We discuss the ethical considerations
19

Our experiment was pre-registered in the AEA RCT registry under ID AEARCTR-0007379. The full set ofexperimental instructions is included in Appendix E.3.

22

underlying our design in Appendix D.
Respondents in the Cover condition are asked whether they would like to schedule the following
Tweet:
I have joined a campaign to immediately deport all illegal Mexican immigrants. Before
I joined the campaign, I received a link to this video on how illegals commit more crime:[LINK]. Sign this petition to immediately deport all illegal Mexicans: [LINK]The key experimental manipulation is similar to that of Experiment 1: respondents in the
No Cover condition are presented with an identical Tweet, but with the “Before I joined thecampaign. . . ” replaced with “After I joined the campaign. . . ”. Although all respondents in fact
watched the video before joining the campaign, it is true that respondents in the Cover condition
received the link to the video before joining, while those in the No Cover condition received thelink after joining.20 This difference in wording suggests to potential readers of the Tweet that
respondents in the Cover group had been exposed to the video by Tucker Carlson before joining
the campaign — and thus potentially joined because they were convinced by the clip’s evidence —while respondents in the No Cover group had not been exposed before joining the campaign, andthus could not have joined due to the clip. As in Experiment 1, then, this manipulation varies theavailability of social cover while fixing the persuasion channel (all respondents are exposed to thesame video) and the anticipated persuasion channel (all respondents know their Tweet’s readers
will be exposed to the video, since it is linked in the Tweet).21
4.1.2

Results

Figure 7 displays the results, which we also show in regression table form in Table 3. We again
find an economically and statistically significant cover effect: 48% of respondents in the No Covercondition authorize the Tweet, while 65% of respondents in the Cover condition authorize theTweet (p < 0.01, a 0.35 standard deviation effect). This estimate is stable to the inclusion of20
One potential concern is that providing a link to respondents in the Cover condition, but not in the No Covercondition, induces differential selection into the campaign. Because we make the source of the clip obvious, we do notview this as a plausible confound. Indeed, we find no statistically significant difference in selection into the campaign
between groups (a 2.6 percentage point difference, p = 0.474), and our worst-case estimate under Lee (2009) bounds
remains statistically significant at the 1% level.
21
In principle, we could have used a similar design as Experiment 1: showing the video to respondents both before
and after they join the campaign. We concluded that such a manipulation would be less natural for a 30-second video
than for a longer article, as in Experiment 1.

23

demographic and partisan controls. The fact that the effect is larger than that estimated in Experiment 1 may reflect that Republicans feel greater stigma in joining a pro-deportation campaign
than Democrats feel in joining an anti-defunding campaign (which is also consistent with the lower
mean authorization rates in this experiment than in Experiment 1); or that Republicans perceive
the Tucker Carlson video as a more compelling rationale vis-a-vis their Twitter followers than
Democrats perceive the Washington Post article vis-a-vis their followers.22

4.2

Experiment 4: Interpretation of Pro-Deportation Rationale

We next examine how the availability of the social cover provided by the Tucker Carlson Tonight
clip shapes an audience’s inference about a dissenter’s underlying motivations and the resulting
social sanctions the dissenter faces.
4.2.1

Sample and experimental design

Sample composition

We conducted our pre-registered Experiment 4 in November 2021 with asample of 1,082 Democrats and Independents recruited from Prolific.23 We focus on Democrats
and Independents, as anti-immigrant expression is less likely to be stigmatized among Republicans.
Our sample is balanced on observables across treatment arms (Appendix Table C3).
Experiment 4 Experiment 4 follows the structure of Experiment 2; Figure 4 outlines the structure of the experiments (with red text corresponding to Experiment 4). Respondents are informedthat they have been matched with a previous survey participant who joined a campaign to deport
all illegal Mexican immigrants. As in Experiment 2, they are then randomized into a Cover anda No Cover condition: respondents in the Cover condition are told that their matched participant
authorized the Tweet corresponding to the Cover condition of Experiment 3 (“Before I joined
the campaign. . . ”) whereas respondents in the No Cover condition are told that their matched
participant authorized the No Cover Tweet (“After I joined the campaign. . . ”). Respondents
then respond to the following open-ended question: “Why do you think your matched participant
chose to donate to the campaign?”. Subsequently, they guess whether their matched participant
authorized a $5 donation to the US Border Crisis Children’s Relief Fund (an organization that22
In our pre-registered Auxiliary Experiment 6 designed to measure the persuasiveness of the rationale, we findmixed evidence for persuasive effects on private opinions; see Appendix C.2 for details and Appendix E.10 for
experimental instructions.
23
Our experiment was pre-registered in the AEA RCT registry under ID AEARCTR-0005462. The full set ofexperimental instructions is included in Appendix E.4.

24

seeks to provide care and basic hygiene items to children along the US–Mexico border) when given
the opportunity to do so, and they choose whether or not to deny a $1 bonus to their matched
participant.24
4.2.2

Results

Figure 8 reveals statistically and economically significant treatment effects. In Panel A of Figure 8, we display the fraction of participants in the Cover and No Cover condition who believe
their matched participant donated to the pro-immigrant organization (results are also reported inregression table form in Panel A of Table 4). 8.5% of respondents in the No Cover condition believe their matched participant donated, compared to 13.4% of respondents in the Cover condition(p < 0.01). Similarly, Panel B of Figure 8 displays the fraction of participants who deny theirmatched participant a bonus (results reported in regression table form in Panel B of Table 4). 80%
of respondents in the No Cover condition deny their matched participant a bonus, compared to74% of respondents in the Cover condition (p = 0.011). As shown in Table 4, these estimates arestable to the inclusion of demographic and partisan controls. We plot results from our analysis of
open-ended text in Appendix Figure C1 using the same procedure described in Section 3.2.2. As
in Experiment 2, respondents in the Cover condition are substantially more likely to use words
referencing the rationale — “watched a video,” “right wing media,” “link” — whereas respondents
in the No Cover condition mention phrases such as “Republican,” “extremist,” and “biased”.

4.3

Generalizing Findings

The social media setting of Experiments 1 and 3 affords a highly natural setting and audienceand a real-stakes outcome — and is of itself a context of policy relevance — but there are twopotential concerns about external validity. First, Twitter users still comprise a relatively small andselected fraction of the population, particularly among Republicans (Wojcik and Hughes, 2019).
Second, our requirement that respondents grant our “Tweetability” app permissions to schedule
posts on their Twitter account likely induces selection into our experiment. While this selection
does not affect the internal validity of Experiments 1 and 3, it might affect the extent to which theresults generalize to the broader population. To address these concerns, we present an additional
experiment (Auxiliary Experiment 7) that sacrifices some of the naturalness of Experiments 1 and 3
for a large and representative sample, while retaining a revealed-preference measure of respondents’24

We randomized the order of these two different outcomes and detect no significant order effects.

25willingness to publicly express dissent. We briefly describe the design and results here, relegating
details to Appendix C.4 and a discussion of ethical considerations to Appendix D.
We conduct this experiment in two waves in January 2020 and September 2020 with a totalof 5,736 Republican and Independent respondents. We outline the design in Appendix Figure C2.
All respondents are first told about the preliminary findings of an unpublished study (Lott, 2018)claiming that immigrants commit more crime than US citizens. Respondents are informed that they
will have the opportunity to authorize a $1 donation to Fund The Wall, an organization seeking
to construct the proposed US–Mexico border wall, and that we will post their individual donation
decision on our website. To vary the availability of a social cover, we tell respondents assigned to
the No Cover treatment that the web page will state that “all participants were surveyed before
Dr. Lott’s study was published in an academic journal.” In the Cover treatment, we instead tell
respondents the web page will state that “all participants were shown the preliminary findings from
Dr. Lott’s study before deciding whether or not to donate to Fund The Wall.”Appendix Table C4 shows that the availability of a social cover increases respondents’ willingness
to authorize the public donation: 46% of respondents authorize the donation in the No Covercondition, while 52% of respondents do so in the Cover condition (p < 0.01).25 Furthermore,examining heterogeneity in treatment effects by the 2016 vote share of the respondents’ county,
we find substantially larger treatment effects in more liberal areas: that is, the availability of asocial cover seems to be more important when the audience contains a larger fraction of people
who disagree with dissenter’s position. This heterogeneity also helps mitigate concerns about
experimenter demand effects driving the results.
In a further experiment (N=3,047; Auxiliary Experiment 8), we find using a similar design asin Experiments 2 and 4 that the availability of this rationale affects interpretation of the motives
underlying the decision to donate to Fund The Wall: donors with a rationale are seen as lessintolerant than those without a rationale.26 Together, these robustness experiments suggest thatthe availability of rationales may be an important determinant of the expression and interpretationof dissent in contexts beyond social media.
25

The smaller effect size in this experiment relative to our Twitter experiments may reflect the fact that we did
not screen out respondents who did not privately support the cause.
26
We provide further details in Appendix C.5.

26

5Discussion and Conclusion

This paper examines how rationales facilitate dissent by lowering the social cost of expressing
controversial opinions. In our model, rationales change some people’s private views or beliefs aboutsocial welfare, but they can also be used to justify dissent, shifting an audience’s inference about
the dissenter’s motivations. We explore these mechanisms among both liberal and conservative
respondents, focusing primarily on a natural setting and outcome: willingness to express dissent onsocial media. First, we show that liberal respondents are more likely to authorize a Tweet opposing
the movement to defund the police when they can credibly ascribe their views to strong scientificevidence. Consistent with our framework, a credible rationale shifts an audience’s inference about
the respondents and reduces resulting social sanctions. Similarly, conservative respondents are
more likely to authorize a Tweet calling for the deportation of all illegal immigrants from Mexico— and are seen as less intolerant after doing so — when they can ascribe their views to a Fox Newsclip.
We now discuss some implications of our framework and empirical results, which may provide
fruitful avenues for future research.
Political correctness and the limitations of rationales

In a “political correctness” culture,certain arguments (rationales) cannot be voiced because they are seen as legitimizing dangerous
or undesirable causes, and so anyone who voices such an argument is seen as supporting the cause
itself. For example, people who argue for the presence of reverse discrimination against men inlabor markets may be seen as sexists: that is, even scientific arguments such as correspondence
studies — which are typically effective rationales — may fail to provide a social cover. In somecases, this may be socially desirable: for instance, equating the use of a rationale with sexism may
prevent sexist individuals from citing rationales they do not believe or cherry-picking arguments
to support their claims. In other cases, political correctness culture may stifle socially important
forms of dissenting expression by stigmatizing rationales that would typically be seen as highly
credible.
Individuals or institutions seeking to eliminate certain forms of public behavior — for better orfor worse — may use multiple levers to silence dissenters. One lever, explored in Section 3.2.3, is toundermine the credibility of rationales directly. Another lever is to manipulate the real or perceived
correlation between knowledge of a rationale and underlying type, tying the rationale directly to the27stigmatized motive.27 Indeed, in the limit in which only people with stigmatized motives are awareof a certain rationale — e.g. because only they consume the extreme news sources through which therationale is broadcast, or because only they follow a fringe public figure who spreads the rationale— the rationale is completely ineffective, as to use it is to reveal one’s motives with certainty. For
instance, giving our experimental respondents the opportunity to cite One America News Network(an extreme right-wing outlet) rather than Washington Post (a mainstream newspaper) or Tucker
Carlson (the most popular opinion news host) would likely eliminate real and perceived social
cover. Tactics to manipulate the real or perceived correlation between motive and rationale include
censoring certain figures or otherwise disallowing them a public platform (e.g. disinviting campus
speakers), or branding particular media sources or speakers as fringe. This can also help explain
how censorship techniques such as China’s “Great Firewall” can be highly effective in repressing
discourse unfriendly to the regime, even if citizens can bypass them relatively easily (Chen andYang, 2019). Further exploring the conditions under which rationales are most effective, and theunifying features of effective rationales, is an important direction for future research.
Political entrepreneurship and populism

Successful politicians often base their campaigns

on simple messages and policy platforms that resonate with the general public. Populist politicians
are particularly skilled at presenting simple explanations for crises, often blaming scapegoats such as
elites or minority groups.28 Our framework can shed light on why some politicians and some appeals
are more effective than others. While the persuasive effects of propaganda are doubtless important(Adena et al., 2015), propaganda may also generate social cover, enabling supporters to speak theirmind more openly and spread the message through their social circle, an effect documented for
Nazi propaganda in Weimar Republic by Satyanath et al. (2017) (see also Bursztyn et al. 2019
for evidence of social networks propagating extreme views about ethnic minorities in Russia). The
strength of this “social amplifier” channel depends not only on the number of individuals who holdstigmatized views, but the number of individuals who could not express these views prior to therationale becoming widespread.
This distinction can provide one explanation for why the Nazis were able to leverage social
networks and associations while other parties, including communists, could not: if antisemitism
27
For example, during the Second Red Scare, Joseph McCarthy and his allies explicitly tied several rationales fordissenting with government policy to Communist sympathies. Famously, physicist J. Robert Oppenheimer — credited
as the “father of the atomic bomb” — was stripped of his security clearances when political opponents branded his
opposition to the development of the hydrogen bomb to alleged Soviet loyalties (Cassidy, 2005).
28
See Guriev and Papaioannou (2020) for a review on the political economy of populism. Bursztyn et al. (2022b)
applies our framework to explore the scapegoating of minorities during economic crises.

