The original design aimed to enroll 180 female-identifying individuals, aged 18 to 65 years, who reported experiencing a sexual assault between 4 weeks and 1 year prior to enrollment, and were above thresholds for PTSD and alcohol misuse (see Textbox 1 for inclusion/exclusion criteria). Sexual assault was defined as any experience of unwanted sexual contact, such as attempted or completed sexual touching or rape (eg, oral, anal, or vaginal penetration [1]). The original start date for enrollment was April 2020, but the COVID-19 pandemic delayed recruitment until March 2021.

Participants were recruited using (1) referrals from clinics, community providers, and emergency rooms; (2) advertisements in newspapers, online classifieds, and on social media; (3) flyers and brochures in local venues (eg, coffee shops and community centers); and (4) emails to enrolled university students. Recruitment originally focused on Western Washington. When the study launched online, recruitment extended across Washington State. Due to slower-than-anticipated recruitment, we began recruitment in California in February 2024 using the same strategies. Recruitment remained slow, however, resulting in a smaller sample than intended.

Demographics (eg, age, sexual orientation, race, ethnicity, education, and treatment history) are assessed via interview. The Trauma History Questionnaire [49] assesses lifetime trauma exposure. Both treatment and trauma exposure are reassessed at the 6-month follow-up.

The primary outcome measures are as follows:

During the 2 active intervention phases (phase 1: 3 weeks; phase 2: 3 weeks), participants are administered weekly measures of PTSD and alcohol use. Participants complete the measures online. Weekly self-reports of PTSD symptoms and drinking are included as primary outcomes as follows:

The behavioral tasks used in this study were adapted for online administration.

Participants are screened on the phone for potential eligibility. Individuals reporting sexual assault, PTSD symptoms, and alcohol use are scheduled for a 2 to 3-hour intake with an assessor over Zoom. Informed consent is obtained and semistructured interviews are administered. Intake assessments are presented to the clinical team (ie, assessors and clinicians) to determine final eligibility.

At randomization appointments, behavioral tasks are administered and self-report surveys are completed via Qualtrics. Participants remain on video for the duration of the appointment with the study coordinator, who is available for questions and monitors engagement. Next, the coordinator uses a custom-built randomization program to assign participants to their initial intervention condition (1:1:1 for IE, AST, or SC). Two stratification variables are used: PTSD severity (PSS-I-5 total ≥36 vs<36) and alcohol use severity (≥6 vs<6 drinking days in the past 2 weeks) to ensure representation of severity across conditions. The randomization algorithm adjusts probabilities based on prior assignments to ensure a similar number of participants in each condition. Assessors stay masked to condition assignments throughout the study.

Participants assigned to IE or AST complete 6 sessions across 3 weeks (phase 1), followed by rerandomization at 1-month postintake to the other active intervention or no additional intervention (phase 2). The second randomization occurs for all participants in the IE and AST conditions, regardless of whether they complete phase 1 intervention sessions or the 1-month postintake assessment. For the second randomization, participants have a 0.5 probability of assignment to the other intervention. Those assigned to the other intervention receive 6 sessions across 3 weeks with a new therapist. Participants assigned to SC complete 6 sessions across 3 weeks (phase 1) and then an additional 6 sessions across 3 weeks (phase 2) with the same therapist. Across both phases, participants complete weekly online self-report surveys assessing alcohol use, PTSD, depression, and fear and reward processes (ie, before intervention sessions 1, 3, and 5; once per week for those assigned to no intervention in phase 2). These weekly assessments are used to model symptom change and monitor treatment progress.

At 1 month, 2 months, and 6 months following randomization, participants meet with the same assessor from intake and complete interviews and online self-report questionnaires. Again, a study coordinator is present during the appointments. At the 6-month follow-up, participants are offered referrals if indicated, and SC participants can choose to receive IE or AST if they lack a meaningful response (defined as PTSD or alcohol use above study-entry criteria thresholds on structured interviews).

The project uses participant tracking, regular contacts, and incentives. Total possible compensation is US $277. This includes US $50 for intake, US $20 for the randomization visit, US $7 for rewards associated with the PRT, US $30 for the 1-month and 2-month follow-ups, US $10 per weekly self-report, a US $15 bonus for completing all weekly self-reports during either phase, and US $50 for the 6-month follow-up.

Assessors are trained to an 80% reliability standard. Interviews are audio recorded and interviewers use semistructured interviews to record their judgment of patient responses. After training, 10% of interviews are randomly selected to assess interrater reliability for PTSD (using PSS-I-5) and depression (using Quick Inventory of Depressive Symptomatology–Clinician Rated) severity, suicidality (using Columbia Suicide Severity Rating Scale), and comorbid diagnoses (using Structured Clinical Interview for DSM-5).

