Effectiveness of an Audiovisual Disaster-Education Intervention on Disaster Risk Perception and Preparedness Belief Among Senior High-School Adolescents (DERAP)

Background. West Kalimantan, including Kubu Raya Regency, is exposed to recurrent seasonal flooding and to land and forest fires with associated haze. Adolescents are rarely the explicit target of preparedness interventions despite being reachable at scale through schools, capable of transmitting preparedness knowledge within households, and themselves vulnerable during emergencies. Audiovisual media engage sight and hearing simultaneously, simplify complex content, and standardize delivery, making a short video a plausible low-cost vehicle for shifting the cognitive precursors of preparedness behavior.

Theoretical framework. The intervention is grounded in the Health Belief Model (HBM). Disaster risk perception corresponds to the upstream perceived-threat component of the HBM, comprising perceived susceptibility and perceived severity. Disaster preparedness belief captures the fuller, more downstream readiness-to-act constellation, combining threat appraisal with perceived benefits, perceived barriers, self-efficacy, and cues to action. Each content block of the video is mapped a priori to a specific HBM construct and to the outcome subscales it is intended to move, which is the content-validity rationale for using one shared intervention to address both co-primary outcomes.

Design. Two-arm, parallel-group, stratified cluster-randomized controlled trial with 1:1 allocation and a superiority framework. The cluster and unit of randomization is the intact class; the unit of analysis is the individual student. Stratification is by grade level (X, XI, XII), so that within each grade an equal number of classes is assigned to each arm. A computer-generated sequence is produced by the study statistician with the seed recorded. Class identifiers without class names are provided to an independent allocation holder who applies the sequence, giving third-party concealed allocation. Within each eligible class a random subsample of twelve students is drawn from the class roster before any class is randomized, and baseline data are collected from all consented students in that subsample before allocation, so that both participant selection and recruitment are complete before assignment is known. Drawing the subsample before allocation is essential, because selecting participants after clusters have been assigned is the principal source of identification and recruitment bias in cluster trials.

Masking. Participants and facilitators cannot be masked because the intervention is overt. Questionnaires are self-administered and identical across arms. The data manager who enters and cleans the data is masked to allocation, and the statistician conducts the primary analysis on an arm-coded dataset. Unmasking occurs only after the primary analysis is locked.

Sample size. Detecting a moderate standardized difference (Cohen d = 0.50) with two-sided alpha 0.05 and 80 percent power requires approximately 63 students per arm under individual randomization. Because the primary analysis adjusts for the baseline score, this requirement is multiplied by (1 minus r squared), where r is the assumed baseline-to-immediate-post correlation, taken as 0.60, giving approximately 40 students per arm. Twelve intact classes are randomized, six per arm, with twelve students randomly sampled and assessed within each class. The resulting design effect is 1 + (12 minus 1) x 0.05 = 1.55, giving approximately 62 evaluable students per arm. Allowing 15 percent attrition to the four-week follow-up gives an enrollment target of 72 students per arm and 144 in total. All students in participating classes view the assigned video; only the randomly drawn subsample completes the questionnaires. Under these assumptions the trial detects a standardized difference of approximately 0.50 at alpha 0.05, or approximately 0.56 under a Bonferroni-adjusted alpha of 0.025 for a joint co-primary claim. If the true intracluster correlation is 0.02, plausible for attitudinal outcomes, the detectable difference falls to approximately 0.45; if it is 0.10, it rises to approximately 0.59. The mediation analysis is powered only for exploratory purposes at this sample size.

Statistical analysis. For each co-primary outcome the primary analysis is a linear mixed-effects model with a random intercept for class and fixed effects for arm, time, and the arm-by-time interaction, adjusting for the baseline score, the stratification factor (grade), and pre-specified confounders (sex, age, prior personal disaster experience, prior exposure to disaster education). The treatment effect is the adjusted between-arm difference at the immediate post-intervention assessment, reported with a 95 percent confidence interval. Because the sample size claims credit for baseline adjustment, the observed baseline-to-post correlation will be reported alongside the primary result, as will the observed intracluster correlation for each outcome. Generalized estimating equations with an exchangeable working correlation are specified as an equivalent alternative. Baseline balance is described rather than significance-tested, following the Consolidated Standards of Reporting Trials (CONSORT) extension for cluster randomized trials. The primary analysis follows the intention-to-treat principle; a per-protocol analysis is secondary. Missing outcome data are handled by multiple imputation under a missing-at-random assumption with complete-case sensitivity analysis. Each co-primary outcome is tested at two-sided alpha 0.05 within its own analysis, and a Bonferroni-adjusted threshold of 0.025 is applied for any combined family-wise claim. The analysis plan is fixed before unmasking.

Fidelity and contamination. Every session is documented on a fidelity log recording that the correct video was played in full and twice, absence of interruptions or substituted content, adherence to the facilitator script, equipment and room conditions, attendance, and any deviation or contaminating event. Contamination within the single school is mitigated by randomizing at class level, separating data-collection days by arm, and scheduling control assessments so they are not preceded by discussion with intervention classes. Residual contamination is expected to bias effects toward the null.

Post-trial provision. After the four-week assessment, control classes are offered the full audiovisual disaster-education intervention.