28was stigmatized, but relatively common and persistent (Voigtländer and Voth, 2012), then Nazi
rhetoric blaming Jews for Germany’s problems generated a large social amplifier, thereby furthering
Nazi views. Blaming elites, on the other hand, was less stigmatized, and thus generated far smaller
amplifiers. Interestingly, Cantoni et al. (2019) show that in the 2017 Bundestag election, Alternative
fur Deutschland (AfD) captured more votes in places that voted for Nazis in 1933 (consistent with
AfD providing right-wing rationales in general) but not in places where antisemitic pogroms were
historically more numerous, as AfD does not use any explicitly antisemitic rhetoric.29
Fake and misleading news

Our findings are also relevant for the debate about the influenceof fake and misleading news on society. Some recent studies suggest that their persuasive effect islimited (Allcott and Gentzkow, 2017; Nyhan, 2018), while others suggest that they can be effectiveat changing behavior (Barrera et al., 2020) and that individuals may have trouble distinguishing
between fake and real news (Angelucci and Prat, 2021) or between facts and opinions (Bursztyn etal., 2022a). Our results point, however, to an alternative mechanism through which misleading news
can affect public expression. Specifically, fake news can generate a “social amplifier”: rationales
that plausibly persuade a small subset of the population can change public behavior among a muchlarger fraction of the population, increasing their willingness to express otherwise-stigmatized viewsby leveraging fake news as a rationale. Interestingly, in Barrera et al. (2020), subjects exposed to
fake news were not only more willing to support an extreme candidate (Marine Le Pen), but also
were unlikely to change their opinion after being exposed to fact-checks — even though these factchecks improved factual knowledge. This evidence is difficult to explain by the persuasive power offake news alone, but it is consistent with the role of fake news as rationales: fake and misleading
news can generate social cover for individuals to express extreme views, and debunking does not
eliminate social cover as long as the fact-check can be plausibly dismissed.
This insight has implications for debunking fake news spread online and offline. Among otherplatforms, Facebook and Twitter have conducted small-scale experiments evaluating strategies tocurtail the spread of misinformation, including warning users before they post an article flagged as
fake news and flagging fake or misleading news when it appears on users’ timelines (e.g., because
29

Germany has strict laws on anti-Semitic speech which criminalize Holocaust denial or “incitement to hatred”(Volksverhetzung). Our logic shows how that laws can effectively prevent certain rationales from being used, eventhough they cannot be fully effective against, for example, dog whistles, “sending a message to certain potential
supporters in such a way as to make it inaudible to others whom it might alienate or deniable for still others who
would find any explicit appeal along those lines offensive” (Goodin and Saward, 2005; Haney-López, 2014; Grosjean etal., 2020), or disguising taste-based discrimination (Becker, 1957) as statistical discrimination (Phelps, 1972; Arrow,1973).

29

a friend shared it). The former initiative decreases the persuasive effect of fake news for a user
who seeks to spread it, while the latter decreases the anticipated persuasiveness of the rationale.
Yet because these experiments have occurred only among a small fraction of users, people havea ready-made social cover when sharing fake news: they can credibly claim that they were notwarned the news was fake.30
Our results highlight the potential importance of eliminating social cover: ensuring that theaudience knows that the poster knew the news had been debunked and nonetheless chose to post it.
A simple path would be to scale the debunking experiments to the entire userbase, thus generating common knowledge that all users are warned before posting fake news. Because the generalequilibrium results of such a change differ significantly from the partial equilibrium results, current
estimates of the effects of debunking on users’ propensity to share fake news may substantially
understate the true effects that would be realized if platforms were to fully scale up the feature.
At the same time, the evidence from Barrera et al. (2020) emphasizes the importance of platforms’
credibility when debunking rationales: when credibility is lacking (for example, as a result of past
mistakes) fake and misleading news retains its power to generate social cover for the expression of
stigmatized views.
Rationales beyond politics: “Acting White” Austen-Smith and Fryer (2005) model negative
stigma associated with educational investment — “Acting White” — which might arise if choosing
to study signals that the individual has limited social opportunities, or if choosing to study signalsthat the individual is weakly attached to their social group. In such settings, providing monetary
incentives for exerting educational effort (as discussed in Levitt et al. 2016) might provide students
with a rationale, allowing them to attribute educational investments not to academic interest but
rather to the incentive. For similar reasons, in these settings, cold-calling after asking a question
might be preferable to allowing students to volunteer answers. Understanding the use of rationales
to generate social cover in educational and other non-political settings is an important area for
future investigation.
30
Indeed, both Twitter and Facebook’s fact-checking efforts have been widely criticized for a lack of transparency,
and it is thus certain that most users lack information about how the platforms fight misinformation (Nyhan, 2017).

30

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Figures
Figure 1: Experiment 1: flow of dissent design
Consent, Twitter login, attention check,demographics

Information provision
Washington Post article on the link between policing
and violent crime

Private support"Would you like to join a nonpartisan campaign that
opposes defunding the police?"No

Survey ends

Yes

Information provision (again)
Given second opportunity to read through the
Washington Post article on the link between policing
and violent crime

Tweet decision (Cover)
Would you like to authorize the following Tweet?
I have joined a campaign to oppose defunding thepolice: LINK. Before joining, I was shown this article
written by a Princeton professor on the strong scientificevidence that defunding the police would increase
violent crime: [LINK]

Tweet decision (No Cover)
Would you like to authorize the following Tweet?
I have joined a campaign to oppose defunding the police:
LINK. After joining, I was shown this article written by a
Princeton professor on the strong scientific evidence thatdefunding the police would increase violent crime: [LINK]

End of study

37

Figure 2: Experiment 1: willingness to post anti-defunding Tweet

Notes: Figure displays the fraction of respondents authorizing the Tweet indicating their opposition to the
movement to defund the police, separately by experimental condition. Error bars indicate 95% confidence intervals.
p-values obtained from a two-sample t-test of equality of means.

38Figure 3: Experiment 1: ruling out alternative interpretations
Panel A: Rainforest placebo experiment

Panel B: Anticipated persuasion experiment

Panel C: Motivation for choosing Tweet with rationale(a) Social Cover(b) Anticipated persuasion(c) Information

Notes: Panel A of Figure 3 displays the fraction of participants who authorize the Tweet in each condition of
the placebo experiment, described in Section 3.1.4. Panel B displays the mean of respondents’ guesses as to thefraction of their followers who would be persuaded by the Tweet to join the campaign, elicited in the anticipatedpersuasion experiment described in Section 3.1.4. Panel C displays the fraction of respondents who mention eachof the three motives when choosing which Tweet to post, elicited in the open-ended text experiment described in
Section 3.1.5. Error bars indicate 95% confidence intervals. p-values obtained from a two-sample t-test of equalityof means.

39

Figure 4: Experiments 2 and 4: flow of inference design
Consent, attention check,demographics

Information about matched respondent
Matched respondent joined campaign to [DEFUND:
oppose defunding the police] [DEPORT: deport allillegal Mexican immigrants]

Partner's Tweet (No Cover)Your partner also agreed to post the Tweet below on their
Twitter account:[DEFUND: I have joined a campaign to oppose
defunding the police: LINK. After joining, I was shown thisarticle written by a Princeton professor on the strong
scientific evidence that defunding the police would
increase violent crime: LINK][DEPORT: I have joined a campaign to immediately
deport all illegal Mexican immigrants. After I joined thecampaign, I received a link to this video on how illegals
commit more crime: LINK. Sign this petition to
immediately deport all illegal Mexicans: LINK. ]Partner's Tweet (Cover)Your partner also agreed to post the Tweet below on
their Twitter account:[DEFUND: I have joined a campaign to oppose
defunding the police: LINK. Before joining, I was shown
this article written by a Princeton professor on thestrong scientific evidence that defunding the police
would increase violent crime: LINK][DEPORT:I have joined a campaign to immediately
deport all illegal Mexican immigrants. Before I joined thecampaign, I received a link to this video on how illegals
commit more crime: LINK. Sign this petition to
immediately deport all illegal Mexicans: LINK.]

Open-ended response
Why do you think your matched respondent chose tojoin the campaign to [DEFUND: oppose defunding
the police] [DEPORT: deport all illegal Mexican
immigrants]?

Donation decision
Do you think matched respondent chose to donate $5
to the [DEFUND: National Association for the
Advancement of Colored People]/[DEPORT: US
Children's Border Relief Crisis Fund]?

Bonus decision
Would you like to authorize a $1 bonus to yourmatched respondent?

End of study

Notes: Experiments 2 and 4 have identical structures, so we present both experiments jointly. Blue text corresponds to Experiment 2, studying opposition to the movement to defund the police; red text corresponds toExperiment 4, studying support for immediately deporting all illegal Mexican immigrants.

40

Figure 5: Experiment 2: Interpretation of anti-defunding Tweet(a) High credibility: beliefs about NAACP donation(b) High credibility: denial of bonus(c) Low credibility: beliefs about NAACP donation(d) Low credibility: denial of bonus

Notes: Panels A and C present the fraction of respondents who believe their matched participant donated to the
NAACP (a pro-black organization). Panels B and D present the fraction of respondents who deny their matched
participant a $1 bonus. Panels A and B present results from the (high-credibility) main experiment; Panels C andD present results from the lower-credibility experiment. Error bars indicate 95% confidence intervals. p-values
obtained from a two-sample t-test of equality of means.

41Figure 6: Experiment 3: design
Consent, Twitter login, attention check,demographics

Information treatment
Clip from Tucker Carlson Tonight on the link between
illegal immigration and crime

No Cover

Cover

Link
Link to Tucker Carlson Tonight clip

Private support"Would you like to join a campaign to immediately
deport all illegal Mexican immigrants?"

No

Survey ends

Yes

Link
Link to Tucker Carlson Tonight clip

Tweet decision
Would you like to authorize the following Tweet?
I have joined a campaign to immediately deport all illegal
Mexican immigrants. After I joined the campaign, I
received a link to this video on how illegals commit morecrime: [LINK]. Sign this petition to immediately deport allillegal Mexicans: [LINK].

Tweet decision
Would you like to authorize the following Tweet?
I have joined a campaign to immediately deport allillegal Mexican immigrants. Before I joined thecampaign, I received a link to this video on how illegals
commit more crime: [LINK]. Sign this petition to
immediately deport all illegal Mexicans: [LINK].

End of study

42

Figure 7: Experiment 3: willingness to post pro-deportation Tweet

Notes: Figure displays the fraction of respondents authorizing the Tweet indicating their support for immediately
deporting all illegal Mexican immigrants. Error bars indicate 95% confidence intervals. p-values obtained from a
two-sample t-test of equality of means.

43Figure 8: Experiment 4: Interpretation of pro-deportation Tweet(a) Beliefs about USBCCRF donation(b) Denial of bonus
Notes: Panel A presents the fraction of respondents who believe their matched participant donated to the US
Border Crisis Children’s Relief Fund. Panel B presents the fraction of respondents who deny their matched
participant a $1 bonus. Error bars indicate 95% confidence intervals. p-values obtained from a two-sample t-testof equality of means.

44

Tables
Table 1: Experiment 1: Willingness to post anti-defunding Tweet
Dependent variable:
Anti-defunding Tweet
(1)

(2)

(3)

Cover

0.123∗∗∗(0.042)0.118∗∗∗(0.042)0.120∗∗∗(0.042)

DV mean
DV std. dev.
Observations
Demographic controls
Partisan controls

0.637
0.481
529
No
No

0.637
0.481
529
Yes
No

0.637
0.481
529
Yes
Yes

Notes: The dependent variable is an indicator taking value
1 if the respondent chose to schedule the post. Demographic
controls include age, age squared, a set of race indicators, a
Hispanic indicator, a male indicator, a set of education indicators. Partisan controls include indicators for “Very conservative”, “Conservative”, “Neither liberal nor conservative”(omitted), “Liberal”, and “Very liberal”. Robust standard
errors are reported.

45

Table 2: Experiment 2: Inference about and social sanctions toward matched anti-defunding
respondent
High credibility
(1)

(2)

Low credibility(3)

Panel A:

(4)

(5)

(6)

Belief partner donatedCover

0.072∗∗(0.029)0.072∗∗(0.029)0.067∗∗(0.029)0.023(0.041)

0.023(0.042)0.019(0.042)

DV mean
DV std. dev.

