Can Religious Framing Rescue Institutional Signals? Experimental Evidence on Norm Change in a Low-Legitimacy Context

Participants are randomly assigned to one of five experimental conditions with equal probability (0.20 each). All participants first complete a demographics and baseline moderators block measuring institutional trust, religiosity, social norm sensitivity, general social desirability response bias, and prior contact with the transgender community.

The control condition (C) receives no information about the Supreme Court case. Four treatment conditions present participants with a vignette describing an anticipated Supreme Court ruling on the Transgender Persons (Protection of Rights) Act 2018:

T1 — Positive institutional signal without religious framing: the Supreme Court is expected to uphold the Act and maintain all existing protections for transgender individuals.

T2 — Negative institutional signal without religious framing: the Supreme Court is expected to strike down the Act and revoke existing protections.

T3 — Positive institutional signal with Islamic religious framing: same as T1, with additional framing citing Islamic principles of justice (adl), compassion (rahmah), and prevention of oppression (zulm), grounded in the teachings of the Holy Quran (Surah An-Nahl 16:90) and the Sunnah.

T4 — Negative institutional signal with Islamic religious framing: same as T2, with additional framing reflecting the Federal Shariat Court's 2023 reasoning that the Act contradicts Quranic teaching on gender categories, drawing on Surah An-Nisa 4:11-12 and the Sunnah.

All vignettes are read aloud by trained enumerators and are designed to reflect real institutional discourse previously used by Pakistani state and religious bodies. A manipulation check immediately following the vignette measures the perceived likelihood of the ruling to test vignette credibility. Outcome measures follow in the order: social norm perception, personal attitudes, behavioural measures, post-treatment institutional trust.

2026-08-30

2027-01-01

Perceived descriptive social norms index: mean response across eleven items measuring what most people in the respondent's area, or in Pakistan, are believed to feel or believe regarding social proximity, labour market inclusion, and educational inclusion of transgender individuals. Seven items (area-level reference group) use a 0–10 count-based response format ("out of 10 people in your area, how many..."); four items (measuring perceived national-level beliefs and trends) use a 5-point Likert scale, reflecting the difference in reference group scope.

Personal attitudes index: mean response across thirteen items measuring respondent's own comfort with and support for social proximity, labour market inclusion, and educational inclusion of transgender individuals (5-point agree/disagree scale).

Donation allocation: amount donated (PKR 0–150, in discrete increments of 0/10/20/50/100/150) from guaranteed participation payment to a transgender employment program.

Service enrolment — cleaning: binary indicator of whether the respondent signs up for free household cleaning and household help services delivered by trained transgender employees.

Service enrolment — tutoring: binary indicator of whether respondents with school-age children enrol in free tutoring services delivered by qualified transgender teachers (conditional on having school-age children in household).

The perceived norms index and personal attitudes index will each be constructed as Anderson (2008) summary indices — standardised z-scores averaged across constituent items — to address multiple outcomes within each family and to maximise power. Because index items are collected on different raw response scales (0–10 count format for area-level norm items, 5-point Likert for national-level norm items and all personal attitude items), each item is standardised against its own distribution (mean and standard deviation, using the control group) before being averaged into its respective index; this standardisation is what permits valid combination of items collected on different raw scales. Reverse-coded items will be recoded before standardisation so that higher values consistently indicate greater acceptance of transgender inclusion. Cronbach's alpha will be reported for each index. The donation measure is a discrete variable (PKR 0 to 150) and will be analysed both in levels and as a binary indicator (donated any amount versus none). Enrolment measures are binary (yes/no) and will be analysed using linear probability models and logistic regression as robustness checks.

Injunctive social norms index: mean response across four items measuring what most people believe should happen, or what transgender individuals are believed to deserve, regarding equal treatment and legal rights. Two items (area-level reference group) use a 0–10 count-based response format; two items (national-level reference group) use a 5-point Likert scale.

Pluralistic ignorance measure: within-respondent gap between personal attitude score and perceived descriptive norm score — a positive gap indicates the respondent is more accepting than they believe their community to be. This measure is purely individual-level and requires no external benchmark.

Pluralistic ignorance perception accuracy (exploratory): a separate check comparing each respondent's perceived descriptive norm score against the actual mean personal attitude score among Control-arm respondents in the same geographic unit, computed independently at Union Council, tehsil, and district level, to assess whether respondents' beliefs about their community's attitudes track the true distribution of attitudes in that community, and whether this accuracy differs across treatment arms.

Labour market perceptions: two items measuring perceived employability of transgender individuals in professional versus informal labour.

Post-treatment institutional trust index: Anderson summary index of five items measuring trust in the Supreme Court and government, repeated post-treatment to enable estimation of whether judicial signals shift institutional legitimacy.

Institutional trust misperception (preference-falsification gap): within-respondent gap between personal trust in the Supreme Court and perceived community trust in the Supreme Court, measured pre- and post-treatment — included as a validity check on social desirability bias in institutional trust reporting, given the general political sensitivity in Pakistan around expressing distrust of the judiciary to an unfamiliar interviewer, rather than as a substantive pluralistic ignorance finding. This measure is purely individual-level and requires no external benchmark.

