Schema Therapy for Patients With Chronic Treatment Resistant Depression

Aims of study: The central aim of this study is to investigate whether Schema Therapy (ST) of longer duration (up to 30 sessions) outperforms the current treatment as usual (TAU) for patients with chronic and treatment resistant depression (CTRD) on depression outcomes at 12 months after baseline measurements, as well as at 6 and 24 months time points after baseline. It is hypothesized that the treatment effect in ST is mediated by changes in the psychological phenomenons called modes, namely Healthy Adult Mode and Vulnerable Child Mode, and that treatment effect is moderated by childhood adversity. A second aim is to expand the understanding of what constitutes a successful therapy by investigating relevant secondary outcomes at the same time points. When dealing with chronic and/or treatment resistant illnesses, other success criteria such as level of functioning, personal recovery, or a completely different, patient-generated outcome, might be more obtainable than improvements in illness symptoms alone. Also, it will be investigated whether schema therapy is more advantageous from a health economic aspect, both in terms of quality of life for the patient and from an economical societal perspective. The final aim for the study is to investigate and define the population of patients with CTRD. It will be attempted to refine the Maudsley Staging Model for CTRD by including (failed) psychotherapy trials. As a part of this, it will be investigated whether patients with Treatment Resistant Depression (TRD) and Chronic Depression (CD), respectively, can be adequately understood as exhibiting similar characteristics in symptoms and response to treatments. Background for study: CTRD-patients seem to differ substantially from non-CTRD patients in numerous respects: factors such as adverse events in childhood, higher prevalence of comorbid personality disorders as well as inhibiting personality features, interpersonal behavior and cognitive styles. With this knowledge, ST may be a particularly promising treatment for CTRD, as it targets both childhood adversity and particular inhibiting personality features. Going to the 'root of problems', ST can potentially have a more enduring effect on the presenting symptoms. Also, CTRD responds differently to psychotherapy than non-CTRD with smaller effects and with fewer 'sudden gains' compared to non-chronic depression. Longer duration of treatment also seems to be necessary; a meta-analysis estimated a minimum of 18 sessions necessary to produce convincing results. It is thus likely that a longer duration of ST therapy, as opposed to the shorter TAU, will still be cost-effective due to greater and/or longer-lasting effects. Clinical practice varies widely in Denmark and internationally, and the extent to which these patients are correctly diagnosed, classified, registered and referred to specialized, prolonged CTRD treatment is unknown and probably not reflecting the true prevalence of CTRD-patients. To some extent, staging models encompass the differential features of CTRD, but even the most elaborate and validated, the Maudsley Staging Model (MSM) does not include treatment with psychotherapy as a variable. The addition of former failed psychotherapy trials could possibly improve the predictive value on factors such as dropout, short- and long-term effect of psychotherapy, and effect of differential types of psychotherapy (long duration ST vs TAU). This could provide essential information for treatment selection as well as short- and even long-term prognosis. Study design: This is a multi-center, two-arm, parallel group, assessor-blinded, randomized controlled superiority study. Participants will be allocated 1 : 1 to either 30 sessions of ST or to treatment as usual (TAU) for treating CTRD. Both treatment conditions will include administration of medical treatment as appropriate, following the usual treatment regimes in Danish secondary mental health services. Data will be collected via interview and self-report at baseline prior to randomization, and again at 6, 12 and 24 months after baseline measurements. The treatment will take place at six psychiatric out-patient clinics in the Southern (Odense; Svendborg) and Capital (Copenhagen/Nørrebro, Frederiksberg (2 clinics), Ballerup) regions of Denmark. Schema therapists: The ST-therapists will be recruited on the basis of willingness to and availability for training. 