0.309
0.462

0.309
0.462

0.309
0.462

0.314
0.465

0.314
0.465

0.314
0.465

Panel B:

Denied bonus to partner−0.074∗∗(0.031)−0.074∗∗(0.031)−0.067∗∗(0.030)−0.019(0.044)−0.028(0.044)−0.015(0.043)

DV mean
DV std. dev.

0.435
0.496

0.435
0.496

0.435
0.496

0.429
0.495

0.429
0.495

0.429
0.495

Observations
Demographic controls
Partisan controls

1,040
No
No

1,037
Yes
No

1,036
Yes
Yes

506
No
No

506
Yes
No

506
Yes
Yes

Cover

Notes: The dependent variable in Panel A is an indicator taking value 1 if the respondent reports
believing that his or her matched partner donated to the US Border Crisis Children’s Relief Fund.
The dependent variable in Panel B is an indicator taking value 1 if the respondent denied hisor her matched partner a $1 bonus. Columns 1–3 report results for the main (high-credibility)
experiment; Columns 4–6 report results for the lower-credibility experiment. Demographic controls include age, age squared, a set of race indicators, a Hispanic indicator, a male indicator, aset of education indicators. Partisan controls include indicators for “Very conservative”, “Conservative”, “Neither liberal nor conservative” (omitted), “Liberal”, and “Very liberal”. Robust
standard errors are reported.

46

Table 3: Experiment 3: Willingness to post pro-deportation Tweet
Dependent variable:
Anti-immigrant Tweet
(1)

(2)

(3)

Cover

0.168∗∗∗(0.043)0.175∗∗∗(0.043)0.173∗∗∗(0.043)

DV mean
DV std. dev.
Observations
Demographic controls
Partisan controls

0.563
0.497
517
No
No

0.563
0.497
517
Yes
No

0.563
0.497
517
Yes
Yes

Notes: The dependent variable is an indicator taking value
1 if the respondent chose to schedule the post. Demographic
controls include age, age squared, a set of race indicators, a
Hispanic indicator, a male indicator, a set of education indicators. Partisan controls include indicators for “Very conservative”, “Conservative”, “Neither liberal nor conservative”(omitted), “Liberal”, and “Very liberal”. Robust standard
errors are reported.

47

Table 4: Experiment 4: Inference about and social sanctions toward matched pro-deportation
respondent(1)
Panel A:

(2)

(3)

Belief partner donatedCover

0.049∗∗∗(0.019)0.051∗∗∗(0.019)0.048∗∗(0.019)

DV mean
DV std. dev.

0.110
0.313

0.110
0.313

0.110
0.313

Panel B:

Denied bonus to partner−0.065∗∗(0.026)−0.065∗∗(0.026)−0.061∗∗(0.026)

DV mean
DV std. dev.

0.771
0.421

0.771
0.421

0.771
0.421

Observations
Demographic controls
Partisan controls

1,082
No
No

1,081
Yes
No

1,081
Yes
Yes

Cover

Notes: The dependent variable in Panel A is an indicator taking value 1 if the respondent reports believing that his or her
matched partner donated to the US Border Crisis Children’s
Relief Fund. The dependent variable in Panel B is an indicatortaking value 1 if the respondent denied his or her matched partner a $1 bonus. Demographic controls include age, age squared,
a set of race indicators, a Hispanic indicator, a male indicator, aset of education indicators. Partisan controls include indicators
for “Very conservative”, “Conservative”, “Neither liberal nor
conservative” (omitted), “Liberal”, and “Very liberal”. Robust
standard errors are reported.

48

Online Appendix:
Not for publication
Our supplementary material is structured as follows. Appendix A provides proofs of all theoreticalresults in Section 2. Appendix B provides supporting material for the experiments presented in
Section 3. Appendix C provides supporting material for the experiments presented in Section 4.
Appendix D discusses the ethical considerations underlying all experimental designs. Finally, Appendix E provides the instruments for all experiments described in the paper.

49

A

Theoretical Results

A.1

Proof of Proposition 1

First, let us prove that for random variable t distributed with c.d.f. H (·) and p.d.f. h (·) ,dE (t | t > τ ) ≤ 1.
dτLet zτ = t − τ be a family of random variables indexed by τ ; we need to show thatE (zτ | zτ ≥ 0)
is non-increasing in τ .
Denoting the c.d.f. of zτ by Fτ (·) and its p.d.f. by fτ (·), we haveZ +∞1yfτ (y) dy.
E (zτ | zτ ≥ 0) =1 − Fτ (0) 0
The integral may be rewritten as
Z y

Z +∞
Z +∞
Z +∞ Z yyfτ (y) dy =fτ (y)
1dx dy =fτ (y) dxdy
0
0
0
0
0
Z +∞ Z +∞Z +∞=fτ (y) dydx =(1 − Fτ (x)) dx,0x0

where we used Fubini’s theorem to change the order of integration.
Note that Fτ (x) = Pr (zτ ≤ x) = Pr (t ≤ x + τ ) = H (x + τ ). We therefore have
Z +∞
Z +∞
1 − Fτ (x)1 − H (x + τ )E (zτ | zτ ≥ 0) =dx =dx.
1 − Fτ (0)1 − H (τ )00
The integrand is non-increasing in τ pointwisely (i.e., for any fixed x ≥ 0), becaused 1 − H (x + τ )h (τ ) (1 − H (x + τ )) − h (x + τ ) (1 − H (τ ))=dτ
1 − H (τ )(1 − H (τ ))2
1 − H (x + τ )h (τ )h (x + τ )−≤ 0,=
1 − H (τ )1 − H (τ ) 1 − H (x + τ )(3)because the first term is positive and the second is nonpositive due to monotone hazard rated
property. This proves that E (zτ | zτ ≥ 0) is non-increasing in τ , and thus dτ
E (t | t > τ ) ≤ 1.
1
Now, for any fixed social cost S, type ti would choose di = 1 if ti > β S − w0 and would choose
di = 0 if the opposite inequality holds. Thus, every equilibrium is characterized by a threshold τ .
This threshold τ satisfies the condition
G (τ ) = −w0 ,

50

(4)

whereG (τ ) = τ −γ
E (ti | ti > τ ) .
β

(5)

d
Since, as we proved, dτE (ti | ti > τ ) ≤ 1 and γ < β, the G (τ ) is strictly increasing in τ , andfurthermoreγd
G (τ ) ≥ 1 − > 0.
dτβThis shows that the equation (4) has a unique solution. This completes the proof. 

A.2

Proof of Proposition 2

Since the distributions are normal, the posterior of citizen i is given by the usual formula
w1 = E (w | s) = w0
We havew1 − w0 =

2
σε2
σw
+
s
.
2 + σ22 + σ2
σw
σw
ε
ε

2
σw
(s − w0 ) ,2 + σ2σw
εso w1 > w0 . From the proof of Proposition 1, the new equilibrium again takes the form of athreshold τ̃ that satisfies
G (τ̃ ) = −w1 ,dwhere G (·) is defined in (5). Since dτG (τ ) > 0 and −w1 < −w0 , we have τ̃ < τ (and furthermore,dsince dτ G (τ ) < 1, the difference τ − τ̃ > w1 − w0 , so the decrease in threshold τ is larger than
the increase in w). Now, τ̃ < τ implies that the share of citizens choosing di = 1 has increased:
1 − H (τ̃ ) > 1 − H (τ ). Lastly, the social cost is now equal γE (ti | ti > τ̃ ) < γE (ti | ti > τ ), so it islower than without the signal s. This completes the proof. 

A.3

Proof of Proposition 3

We start by establishing the uniqueness of equilibrium in this case.31 Let S̄ be the social cost ofchoosing di = 1 in a hypothetical equilibrium. Then the citizen would choose di = 1 if ti > β1 S̄ − whfollowing signal sh and if ti > β1 S̄ −wl following signal sl . This implies that there are two thresholds,
τh and τl , that satisfy τl − τh = wh − wl . Denote τ̄ = β1 S̄ − w0 ; then τh = τ̄ + w0 − wh andτl = τ̄ + w0 − wl . From now on we describe the equilibrium in terms of τ̄ .
In what follows, we use the following probabilities. We denotep (x, y) = µ (1 − H (x)) + (1 − µ) (1 − H (y)) ,31

Notice first that our assumption of rational expectation of ti conditional on di = 1 allows us to bypass thediscussion of whether members of the audience get signals sl , sh , or both. Rational expectation can be formed inpractice if people had prior interactions with those who choose di = 1 and learned their type, which allows them tomake a correct expectation in equilibrium about individuals who choose di = 1 with a given piece of evidence. An
alternative way is to assume that the audience is sophisticated, understands the whole signal structure, but does notknow which signal citizen i got, and faces the signal decomposition problem as a result.

51

so


p (τ̄ + w0 − wh , τ̄ + w0 − wl ) = p

1
1
S̄ − wh , S̄ − wlββis the probability of choosing di = 1 if the citizen faces social cost S̄. We also let
q (x, y) =µ (1 − H (x)),
p (x, y)so q (τ̄ + w0 − wh , τ̄ + w0 − wl ) is the equilibrium conditional probability that citizen i got signal
sh conditional on choosing di = 1.
Define the functionS̄ (z) = γq (z + w0 − wh , z + w0 − wl ) E (ti | ti > z + w0 − wh )+γ (1 − q (z + w0 − wh , z + w0 − wl )) E (ti | ti > z + w0 − wl ) .
In equilibrium characterized by τ̄ , the social cost of choosing di = 1 equals S̄ (τ̄ ). Given the above,
thresholds τh = τ̄ + w0 − wh and τl = τ̄ + w0 − wl are equilibrium thresholds for choosing di = 1
after getting signals sh and sl , respectively, if and only if τ̄ solves the equationτ̄ −1S̄ (τ̄ ) = −w0 .
β

(6)

d 1
Let us show that dz
γ S̄ (z) ≤ 1. Indeed, from the proof of Proposition 1, we havedE (ti | ti > z + w0 − wh ) ≤ 1;dz
d
E (ti | ti > z + w0 − wl ) ≤ 1.
dz
Furthermore,
E (ti | ti > z + w0 − wl ) > E (ti | ti > z + w0 − wh ) .
Lastly, we haveq (z + w0 − wh , z + w0 − wl ) ==µ (1 − H (z + w0 − wh ))µ (1 − H (z + w0 − wh )) + (1 − µ) (1 − H (z + w0 − wl ))1.
1−µ 1−H(z+w0 −wl )1 + µ 1−H(z+w0 −wh )Now,d 1 − H (u + (wh − wl ))d 1 − H (z + w0 − wl )=≤ 0,
dz 1 − H (z + w0 − wh )du1 − H (u)where we denoted u = z + w0 − wh and used the calculation (3) from the proof of Proposition 1.

