Symptoms of depression and anxiety will be the primary endpoints because of their high self-reported prevalence of up to 42% in refugee populations and therefore their high relevance to participants (7, 8). The intervention START NOW also aims to improve emotion regulation, mindfulness and interpersonal effectiveness, which are effective skills in decreasing symptoms of depression and anxiety (20–22).

Secondary endpoints include perceived stress, social-ecological resilience, and facial emotion recognition.

We chose perceived stress as a secondary endpoint because of the many pre-, peri- and post-migration stressors that are risk factors for refugees’ mental health. These risk factors could be better managed since the intervention START NOW aims at improving distress tolerance (22). Adding to that, perceived stress has been found to mediate effects of protective resilience factors such as self-esteem on depression (23).

We included social-ecological resilience as another secondary endpoint because it has often been used to assess the effectiveness of interventions in pre-post and longitudinal designs (e.g., (24)).

We chose the secondary endpoint of facial emotion recognition (ER) because performance on measures of emotion recognition is a first step in emotion regulation (25). Consistent with the content and goals of CBTs, certain types of biases in ER that are associated with depressive symptoms, such as labeling emotionally neutral stimuli as negatively valenced, can be reduced following the START NOW intervention (26, 27).

Based on our primary and secondary endpoints, we have formulated the following hypotheses.

Additionally, besides investigating the intervention’s effectiveness, we aim to examine potential mediators to uncover the mechanisms of action (28). Specifically, we hypothesize:

The study is a confirmatory, randomized controlled trial with two arms that takes place in a monocentric, national setting and assesses effectiveness.

To evaluate feasibility, qualitative semi-structured interviews will be conducted with specialists working with refugees prior to the intervention study. These interviews will follow an inductive and explorative approach and involve staff from institutions such as asylum centers and dormitories for unaccompanied minors. To estimate the feasibility and effectiveness of this trial, specialists will be interviewed about their daily challenges, language and cultural barriers, as well as potential difficulties with the implementation and adaptation of START NOW. The inclusion of qualitative information can help to better understand how a complex intervention such as START NOW can work and aid in the adaptation process of the intervention (31).

After the conduction of these interviews, possible participants taking part in the intervention study are screened for eligibility. For those who are eligible, the study duration will be 6 months, including three assessments (shown in Figure 1): a baseline assessment (t1), a post-treatment assessment (t2), and a 12-weeks follow-up assessment (t3). In case a participant has missed a session, they will be marked as absent and the number of sessions will be taken into consideration in the data analysis. To minimize bias, participants will be randomly assigned to one of two experimental group conditions, (1) group skills training using an adapted version of START NOW, (2) TAU. Randomization should take place within 2 weeks before the intervention, after the baseline assessment (t1) has been conducted. Between t1 and t2, the intervention phase takes place over a period of 10 weeks, with one session per week for each group. The study takes place in a group setting since conducting mental health interventions via group workshops, which aim to enhance social interaction was observed to have a positive impact on participants’ mental health (19). For ethical reasons and to increase study-related commitment, participants in the control group (receiving TAU) as well as non-eligible participants will be offered the chance to receive treatment after the study concludes.

The overall study duration will be 2 years, starting in March 2024 with recruitment and ending in March 2026. In collaboration with the Department of Economic, Social and Environmental Affairs of Basel-Stadt, the study team will recruit participants from social welfare, migration + integration and inpatient counseling facilities, such as residential homes for unaccompanied minors, as well as associated organizations such as the Center for Social Pedagogy and Psychotherapy in Basel. At this point, institutions will also be asked if some of their staff are willing to participate in qualitative semi-structured feasibility interviews before the start of the intervention study. In addition, we will contact associated networks for young people with a migration background, such as leisure activities or clubs and other institutions in Basel-Land. The relevant institutions and networks will be informed about the study by email or by telephone. Interested institutions will be given flyers and interested young people will be referred to our team.

