# A10 prospective analysis specification · version 1.0

## Scope and implementation state

This is a primary-study protocol with completed CCD audits and artificial design calculations. No trial participants, ethics approval, registration, allocation, or observed intervention effect are represented as completed. Finalize the pilot, permissions, analysis implementation and registration before allocation. The public Python tool implements the administrative audit, artificial simulation and a pair-summary mathematical utility. It does not implement or validate the proposed multiple-imputation, longitudinal, measurement-invariance or qualitative pipelines.

## Population, cohort and allocation

Plan 64 regular public schools in 32 matched pairs, with 40 baseline students per school. The target is 20 students in each of grades 7 and 8 where the eligible roster permits. The historical CCD filter requires updated status 1, 3, 4, 5 or 8, school type 1, and both grades offered. Contemporary eligibility, grade-specific enrollment, consent, accessibility and governance must be confirmed separately. Preserve NCESSCH and LEAID as 12- and 7-character strings. Administrative categories do not identify culture.

Match using prespecified baseline/context variables, within LEA where feasible. Investigate shared design teams before assignment. A change of assignment unit requires an amendment and new design calculation. Lock pairs, eligible roster, consent and baseline records before an independent custodian randomly assigns one school per pair. Do not replace absent baseline students with postassignment recruits. Preserve the allocation method and seed securely until disclosure cannot influence recruitment.

## Outcomes and inferential hierarchy

Primary: week-24 minus baseline change in a permission-cleared PSSM score. Proposed scoring uses the original reverse key and mean of 1–5 keyed responses if at least 16 of 18 items are answered. The ≥16 completion rule is proposed, not claimed to be validated by Goodenow. Fewer than 16 responses yield a missing occasion score, never zero. A separate pilot must lock the wording, permission, translations, key and completion rule before allocation. All consenting baseline cohort members remain targets even when a score is missing.

Secondary: blinded transfer score (0–16) at week 24; week-36 transfer and belonging; governance, burden and exposure measures. Fixed-sequence testing first tests primary belonging at two-sided alpha .05. Only if that rejects does week-24 transfer receive a confirmatory .05 test. Otherwise transfer p-values are descriptive. Other comparisons and interactions remain exploratory with unadjusted intervals labeled accordingly. Report raw units; standardized effects use an explicitly defined pooled baseline SD. The simulated .30-SD effect is a planning assumption, not a success threshold.

## Equal-school contrast and uncertainty

For pair j, let d_j be the treated school's mean within-student change minus the comparison school's corresponding mean. With J pairs, estimate tau = mean(d_j), variance s_d²/J and a 95% t interval with J−1 degrees of freedom. Schools and pairs receive equal weights; students receive equal weights within each school's fixed baseline cohort. The student-weighted sensitivity estimand is different and must be labeled.

A Fisher sharp-null analysis flips assignment within the locked pairs. Use 99,999 reproducible draws for the planned 32-pair trial and p = (1 + count of |T_perm| ≥ |T_obs|)/(1 + 99,999). The custodian preserves the analysis seed. This tests a sharp null under allowed allocations, not an assertion that every subgroup's average effect is zero. With missing outcomes, exact complete-data randomization guarantees do not automatically extend to imputed outcomes. Describe the complete-outcome test's missingness/conditioning limitation and treat imputed inference as model-assisted. Outcome-relevant interference imposes additional limits on the pair-based interval.

## Missing outcomes and proposed imputation

Distinguish item, occasion, student and whole-school loss. Do not assign zeros, fabricate follow-up or replace missing students. The initial plan uses 50 posterior-predictive completed datasets, increased if the Monte Carlo error exceeds 10% of the inferential standard error or independent repeated draws show unstable tail estimates.

A proposed joint model treats the four occasion scores as bounded continuous outcomes using a truncated normal distribution on 1–5. Include occasion indicators, assignment-by-occasion terms, grade, language version, pair indicators, school random intercepts and student random intercepts. Model baseline as an outcome so missing baseline values can be drawn. Decide and lock before analysis whether baseline treatment means are constrained equal; examine an unconstrained version as sensitivity. Include permitted, prespecified follow-up predictors without selecting variables for significance.

Candidate priors are Normal(3,1) for the intercept, Normal(0,1) for other coefficients in raw score units and half-Normal(0,1) for random-effect and residual SDs. If a correlation structure is introduced, use an LKJ(2) prior and identify the amendment. Check prior-predictive coverage. Diagnose four chains, R-hat below 1.01, effective sample sizes at least 400 for primary parameters, posterior-predictive score patterns and independent software tests. Failure to achieve reliable fit blocks claims dependent on these imputations. This continuous-score approximation does not establish ordinal invariance; a permission-cleared item-level ordinal model is a possible sensitivity requiring separate validation.