52

dThis immediately implies that dz
q (z + w0 − wh , z + w0 − wl ) ≥ 0. Summing up, we havedd 1S̄ (z) = q (z + w0 − wh , z + w0 − wl ) E (ti | ti > z + w0 − wh )
dz γ
dz
d
+ (1 − q (z + w0 − wh , z + w0 − wl )) E (ti | ti > z + w0 − wl )

 dz
d
+
q (z + w0 − wh , z + w0 − wl )dz
× (E (ti | ti > z + w0 − wh ) − E (ti | ti > z + w0 − wl )) .
Notice that the sum of the first two lines does not exceed 1 (since both derivatives do not exceed1), and term on the third line is positive and the one on the fourth is negative, so their product is
d 1
negative. This proves that dz
γ S̄ (z) ≤ 1. Now, as in the proof of Proposition 1 this implies thatthe equation (6) has a unique solution τ̄ , which proves the uniqueness of equilibrium in this case.
Let us now show that in this solution, τ̄ < τ and S̄ (τ̄ ) < S (τ ), where S (τ ) = γ1 E (ti | ti > τ )is the equilibrium social cost in the absence of any signal, in the unique solution τ . To do this, it
is sufficient to show that S̄ (τ ) < S (τ ). Indeed, this would imply thatτ−11S̄ (τ ) > τ − S (τ ) = −w0 ,ββand since τ̄ satisfies (6) and the function x − β1 S̄ (x) is increasing, we would get τ̄ < τ . Then wewould getS̄ (τ̄ ) = β (τ̄ + w0 ) < β (τ + w0 ) = S (τ ) ,as required. So, to complete the proof, we need to show that S̄ (τ ) < S (τ ).
In the light of condition (2) and by continuity of H (·), there exists ŵh ∈ (0, wh ) such thatµ (H (τ ) − H (τ − (ŵh − w0 ))) = (1 − µ) (H (τ + (w0 − wl )) − H (τ )) .
Let Ŝ denote the valueŜ = γq (τ + w0 − ŵh , τ + w0 − wl ) E (ti | ti > τ + w0 − ŵh )+γ (1 − q (τ + w0 − ŵh , τ + w0 − wl )) E (ti | ti > τ + w0 − wl ) ;in other words, the expression for Ŝ is analogous to S̄ (τ ), except that wh is replaced by ŵh .
We now show that S̄ (τ ) < Ŝ < S (τ ). To prove the first inequality, we use some algebra toestablish that
11S̄ (τ ) = (1 − ρ) Ŝ + ρE (ti | ti ∈ (τ + w0 − wh , τ + w0 − ŵh )) ,
γ
γ
where
ρ = q (τ + w0 − wh , τ + w0 − wl )H (τ + w0 − ŵh ) − H (τ + w0 − wh ).
1 − H (τ + w0 − wh )Since ρ > 0 and γ1 Ŝ < E (ti | ti ∈ (τ + w0 − wh , τ + w0 − ŵh )) as the former is an expectation takenover values to the right of τ + w0 − ŵh while the latter expectation is taken over values to the left

53

of that point, we get S̄ (τ ) < Ŝ.
Let us now prove that Ŝ < S (τ ). Spelling out q (τ + w0 − ŵh , τ + w0 − wl ) and expectationsin the definition of Ŝ, we haveR∞
xh (x) dx
1
S (τ ) − Ŝ= τγ
1 − H (τ )R∞R∞µ τ +w0 −ŵh xh (x) dx + (1 − µ) τ +w0 −wl xh (x) dx−.
µ (1 − H (τ + w0 − ŵh )) + (1 − µ) (1 − H (τ + w0 − wl ))Notice that by the definition of ŵh the denominators in both terms are equal, hence S (τ ) − Ŝ has
the same sign as
 Z ∞

Z ∞
Z ∞
xh (x) dx − µ
xh (x) dx + (1 − µ)xh (x) dx
τ +w0 −ŵhτ

τ +w0 −wlZ τ +w0 −wl= (1 − µ)Z τ
xh (x) dx − µτxh (x) dx
τ +w0 −ŵh= (1 − µ) (H (τ + w0 − wl ) − H (τ )) E (ti | ti ∈ (τ, τ + w0 − wl ))−µ (H (τ ) − H (τ + w0 − ŵh )) E (ti | ti ∈ (τ + w0 − ŵh , τ )) .
Since the coefficients in front of the expectations in the last two lines are the same (again, by the
choice of ŵh ), the sign of this expression is the same as the sign ofE (ti | ti ∈ (τ, τ + w0 − wl )) − E (ti | ti ∈ (τ + w0 − ŵh , τ )) ,which is positive, because the first term is greater than τ and the second is less than that. Therefore,Ŝ < S (τ ).
We have thus proved that S̄ (τ ) < Ŝ < S (τ ) which, as we showed earlier, implies the results
stated. This completes the proof. 

54

Table B1: Overview of Data Collections
Experiment

ProviderDatesExperiment 1: Willingness to post anti-defunding Tweet –Democrats authorizing Twitter access (N=1,122)

Luc.id,Cloudresearch

October 2021

Experiment 2:
Interpretation of anti-defunding Tweet –Democrats (N=1,040)

Prolific

November 2021

Experiment 3: Willingness to post pro-deportation Tweet – Republicans authorizing Twitter access (N=1,130)

Luc.idMarch 2021

Experiment 4: Interpretation of pro-deportation Tweet – Republicans (N=1,082)

Prolific

November 2021

Auxiliary Experiment 1: Persuasiveness of anti-defunding article– Democrats (N=1,008)

Prolific

December 2021

Auxiliary Experiment 2: Placebo: willingness to post proconservation Tweet – respondents authorizing Twitter access(N=483)Luc.id,Cloudresearch

December 2021
and January 2022

Auxiliary Experiment 3: Anticipated persuasiveness of antidefunding Tweet – Democrats (N=501)

Prolific

November 2021

Auxiliary Experiment 4: Motives underlying the choice –Democrats with Twitter account (N=400)

ProlificJanuary 2022

Auxiliary Experiment 5: Interpretation of lower-credibility antidefunding Tweet – Democrats (N=506)

Prolific

November 2021

Auxiliary Experiment 6: Persuasiveness of pro-deportation Tweet– Republicans (N=2,012)

Prolific, Lucid

December 2021

Auxiliary Experiment 7 (wave 1): Willingness to donate to antiimmigrant organization – Conservatives (N=4,457 )Luc.idJanuary 2020

Auxiliary Experiment 7 (wave 2): Willingness to donate to antiimmigrant organization – Conservatives (N=1,299)

Luc.idSeptember 2020

Auxiliary Experiment 8: Interpretation of anti-immigrant donation – Liberals (N=3,047)

Luc.idFebruary 2020

Panel A: Main Experiments

Panel B: Auxiliary Experiments

Notes: Reported sample sizes for Experiment 1, Experiment 3, and Auxiliary Experiment 2 include
respondents who chose not to join the campaigns and therefore are not included in the sample weanalyze.

55

B

Anti-Defunding Experiments: Additional Material

B.1

Experiment 1: Additional Figures and Tables
Table B2: Experiment 1: Balance of covariates
OverallCover

No Coverp-valuemean

std.dev.

mean

mean

(R=NR)

Age

39.87715.13039.29340.514

0.355

Black
Asian
White
Hispanic

0.214
0.076
0.671
0.183

0.410
0.265
0.470
0.387

0.228
0.072
0.670
0.159

0.198
0.079
0.672
0.209

0.391
0.775
0.968
0.138

Male

0.580

0.494

0.572

0.589

0.702

High school diploma
Bachelors degree

0.975
0.435

0.155
0.496

0.975
0.417

0.976
0.455

0.903
0.381

Notes: p-values based on robust standard errors reported.

B.2

Auxiliary Experiment 1: Persuasiveness of Defunding Rationale

We conducted this pre-registered experiment in December 2021 with a sample of 1,008 Democrats
and Independents recruited from Prolific.32 After completing a set of demographic questions,
respondents assigned to the treatment group read Sharkey’s article in the Washington Post, while
respondents assigned to the control group did not read the article. They then respond to thefollowing two questions: “Do you think that funding for the police should be increased, decreased,or stay the same?” and “How do you think increasing funding for the police would affect violent
crime?”. We code both questions from -2 (“Decreased a lot” and “Strongly decrease violent crime”,
respectively) to 2 (“Increased a lot” and “Strongly decrease violent crime”, respectively).
Table B3 displays results, with Columns 1–3 corresponding to the first measure and Columns 4–
6 corresponding to the second measure. We find a significant effect on both measures, with an effectsize of around 0.25 standard deviations for the first outcome and 0.12 standard deviations for thesecond outcome.

B.3

Auxiliary Experiment 2: Rainforest Placebo

B.3.1

Design and results

We conducted this experiment in December 2021 and January 2022 with a sample of 483 Democrats
and Independents recruited from Luc.id and CloudResearch. Respondents logged in to the survey
with their Twitter accounts using the same procedure as in Experiment 1. The design is similar
to that of Experiment 1, but examines a different (non-stigmatized) context: willingness to post
32

The pre-registration is available in the AEA RCT registry under ID AEARCTR-0008624.

56

Table B3: Persuasive effects of anti-defunding article
Dependent variable:
BeliefProvided article
DV mean
DV std. dev.
Observations
Demographic controls
Partisan controls

Policy preference

(1)

(2)

(3)

(4)

(5)

(6)

−0.236∗∗∗(0.056)−0.245∗∗∗(0.055)−0.245∗∗∗(0.055)0.135∗(0.071)0.121∗(0.068)0.122∗(0.068)-0.080
0.902
1,008
No
No

-0.080
0.902
1,007
Yes
No

-0.080
0.902
1,007
Yes
Yes

-0.568
1.133
1,008
No
No

-0.568
1.133
1,007
Yes
No

-0.568
1.133
1,007
Yes
Yes

Notes: The dependent variable in Columns 1–3 is the respondent’s reported belief as to the effectof increasing funding for the police on violence crime, coded between -2 (“Strongly decrease violent
crime”) and 2 (“Strongly increase violent crime”). The dependent variable in Columns 4–6 is the
respondent’s reported preference for changing police funding, ranging from -2 (“Decreased a lot”)
to 2 (“Increased a lot”). Demographic controls include age, age squared, a set of race indicators, a
Hispanic indicator, a male indicator, a set of education indicators. Partisan controls include indicators
for “Very conservative”, “Conservative”, “Neither liberal nor conservative” (omitted), “Liberal”, and“Very liberal”. Robust standard errors are reported.

a Tweet supporting efforts to conserve the Amazon rainforest.33 Rather than reading an article
about the likely effects of defunding the police, respondents read a Reuters article reporting on a
study conducted by the Science Panel for the Amazon which finds that over 10,000 species are at
risk from deforestation in the Amazon (Science Panel for the Amazon, 2021). The Cover Tweet
reads:
I’ve joined a campaign to immediately stop the destruction of the Amazon rainforest!
Before I joined the campaign, I was shown this article about how 10,000 species risk
extinction in Amazon: [LINK]. Join the campaign and sign the petition: [LINK].
The No Cover Tweet is identical, but replaces “Before I joined the campaign. . . ” with “AfterI joined the campaign. . . ”.
Appendix Table B5 shows no significant difference between posting rates in the Cover and
No Cover conditions, and the difference in effect sizes between the defunding experiment andthe placebo experiment is large in magnitude (16 percentage points) and significant at the 5%
level, suggesting effects are indeed driven by (anticipated) changes in the stigma associated with
dissenting expression rather than some other independent effect of the wording.

B.4

Auxiliary Experiment 3: Anticipated Persuasion Experiment

We conducted this experiment in November 2021 with a sample of 501 Democrats and Independents
recruited from Prolific. Only Democrats and Independents with Twitter accounts were eligible to33

Table B4 shows that our sample is balanced on observables across treatment arms.

57

Table B4: Rainforest placebo: Balance of covariates
OverallCover

No Coverp-valuemean

std.dev.

mean

mean

(R=NR)

Age

39.11013.24438.14640.043

0.201

Black
Asian
White
Hispanic

0.135
0.047
0.768
0.163

0.342
0.212
0.423
0.370

0.172
0.025
0.739
0.166

0.099
0.068
0.796
0.160

0.056
0.074
0.226
0.902

Male

0.473

0.500

0.529

0.420

0.052

High school diploma
Bachelors degree

0.984
0.392

0.124
0.489

0.981
0.376

0.988
0.407

0.628
0.565

Notes: p-values based on robust standard errors reported.

Table B5: Willingness to post pro-conservation Tweet (placebo)
Dependent variable:
Pro-conservation Tweet
(1)

(2)

(3)

−0.044(0.044)−0.049(0.044)−0.052(0.045)

DV mean
0.812
DV std. dev.
0.391
Observations
319
Demographic controls No
Partisan controls
No

0.812
0.391
319
Yes
No

0.812
0.391
319
Yes
Yes

Cover

Notes: The dependent variable is an indicator taking
value 1 if the respondent chose to schedule the post. Demographic controls include age, age squared, a set of raceindicators, a Hispanic indicator, a male indicator, a setof education indicators. Partisan controls include indicators for “Very conservative”, “Conservative”, “Neither
liberal nor conservative” (omitted), “Liberal”, and “Veryliberal”. Robust standard errors are reported.

take the survey. After completing a set of demographic questions, respondents read Sharkey’s
article in the Washington Post. As in Experiment 1, respondents are asked if they would like tojoin the campaign to oppose the movement to defund the police, only those who indicate thatthey would like to join the campaign proceed with the experiment, and those who do proceed are
given a chance to re-read the article. They are then randomly shown either the Cover or the No
Cover Tweet from Experiment 1 and are asked: “Suppose you posted the Tweet above on your58

account. If you had to guess, what percentage of people who saw your Tweet would choose to join
the campaign to oppose defunding the police?”
Table B6 displays results. Reassuringly, we find no significant difference between the anticipatedpersuasiveness of the Tweets, suggesting that differential posting rates are instead driven by changes
in anticipated stigma.
Table B6: Anticipated persuasiveness of Tweet
Dependent variable:
Perceived percentage persuaded
(1)

(2)

(3)

1.897
(2.125)

2.190(2.114)2.504(2.123)

DV mean
26.309DV std. dev.
23.764
Observations
501
Demographic controls No
Partisan controlsNo26.30923.764
501
Yes
No

26.30923.764
501
Yes
Yes

Cover

Notes: The dependent variable is the respondent’s guess as to thepercentage of their followers who would join the campaign if they
saw the Tweet. Demographic controls include age, age squared,
a set of race indicators, a Hispanic indicator, a male indicator,
a set of education indicators. Partisan controls include indicators for “Very conservative”, “Conservative”, “Neither liberal nor
conservative” (omitted), “Liberal”, and “Very liberal”. Robust
standard errors are reported.