21 therapists will be trained in order to ensure enough available therapists in the case of therapist drop-out from the study. As the risk for dropout of therapists has proven to be high, privately practicing psychologists with schema therapy and prior psychiatric experience will be employed to provide treatment as needed on the sites. All therapists should have degrees within psychology, medicine, physiotherapy, nursing, or social work as well as prior psychotherapeutic experience. After training in ST, the therapists' competency and adherence to the treatment protocol will be evaluated, and therapists performing under the required level of competency will not be providing treatment in the study. This is done by submission of one video recorded therapy session by each therapist with a current patient at the treatment site. This patient is not part of the study intervention group, and no further data is collected on the patient. While the patient in the video will receive some sort of schema therapeutic intervention, this is thought to be within the scope of the treatment that the patient would have otherwise received in treatment at the site. The patient will be asked at the previous therapy session whether they would be willing to be video recorded at the next session for the purpose of the study. A separate information sheet will be distributed for this purpose right before the initiation of recording. Throughout the study, therapists will receive 1,5 hours of monthly supervision in groups of up to 10 therapists. A selection of the therapy sessions for each therapist will be video-recorded and evaluated for adherence by research assistants A (after the conclusion of intake assessments) and B. Concomitant treatment: Psychopharmacological treatment and changes in medicine prescriptions are permitted by the psychiatrists working at the treatment sites, since this is a part of the regular depression treatment in the Danish secondary psychiatric sector. Medication use will be monitored via the electronic journal system. Concomitant psychopharmacological or psychotherapeutic treatment outside of the treatment sites is discouraged, but participants will still be included in the intent-to-treat-analyses. Concomitant treatment will be registered as part of study data. Sample size: Sample size planning is based on previous studies that used the short form of the Hamilton Rating Scale for Depression (HAM-D6) as their primary or secondary outcome. In previous studies, the standard deviation of HAM-D6 scores at end-of-treatment was around 3.5 within the intervention arms . A difference of 2 units on the HAM-D6 (i.e., d=0.57) is considered clinically relevant; this is the difference we would not like to miss in the comparison of the group averages at the 12 month measurement point. On the HAM-D6 scale (range 0…22), 2 units correspond to an improvement on two of the six items (depressed mood, guilt feelings, work and interest, psychomotor retardation, psychic anxiety, general somatic symptoms). At the conventional significance level of α=0.05 two-tailed, a total of N=100 participants need to be randomized to detect the relevant group difference with 80% power. The number of randomized participants should be increased to account for clustering and dropout. The therapy is administered individually (not in groups); therefore, cluster effects are expected to be low (intra-cluster correlation = 0.01), but not zero because several participants are treated by the same therapist. Dropout is assumed to be substantial in this patient population and should be compensated in the sample size calculation even if the main analysis uses imputation of missing data. With a cluster size of around 5 participants per therapist, and accounting for a dropout of approximately 20%, the total sample size should be increased to a total of 129 participants, randomized 1:1 in each intervention arm. Recruitment, participant information and consent: When referred to psychiatric treatment in the Mental Health Services, Capital and Southern Regions of Denmark, all new patients routinely go through a treatment intake interview. At this interview, the site's clinicians will also evaluate the possible participants' eligibility for the study. Interested individuals are then contacted by the research team who will give further verbal and written information about the study by telephone and e-mail. If the participant is still interested and eligible, a minimum of 24 hours is given before the baseline interview to consider whether they would like to participate or not. The baseline assessment interview takes place in a quiet setting, either with physical presence in an office at a research or treatment site, or if preferred by the participant, online on a secure platform. Written informed consent is collected. The participants will be informed that participation is voluntary and that withdrawal from the study is possible at any time without implications for the treatment to which they were referred. The participants do not receive any monetary or other reimbursements, gifts or rewards for their participation. Assignment to interventions, randomization and concealment of treatment allocation: Following screening and baseline assessment, participants will be randomized to either ST or TAU with a 1:1 allocation. The randomization was stratified by depression severity (moderate or severe; HAM-D6) and childhood maltreatment (Childhood Trauma Questionnaire (CTQ), dichotomized) at baseline for the first 14 included patients; however, this was changed to stratification for site for the remainder of included patients. The data management system Redcap (Research Electronic Data Capture), a secure web application for building and managing online surveys and databases, will execute randomization. Adequate allocation concealment is secured by not performing the randomization until after baseline assessment and recruitment into the trial. After randomization, the baseline assessor (Assistant A) will inform the relevant clinic about the treatment allocation. Thus, assistant A will be the only researcher knowledgeable about the results of randomization and will therefore not be involved in the outcome or follow-up assessments. Information from the electronic patient journals: After a participant has agreed to participate in the study, written consent will be obtained from the participant for the research team to be able to access the participant's electronic patient journals in order to obtain information about given psychotherapeutic, psychopharmacological or other psychiatric treatment before or during the trial. This information is used to be able to evaluate the participant's degree of treatment resistance and the extent of given treatment as part of the scientific evaluation in relation to the study's purpose, and further to be able to control and monitor for quality and adherence to treatment. Also, consent will be collected about being contacted in the case of treatment dropout in order to obtain information about the cause of the dropout. Plans to promote participant retention and complete follow-up: As a natural part of psychotherapeutic treatment, study participants who utter doubt as to whether to stay in treatment will be invited by their therapist to a collaborative and motivational inquiry about their doubts. Study participants who are absent from therapy sessions without notice will be contacted for a similar inquiry. At the 6-, 12-, and 24-month time points after baseline measurements, the participants will be contacted by phone, text message and/or secure e-mail and asked to participate in a clinical assessment, where they will also fill out the self-report measures. If necessary, the assessment can take place in the participant's own home. Statistical analyses \[please note that the section on statistical and health economic analyses was copied from the Statistical Analysis plan which was published before the data collection had finished. Reference: Arendt, IM.T.P., Gondan, M., Juul, S. et al. Statistical analysis plan for a parallel group randomized clinical trial comparing schema therapy versus treatment as usual for outpatients with difficult-to-treat depression (DEPRE-ST). Trials 26, 334 (2025). https://doi.org/10.1186/s13063-025-09012-4) All analyses will be done by data analysists who are blinded to treatment condition of the two groups, that is, treatment arms will be labelled "Treatment A" and "Treatment B." Two different abstracts for the outcome article with opposing results of the two treatments and resulting conclusions will be written before unbreaking the blind, as described in the study protocol. Interim analyses Interim analyses are planned to take place when 50% of the 6-month follow-up data have been collected. An external data safety monitoring committee (DSMC) with no allegiance to the trialists will perform the interim analyses and decide whether to stop or continue the trial based on convincing benefit or harm of the interventions. The DSMC will receive blinded data but can be unblinded upon request. Focus will be on data from the 6-month follow-up regarding serious adverse events, significant differences between groups on the primary outcome, and serious deterioration on the primary outcome. The following statistical analyses are proposed, but the DSMC can perform other analyses and require more data if deemed necessary: Inferiority: A t-test for independent groups will be used to test for differences between study arms. If this test is significant at the one-tailed 2.5% and indicates that ST is inferior, the DSMC will reassess the costs and benefits of the trial and consider early stopping. Serious adverse events: A chi-square test will be used to test for differences between groups in the number of participants with one or more serious adverse events (emergency room visits for somatic or psychiatric reasons, documented suicide attempts or self-harm). If this test is significant at the one-tailed 2.5% and indicates a substantial increase in adverse events under schema therapy, the DSMC will reassess the costs and benefits of the trial and consider early stopping. In case of low event counts, Barnard's test will be used to avoid poor asymptotic behavior of the chi-square test. Serious deterioration: A chi-square test will be used to test for differences between groups in the number of participants with an increase of 2 or more points on the primary outcome (HAMD-6). If this test is significant at the one-tailed 2.5% and indicates serious deterioration under schema therapy, the DSMC will reassess the costs and benefits of the trial and consider early stopping. In case of low event counts, Barnard's test will be used to avoid poor asymptotic behavior of the chi-square test. All interim analyses will be performed on the available data without imputation of missing data. An adjustment of the significance level is not needed, since a stop for efficacy is not planned. Primary analysis The primary analysis will be based on the intention-to-treat principle (i.e., including all randomized patients who will be analyzed according to their initial randomization, regardless of the actual treatment received), using