Contribution
A randomized test of the contact hypothesis in an ongoing conflict setting, on a random sample of the people who riot rather than volunteers, with prejudice and discrimination measured separately. Its two findings are that cooperative contact can change behaviour toward the out-group while leaving stated attitudes where they were, and that a pure control arm changes what the usual mixed-against-unmixed comparison means: most of that contrast is the single-religion classes becoming more discriminatory.
Key insight
The usual contact comparison has two moving parts. Against people who took no course, the mixed classes discriminated about as much as before and the single-religion classes discriminated more, because they gave their new generosity mostly to their own side. So “contact reduced discrimination” here is better read as “contact prevented the rise that same-group contact produced”. The authors call it a substitution effect: time with the out-group is time not spent bonding with the in-group.
Assumptions
- Population. Men aged 18–25 in the sixteen poorest Kaduna neighbourhoods with a history of violence, sampled by random walk; women and six neighbourhoods suspected of Boko Haram cells excluded.
- Treatment. 30 class sections (20 mixed, 10 single-religion), four hours a week for sixteen weeks, 29 sessions, pairs sharing a laptop on cooperative tasks, no peace or anti-prejudice content, and incentives (a ₦200 stipend per class, a laptop raffle). Students and teachers were told it was an educational programme.
- Randomization at three levels: invitation to the course (549) against survey-only control (300); mixed against single-religion class; same- against other-religion partner within mixed classes.
- Measures, endline only, four to six weeks after the course: prejudice by three stereotype indices (negative attributes, positive attributes, a three-pair out-group evaluation), self-completed and sealed; discrimination by ten rounds each of a dictator game (divide ₦100) and a destruction game (destroy another’s ₦50 notes for ₦10 each), against recipients named by first name, which signals religion, and for course participants flagged as classmate or not. No prejudice baseline, by design, to avoid priming.
- Estimation. Intent-to-treat OLS, no covariates in the main tables; game standard errors clustered by respondent, with round fixed effects. Compliance 84%; attrition 6% (4% treated, 10% control).
Key results
- Prejudice (Tables 2–4). No arm reduced it. Of 27 coefficients two are significant at p < 0.05 and they point opposite ways (Christians in the course disagreed more with both negative and positive attributes of Muslims). The authors report over 90% power for r = −0.21. The mediator items (knowledge, anxiety, empathy) moved only for Muslims’ anxiety under course assignment.
- Program effect (Table 5, cols 1–3). The course raised dictator giving by about 0.47 bills (₦4.7, about ₦4 by the text) to in-group and out-group alike, with no change in the gap.
- Contact effect (Table 5, cols 4–6). Mixed class × out-group recipient: +0.39 bills, p < 0.01, against a gap of −0.55, about 70% of it. Muslims +0.25 (p < 0.10) of −0.58; Christians +0.52 of −0.51, all of it.
- Against the control (Table 6). Gap between in-group and out-group giving: control 0.19, single-religion class 0.54, mixed class 0.17. By religion: Muslims 0.33, 0.58, 0.34; Christians 0.02, 0.51, 0.00.
- Destruction game (Table 7). The course cut destruction by about 10% (−0.07 on 0.70), driven by Christians. Mixed class × out-group: −0.05 (p < 0.10), Christians −0.08 (p < 0.10). Other-religion partner × out-group: −0.07 (p < 0.10), Christians −0.10 (p < 0.05).
- Partner dose (Table 5, cols 7–9). No further reduction in dictator-game discrimination from an other-religion partner; a further rise in giving to everyone among Christians.
- Strangers (text; appendix not read). Restricted to recipients who were not classmates, the mixed-class effect on dictator giving halves and is not significant; among Christians it stays large and significant. In the destruction game there is no overall reduction toward strangers; Christians’ effects are of comparable size.
Claims
| id | claim | strength | support |
|---|---|---|---|
| C1 | Sixteen weeks of cooperative intergroup contact did not change stated prejudice | moderate | three indices, nulls with stated power; endline only, self-report |
| C2 | Mixed classes discriminated less than single-religion classes in incentivized games | moderate | Table 5 (p < 0.01 dictator), Table 7 (p < 0.10 destruction); randomized |
| C3 | The contrast is mostly a rise in discrimination in single-religion classes | moderate | Table 6, a comparison of means against the control, no test reported |
| C4 | Contact reduced discrimination toward unfamiliar out-group members | weak | Christians only; the overall stranger effect is not significant; appendix tables not read |
| C5 | Behaviour changed before attitudes, as self-perception theory predicts | weak | offered as one of four interpretations; untested, one endline |
| C6 | Valued programme content draws participants and raises generosity to all | moderate | the program effect in Tables 5 and 7 |
Concepts
- Prejudice: “negative beliefs about or attitudes toward an individual based solely on membership in a particular social group”, measured by stereotype agreement.