59

B.5

Experiment 2: Additional Figures and Tables
Table B7: Experiment 2: Balance of covariates
OverallCover

No Coverp-valuemean

std.dev.

mean

mean

(R=NR)

Age

30.725

11.25830.68630.763

0.912

Black
Asian
White
Hispanic

0.070
0.085
0.773
0.112

0.256
0.279
0.419
0.315

0.086
0.089
0.766
0.093

0.055
0.080
0.781
0.130

0.057
0.589
0.563
0.060

Male

0.374

0.484

0.384

0.365

0.522

High school diploma
Bachelors degree

0.997
0.572

0.054
0.495

0.996
0.562

0.998
0.582

0.552
0.520

Notes: p-values based on robust standard errors reported.

60

Figure B1: Experiment 2: most distinctive phrases in each condition

Notes: Appendix Figure B1 plots phrases by their associated χ2 statistic, limiting to the top 100 phrases andmultiplying the χ2 of phrases more characteristic of the “No Cover” condition by -1. The words “article” and“read” have χ2 values of greater than 0.001 and have been suppressed to facilitate visualization of the remainingphrases.

61

Table B8: Experiment 2 (lower-credibility): Balance of covariates
OverallCover

No Coverp-valuemean

std.dev.

mean

mean

(R=NR)

Age

35.366

14.58535.27535.458

0.888

Black
Asian
White
Hispanic

0.053
0.132
0.771
0.107

0.225
0.339
0.421
0.309

0.043
0.137
0.773
0.141

0.064
0.127
0.769
0.072

0.303
0.747
0.923
0.011

Male

0.496

0.500

0.502

0.490

0.789

High school diploma
Bachelors degree

0.996
0.597

0.063
0.491

0.992
0.600

1.000
0.594

0.160
0.884

Notes: p-values based on robust standard errors reported.

62

C

Anti-Immigrant Experiments: Additional Material

C.1

Experiment 3: Additional Tables
Table C1: Experiment 3: Balance of covariates
OverallCover

No Coverp-valuemean

std.dev.

mean

mean

(R=NR)

Age

49.422

13.62348.70950.094

0.248

Black
Asian
White
Hispanic

0.014
0.015
0.952
0.066

0.116
0.124
0.215
0.248

0.012
0.016
0.952
0.052

0.015
0.015
0.951
0.079

0.762
0.934
0.955
0.214

Male

0.503

0.500

0.490

0.515

0.571

High school diploma
Bachelors degree

0.994
0.385

0.076
0.487

0.996
0.343

0.992
0.425

0.598
0.055

Notes: p-values based on robust standard errors reported.

C.2

Auxiliary Experiment 6: Persuasiveness of Deportation Rationale

We conducted a first pre-registered experiment in December 2021 with a sample of 1,008 Republicans recruited from Prolific.34 After completing a set of demographic questions, respondents
assigned to the treatment group viewed the clip from Tucker Carlson Tonight, while respondents
assigned to the control group did not view the clip. They then indicated their agreement with thefollowing two statements: “Illegal immigrants are not much more likely to commit serious crimes
than U.S. citizens” and “The US should immediately deport all illegal Mexican immigrants.” We
code both questions from -2 (“Strongly disagree”) to 2 (“Strongly agree”).
Contrary to our pre-registered prediction, we did not estimate a statistically significant effectof viewing the video on either outcome. Two logistical problems complicate interpretation of thisresult. First, when setting up the survey, we forgot to exclude respondents from some previous
experiments which included the video. Thus, some respondents in the Control condition had seen
the video in previous experiments. Second, there was a highly limited sample of Republicans
available on Prolific (fewer than 2000 who met our screening criteria), and we had to pay a higher
than usual rate in order to meet our pre-registered sample size. This potentially induced selection
into the survey.
We thus ran the same experiment on Luc.id, with the same sample restrictions. Table C2 displays results, with Columns 1–3 corresponding to the first measure and Columns 4–6 corresponding
to the second measure. We find a significant effect on both measures, with an effect size of around0.12 standard deviations for the first outcome and 0.18 standard deviations for the second outcome.
Overall, we take the evidence for the effects of the clip on persuasion as mixed.
34

The pre-registration is available in the AEA RCT registry under ID AEARCTR-0008624.

63

Table C2: Persuasive effects of Tucker Carlson Tonight video
Dependent variable:
BeliefPolicy preference

(1)

(2)

(3)

(4)

(5)

(6)

Provided article−0.133∗(0.070)−0.123∗(0.071)−0.123∗(0.071)0.177∗∗(0.074)0.179∗∗(0.073)0.180∗∗(0.073)

DV mean
DV std. dev.
Observations
Demographic controls
Partisan controls

0.643
1.112
1,004
No
No

0.643
1.112
1,002
Yes
No

0.643
1.112
1,002
Yes
Yes

0.740
1.173
1,004
No
No

0.740
1.173
1,002
Yes
No

0.740
1.173
1,002
Yes
Yes

Notes: The dependent variable in Columns 1–3 is the respondent’s reported agreement with thestatement “Illegal immigrants are more likely to commit serious crimes than US citizens,” coded
between -2 (“Strongly disagree”) and 2 (“Strongly agree”). The dependent variable in Columns
4–6 is the respondent’s reported agreement with the statement “The US should immediately
deport all illegal Mexican immigrants,” ranging from -2 (“Strongly disagree”) to 2 (“Strongly
agree”). Demographic controls include age, age squared, a set of race indicators, a Hispanic
indicator, a male indicator, a set of education indicators. Partisan controls include indicators for“Very conservative”, “Conservative”, “Neither liberal nor conservative” (omitted), “Liberal”,
and “Very liberal”. Robust standard errors are reported.

64

C.3

Experiment 4: Additional Tables
Table C3: Experiment 4: Balance of covariates
OverallCover

No Coverp-valuemean

std.dev.

mean

mean

(R=NR)

Age

31.72912.25632.40831.046

0.068

Black
Asian
White
Hispanic

0.069
0.100
0.767
0.118

0.254
0.300
0.423
0.323

0.063
0.090
0.785
0.109

0.076
0.109
0.750
0.128

0.389
0.297
0.174
0.325

Male

0.479

0.500

0.492

0.466

0.392

High school diploma
Bachelors degree

0.995
0.589

0.068
0.492

0.994
0.590

0.996
0.588

0.659
0.939

Notes: p-values based on robust standard errors reported.

65

Figure C1: Experiment 4: most distinctive phrases in each condition

Notes: Appendix Figure C1 plots phrases by their associated χ2 statistic, limiting to the top 100 phrases andmultiplying the χ2 of phrases more characteristic of the “No Cover” condition by -1.

66

C.4

Auxiliary Experiment 7: Anti-Immigrant Expression Among More Representative Sample

The social media setting of Experiments 1 and 3 affords a highly natural setting and real-stakes
outcome — and is of itself a context of policy relevance — but there are two potential concerns about
external validity. First, Twitter users still comprise a relatively small and selected fraction of the
population, particularly among Republicans (Wojcik and Hughes, 2019). Second, our requirementthat respondents grant our “Tweetability” app permissions to schedule posts on their Twitter
account likely induces selection into our experiment. While this selection does not affect the internal
validity of Experiments 1 and 3, it might affect the extent to which the results generalize to thebroader population. A third, and related, limitation of these experiments is that we are unable
to examine heterogeneity in the effect of the rationale based on the composition of a respondent’s
audience, both because we cannot observe their audience and because we are insufficiently powered
to do so. To address these concerns, this section presents an additional experiment that sacrificessome of the naturalness of Experiments 1 and 3 for a large and representative sample (whose
geographic location and thus whose local environment we can observe), while retaining a revealedpreference measure of respondents’ willingness to publicly express dissent. We discuss ethicalconsiderations in Appendix D.
C.4.1

Sample and experimental design

Sample composition We conducted Auxiliary Experiment 7 in January 2020 (wave 1) and
September 2020 (wave 2) with a sample of Republicans and Independents recruited through Luc.id.35
Our sample of respondents is broadly representative of Independents and Republicans in the UnitedStates (Appendix Table C7) and is well-balanced on observables across treatment arms (Appendix
Table C6). The two waves had a largely similar design. The most important differences are thatwave 1 included a pure control condition and had a more heavy-handed set of instructions. In thedescription of the design below, we focus of the leaner set of instructions from wave 2.
Information: Lott study After completing a series of demographic and other backgroundquestions, respondents are assigned to two main conditions: No Cover and Cover.
Specifically, all respondents are first told about the preliminary findings of an unpublishedstudy (Lott, 2018) claiming that immigrants commit more crime than US citizens. Respondents
are informed that they will have the opportunity to authorize a $1 donation to Fund The Wall,an organization seeking to construct the proposed US–Mexico border wall, and that we will post
their individual donation decision on our website. To vary the availability of a social cover, we tell
respondents assigned to the No Cover treatment that the web page will state that “all participants
were surveyed before Dr. Lott’s study was published in an academic journal.” In the Covertreatment, respondents are instead told that the web page will state that “all participants wereshown the the preliminary findings from Dr. Lott’s study before deciding whether or not to donate
to Fund The Wall.” We tell respondents in the Cover and No Cover conditions about a recent
study (Lott, 2018) which argues that undocumented immigrants commit more crimes and more
serious crimes than US citizens.36 This study has been widely covered by the media, including
35

Wave 1 of the experiment was pre-registered in the AEA RCT registry under ID AEARCTR-0005308.
Wave 1 of study also had a pure Control condition in which respondents do not learn about the study. We
include a discussion of the results from the Control condition below.
36

67

The Washington Times, National Review, and Fox News, and has been repeatedly cited by Trumpadministration officials. We also truthfully tell our respondents that a number of sources (including
a researcher affiliated with the Cato Institute, a libertarian think tank) have recently challenged
some of the study’s methods, claiming that errors in analysis invalidate its results.
Visible donation decisions We ask respondents to consent to us accessing their name, city, andoperating system from the survey provider (which confirmed that they would provide us with thisdata subject to participant consent) and give respondents the option to terminate the survey if they
do not consent. Respondents are informed that they will have the opportunity to authorize a $1
donation to Fund The Wall, an organization seeking to construct the proposed US–Mexico borderwall, and that we will post the results from the survey, including their individual donation decision,on our study website.37 To vary the availability of a social cover, we tell respondents assigned to
the No Cover treatment that the web page will state that “all participants were surveyed before
Dr. Lott’s study was published in an academic journal.” In the Cover treatment, respondents are
instead told that the web page will state that “all participants were shown the the preliminary
findings from Dr. Lott’s study before deciding whether or not to donate to Fund The Wall.”We also inform our respondents that “As researchers, we believe it is important to communicate
our findings about political and social attitudes in [City of respondent] to the public”.38 We theninform our respondents that “We will promote our website via Facebook ads to [City of respondent]
residents”. This generates a plausible social cost for acting in a way that will be stigmatized in the
respondent’s area. After informing respondents about the content of the website, we ask people
whether they “would like to authorize a $ donation to Fund The Wall?”37
To minimize experimenter demand concerns, we in fact informed our respondents that we would randomly
select one of two organizations — Fund the Wall, or the Texas Civil Rights Project, an organization that (among
other activities) worked to legally challenge the wall’s construction — and that they would have the opportunity toauthorize a $1 donation to this organization. In practice, we randomized almost all respondents to Fund the Wall tomaximize statistical power for our comparison of interest.
38
We used participants’ IP address to capture and display their current location (i.e. their city).

68

Figure C2: Auxiliary Experiment 7: Design
Consent, attention check,demographics

Consent, attention check,Cover
demographics

No CoverControl

Information about Lott (2018)

Reconsent"I consent to researchers accessing...first and last
name, city, and operating system."

Description of public donation decision andwebsite screenshot"The page lists individual donation decisions andwhether each participant decided to authorize the
donation to Fund the Wall"No Cover"The page states that all participants madetheir decisions before Dr. Lott's study was
published"

Cover"The page states that all participants weretold about Dr. Lott's study"

Donation decision"Would you like to authorize a $1 donation to Fundthe Wall?"

