Silence to Solidarity: How Communication About a Minority Affects Discrimination

This paper examines how two types of communication about a minority group affect discriminatory behavior: (i) horizontal communication between majority-group members, and (ii) top-down communication from agents of authority such as the legal system. The setting is urban Chennai, India, where the paper measures discrimination against thirunangai — a community of transgender women who are India’s most visible LGBTQ+ group — in a field experiment with 3,397 participants.

Discrimination is measured using incentivized hiring choices. Participants are offered a free grocery delivery and make 10 binary choices over which worker will carry out the delivery, with worker gender (cisgender male, cisgender female, or transgender) varying across options. The stakes are real: one choice is randomly selected and implemented 2–9 weeks later. Participants in the control condition are highly discriminatory: they are 19 percentage points (32%) less likely to hire a transgender worker than a non-transgender worker (p<0.001), and are willing to sacrifice grocery items worth 1.9 times their median daily per capita food expenditure to avoid a 15-minute interaction with a transgender worker.

The first main treatment involves randomly assigning participants to a 3-person group discussion with two neighbors, in which they discuss and make collective hiring choices over the same options. The key outcome is participants’ subsequent private, individual hiring choices. The discussion eliminates anti-transgender discrimination on average: participants in the discussion arm are 17 percentage points (42%) more likely to select a transgender worker in their private post-discussion choices relative to the control group (p<0.001), so that discrimination is no longer statistically distinguishable from zero (p=0.30). The discussion’s effect is partially persistent: approximately one month later, discussion participants are still 4 percentage points more likely to select transgender workers in hypothetical hiring choices (p=0.03), representing roughly 25% of the short-run effect.

The second main treatment cross-randomizes a video shown before hiring choices. The legal rights video informs participants of a Supreme Court ruling affirming that transgender people hold the same fundamental constitutional rights as other citizens. This reduces discrimination by 10.3 percentage points (p<0.001). A rights messaging video — which argues that transgender people should have equal rights without invoking legal authority — reduces discrimination by a smaller 5.8 percentage points (p=0.001), and there is some evidence the legal-authority version is more effective (p of difference in [0.01, 0.12]). However, the legal rights video’s effect is only 59% as large as the discussion’s effect (p of difference in [0.002, 0.04]), and it does not persist at the one-month follow-up (p in [0.12, 0.51]).

The paper rules out two candidate mechanisms for the discussion’s effects and supports a third. First, the discussion does not work primarily through correcting misperceived norms: while control-group participants do overestimate peer discrimination by 5 percentage points, the discussion reduces predicted discrimination by 24 percentage points — far more than a corrected misperception could explain (at most 21% of the effect under generous assumptions). Second, the discussion does not work through virtue signaling alone: a “No discussion (public)” arm in which participants make individually-visible choices shows no reduction in discrimination on average (p=0.83). Third, the paper provides affirmative evidence for a persuasion channel: participants in a “listener” arm, who silently observe a 2-person discussion without participating, discriminate 13 percentage points less than the control group (p<0.001), an effect that is highly persistent at the 2–9 week follow-up (11 percentage points, p<0.001). The persuasion mechanism is further supported by the finding that pro-trans participants are more vocal: each additional transgender worker chosen in post-discussion private choices is associated with a 32% higher probability of speaking first (p=0.03) and a 27% higher probability of dominating the discussion (p=0.02). Statements about transgender workers during discussions were 5.7 times more likely to be positive than negative. Listeners who heard moral argumentation about equality, rights, and giving opportunities subsequently discriminated less (p<0.001).

Scope conditions: the study is conducted among urban Chennai residents (85% female), where transgender identity is visually recognizable and socially salient, awareness of the 2014 Supreme Court ruling is low (36% could not identify a single legal right transgender people hold), and a wedge exists between descriptive norms (high actual discrimination) and prescriptive norms (93% of the control group rate explicit discrimination as wrong). The model’s “sweet spot” logic implies these effects may not generalize to settings where discrimination is either near-universal (no privately pro-trans individuals to be vocal) or already minimal (no incentive to persuade).

Q: How is anti-transgender discrimination measured in the experiment? A: Participants make 10 incentive-compatible binary hiring choices over grocery delivery workers, with one choice randomly selected and implemented 2–9 weeks later. Discrimination is defined as the reduction in the probability of selecting the alternative worker when that worker is transgender versus non-transgender, conditional on other option characteristics such as items offered and reliability score. Participants are told they will have a 15-minute conversation with the selected worker, ensuring anticipated social contact. The design is framed as market research to obfuscate the study’s purpose; only 8% correctly guessed the true focus.