- Discrimination: treatment that “differs based solely on group affiliation”, measured as the gap between play toward in-group and out-group recipients.
- In-group bonding effect: the rise in in-group-favouring play among those given contact with unfamiliar members of their own group.
- Program effect / contact effect / contact dosage effect: the three randomized comparisons (course against control; mixed against single-religion class; other- against same-religion partner).
Connections
The authors place themselves against Pettigrew and Tropp’s optimism (LIT-1413) and use its mean r = −0.21 for their power analysis; they cite the 2008 mediator meta-analysis (LIT-1405) for knowledge, anxiety and empathy, and find none of the three moved. Paluck, Green and Green (LIT-1420, NOTE-1393) include this study among their three pre-registered trials, pooled at 0.016; this reading shows that their near-zero is the prejudice null, while the trial’s own headline is a behavioural effect. The authors’ precedent for behaviour changing without attitudes is Paluck’s Rwanda radio study. Their Discussion cites Bem’s self-perception and Fazio on behaviour preceding attitude.
Bearing on the record
- QUESTION-262. It meets the question’s measurement demand, conduct scored by evidence that does not pass through the interpretation under test (incentivized, private, sealed games), and its stranger rounds are the “unfamiliar group members” the question names. It does not draw the question’s first contrast. There is no arm with favourable information and no taking part; the course arms differ in who one took part with, not in whether one took part. Its “local against general” result is split: the effect on strangers holds for Christians and not overall. And it adds a contrast the question lacks: the comparison that matters may be same-group against cross-group taking part, since same-group cooperation itself moved conduct, toward more discrimination. A note on the question should say that its “near zero” for pre-registered trials is, for this study, a null on attitudes beside a positive result on behaviour.
- CLAIM-430. The pattern, conduct moved and stated view did not, is what part 2 of the claim, taking part before the reinterpretation, would show at the moment of measurement. It is not evidence that the reinterpretation follows: there is one endline, no later attitude measure, and the authors give the order only as one of four readings. Their first reading cuts against the claim’s mechanism. If the behavioural contrast is mostly in-group bonding in the single-religion classes, the mixed classes were not given a new way of relating; they were spared a reinforced old one. The trial does not touch the claim’s second defeater, since it has no information arm. The anonymous-favour defeater is not tested either.
- CLAIM-275. One more instance of conduct changing without a prior change of interpretation, in a randomized design. It does not show the act making the interpretation available.
- CLAIM-403. The trial measured no change in whose testimony moves judgement; its outcomes are stereotype ratings and allocations.
No instruction for machine-learning practice; nothing for the anthology.
Limitations
- Behaviour in games. Discrimination is play in two games against named strangers, at home, a month after the course; not conduct in daily life, and no conflict behaviour.
- Small effects in the destruction game, mostly at p < 0.10, and three comparisons by two religions per game invite multiplicity, which the paper does not correct for. The authors report that the religion × treatment interactions are not significant, so the difference between Christians and Muslims they discuss is not established either.
- Registration after data collection. The EGAP registration is dated 12 August 2015 (ID 20150617AA), seven months after the January 2015 endline; it attests registration before the researchers had the outcome data. It lists five outcome families (prejudice, discrimination, cooperation, conflict-related behaviour and attitudes, trust), 720 subjects, pre-specified controls and difference-in- differences where possible; the paper reports two families, 849 subjects and parsimonious models, with the pre-specified controls in the appendix. Whether the other three families are reported elsewhere was not checked.
- The partner arm may be a weak dose: with at most sixteen students a class, the authors say, the difference between partners may have been small.
- Slips. The text’s “approximately ₦4” program effect is 0.47 bills of ₦10, ₦4.7 (footnote 39’s ₦26 to ₦30 rounds the same way). In the extracted text the paragraph on stranger play in the destruction game precedes the section that introduces Table 7, a layout effect. No error of substance found.
Open questions
- Does stated prejudice move later in the mixed classes, as the self-perception reading predicts? A second endline would say.
- Would an arm that received the course’s cross-group content without the shared work, for instance watching mixed pairs work, change conduct as much? That is QUESTION-262’s first contrast and CLAIM-430’s second defeater, and this design does not draw it.