Post-treatment questions and perceived
purposeEnd of study

69

Control(Blank)C.4.2

Results

Average treatment effects To identify the joint effects of direct persuasion and anticipatedpersuasion of the audience (i.e. the direct persuasive effect of learning about the Lott study inaddition to the indirect effect of learning that one’s audience has learned about the Lott study andmay thus be more likely to approve of the donation), we compare the Control condition with the
No Cover condition. To identify the cover effect of rationales, we compare the No Cover condition
to the Cover condition. This design thus allows us to benchmark the cover effect of rationales effectagainst the joint effect of persuasion and anticipated persuasion.
Table C4 displays mean donation rates by condition. We find a statistically significant effecton respondents’ willingness to authorize a donation to Fund the Wall: respondents in the Covercondition are 7 percentage points more likely to authorize the donation than respondents in the No
Cover condition (as shown in Column 6 of Table C4 which pools observations across all conditions).
As shown in Panel A of Table C4, effect sizes are almost identical in our pre-specified main study,
our pilot study, and a replication several months later. In contrast to the Cover vs. No Covercomparison, respondents in the No Cover condition are only 1 percentage point more likely toauthorize a donation than respondents in the Control condition, suggesting that the combined
effects of persuasion and anticipated persuasion are small. Relatively small persuasion effects arein line with other information provision experiments in the immigration domain, which typicallyfind relatively small or null effects on behavior and stated preferences (Alesina et al., 2019; Hopkins
et al., 2019; Grigorieff et al., 2020; Haaland and Roth, 2020), and are also consistent with the mixed
evidence on persuasion we find in Experiments 3 and 4.
Heterogeneity by local vote shares The audience’s composition — in this case, the fraction
who approve of the decision to donate — should affect the magnitude of the rationale effect. Because
we informed respondents that we would promote the website within their geographical area, wemight expect that, controlling for respondents’ own private views, respondents in areas with agreater fraction of Republicans (who are likely to approve of the decision to donate to Fund the Walleven in the absence of a rationale) should be less sensitive to the availability of a rationale than thosein areas with a lower fraction of Republicans. We thus pre-registered investigating heterogeneity
by the 2016 Republican vote share of the respondents’ county, which we do by interacting ourtreatment indicators with vote shares (standardized, for ease of interpretation). We flexibly control
for differential effect of partisanship by also controlling for the interactions between partisanshipand the 2016 Republican vote share. Panel B of Table C4 displays the results, revealing striking
heterogeneity by the Republican vote share of respondents’ counties. The estimated interaction islarge in magnitude: a one standard deviation increase in the Republican vote share of a respondent’s
county is associated with halving the magnitude of the cover effect of rationales. Of course, theseresults cannot be interpreted as a causal effect of differences in the composition of respondents’audiences: it may be, for example, that Republicans in Democratic areas feel a greater need tosignal their support for the study by publicly donating.
C.4.3

Addressing experimenter demand concerns

One concern is that our instructions in Experiment 7, by directly informing (and reminding) respondents about their audience’s information sets, induced experimenter demand effects or otherwise
compromised external validity. A priori, it seems plausible that showing participants information
70

Table C4: Willingness to donate to anti-immigrant cause
Dependent variable:
Donated to Fund the Wall
(1)

(2)

(3)

Panel A:

(4)

(5)

(6)

0.053∗∗(0.026)0.070∗∗∗(0.014)

Non-interacted specification

Cover

0.063∗∗∗(0.020)0.065∗∗∗(0.018)0.074∗∗∗(0.016)

Control−0.001(0.020)−0.005(0.018)−0.001(0.017)0.018(0.016)p-value (Cover = Control) 0.0013< 0.001< 0.001

0.0012

Panel B:

0.066∗∗(0.028)Interacted specification

Cover

0.061∗∗∗(0.020)0.063∗∗∗(0.019)0.071∗∗∗(0.016)0.042(0.030)0.026(0.028)0.063∗∗∗(0.014)

Cover × Rep vote share−0.030(0.020)−0.038∗∗(0.019)−0.038∗∗(0.017)−0.062∗∗(0.028)−0.073∗∗∗(0.027)−0.042∗∗∗(0.014)Control−0.001(0.020)−0.004(0.018)−0.001(0.017)0.017(0.016)

Control × Rep vote share

0.013(0.020)0.010(0.018)0.010(0.017)0.015(0.016)

Rep vote share

0.052∗∗∗(0.015)0.0002(0.018)−0.0004(0.016)0.020(0.019)0.019(0.035)0.001(0.015)

Waves included

1

1

P+1

2

2

P+1+2

0.488
0.500
3,751
No

0.488
0.500
3,751
Yes

0.497
0.500
4,457
Yes

0.484
0.500
1,279
No

0.484
0.500
1,279
Yes

0.494
0.500
5,736
Yes

DV mean
DV std. dev.
Observations
Individual controls

Notes: The dependent variable is an indicator taking value 1 if the respondent donated to Fund the Wall.
Columns 1–2 report results estimated on the sample from the Wave 1; Column 3 pools the sample from the
Wave 1 with the sample from the pilot; Columns 4–5 consider only the sample from the Wave 2; and Column 6
pools all waves. In Panel B, the county Republican vote share is from the 2016 US Presidential election and isscaled to a standard normal distribution. The specifications in Columns 2–3 and Columns 5–6 of Panel B include
the interactions between our set of partisan controls and the 2016 Republican vote share. Demographic controls
include age, age squared, a set of race indicators, a Hispanic indicator, a male indicator, a set of education
indicators. Partisan controls include indicators for “Very conservative”, “Conservative”, “Neither liberal nor
conservative” (omitted), “Liberal”, and “Very liberal”. Robust standard errors are reported.

71

about the Lott study might induce demand effects and thus affect donation rates, but even if
such demand effects are present, they do not bias our main comparison of interest (Cover vs. No
Cover ), given that participants in both treatment arms are shown identical information about the
study. More concerning is the possibility the treatment manipulation of beliefs about the audience’s
information set induced differential experimenter demand effects between these two conditions.
Hand-coding of perceived purpose We also ask respondents to respond in open-ended form
to the question “If you had to guess, what would you say the purpose of this study was?” We use
responses to assess demand effects in two ways. First, we hired two independent research assistants
to hand-code the responses. Appendix Table C5 in the Appendix shows that the majority of our
respondents believed that we wanted to study the effects of information on anti-immigrant sentimentor participant’s willingness to have their decisions posted on the website. Fewer than 1 percent of oursample correctly guessed the true purpose of our experiment (Column 1). The table also shows thaton almost all of the dimensions we code, beliefs about the purpose of the study do not significantly
differ between the Cover and No Cover conditions. The exception is Public Image (Column 3):
respondents in the Cover condition are 2 percentage points more likely than respondents in the
No Cover condition to believe that the study was about whether people were willing to publicly
express political views. Although statistically significant, this difference is small in magnitude andcannot explain our effect sizes. We do find significant differences in perceived purpose between
the Control condition the other two conditions, likely because we provided respondents in the No
Cover and Cover conditions, but not in the Control condition, information about the Lott study.
However, these differences do not affect our main comparison of interest (No Cover vs. Cover ).

72

Table C5: Anti-immigrant donations: Perceived purpose of study
Dependent variable:
Cover
(1)

Immigration attitudes(2)

Public image(3)

Information(4)

Persuasion(5)

Biased(6)

Cover−0.005(0.003)0.010(0.015)0.019∗∗(0.010)0.011(0.015)−0.012(0.012)−0.0004(0.014)Control−0.003(0.003)0.131∗∗∗(0.016)

0.037∗∗∗(0.010)−0.013(0.016)−0.080∗∗∗(0.012)−0.041∗∗∗(0.014)p-value (Cover = Control)

0.62< 0.001

0.081

0.13

< 0.001

0.0042

DV mean
DV std. dev.
Observations
Individual controls

0.007
0.084
4,454
Yes

0.227
0.419
4,454
Yes

0.084
0.277
4,454
Yes

0.239
0.426
4,453
Yes

0.121
0.327
4,454
Yes

0.176
0.381
4,452
Yes

73

Notes: The dependent variable in each column is an indicator taking value 1 if the respondent’s perceived purpose of the study wascoded to fall into the corresponding category. “Cover” takes value 1 if the respondent correctly inferred the study was about whether
the ability to link one’s donation decision to the Lott study would affect the donation decision. “Immigration attitudes” takes value 1
if the respondent stated the study was about attitudes toward immigration. “Public image” takes value 1 if the respondent stated thestudy was about whether knowing one’s decision will be observable to others would affect the donation decision. “Information” takes
value 1 if the respondent stated the study was about disseminating information about immigration. “Persuasion” takes value 1 if the
respondent stated the researchers were attempting to persuade them either to donate or not to donate. “Bias” takes value 1 if the
respondent stated the researchers were biased. “Other” takes value 1 if the respondent stated a purpose that did not fall into any of
the above categories. Categories other than “Other” are not mutually exclusive. All specifications pool the main experiment and thepilot and control for demographics and partisan affiliation. Demographic controls include age, age squared, a set of race indicators,
a Hispanic indicator, a male indicator, a set of education indicators. Partisan controls include indicators for “Very conservative”,“Conservative”, “Neither liberal nor conservative” (omitted), “Liberal”, and “Very liberal”. Robust standard errors are reported.

Natural language processing Second, we use natural language processing techniques (in particular, BERT, introduced in Devlin et al. 2019) alongside a neural network classifier to predict
treatment status given the participant’s response to the open-ended elicitation of perceived purpose. The intuition is simple: if respondents do not perceive differences in the purpose of the study
across conditions, there is no scope for experimenter demand effects to affect the results.
At a high level, our exercise proceeds in three steps. After splitting our sample into a training
set (75%) and a test set (25%), we create high-dimensional vector representations, or contextual
embeddings, of each respondent’s answer to the question “If you had to guess, what would you
say the purpose of this study was?”. These embeddings capture semantic meaning.39 We thentrain a neural network classifier on the training set to predict the respondent’s treatment condition(Control, Cover, or No Cover ) based on their contextual embedding. Finally, we calculate accuracy
on the test set.
To generate contextual embeddings for each response, we use DistilBERT (Sanh et al., 2020), atransformer modeled on the BERT (Devlin et al., 2019) architecture that achieves similar performance at substantially lower computational cost. Our implementation is provided by HuggingFace;
we use all default parameter values and train the model for the default three epochs.40 This step
outputs a 768-dimensional vector embedding for each respondent. We next train a neural network
for sequence classification on the training set, again using the HuggingFace implementation withdefault parameter values, to predict the respondent’s treatment condition based on their embedding. 41 Using this trained model, we predict treatment conditions in the test set and compare
predicted conditions with actual conditions.
In order to facilitate comparing classifier accuracy when distinguishing between the Cover and
No Cover condition vs. distinguishing between Control and the other two conditions, we repeat
the exercise above three times, each time excluding from both the training set and the test set oneof the three conditions. Our classifier achieves 51% accuracy when distinguishing between Coverand No Cover, and we are unable to rule out the null hypothesis of 50% accuracy (p = 0.48). In
contrast, our classifier achieves 60% accuracy when distinguishing between Control and No Coverand 58% accuracy when distinguishing between Control and Cover, with both rates statisticallydistinguishable from 50% accuracy (p < 0.001). Thus, as expected, respondents hold different
beliefs about the purpose of the study in Control vs. the other two conditions, but not between
Cover and No Cover. Given the differences documented through the hand-coding exercise, we view
this result as validation for our method, as it demonstrates that we would likely detect substantial
differences in perceived purpose between the Cover and No Cover conditions if such differenceswere present.
C.4.4

Additional tables

39

See Liu et al. (2020) for a review of contextual embeddings.
See https://huggingface.co/docs/transformers/model_doc/distilbert.
41
See https://huggingface.co/docs/transformers/training.

40

74

Table C6: Anti-immigrant donations: Balance of covariates
OverallCover

No CoverControlp-values

mean

std.dev.

mean

mean

mean

(E=NE)(E=C)(NE=C)

Age

45.07715.72445.17144.84545.209

0.611

0.951

0.560

Black
Asian
White
Hispanic

0.076
0.043
0.824
0.106

0.265
0.203
0.381
0.308

0.070
0.041
0.828
0.112

0.089
0.042
0.815
0.105

0.069
0.045
0.830
0.102

0.075
0.886
0.414
0.580

0.965
0.588
0.887
0.419

0.063
0.690
0.330
0.804

Male

0.498

0.500

0.495

0.503

0.497

0.686

0.925

0.751

High school diploma
Bachelors degree

0.977
0.376

0.151
0.484

0.976
0.394

0.976
0.367

0.977
0.369

0.965
0.166

0.908
0.196

0.944
0.910

Republican

0.425

0.494

0.417

0.436

0.421

0.327

0.825

0.439

75

Notes: p-values based on robust standard errors reported. Attriters dropped from sample.

Table C7: Anti-immigrant donations: Sample representativeness
Lott

Pew (Inds and Reps)

Age

45.11

47.17

Black
White
Asian
Hispanic

0.08
0.82
0.04
0.11

0.05
0.77
0.03
0.11

Male

0.49

0.52

High school diploma
Bachelors degree or higher

0.98
0.37

0.93
0.31

Observation

4553

5501

Notes: Table displays mean characteristics, comparing the experimental sample with the 2018 Pew Research Center’s American
Trends Panel, Wave 39. Attriters are dropped from sample.