Institutional trust perception accuracy (exploratory): a separate check comparing each respondent's perceived-community-trust score against the actual mean personal trust score among Control-arm respondents in the same geographic unit, computed independently at Union Council, tehsil, and district level, to assess whether respondents' beliefs about their community's trust track the true distribution of trust in that community, and whether this accuracy differs across treatment arms.

Religious identity activation: single post-treatment item measuring the extent to which religious beliefs influenced the respondent's views during the survey — mechanism test for religious framing effects.

Leaflet acceptance: binary indicator of whether respondent accepts a leaflet about transgender employment opportunities for sharing with others — measure of willingness to be publicly associated with transgender inclusion.

Response-mode validity check: comparison of attitude and norm-perception index scores between verbal and card-based (non-verbal) response conditions, pooled across treatment arms, to assess whether response format affects reporting on sensitive items.

Service enrolment persistence (exploratory, subject to feasibility): a brief follow-up contact with respondents who enrolled in either the cleaning/household help or tutoring service, conducted several weeks after the baseline survey, to assess whether the initial enrolment decision translated into actual service uptake, and whether this persistence differs across treatment arms. This follow-up is conditional on field operational capacity and is not itself a primary registered outcome; if conducted, results will be reported as exploratory and will not be used to revise conclusions drawn from the primary pre-registered enrolment measures.

Pluralistic ignorance will be computed as the individual-level difference between the respondent's personal attitudes index score and their perceived descriptive norms index score. A positive value indicates the respondent is more accepting than they perceive their community to be, consistent with pluralistic ignorance in the inclusion direction. Treatment effects on pluralistic ignorance will be estimated both directly (as a constructed outcome) and by comparing treatment effects on the two underlying indices separately, allowing identification of whether signals primarily shift perceived norms, personal attitudes, or both. This measure is computed entirely at the individual level and does not depend on any geographic benchmark.

Separately, the pluralistic ignorance perception accuracy check benchmarks perceived descriptive norms ("میرا علاقہ" / "my area" in the Urdu instrument) against the average personal attitudes index score among Control-arm respondents at three levels of geographic aggregation — Union Council, tehsil, and district — to assess whether this accuracy is sensitive to the scale at which "community" is defined, given known limits on statistical precision at the Union Council level with the achieved per-arm sample size. Given this precision limitation, the tehsil-level version is treated as primary for this specific check, with Union Council and district-level versions reported as robustness variants.

The institutional trust misperception gap is constructed identically to the pluralistic ignorance measure above (personal score minus perceived-community score, both standardised before differencing) but is interpreted in the opposite direction: a positive gap here is expected given the general sensitivity around openly expressing distrust of state institutions in the current political climate, and serves as a check on desirability bias in institutional trust reporting rather than as evidence about genuine community norms. This measure is computed entirely at the individual level and does not depend on any geographic benchmark.

Separately, the institutional trust perception accuracy check benchmarks perceived-community trust against the average personal trust score among Control-arm respondents at the same three levels of geographic aggregation — Union Council, tehsil, and district — for the same reason and with the same tehsil-level-as-primary approach as the pluralistic ignorance accuracy check above.

The post-treatment institutional trust index will be analysed using both a difference-in-differences specification and an ANCOVA specification (post-treatment score regressed on treatment arm indicators, controlling for the pre-treatment score as a covariate). Because treatment is individually randomised, both approaches yield unbiased estimates of the treatment effect; however, ANCOVA is expected to provide a more statistically powerful and more precise test of whether judicial signals shift institutional legitimacy, consistent with established methodological findings that ANCOVA dominates change-score analysis in randomised designs (Van Breukelen, 2006). The ANCOVA specification will serve as the primary specification for this outcome, with the DiD estimate reported as a robustness check.

Independently of treatment arm, 10% of respondents complete the survey using standard verbal response elicitation while 90% use a non-verbal, card-based method in which the respondent points to a response rather than stating it aloud. This assignment is orthogonal to treatment and is not crossed with treatment arm in any planned analysis of primary outcomes; the comparison is included solely to assess measurement validity.

The service enrolment persistence check, if conducted, addresses the distinction between an immediate enrolment decision — a "flow" outcome potentially sensitive to short-term emotional or social-desirability responses to the vignette — and durable behavioural follow-through, better evidence of a genuine change in willingness to engage with transgender-provided services. Because this follow-up depends on field team capacity and resources beyond the primary data collection window, it is registered here as a conditional, exploratory extension rather than a primary outcome.

The study uses a between-subjects randomised vignette experiment embedded in a household survey. The design has five arms — one control and four treatments — with equal probability of assignment (0.20 per arm). Assignment is individual-level, implemented through the KoboToolbox survey instrument administered by trained enumerators on tablets during face-to-face household visits.

The four treatment conditions follow a 2x2 factorial structure crossing two dimensions: policy direction (positive ruling upholding the Transgender Persons Act versus negative ruling striking it down) and religious framing (absent versus present). The control condition receives no information about the Supreme Court case.