In every completed dataset compute the same school changes, pair contrast and within-imputation variance. Pool using total variance T = mean(U_m) + (1 + 1/M)B, where B is between-imputation variance. Use the Barnard–Rubin small-sample degrees-of-freedom adjustment with complete-data degrees of freedom J−1. This planned pooling requires an independently tested implementation. Display complete-case and imputed results together.

For nonignorable-missingness sensitivity, shift imputed treatment and comparison occasion scores independently by −.50, −.25, 0, +.25 and +.50 raw points, truncate to 1–5 and report all 25 contrasts. Show larger adverse shifts and worst/best bounds where feasible. This is a tipping-point diagnostic, not a realistic probability model for every missingness mechanism. Analyze whole-school loss separately: many student imputations cannot create independent schools. Report when the assumptions or uncertainty prevent a useful conclusion.

## Longitudinal and measurement analyses

A secondary mixed model includes pair, occasion, assignment-by-occasion, grade and form/language terms, with school and student random intercepts. Lock covariance choices before unblinding and use appropriate small-sample uncertainty. Do not choose the primary result by the smallest model p-value.

Ordinal checks examine configural structure, loadings and thresholds across time and major language versions, respecting repeated-item dependence and ordinal identification. Examine residuals, response-category occupancy, fit change and substantive interpretation jointly. Chen's fit-sensitivity research does not supply a universal cutoff. Configural fit alone cannot authorize latent mean comparison. Partial-invariance sensitivity must not redefine the primary score until it becomes favorable. Small groups may be too small for defensible invariance tests; do not merge them into a manufactured culture. Restrict subgroup interpretation to voluntary, appropriate information rather than inferred CCD race categories.

## Interference, qualitative evidence and harms

The design does not randomize network saturation and cannot separately identify direct and indirect effects. Log school-level shared teams and actual material exchanges without scraping a student social graph. Explain whether the offer contrast plausibly approximates an isolated effect or reflects a particular allocation environment. Scalar exposure attenuation in the simulation is not a fitted spillover correction.

Qualitative sampling includes refusals, low fidelity and unresolved disagreements in both arms. At least two analysts examine counterexamples and preserve reasoned differences. Quotes require separate permissions and disclosure review. Member reflection checks fairness of an interpretation; it does not require consensus or allow an institution to erase adverse findings.

The ethics and governance process must set burden thresholds before allocation. No validated threshold is invented. Unauthorized disclosure, credible retaliation or coerced identity disclosure prompts immediate safeguarding review and suspension of the implicated activity. Record unequal time, costs and unpaid labor. An average benefit does not excuse a foreseeable harm.

## Executed artificial design calculation

Seed 20261016; 10,000 replicates per scenario; 24, 32 or 40 pairs; outcome ICC .05 or .10; comparison exposure 0 or .25. Every artificial school begins with 40 students. Draw school retention probability p from Beta(6.8,1.2), then retained m from Binomial(40,p), with m = max(m,12). Cohorts therefore stay within 12–40; export achieved mean, CV and limits. Assume baseline/endline correlation .60 at school and individual levels, individual outcome variance 1 and constant unattenuated difference .30 baseline-outcome SD.

For each school, Var(change mean) = 2(1−.60)[ICC + (1−ICC)/m]. Independent conditional Gaussian pair noise has variance equal to the sum of the two school variances; no additional matching benefit is assumed. Assigned difference is .30(1−comparison exposure). Test by a two-sided paired t test at alpha .05. Report power, Monte Carlo SE = sqrt[p(1−p)/10,000], null rejection and achieved retention. No participant outcomes or actual network process are simulated. The calculation omits bounded/non-Gaussian scores, informative attrition, school loss, noninvariance and heterogeneous responses; it does not validate the imputation model.

## Administrative source audit

The executed audit streams all 102,274 directory rows and 11,209,338 membership rows. Full long-cell duplicate checking is explicitly not performed. The Education Unit Total restriction is checked separately for one row per school. Blank and flagged counts remain unavailable; they are never changed to zero. Across all 11,209,338 long membership records, 66,138 student-count cells are blank: 12,421 flagged Missing, 53,567 Not reported and 150 Suppressed. These detailed-cell counts do not mean that 66,138 of the 99,678 selected school totals are missing. The release companion documents these flag categories and counts. No negative numeric value was observed in this release. The selected total can include adult education and does not establish grade-7/8 sample capacity. Source hashes, URLs and verification dates are recorded in source-audit.json. The public package contains aggregate diagnostics and artificial results, not raw administrative archives or participant records.