Q: How large is baseline discrimination in the control group? A: In the No discussion (private) control condition, participants are 19 percentage points (32%) less likely to hire a transgender worker than a non-transgender worker (p<0.001). In willingness-to-pay terms, participants sacrifice grocery items worth 1.9 times their median daily per capita food expenditure (Rs. 127 on a base of Rs. 67) to avoid selecting a transgender worker. Even when a transgender worker dominates on both items and reliability score, participants in the control group still select the non-transgender worker 47% of the time.

Q: What is the main effect of the 3-person group discussion on subsequent discrimination? A: Participants who engage in a group discussion with two neighbors are 17 percentage points more likely to select a transgender worker in their subsequent private individual choices (p<0.001). This eliminates average discrimination entirely: in the discussion arm, the probability of selecting a transgender worker is not statistically distinguishable from the probability of selecting a non-transgender worker (p=0.30). The willingness-to-pay to avoid a transgender worker falls from Rs. 127 to Rs. 13 (p of difference < 0.001), and is no longer significantly different from zero (p=0.265).

Q: How persistent are the effects of the group discussion? A: At the 2–9 week follow-up survey (mean 35 days), discussion participants are approximately 4 percentage points more likely to select transgender workers in hypothetical hiring choices (p=0.03). This represents approximately 25% of the short-run 17 percentage point effect, a decay rate comparable to the persistence of US political advertising effects in the political science literature (Hill et al., 2013, estimate 10–15% remaining after 30 days).

Q: What is the effect of the legal rights video, and how does it compare to the discussion? A: The legal rights video — informing participants of the Supreme Court ruling affirming transgender people’s fundamental constitutional rights — increases the probability of selecting a transgender worker by 10.3 percentage points (p<0.001). The rights messaging video, which argues that transgender people should have equal rights without invoking legal authority, increases it by 5.8 percentage points (p=0.001). The legal rights video’s effect is only 59% as large as the discussion’s 17 percentage point effect (p of difference in [0.002, 0.04]), and unlike the discussion, neither video’s effect is detectable at the one-month follow-up (p in [0.12, 0.51]).

Q: Does the legal rights video work through a different channel than the rights messaging video? A: There is evidence that the legal authority of the Supreme Court matters beyond the content of the rights message. The legal rights video is more effective than the rights messaging video at reducing discrimination (p of difference in [0.01, 0.12]), and the legal rights video (but not the rights messaging) affects participants’ beliefs about the legal status of transgender people (as measured by a summary index). Both videos shift perceived descriptive norms — participants predict others will select transgender workers more, by 2–6 percentage points — but neither significantly affects attitudes as measured by a list experiment or disapproval questions.

Q: Does the discussion work through correcting misperceived norms? A: This channel can account for at most a small fraction of the effect. Control-group participants do overestimate peer discrimination by 5 percentage points in incentivized predictions (p<0.001, as measured by predicted probability of selecting a transgender worker). However, the discussion reduces predicted discrimination by 24 percentage points (p<0.001), far exceeding the initial misperception. Even under generous assumptions in which the misperception is precisely corrected, this mechanism could account for no more than 21% of the discussion’s treatment effect (95% CI: [8.9%, 32.5%]).

Q: Does the discussion work through virtue signaling? A: The evidence rules out virtue signaling as the primary channel. The “No discussion (public)” treatment arm makes participants’ individual hiring choices visible to their group members, exogenously increasing social image concerns in the absence of a discussion. This has no detectable average effect on discrimination (p=0.83), indicating that social image concerns alone — without the persuasive content of an actual discussion — do not explain the reduction in discrimination generated by the group discussion.

Q: What is the evidence for the persuasion mechanism? A: The “listener” treatment arm provides direct evidence. In this arm, one participant silently observes a 2-person discussion without speaking, then makes private individual choices. Listeners discriminate 13 percentage points less than the control group (p<0.001), an effect statistically indistinguishable from full discussion participants. Since listeners changed their behavior based solely on what they heard and saw, this constitutes evidence of persuasion. The listener effect is highly persistent at the 2–9 week follow-up (11 percentage points, p<0.001) and holds on a robustness outcome designed to be completely private. The implied persuasion rate is 29%, described as high relative to values in the literature (DellaVigna & Gentzkow, 2010).

Q: Why do pro-trans participants persuade others — what drives the discussion’s content? A: Pro-trans participants are disproportionately vocal. Each additional transgender worker chosen in post-discussion private choices (a proxy for pro-trans private attitudes) is associated with a 32% higher probability of speaking first (p=0.03) and a 27% higher probability of dominating the discussion (p=0.02), but only when discussing a choice involving a transgender worker. The overall tone of discussions is strongly pro-trans: statements about transgender workers are 5.7 times more likely to be positive than negative. Participants who hear moral argumentation about equality, rights, and giving opportunities subsequently discriminate significantly less (p<0.001).