conservative, multiple imputation of missing outcomes by jump to reference. The effect of the treatment will be presented as the covariate-adjusted difference between the average change scores in the two arms, with its two-tailed 95% confidence interval. In other words, superiority of ST will be claimed if the change in ST is significantly better than the change in TAU, at a two-tailed significance level of 5%. Analyses will be performed when all 12-month assessments have been completed. The HAMD-6 score is assumed to be an interval-scaled variable, with normally distributed residuals. The therapies will be compared using a multilevel linear regression with therapy (ST vs. TAU) as the main effect, adjusted for treatment site (categorical, 6 levels) and the HAMD-6 score at baseline as covariates, and therapist as a random intercept. Efficacy of ST vs. TAU will be expressed by the covariate-adjusted difference between the change scores of the experimental versus the control intervention, along with its two-tailed 95% confidence interval. Superiority of ST will be claimed if this confidence interval is above zero. After adjustment for baseline severity, this estimate is numerically identical to the comparison of the raw scores between the treatment arms at end-of-therapy. Secondary outcomes will be analyzed in the same way, with the same 95% confidence intervals. If the respective endpoint is not available in the baseline assessment by design (e.g., NEQ), the baseline HAMD-6 will be used as a baseline covariate, and effect estimates will be based on raw scores instead of change scores. Missing outcomes will be multiply imputed by a 'jump to the reference treatment,' that is, we assume that patients with missing data in ST score similar to patients in TAU. This analysis method is implemented in the R package RefBasedMI. Box 1 in the study's Statistical analysis plan (Additional file 3) shows the R code for the analysis using RefBasedMI's own example data. Secondary outcomes will be analyzed in the same manner. Sensitivity analyses To assess the impact of the imputation procedure, we will run a number of sensitivity analyses for the primary outcome: A first sensitivity analysis will be based under the usual assumption of missingness-at-random. This supersedes the initially planned regression imputation with dropout status and secondary outcomes in the imputation model. The reason for this change of strategy is that primary and secondary outcomes are collected at the same session. Therefore, practically speaking, missing data in secondary outcomes co-occur with gaps in the primary outcome, so imputation by secondary outcomes will not help much-it will mostly mirror the results of the analysis with available cases. A second sensitivity analysis will be carried out for the subset of per-protocol participants with available outcome data, without imputation of missing outcomes. Further sensitivity analyses will be made with best-best and worst-worst case imputation of missing outcomes, and without adjustment for covariates. To rule out bias due to ceiling or floor effects in the outcome, a final sensitivity analysis will be carried out using negative binomial regression, with HAMD-6 treated as count data (i.e., a score of 10 points will be counted as ten "events"). Results of this analysis will be presented as rate ratios for therapy type, adjusted for baseline severity and treatment site. Subgroup analyses Subgroup analyses are performed with the purpose of assessing homogeneity of the treatment effects and further to reveal potentially harmful effects in specific subpopulations of patients. Subgroup effects will be investigated by adding treatment-by-covariate interactions to the primary analysis model and by illustrating the subgroup-specific therapy effects in forest plots (see the Statistical Analysis Plan, Box 4, Additional file 3, for example code). Patients with childhood adversity and corresponding early maladaptive schema may benefit more from ST than patients with less severe adverse experiences in childhood. This will be analyzed by adding the interaction of therapy x adversity (CTQ, dichotomized as present/not present of moderate to severe childhood adversity on one or more of the five domains: physical, emotional or sexual abuse, emotional or psychical neglect, with cutoffs as suggested by Bernstein et al.) to the statistical model of the primary analysis, and by estimating stratum-specific therapy effects in participants with and without adversity experiences. Further, we will explore therapy x site interactions, as recommended in the International Conference on Harmonisation E9 guideline. Additional subgroup analyses will be made for depression symptoms at baseline, sex (male, female), and psychiatric comorbidities as measured in the M.I.N.I. interview (present; not present). It is understood that such subgroup analyses are exploratory, subject to lack of statistical power and, at the same time, multiple testing issues. Any observed subgroup effect will be interpreted in the light of its psychological plausibility, weighed against statistical artifacts such as regression to the mean (e.g., treatment x severity interactions). Observed effects in the primary outcome will be