The IE protocol consists of six 50-minute manualized telehealth sessions delivered twice-weekly over 3 weeks. IE is based on the prolonged exposure manual [22] and includes psychoeducation, repeated imaginal exposure to the trauma memory, processing of the exposure and memory content, and consolidation of new learning. IE does not include in vivo exposure or homework. During IE, the client recounts the memory of the sexual assault, with the therapist probing for the client’s distress ratings approximately every 5 minutes. Processing includes praise, inquiries about the client’s experience, reflections on revisiting the trauma memory, and promoting adaptive meaning-making. This brief IE intervention has shown previous efficacy [23,53].

The AST protocol [] (MA Bedard-Gilligan et al, unpublished data, 2020) consists of six 50-minute manualized telehealth sessions delivered twice-weekly over 3 weeks. AST is based on brief cognitive behavioral programs commonly used in alcohol treatment [54,55]. “At-home-practice” with accompanying worksheets is included. AST addresses reward deficits. It focuses on increasing alcohol-free rewarding activities and learning tools to address barriers and increase support around rewarding activities. Increasing alternative rewarding activities is presented as an approach to reducing the negative effects of drinking by finding more adaptive ways to experience rewards in life.

SC consists of 12 20-minute phone sessions delivered twice-weekly for 6 weeks (MA Bedard-Gilligan and LA Zoellner, unpublished data, 2020). SC is a semistructured active control therapy and has demonstrated symptom reductions for trauma survivors [56]. The intervention combines psychoeducation, self-monitoring, directed writing outside sessions (ie, ~20 minutes about nontrauma-related stressors twice-weekly), and support. Sessions are not trauma-focused or alcohol-focused. Therapists are nondirective, ask open-ended questions, and provide validation. If the patient discloses assault-related or drinking-related stressors, the therapist uses supportive strategies, but does not instigate conversations about PTSD, assault, or alcohol use, and does not engage in any formal cognitive restructuring, exposure, or alcohol change strategies (eg, motivational interviewing).

As a first step in our analyses, we will calculate descriptive information on demographic characteristics, index traumatic event (ie, recent sexual assault), and trauma and treatment history by condition. We will also calculate means and standard deviations for all primary outcomes by condition and time point and calculate the prevalence of a 20% reduction in primary outcome measures at 1-month, 2-month, and 6-month follow-up. This descriptive information will be included in our outcome papers, making for straightforward use of study results in meta-analyses.

We will assess differences in completion rates for the 1-month, 2-month, and 6-month follow-up assessments using chi-square tests for contingency tables. Assessment of condition differences in completion of weekly self-report assessments will involve comparing the number of assessments completed and common patterns of attrition (eg, completion of all assessments, early dropout, late dropout, and intermittent missed assessments). Modeling of condition differences will use maximum likelihood estimation, with variances and covariances of model covariates estimated, or multiple imputation so that participants with partial data (eg, missed follow-ups) will be included with the assumption that data are missing at random (MAR) after accounting for nonmissing covariates [58]. This approach will reduce bias in model estimates due to missingness associated with condition assignment, baseline measures of PTSD symptom severity, alcohol use, and time since the traumatic event. We will also use pattern-mixture modeling to assess whether estimates of condition differences vary across different patterns of missingness and there is evidence of the MAR assumption not holding [59].

The study involves 3 conditions in phase 1 and 5 conditions in phase 2, and the aims call for multiple-condition comparisons at multiple time points on multiple outcomes. This can potentially lead to inflated type I errors when using a statistical significance criterion of P<.05. Although we will report P values, our primary guard against type I errors will be to present clear information on effect sizes and uncertainty of estimates. Condition differences will be expressed (1) on the metric of continuous outcomes and as standardized effects (d), (2) as percentage differences in counts for count outcomes, and (3) as prevalence differences for dichotomous outcomes. Estimates of uncertainty will be shown as confidence intervals. Another guard against overinterpreting chance findings will be to present condition differences in terms of a hierarchy of more general contrasts (eg, any assignments involving IE or AST vs SC) before considering more specific contrasts (eg, IE->AST vs AST->IE). In other words, the findings regarding more specific contrasts between any 2 of 5 conditions after phase 2 will be presented within the context of broader contrasts.