Q: Does the discussion work by changing statistical (belief-based) discrimination? A: Partially, baseline discrimination in the control group is partly statistical: despite transgender workers having the same average reliability scores as others, participants rate them as less likely to complete a delivery, and revealing the true reliability score makes participants 2.9 percentage points more likely to select a transgender worker (an effect unique to transgender workers). However, the discussion does not significantly affect beliefs about transgender workers’ reliability, and there is no detected reduction in the belief-based component of discrimination in the discussion arm (though the test is underpowered).

Q: Are the effects of the discussion and the legal rights video additive? A: The two interventions appear to combine approximately linearly for the legal rights video: there are no detected interaction effects (p in [0.83, 0.96]). By contrast, there is weak evidence of a negative interaction between the rights messaging video and the discussion, suggesting these two may be substitutes — consistent with the rights messaging video’s content being similar to the pro-trans moral argumentation already present in discussions.

Q: What alternative explanations are ruled out? A: The paper tests and finds no support for: (i) photo characteristics such as perceived caste driving results; (ii) social image concerns affecting even post-discussion private choices (the “extra private” robustness outcome designed to be unobservable by neighbors yields similar results); (iii) increased contemplation or deliberation about choices; (iv) experimenter demand effects or social desirability bias (treatment effects do not differ for the 8% who guessed the study’s purpose); (v) increased salience of the transgender category; and (vi) cheap talk from low stakes (choices were incentive-compatible and implemented).

Q: What is the study’s theoretical model for why pro-trans participants speak out? A: The paper develops a model combining social signaling (people want to fit in with their group; Bénabou & Tirole, 2006) with direct persuasion (participants can change each other’s preferences through messages). Under the right conditions, only pro-trans participants send persuasive pro-trans messages. This occurs in a “sweet spot” range: when average discrimination is not so strong that no one is privately pro-trans, and not so weak that pro-trans participants lack an incentive to persuade (since they are already in the majority). The context in Chennai — high actual discrimination but strong social norms against it — satisfies this sweet spot condition.

Q: What are the policy implications regarding horizontal versus top-down communication? A: In this context, facilitating horizontal communication between neighbors is a more effective tool for reducing discrimination than top-down communication about legal rights: the discussion’s effect is 1.7 times larger than the legal rights video (17 p.p. vs. 10.3 p.p.) and partially persists at one month, whereas the legal rights video’s effect does not persist. However, the legal rights video does reduce discrimination relative to the rights messaging video, suggesting that communicating the legal authority of the Supreme Court carries independent weight beyond rights advocacy messaging. Both interventions are complementary when combined.

Horizontal communication: Communication between members of the majority group about a minority, as distinct from contact between majority and minority groups or top-down communication from authority. In this paper, operationalized as a group discussion among three neighbors who make collective hiring choices.

Top-down communication: Communication from agents of authority — here, the legal system — about a minority group’s rights. Measured via a video informing participants of a Supreme Court ruling affirming transgender people’s constitutional rights.

Anti-transgender discrimination: In the paper’s own measurement, the reduction in the probability that a worker is chosen because they are transgender (relative to being non-transgender), conditional on other delivery option characteristics. Measured in incentivized, privately-elicited binary hiring choices.

Expressive law hypothesis: The theory that changes in the law affect behavior by changing people’s perception of the prevailing social norm, not (only) through deterrence. The paper tests this by comparing a legal rights video (invoking Supreme Court authority) to a rights messaging video with identical content but no legal backing, finding the legal-authority version more effective.

Persuasion channel: The mechanism by which discussion participants change each other’s preferences through persuasive messages, particularly moral arguments about equality and rights. Distinguished in the paper from virtue signaling (publicly visible pro-trans behavior) and norm correction (updating misperceived beliefs about peer behavior).

Pluralistic ignorance: A setting in which people misperceive how common discriminatory attitudes are among their peers, potentially hiding genuine minority support for the discriminated group. The paper tests this as a candidate mechanism and finds it can account for at most 21% of the discussion effect.

Sweet spot condition: The range of average group discrimination levels in which pro-trans participants have both the motivation and opportunity to speak out persuasively — discrimination is not so universal that no one is privately pro-trans, and not so minimal that the pro-trans participants feel no need to persuade others. The paper argues the Chennai context satisfies this condition.