On site or during a video call, the investigators (study team members) will explain to each participant the nature of the study, its purpose, the procedures involved, the expected duration, the potential risks and benefits, and any inconvenience that may be involved. Each participant will be informed that participation in the study is voluntary, that he or she may withdraw from the study at any time, and that withdrawal of consent will not affect subsequent medical care and treatment. If necessary, a translator (professional translator or bilingual native speaker from the institution staff) will also be present. All participants in the study will receive a participant information sheet and a consent form describing the study and providing sufficient information in the native language of the participants so they can make an informed decision about their participation in the study. The participant will be given 1 week to decide whether to participate. The formal consent of a participant, using the approved consent form, will be obtained before the participant is submitted to any study procedure. The consent form will be signed by the participant, sent with a prepaid envelope and dated upon arrival by the investigator or his designee. The date of receipt of the consent form is the date of inclusion for participation in the study. A copy of the signed informed consent will be given to the study participant. The consent form will be retained as part of the study records. The informed consent process will be documented and any discrepancies in the process described in the protocol will be explained.

After informed consent has been given, participants will be screened for eligibility. Any participants can withdraw from the study at any time without personal disadvantages and without having to give a reason. The applicants can also decide about termination of treatment in case of protocol violations or if the applicants believe continuation in the study would be detrimental to the participants` well-being. If participants withdraw their participation prior to randomization, other eligible individuals can move up. Premature withdrawals in the group training will not be replaced after the beginning of the intervention. Relevant additional treatments (e.g., individual psychotherapy) administered to the participant upon entry to the trial or at any time during trial participation are regarded as concomitant treatments and will be documented as well as concomitant medication.

After the screening process, eligible persons will be notified by the project management through their institution about their participation opportunity. If someone is not eligible, both the institution as well as the individual will be notified online via mail. If eligible participants still wish to take part, they are randomly assigned to a group. In general, randomization will be done within each institution by randomly assigning participants to either the intervention or control group using computer algorithms. If not enough adolescents within an institution wish to participate, we will make an adjustment to the general randomization process by creating cross-institutional groups. Participants will be randomized in separate steps for each gender group. In this way, we ensure a random distribution between the intervention and control groups within each gender group and a safe environment for all participants. This is in tune with cultural norms and expectations of the target population, and this way, our results are more likely to provide important insights around cultural idioms of distress that may be gender specific (32).

The study population consists of adolescent refugees between the ages of 15 and 18 who are temporarily or permanently resettled in Switzerland and have given informed consent. In November 2023, the majority of new arrivals to the asylum procedure in Switzerland were from the following countries: Ukraine, Turkey, Afghanistan and Algeria (33). For this reason, our participants will presumably consist of homogeneous groups from these nations, as groups with the same migration background show greater intervention effectiveness than groups with different migration backgrounds (34).

The design of our study has been developed considering the conditions of regular clinical practice and focusing on outcomes crucial for making clinical decisions. In this context, the eligibility criteria enable the source population to represent diverse characteristics of external populations, accounting for comorbidities and varying compliance rates (35).

According to this study population, study inclusion criteria include:

Study exclusion criteria include:

We included underage participants since there is a lack of culturally adapted, low-threshold interventions targeting this demographic, notwithstanding the fact that approximately 50 % of all psychiatric disorders manifest in individuals at the age of 14 (39). Symptoms showing that a participant is unwilling to participate in the study will result in the participant being excluded from participation.

An overview of all study measures can be found in Table 1. All questionnaires will be employed online via REDcap. They will be used in German, English, Turkish, Persian, Ukrainian and Arabic. Questionnaires that are not yet available in these languages will be translated using the Multiple-Forward-Approach.

The sample size is estimated based on a power analysis for repeated measures ANOVA including within-between interaction with 3 measuring time-points (t1, t2 and t3) and 2*2 groups (intervention vs. TAU, female vs. male). Standard parameters are set at alpha = 0.05, power = 0.95, and a clinically meaningful medium effect size f = 0.25. Considering an attrition rate of 30% (59), the total number of participants should be 80, with approximately 40 participants in the treatment (treatment groups of 5 to 10 participants each) and 40 participants in the control group.