Analyses will follow an intent-to-treat (ITT) approach, based on data from all randomized participants, regardless of treatment completion. Analyses will provide estimates of condition differences at follow-up time points, adjusted for covariates, with the representation of uncertainty in these estimates provided by confidence intervals. At each follow-up assessment, the primary assessment of condition differences in PTSD severity (ie, PSS-I-5) and alcohol use (ie, TLFB) will be assessed with regression models that control for preintervention baseline PSSI-5-I scale score, baseline TLFB measure of past-month drinking days, and months since assault. Assessing condition differences at each of the 3 follow-up time points addresses analytically different questions, with differences at 1-month and 2-month follow-ups capturing immediate postintervention effects on PTSD symptom severity and alcohol use and differences at 6-month follow-up showing whether differences are maintained multiple months after completing the intervention phase. Assessing differences controlling for baseline provides more precise estimates of condition differences than using change scores [60]. For models with average drinks consumed on drinking days as the outcome, intake scores on that measure will also be included as a covariate. Estimated effects of indicator-coded condition assignment will be used to assess condition differences [61].

At 1-month follow-up, we will address aim 1 with contrasts between (1) both IE and AST and SC and (2) IE and AST. At 2-month and 6-month follow-ups, we will examine contrasts between all conditions involving IE or AST (alone or in combination) and SC. We will address Aim 2 by contrasting (1) IE alone or AST alone with conditions involving both IE and AST and (2) conditions involving both IE and AST, comparing by which intervention is first.

Additionally, as an illustration of condition differences, we will use multilevel growth models [62] to compare conditions involving IE or AST with SC in terms of change across the 4 time points (aim 1). Spline models will include two specifications of time to represent (1) change across the active intervention period between baseline and 2-month follow-up, when the conditions involving IE and AST are hypothesized to improve relative to SC; and (2) change between 2-month and 6-month follow-ups, when improvements that occurred during the active intervention are hypothesized to be maintained. Results will be shown graphically in terms of marginal expected values by condition and time point, adjusting for model covariates. PTSD severity and average drinks consumed on drinking days are expected to have approximately normal distributions, and linear models will be used. Condition effect estimates from linear models have a straightforward interpretation as differences on the metric of the dependent variable. We will also calculate standardized effects (d) based on the unstandardized effect estimates divided by the baseline SD of the given outcome. Generalized linear models with a negative binomial distributional specification will be used for the count measure of drinking days. Effects for drinking days will be expressed as count ratios, interpretable as the percentage difference in drinking days associated with the condition [63]. For growth models, marginal estimates will provide model-expected values of outcomes at each time point by condition adjusted for covariates.

We will use multilevel growth models to analyze data from weekly self-administered measures of PTSD, drinking, alcohol cravings, and fear and reward collected through the 2-month follow-up. This will involve 9 time points of data: baseline followed by 6 weekly assessments and 2 follow-ups. The models will include specifications of time to represent the weekly rate of change between baseline and 1-month follow-up (phase 1), followed by the rate of change between the 1-month and 2-month postbaseline follow-ups (phase 2). A similar hierarchy of contrasts will be assessed, with IE and AST vs SC being of primary interest in differences in change in phase 1 and conditions in either IE or AST vs SC being of interest in phase 2.

Exploratory analyses addressing aim 3 will examine recovery and intervention effects based on baseline performance on fear (ie, AX+/BX–) and reward (ie, PRT) tasks and time since assault. Each of these variables will be added to the regression models described in the Aim 1 and Aim 2: Condition Differences at 1-Month, 2-Month, and 6-Month Follow-Ups section, first to assess main effects on recovery (ie, as reflected in decrease in PTSD symptoms and alcohol use) and second, to assess condition differences at different levels of these potential moderators. Estimates of intervention effects across scores on the fear and reward tasks and at different lengths of time since assault will be generated from models with interaction terms (ie, condition by moderators).

Based on findings from prior clinical trials [64], we expected medium-to-large intervention effects. Accordingly, the design called for a total sample size of 180. Primary power analyses were based on ANOVA models using the power calculator in Stata 15.0 (StataCorp LLC). Accounting for 25% attrition between baseline and follow-up, an enrolled sample of 180 provides 0.8 power with an α of .05 to detect a d of 0.6 for differences between any 2 of the initial 3 conditions (ie, aim 1 hypotheses). For aim 2 analyses, where some condition-defined contrasts involve groups half the size of the initial groups (eg, IE or AST only), contrasts between these smaller groups have 0.8 power to detect a d of 0.86. Precision of estimates will be increased by including baseline scores of outcomes as covariates and estimation that allows for the inclusion of cases with partial data.