The survey flow is: demographics and baseline moderators (including pre-treatment institutional trust, perceived institutional trust, religiosity, and general social desirability response tendency) → prior knowledge questions → randomisation → vignette or control → manipulation check → outcome measures (social norm perception, personal attitudes, behavioural measures) → post-treatment institutional trust measures.

Household sampling uses a population-weighted sampling frame across 68 Union Councils in urban Lahore. Within each sampled UC, gridded population data (WorldPop 2025, 100-metre resolution) is used to select starting points via probability-proportional-to-size sampling without replacement, weighted by each grid cell's estimated population, with a small random offset applied within each selected cell. Five starting points are generated per UC (ten for the two double-weighted UCs), for 350 starting points in total. From each starting point, enumerators follow a systematic right-hand-rule walk protocol, approaching every third household. Non-response at a given position in the walk sequence triggers a bounded substitution attempt (the immediately preceding household, then the immediately following household, maximum two attempts) before the systematic sequence resumes; unavailable respondents (rather than outright refusals) are offered a same-day callback at a different time, followed by a different-day callback if the first is unsuccessful, before substitution is applied. Enumerators continue sampling further along the same systematic sequence at a given starting point, as needed, until ten quality-assurance-valid interviews are achieved at that point, rather than working to a fixed pre-calculated number of approaches per point. Within each household, one adult is randomly selected using a random draw generated within the survey software.

Independently of treatment assignment, respondents are randomly assigned to one of two response elicitation modes for all scale-based items (10% verbal, 90% non-verbal card-based response), included as a measurement validity check and not crossed with treatment arm in the analysis of primary outcomes.

Not available

Treatment assignment is generated within the KoboToolbox survey instrument at the start of each interview using the formula once(int(random()*5)+1), which draws a value between 1 and 5 with equal probability (0.20 each) and fixes it for the remainder of that respondent's session. Assignment is independently generated per submission. Response mode (verbal vs. card-based) is assigned independently using an analogous formula with unequal probability weighting (0.10 / 0.90). The full de-identified assignment log for both randomisations will be archived and made available in the replication package.

Individual adult respondents. Randomisation occurs at the individual level — each respondent is independently assigned to a treatment arm regardless of which household or street they are from. Treatment is not clustered at the household, street, or UC level. Standard errors will be clustered at the UC level to account for potential within-UC correlation in outcomes arising from shared neighbourhood norms and social networks.

No

68 unique Union Councils in urban Lahore (70 sampling slots; two UCs are double-weighted and receive double the standard number of starting points). This is the unit used for standard error clustering in estimation, not the randomisation unit.

3,500 individual adult respondents is the target completed and QA-validated, analysed sample. Household-level non-response and unavailability are addressed in real time through the field substitution and callback protocol described under Experimental Design. Rather than working to a fixed pre-calculated number of household approaches per starting point, enumerators continue sampling further along the same systematic walk sequence at a given starting point, as needed, until ten quality-assurance-valid interviews are achieved at that point, across 350 starting points in total. This approach responds to realised non-response and invalidation directly at each point rather than relying on an ex-ante attrition buffer; if invalidation at a given point is unusually high, more households are approached at that specific point rather than the shortfall being distributed across the sample.

700 respondents per arm across five arms (Control: 700; T1 Positive, no religious framing: 700; T2 Negative, no religious framing: 700; T3 Positive, with religious framing: 700; T4 Negative, with religious framing: 700). Equal allocation across arms, total N = 3,500.

Based on effect sizes reported in Tankard and Paluck (2017) for comparable institutional signalling vignette experiments — standardised effect sizes of d=0.15 to d=0.25 on norm perception and attitude outcomes — the following power calculations apply at the study's target sample size: At n=700 per arm, two-arm comparison (any treatment vs. control), two-tailed alpha=0.05, power=0.80: minimum detectable effect size d=0.15. The study is adequately powered to detect main treatment effects at or below the lower bound of effect sizes observed in comparable experiments. For pre-registered heterogeneity analyses (religiosity and prior knowledge moderators), splitting each arm on a binary moderator produces subgroups of approximately 350 respondents. Minimum detectable interaction effect sizes at 80% power for n=350 per subgroup: d=0.21. The study is powered for heterogeneity tests of moderate interaction effects; smaller interactions will be reported as directional with appropriate confidence intervals. For behavioural outcomes (donation allocation, service enrolment), power calculations assume a base rate of 30% enrolment in the control group based on comparable NGO opt-in experiments in South Asia. At n=700 per arm, the study detects differences in proportions of approximately 6.9 percentage points at 80% power. Because the field protocol targets at least 3,500 QA-valid observations and may yield a modestly larger realised sample depending on the actual invalidation rate, all power calculations above should be read as conservative upper bounds on minimum detectable effect size; a larger realised sample would tighten the main-effect MDE somewhat more than the heterogeneity MDE, reflecting the structurally lower sensitivity of interaction-effect power to sample size increases.