C.5

Auxiliary Experiment 8: Interpretation of Lott Rationale

This section presents a pre-registered experiment in which we explore how learning that a previous
participant had read the Lott study prior to making their donation decision shapes an audience’s
inference about the participant’s motives and resulting social sanctions.42 The experimental designis broadly similar to that of Experiments 2 and 4, but in addition to examining inference only about
the matched participant’s prejudice, we also examine inference about persuadability (or gullibility)— i.e. the extent to which a matched participant might be persuaded by a rationale. This ismeant to capture arguments of the form “I have nothing against immigrants. . . I just believe thestudy.” Of course, persuadability is only one of a set of potential reasons for donating after being
exposed to information suggesting immigrants commit more crimes (which is why we choose not
to explicitly study it in the main experiments presented in this paper); alternative reasons include
lower tolerance for crime, higher levels of risk aversion, etc. We chose to focus on persuadability
in this experiment because it is arguably the most natural “second type,” because it was the mostfrequent reason cited in our pilot results, and because it is most consistently and objectively coded.
C.5.1

Sample and Experimental Design

Sample composition We recruited a sample of 3,047 Democrats through Luc.id in February
2020.43 Our sample of respondents is broadly representative of Democrats and Independents in
the United States (Table C8), though slightly more white and educated, and well-balanced on
observables across treatment arms (Table C9).
42

The pre-registration is available in the AEA RCT registry under ID AEARCTR-0005462.
In our pre-registration, we specified that in some specifications, we would pool data from a pilot (N = 2, 019)
with the data from the main experiment. The pilot instrument was virtually identical to the instrument used in themain experiment. We report both unpooled and pooled specifications.
43

76

Table C8: Interpretation of Lott rationale: Sample representativeness
Lott

Pew (Inds and Dems)

Age

41.35

45.86

Black
White
Asian
Hispanic

0.18
0.70
0.05
0.14

0.18
0.59
0.05
0.15

Male

0.45

0.46

High school diploma
Bachelors degree or higher

0.98
0.45

0.89
0.35

Observation

3133

6627

Notes: Table displays mean characteristics, comparing the experimental sample with the 2018 Pew Research Center’s American Trends
Panel, Wave 39. Attriters are dropped from sample.

Table C9: Interpretation of Lott rationale: Balance of covariates
OverallCover

No Coverp-valuemean

std.dev.

mean

mean

(R=NR)

Age

41.376

15.63941.70341.048

0.247

Black
Asian
White
Hispanic

0.182
0.045
0.710
0.140

0.386
0.208
0.454
0.347

0.186
0.049
0.703
0.136

0.179
0.042
0.716
0.144

0.612
0.386
0.455
0.561

Male

0.450

0.498

0.451

0.448

0.840

High school diploma
Bachelors degree

0.983
0.446

0.130
0.497

0.983
0.454

0.983
0.439

0.998
0.391

Notes: p-values based on robust standard errors reported.

Information provision Figure C3 outlines the structure of the experiment. We tell all respondents about the Lott study (Lott, 2018) described in Section C.4 and about the fact that the study
has been challenged on methodological grounds.44 We then tell respondents that we conducted a
project on political and social attitudes in the United States earlier in the year, and that participants in this previous study were given an opportunity to authorize a $1 donation to Fund the44

Once again, in order to ensure that our respondents are not misinformed, we debrief them at the end of thestudy and provide them with a meta-analysis summarizing the work on the effects of immigration on crime (Ousey
and Kubrin, 2018).

77

Wall. We inform participants that we have matched them with one of these respondents, and that
this respondent chose to authorize the donation. Respondents in the Cover condition are told that
their matched respondent was informed about the study before deciding whether or not to authorize
the donation to Fund the Wall, while respondents in the No Cover condition are told that theirmatched respondent was not informed about the study before making their donation decision.45
45

Because all participants in the donations experiment were informed of the study before making their donation
decision, in order to avoid deception, we ran a small auxiliary version of this experiment in which some respondents
were not informed. These are the participants with whom we match respondents in the experiment described in thissection.

78

Figure C3: Interpretation of Lott rationale: design
Consent, attention check,demographics

Information about Lott (2018)

No Cover- "Your matched respondent was
not informed about Dr. Lott's study"

Cover- "Your matched respondent was informed
about Dr. Lott's study"- Your matched respondent decided toauthorize the $1 donation to Fund the Wall

- Your matched respondent decided toauthorize the $1 donation to Fund the Wall

Perceived motive (open-ended)"Why do you think your matched
respondent chose to donate to Fundthe Wall?

Gullibility Scale"If you had to guess, how do you think
your matched respondent scored on the
Gullibility Scale?"

Foreign Culture Tolerance Scale"If you had to guess, how do you think
your matched respondent scored on theForeign Culture Tolerance Scale?"

Post-treatment questions, perceived
purpose, and feedback

End of study79

Measuring inference After learning whether or not their matched respondent knew about the
study, all participants respond to the following open-ended question: “Why do you think yourmatched respondent chose to donate to Fund the Wall?” These open-ended responses form theraw data for our first measure of inference, which we analyze using the following (pre-registered)procedure. We begin with five “seed words” for each of the two dimensions: for intolerance, we choseracist, biased, xenophobic, intolerant, and prejudiced ; and for persuadability, we chose convinced,
persuaded, gullible, naive, and sucker. We add all “most relevant” synonyms for these words, asclassified by the website www.thesaurus.com. In order to capture different parts of speech, we stem
all words in our list (e.g., xenophobic → xenophob, gullible → gullib), for a total of 23 intolerancerelated stems and 30 persuadability-related stems (Gentzkow et al., 2019). We then define two
indicator variables, one for the presence of an intolerance-related stem and another for the presenceof the persuadability-related stem, and we estimate treatment effects on the probability that the
respondent uses at least one word in each list.46
For our second measure of inference, participants are then cross-randomized into one of two conditions: “tolerance” and “persuadability”.47 Participants in the “tolerance” condition are told that
their matched respondent completed the “Foreign Culture Tolerance Scale,” a “short questionnairemeasuring tolerance toward foreign values and traditions,” before making their donation decisions.
Participants in the “persuadability” condition are told that their matched respondent completed
the “Gullibility Scale,” a “short questionnaire which measures how easily people are manipulated
by evidence from untrustworthy sources,” before making their donation decisions. All participants
are asked to guess their respondent’s score; we incentivize this guess by informing them that if theycorrectly guess the score, they will be entered into a lottery for a $50 Amazon gift card.

C.6

Results

Columns 1–3 of Table C10 displays results for our text-based measure of inference. Participantsin the Cover condition are 7 percentage points less likely to use a stem related to intolerance
when describing their matched respondent’s motive, compared to a mean of 17 percent among
participants in the No Cover condition (p < 0.001). These same participants are also 3 percentage
points more likely to use words related to persuadability (p < 0.001), relative to a mean of 7 percent
among participants in the No Cover condition.48 These effect sizes highlight that the availabilityof a rationale strongly changes people’s inference about their matched respondent’s motives. Thatthe effect on intolerance is larger than the effect on persuadability is consistent with the factthat persuadability is only one of several possible “second types” to which respondents might besubstituting. These results are stable to the inclusion of demographic and partisan controls.
Columns 4–6 display results from our structured belief measures. Respondents in the Covercondition rate their matched participant 0.13 standard deviations lower on the intolerance scale(p < 0.001) and 0.32 standard deviations higher on the gullibility scale (p < 0.001) than partic46

Responses that contain both an intolerance-related stem and a persuadability-related stem will have both intolerance and persuadability indicators equal to one, whereas responses that contain neither type of stem will have bothindicators equal to zero. Thus, our results are unbiased even if participants perceive a nonzero correlation between
intolerance and persuadability.
47
We measure type inference using a “between” design (in which each respondent is asked only about a single
dimension) rather than a “within” design (in which respondents are asked about both dimensions). We employ abetween design in order to minimize experimenter demand effects and to avoid order effects (Haaland et al., 2021).
48
We were intentionally conservative when choosing stem words in order to minimize the rate of false positives.

80ipants in the No Cover condition. As with the text analysis measure, effects are similar in thepilot and in the pre-registered main experiment, are robust to the inclusion of control variables,
and are precisely estimated. Our two measures of type inference are also highly correlated: on
average, a respondent who uses a word related to intolerance (persuadability) when describing thematched respondent’s motive rates the matched respondent as around half a standard deviation
more intolerant (persuadable) than a respondent who does not use such a word.
Table C10: Interpretation of Lott rationale: type inference
Used word
(1)

(2)

(3)

Panel A:
Cover
Individual controls
Observations
DV mean
DV std. dev.

Inferred score
(4)

(5)

(6)

Inference about intolerance−0.070∗∗∗(0.012)−0.068∗∗∗(0.012)−0.068∗∗∗(0.012)−0.134∗∗∗(0.051)−0.133∗∗∗(0.051)−0.152∗∗∗(0.039)

No
3,047
0.137
0.344

Yes
3,047
0.137
0.344

Yes
3,047
0.137
0.344

No
1,524
0.000
1.000

Yes
1,524
0.000
1.000

Yes
2,532
0.000
1.000

Panel B:

Inference about persuadability

Cover

0.031∗∗∗(0.010)0.032∗∗∗(0.010)0.032∗∗∗(0.010)0.321∗∗∗(0.050)0.310∗∗∗(0.050)0.317∗∗∗(0.039)Observations
DV mean
DV std. dev.

3,047
0.084
0.278

3,047
0.084
0.278

3,047
0.084
0.278

1,523
0.000
1.000

1,523
0.000
1.000

2,533
0.000
1.000

Notes: The dependent variable in Columns 1–3 is an indicator taking value 1 if the respondent used a
key word when describing their matched partner’s motive. The dependent variable in Columns 4–6 is the
respondent’s (standardized) guess about their matched partner’s score on the test. Panel A reports resultsfor inference about intolerance; Panel B reports results for inference about persuadability. Demographic
controls include age, age squared, a set of race indicators, a Hispanic indicator, a male indicator, a set of
education indicators. Partisan controls include indicators for “Very conservative”, “Conservative”, “Neither
liberal nor conservative” (omitted), “Liberal”, and “Very liberal”. Robust standard errors are reported.

Taken together, our evidence suggests that when judging others’ motives, people believe thatthose who donated with a rationale are more persuadable and less intolerant than those who donatedwithout a rationale.

81

D

Ethical Considerations

Understanding dissenting expression is of great social importance. Identifying the drivers of xenophobic expression is crucial in designing policies best-suited to curbing it, while understanding
barriers to dissenting expression in situations where such expression is desirable — for example,
speaking out against unjust practices or systems — may help design contexts with lower suchbarriers.
Nonetheless, ethically conducting revealed-preference experiments on dissenting expression —particularly xenophobic expression — requires balancing three often contradictory objectives: avoiding explicitly deceiving respondents, avoiding compromising respondents’ privacy, and avoiding increasing public xenophobic expression. In this section, we provide a more detailed explanationof how our experimental designs balance these objectives. Of course, all experiments obtained
approval from multiple Institutional Review Boards.