compared to the corresponding results in the relevant secondary outcomes. Health economic analysis The health economic analysis investigates the health-related quality of life as measured on the EQ-5D-5L and has its primary timepoint at 24 months after randomization. The EQ-5D-5L instrument includes five dimensions (mobility, self-care, usual activities, pain/discomfort, and anxiety/depression), each with five levels of severity. EQ-5D-5L responses will be converted into Quality-Adjusted Life Years (QALYs) using Danish utility weights. Cost data will include direct health care costs and lost productivity costs. Direct health care costs will include costs of primary and secondary health care services and prescription medication. Unit costs of General Practitioner services and other medical specialists will be based on the prevailing National Health Insurance fee schedules. Direct costs, including in-patient and out-patient health care costs, will be calculated using Diagnostic Related Groups (DRG) weights and specific out-patient tariffs. These cost estimates are all based on data from the Danish Ministry of Health and reflect the average cost of treating patients with similar conditions in a Danish hospital. The participants' use of prescription medication and information on retail price on each transaction will be derived from the Register of Medical Product Statistics. Lost productivity costs defined as difference in earned income between the groups and data on transfer payments will be derived from The Danish National Labour Market Authority's DREAM database \[52\]. The incremental cost-effectiveness ratio (ICER) will be estimating the difference between intervention and control group in QALYs/costs. Non-parametric bootstrapping will be used to estimate confidence intervals for the ICER. Results will be presented in the cost-effectiveness plane, and a cost-effectiveness acceptability curve will illustrate the probability that the intervention is cost-effective compared to an alternative, given different values of willingness to pay for a unit of health benefit. Harms and adverse event: The election of ST was made under the hypothesis that ST will be of particular benefit to CRTD-patients. The treatment itself is not expected to have serious side effects, however, psychotherapy as well as the intake interview, and/or the filling out of questionnaires can induce temporary emotional stress when uncovering or with dense emotional issues. If deterioration in the participant's mental health occurs during the course of the study, this will be naturally addressed with the participant's therapist. If it happens momentarily in the intake session, the research assistants, who will also have a Master's degree in Psychology, will be handling this appropriately after training and under supervision by the project manager, an authorized psychologist. Adverse events such as suicidal attempts, admittance to a psychiatric ward, or substantial self-harm are already routinely reported and addressed systematically with appropriate measures in the psychiatric secondary care system. Such events will therefore be recorded as part of the study. Finally, the Negative Effects Questionnaire as a part of the secondary outcomes will address adverse events more broadly to qualify which events are potential harms of treatment and which are unrelated to treatment. Further, as recommended by the European Medicines Agency, subgroup analyses to detect symptom deterioration will be performed, even in the case of no statistically significant difference between treatments. This is to ensure that any subgroup with a differential negative effect of treatment is detected in order to provide contraindications towards a particular treatment for certain participants. Pilot study: Prior to the commencement of the trial, a pilot study, N=4, will be performed to evaluate outcome measures' relevance and applicability, the procedure for inclusion of participants, including an evaluation of participant flow, and the therapist training program and implementation across treatment sites. The pilot will inform the large-scale study and allow for smaller adjustments to ensure a smooth inclusion and treatment phase and the following of the time schedule. The participants in the pilot study will all receive TAU after the intake interview. Data from the participants in the pilot study will not be included in the full-scale data analysis. Planned publications: A total of 5 articles are planned for the study; articles 1-3 during the PhD, and articles 4-5 during the post doc-period. 1. Schema therapy for chronic, treatment resistant depression - study protocol of a randomized controlled trial 2. Systematic review of schema therapy for mental disorders - reviewing the current evidence base 3. A randomized controlled superiority study of prolonged schema therapy vs TAU for chronic treatment resistant depression - symptoms, functioning and patient-generated treatment goals 4. Follow-up of a randomized controlled study of schema therapy vs TAU for chronic treatment resistant depression. 5. Chronicity and treatment resistance in patients with depression. Proposition for a predictive staging model including psychotherapeutic treatment.