For statistical analyses, we will use R with its graphical user interface R Studio. The significance level will be 0.05 for all analyses. An effect of at least moderate size will be considered as clinically relevant. To test our hypotheses, we will use multilevel models with primary and secondary outcome measures as dependent variables (three individual models for depression, perceived stress, and emotion recognition), and with timepoint (baseline, post-treatment, follow-up) and intervention condition (START NOW vs. TAU) including their interaction as independent variables. A significant interaction between intervention condition and time suggests a difference in symptom change depending on treatment group. In case of significant main or interaction effects, we will evaluate post-hoc contrast considering time and intervention condition. Treatment group will be added as level two in the multilevel framework.

Using multilevel models will allow to analyze data on the observational level, which provides more information in contrast to calculating change scores or using repeated measures ANOVA, increasing measurement accuracy and power. In addition, multilevel mixed models can handle missing observations and allow to examine random effects at the intercept and slope level. Furthermore, we will test model improvement when considering quadratic versus linear trends for time, random effects for time, and correlation structure between timepoints. Covariates, including participant age, gender, and post-migration stress will be added if they differ between intervention groups. On group level, possible covariates include facilitator, institution or cultural background.

To analyze perceived stress and resilience as potential mechanisms in treatment success, we will use bias-corrected bootstrap mediation models with intervention condition as predictor, change in symptoms of depression as outcome, and change in stress/resilience as mediator. Change in symptoms of depression and indicators of stress/resilience will consist of participant’s random slope for time extracted from the multilevel mixed models depending on results of the first hypothesis.

The qualitative interviews will apply an inductive approach and follow empirical guidelines as suggested by Mayring (60). The aim is to conduct an estimate of five to eight interviews across different institutions, each of around 30 min in length. After recording (audio), the interviews will be transcribed and the audio files will be destroyed. Pertaining to the inductive categorization, evaluation and illustration of the qualitative data, MAXQDA will be employed (61).

This study protocol presents a randomized controlled trial testing the effectiveness of a culturally adapted version of START NOW in reducing mental health problems in refugees. To date, there is a significant lack of RCTs investigating the effectiveness of culturally adapted interventions for adolescent refugees (19). Consequently, the present study considers the need to create an intervention method that combines different theoretical rationales while addressing core problems of adolescent refugees and applying culturally adapted strategies and materials. Our population of interest addresses the fact that ethnic minorities are generally underrepresented in clinical trials in high-income countries (62).

The strengths of this study also include the highly ecological validity as it measures the extent of beneficial effects within real-world conditions (63). Our study design also adapts to the need of implementing and evaluating interventions within the community where clients reside (64). This is of major relevance for staff workers dealing with adolescent refugees since it saves time and cost. Thus, the implementation of evidence-based interventions within institutions is needed to strengthen the chance of continuous care and diminish the stigma associated with mental health services (65). Therefore, the findings of this study will be highly relevant to refugee health care and are intended to stimulate further discussion on how to improve, if not directly increase, the quality of care for adolescent refugees.

One of the challenges of this project may be self-selection bias if certain refugees are more likely to volunteer for the intervention. This could affect the generalizability of the results to the wider refugee population. To reduce this bias, we offer high, but still appropriate, incentives of 20 CHF in vouchers for each assessment (t1 – t3). There also may be differences in the delivery of the intervention or usual care between facilitators. To counteract this bias, all facilitators receive extensive pre-training that provides the same content to all. Additionally, facilitators will be included as possible influences at level two in the multilevel framework.

Another limitation is the lack of blinding among participants and facilitators, a frequent cause of bias in RCTs that include non-pharmacological interventions. Known problems associated with lack of patient blinding, such as response bias with self-reported outcomes, relate primarily to studies with a predominantly explanatory aim (66). For instance, attrition rates may be simultaneously regarded as both sources of bias and outcomes influenced by the intervention (66). It is therefore important to understand and address the reasons for dropout. In multilevel models, a sub-model accounts for missing data. The selection model improves the analysis of growth curves by using logistic regressions to show how likely it is to have missing data at each time. Meanwhile, the pattern mixture approach looks at each group of missing data separately and then combines the results (67). Thereby, multilevel modeling makes use of all available information without needing to resort to list wise deletion. Another method of minimizing bias is that only well-validated questionnaires will be used during assessments.

Promotion and initial recruitment of participants: March 2024.

First baseline assessment: August 2024.

Last follow-up assessment: March 2026.

Publication of results: December 2026.