D.1

Considerations related to information provision (Experiments 3–4 and Lottexperiment)

The information on the link between illegal immigration and violent crime we provide to respondents (the clip from Tucker Carlson Tonight in Experiments 3–4 and the Lott (2018) study in therobustness experiment) paints an incomplete picture of the academic literature, which generally
finds null or negative effects of illegal immigration on violent crime. Although we do not endorse
either piece of evidence — indeed, we explicitly inform respondents in the Lott experiment that the
study has been challenged by reputable sources — we nonetheless debrief all respondents at theend of the study, providing them with an accessible academic overview of the link between illegal
immigration and violent crime (Ousey and Kubrin, 2018) and a list of further readings.49
Tucker Carlson Tonight clip In Experiments 3–4, we provide respondents with video clip
from Tucker Carlson Tonight, the most popular cable news show in the country. While we do
not endorse the message, the raw numbers presented in the video clip are taken from the U.S.
Sentencing Commission and are factually correct. While we debrief respondents with the abovedescribed meta-study at the end of the survey, this is strictly speaking unnecessary, as the numbers
cited in the video clip are not factually wrong.
Lott study In the Lott experiment, treated respondents receive information about a study byJohn Lott claiming that illegal immigrants commit more crime. Lott holds a PhD in economics
from UCLA and has previously held positions at Yale University, the University of Chicago, and theDepartment of Justice. The working paper we describe — Lott (2018) — has been extensively citedby the Trump administration and is posted on the Social Science Research Network. In other words,
it is a real study by an academic economist. The study has been challenged on methodologicalgrounds, but we inform all respondents about this controversy on the very same screen where
we present the study.50 While we again debrief respondents, this is not strictly necessary, as
respondents had already been informed that the study’s methodology had been challenged.
49

It is common practice to mislead respondents by omitting relevant details from the instructions. Indeed, correspondence studies generally rely on outright deception by sending out fake resumes to employers.
50
Specifically, at the information page, all respondents are informed about the following: “However, a number ofsources (including a researcher affiliated with the Cato Institute, a non-partisan libertarian think tank) have recently

82

D.2

Considerations related to privacy and deception (Experiments 1, 3, andLott experiment)

Given that our mechanism examines the effect of perceived social stigma on behavior, it is crucial
that respondents in Experiments 1 and 3 and in the Lott experiment believe that their decisions will
be visible to others. Although our experiments avoid explicit deception, protecting participants’privacy in this context required us to mislead respondents. We distinguish between the ethical andpractical problems associated with deception (the latter relating to concerns about subject poolcontamination), addressing the first concern in this section and the second in Section D.3.
D.2.1

Experiments 1 and 3

Twitter login All respondents were required to log in via their Twitter accounts to the “Tweetability” app we created. This app is governed by the Twitter API’s terms of service and has thesecond most restrictive set of permissions among the three application scopes Twitter provides(“Read” and “Write”). That is, the app does not have access to users’ passwords, messages, or
account settings, but it is able to post Tweets from the users’ accounts. We do not use this functionality in any way, and no information that could compromise users’ accounts is ever accessedor downloaded. We explicitly inform respondents of the app’s permissions in transparent language
and give them the option to end the survey if they are uncomfortable granting the app these permissions. We also inform respondents that the app’s data, including the tokens that give us accessto post on their accounts, will be deleted by no later than August 1, 2021 (Experiment 3) and
December 1, 2021 (Experiment 1). Tokens were indeed deleted immediately after collection.
Twitter posts Our key outcome is whether respondents are willing to post a Tweet including
a link to a petition to immediately deport all illegal Mexican immigrants. We were not willingto consider designs that asked respondents to actually post such Tweets. We thus asked them to“schedule” their Tweet for the future (using the Tweetability app), to be posted “if/when we havefinished surveying people in all US counties”. Because we targeted fewer total respondents than
the total number of US counties, these posts will never be published. This formulation is therefore
misleading, even if it is not explicitly deceptive. Given our desire to avoid leading respondents topublicly post political content (particularly xenophobic content, as in Experiment 3) as part of oursurvey, we and our Institutional Review Board felt comfortable with this formulation.
D.2.2

Lott experiment

Identifiable donations We asked participants to consent to us accessing their name and cityfrom their survey provider (which confirmed that we could collect this data subject to participant
consent). All participants had the option to terminate the survey if they did not consent. We
informed those that consented that upon the publication of the Lott study in an academic journal,
we would post the results from the survey, including their individual donation decision, on ourstudy website. While we intend to do so should the study be published in an academic journal, thisstatement is somewhat misleading because it is unlikely that the study will ever be published (given
its methodological errors and the fact that Lott has rarely published in peer-reviewed academic
challenged some of the study’s methods, claiming that errors in analysis invalidate its results. Dr. Lott has responded
to this critique with a defense of the study’s methods, but the issue remains unresolved.”

83journals over the past decade). Despite participants consenting to us accessing and publishing theirnames, and the fact that only a small minority of the Republican and Independent participants arelikely to be uniquely identifiable based on their first and last name alone (i.e. absent geographicalor other identifiers), we still viewed it as desirable to preserve their anonymity: the formulation of
our experiment allows us to do so with high probability.
Cover manipulation Conceptually, in the No Cover condition for the donations experiment,
we would like to show respondents a website screenshot stating that “No participants were told
about Dr. Lott’s study.” However, because these participants did in fact learn about the study,
such a screenshot would be deceptive. Instead, we exploit the fact that Lott’s study had not yet
been published in an academic journal (a fact about which we explicitly informed all respondents
when describing the website). In particular, we show respondents a website screenshot statingthat “We surveyed respondents earlier this year before Dr. Lott’s study was published.” In thesurvey, we write that “the website states that you were surveyed before the study was publishedand does not mention that you were shown an early summary of the study’s findings.” Respondents
in this condition thus believe that their audience will believe that they (the respondents) had no
information excusing their decision to donate to Fund the Wall.
This formulation is misleading in that it relies on an academic, rather than commonplace,understanding of the word “published” (that is, “published in an academic journal” rather than“made available for public readership”). However, survey respondents themselves are not misled, as
they are fully aware of the study’s status and are fully aware of what others reviewing the donation
decisions are likely to believe. The group that may be misled is thus the group who visit the website
listing donation decisions. Given the low probability that this website will ever be published, weand our Institutional Review Board felt comfortable using this formulation.

D.3

Considerations related to subject pool contamination (Experiments 1, 3,
and Lott experiment)

An important concern with deceptive or misleading experiments is that they can contaminate thesubject pool by lowering trust in scientists and making respondents less likely to participate in
future research studies. Of course, this can only happen if respondents know that they are being
misled.
In the Lott experiment, subjects are told we will publish the website once Lott’s study is
published in an academic journal. Although we privately believe that the Lott (2018) study isvery unlikely to be published in a journal, subjects do not know (and never learn) this. (If thestudy is published, we are prepared to set up the web page in line with the instructions provided
to respondents.) Similarly, in Experiments 1 and 3, subjects are told we will post their Tweets
when and if we reach survey respondents on all US counties before August 1, 2021 (Experiment3) or December 1, 2021 (Experiment 1). Although we privately targeted fewer respondents than
the number of US counties, ensuring that this condition would not be met, subjects do not know
(and never learn) this is the case. In other words, it is not possible for respondents to know thatthey have been misled about the implementation of the main outcomes (unless they independently
find our working paper). To further substantiate the claim that our experiments had no effect on
respondents’ trust in social science experiments, we asked Luc.id to calculate the number of studies
in which each respondent participated in the following nine months. In Figure D1, we examine84

whether this number varies by experimental condition. We find no differences across the threetreatment conditions (including the Control condition, in which respondents were not exposed toany information about immigrants).
While it is technically possible that the experimental conditions induced differential trust insocial science that was not reflected in the number of studies in which respondents participated, weview this contingency as unlikely in light of the reasoning above. Furthermore, concerns about contaminating the experimental subject pool are most important in an economic lab with clear rules
against deception. In online survey marketplaces, where survey participants are expected to regularly participate in studies by psychologists in which explicit deception is common, considerations
about contaminating the subject pool are less relevant.
Figure D1: Subsequent survey behavior of respondents

Notes: Figure D1 presents the results of our analysis of the subsequent survey behavior of the respondents in
the Lott experiment between the end of collection and December 2020. The figure presents the mean numberof surveys (top panel) and the mean of the winsorized number of surveys (bottom panel) in which respondents
participated, with the winsorization at the 0.98 quantile.

D.4

Considerations related to starting political Twitter campaigns (Experiments 1 and 3)

As discussed in Appendix D.2, we designed our experiment to ensure that none of the Tweets would
ever be posted. It is of course possible that respondents independently posted political content on

85

Twitter as a result of our experiment. This is a concern for Experiment 3, in which respondents
were exposed to a clip presenting a misleading narrative about the link between illegal immigrationand crime.
To examine whether this was the case, we accessed all Twitter posts made by respondents
between the date of experimental collection and August 1, 2021 (the date by which we promised
respondents that our access to their accounts and any Twitter-related data would be deleted).
We used simple text analysis techniques to identify which posts concern immigrants and quantify the sentiment and content of these posts. The results of this analysis are presented in Figure D2 and Table D1. We find no evidence that respondents in our experiment begin posting
more immigrant-related Tweets or more negative content about immigrants after participating(Figure D2). Restricting to the period after the experiment, we find no evidence that respondents
in the Cover condition post more or fewer Tweets in general, more or fewer Tweets specifically
about immigrants, or more or less negative Tweets about immigrants than respondents in our No
Cover condition (Table D1). This evidence further strengthens our confidence that our experiment
did not contribute to anti-immigrant discourse on social media.
Figure D2: Twitter activity of respondents before and after experimentNotes: Figure D2 presents various measures of the Twitter activity of respondents before and after Experiment 3,
conducted between March 17 and March 22, 2021 (shaded in a gray rectangle). The left panel of the figure presents
the average number of immigrant-related Tweets; the middle panel the average sentiment of immigrant-related
Tweets; and the right panel the total expressed sentiment of immigrant-related Tweets.

86Table D1: Subsequent Twitter behavior of respondents
Dependent variable:Tw.
(1)

Tw. (w)(2)

Imm. Tw.
(3)

Imm. Tw. (w)(4)

Imm. sent.
(5)

Tot. imm. sent.
(6)

Cover

−44.414(29.941)−9.298(9.462)−0.583(0.416)−0.152(0.117)0.005(0.012)0.024(0.062)

Constant

80.075∗∗∗(20.862)35.951∗∗∗(6.593)0.970∗∗∗(0.290)0.383∗∗∗(0.082)0.003(0.008)−0.052(0.043)

517

517

517

517

517

517

Observations

Notes: Table D1 presents the results of our analysis of the subsequent Twitter behavior of the respondents inExperiment 3 between the end of our experiment and August 1, 2021. Table presents regressions of various measuresof behavior on an indicator for whether the respondent was in the Cover condition: Columns 1 and 2 consider the
total number of Tweets, Columns 3 and 4 the total number of immigrant-related Tweets, Column 5 the sentimentof immigrant-related Tweets, and Column 6 the sentiment of immigrant-related Tweets multiplied by the number ofTweets. Columns 2 and 4 winsorize the dependent variable at the 0.98 quantile.

87

E

Experimental Instructions

E.1

Experiment 1: Expression of dissent – Democrats

E.1.1

Attention screener

88E.1.2

Twitter information and login

89E.1.3Background questions

90

91

E.1.4Pre-treatment outcomes

92

93

94

95

E.1.5Treatment: “Before” wording (rationale)96E.1.6

Treatment: “After” wording (no rationale)

97

E.2

Experiment 2: Interpretation of dissent – Democrats

E.2.1

Attention screener and background questions

98

99

100

E.2.2Treatment: “Before” wording (rationale)

101

102

103

E.2.3Treatment: “After” wording (no rationale)

104

105

106

E.3

Experiment 3: Expression of dissent – Republicans

E.3.1

Attention screener

107E.3.2

Twitter information and login

108

109

E.3.3

Demographics

110

111

E.3.4

Video clip112

E.3.5Treatment: “After” wording

113

114

115

E.3.6

Treatment: “Before” wording

116

117

118

E.4

Experiment 4: Interpretation of dissent – Republicans

E.4.1

Attention screener and background questions

119

120

121

E.4.2Treatment: “Before” condition (rationale)

122

123

124

E.4.3Treatment: “After” condition (no rationale)

125

126

127

E.5

Auxiliary Experiment 1: Persuasion experiment – Democrats

E.5.1

Pre-treatment beliefs

128E.5.2

Information treatment (treatment group only)

E.5.3

Post-treatment outcomes

129

E.6

Auxiliary Experiment 2: Rainforest placebo

E.6.1

Pre-treatment questions

130

131

132

133

E.6.2Treatment: “Before” wording (rationale)134E.6.3Treatment: “After” wording (no rationale)

135

E.7

Auxiliary Experiment 3: Anticipated persuasion – Democrats

E.7.1

Treatment: “Before” wording (rationale)136E.7.2Treatment: “After” wording (no rationale)

137

E.8

Auxiliary Experiment 4: Open-ended explanations of preferred anti-defunding
Tweet – Democrats

E.8.1

Pre-treatment questions

138

139

140

141

E.8.2Treatment: “Before” wording (rationale)142E.8.3Treatment: “After” wording (no rationale)

143

E.9

Auxiliary Experiments 5: Interpretation of dissent with low-credibility rationale

E.9.1

Treatment: “Before” condition (rationale)

144

145

146

E.9.2Treatment: “After” condition (no rationale)

147

148

149

E.10

Auxiliary Experiment 6: Persuasion experiment – Republicans

E.10.1Pre-treatment beliefs

150E.10.2

Information treatment (only shown to respondents in the treatment group)151E.10.3

Post-treatment outcomes

152

E.11

Auxiliary Experiment 7 (wave 2): Expression of dissent with visible donation

E.11.1Pre-treatment questions

153

154

155

E.11.2

No Rationale condition

156

157

E.11.3

Rationale condition

158

159

E.12

Auxiliary Experiment 8: Interpretation of dissent with visible donation

E.12.1Pre-treatment information160E.12.2

No Rationale condition

161

162

163

164

165

E.12.3

Rationale condition

166

167

168

169

170