Transdiagnostic efficacy of a group exercise intervention for outpatients with heterogenous psychiatric disorders: a randomized controlled trial

The study was conducted at the University of Tuebingen. Active enrollment lasted from April 2018 to October 2019. The study was registered on ClinicalTrials.gov (ID: NCT03542396, 25/04/2018) and approved by the local ethics committee for psychological research (Az_Wolf_2018_0108_99). A block-randomized (allocation ratio 1:1) parallel trial with two treatment arms (intervention group, control group) and three measurement points (pre-, intermediate-, post-treatment assessment) was conducted. Primary outcomes were assessed at pre- and post-treatment assessment; secondary outcome at pre-, intermediate- and post-treatment assessment. The study was reported according to the Consolidated Standards of Reporting Trials (CONSORT) statement [51].

Recruiting was performed at the outpatient clinic of the University of Tuebingen, medical and psychotherapist’s offices, and by media advertising. Inclusion criteria were age between 18 and 65 years, fluent in German, no medical contraindications for exercise (participants needed to receive a medical consultation prior to the intervention that confirmed participant’s ability to exercise), on a waiting-list for outpatient psychotherapy and diagnosed according to DSM-IV-TR with at least one of the following disorders: depressive disorders (F32, F33, F34.1), anxiety disorders (F40.0, F40.1, F40.2, F41.0, F41.1, F41.2, F42, F43.1, insomnia (F51.0), and ADHD (F90.0, F90.1, F98.8). Exclusion criteria included: acute substance use disorders (F10.2, F11.2, F12.2, F13.2, F14.2, F15.2, F16.2, F18.2, F19.2), chronic pain disorder (F45.1), eating disorders (lifetime; F50), bipolar disorder (lifetime; F31), antisocial personality disorder (F60.2), borderline personality disorder (F60.3), acute suicidal tendencies, regular exercise (≥ 30 min/week), change (i.e., reduction and increase) of psychopharmaceuticals (≤ 2 months). Any change in treatment led to a withdrawal from the study.

The sample size was determined a-priori through power analysis, using G*Power ([52], v. 3.1.9.7.). A moderate to large effect (Cohen’s d = 0.74) of the mean post-difference between the two groups for the primary outcome was expected. Effect estimation was the median of the effect of exercise on disorder-specific symptoms of depressive disorders, anxiety disorders and insomnia. Since a small number of eligible participants with ADHD was expected, the effect of exercise on symptoms of ADHD was not included in the effect estimation. Effect sizes were derived from the most recent meta-analyses and RCTs available at the time of trial design [36, 40, 53]. With significance level: α = .05, Power: 1-β = .80, allocation ratio N2/N1: ε = 1, the required sample size for a two-tailed t-test for independent samples was N = 60. With an expected dropout rate of 18% for a clinical sample in an RCT [38], the total sample resulted in N = 71. This resulted in a group size of approximately n = 36 for each group.

Psychologists performed a preliminary telephone screening of eligibility criteria. Eligible participants were invited to the University of Tuebingen where they first completed a demographic questionnaire. Research assistants, who were trained in the conduction of structured clinical interviews, conducted the structured clinical interview for DSM-IV (SCID) [54] for eligibility criteria. ADHD was diagnosed by DSM-IV criteria through the Homburg ADHD Scales for Adults (HASE) [55]. Primary insomnia was diagnosed by DSM-IV criteria combined with the Pittsburgh Sleep Quality Index (PSQI) [56]. Participants signed an informed consent form and completed online questionnaires via a secure online survey software Sosci Survey [57] prior to randomization. This pre-treatment assessment was conducted on an average of 23.15 days (SD = 22.19) prior to the start of the intervention.

The 12-week exercise intervention “ImPuls” [69] was conducted in a group format of three to four participants and divided into a supervised and non-supervised period. Behaviour change techniques (BCTs), such as self-efficacy, goal setting, self-monitoring, formation of concrete exercise plans and coping planning, were integrated to promote sustained exercise behaviour change [49, 70]. Intervention contents are displayed in Fig. 1 and Table 1.

Individuals from both study arms, who fulfilled any exclusion criteria (i.e., change of treatment, contraindications for exercise) during the intervention, were excluded from post-data collection, 18.1% (n = 13). Since the current study contained exclusion criteria that could change during study participation (e.g., change of treatment), data from participants, who did no longer meet eligibility criteria needed to be excluded from post-data collection in order to reduce the risk of bias in the intervention effect estimate [79]. Missing data was assessed at scale level. Linear mixed models, using maximum likelihood estimations, were conducted to handle missing data (also participants’ data of those who were excluded from post-data-collection). Linear mixed models, based on all observed data, can be a valid and unbiased method to handle data that is missing at random [80].

Potential outliers were identified through three measures: Leverage, Cook’s Distance, and Studentized Residuals. Cases with greater than three time the average leverage, cook’s distance greater than 1, and studentized residuals greater than 3 [81, 82], were considered as potential outliers or influential data points. To evaluate the influence of potential outliers on results of linear mixed models, they were calculated again without cases that either exceeded the cut-off value of all three measures, or exceeded the cut-off values of cook’s distance and leverage, or exceeded the cut-off value of cook’s distance. Post-difference and interaction-effect sizes were then compared to those of linear mixed models including the complete data set.

Assumptions of linear mixed models and linear regressions (i.e., linearity, normality of the residuals, homoscedasticity, and multicollinearity) were visually inspected. If residuals of linear mixed models were not normally distributed, data was log-transformed.

For data preparation the Statistical Package for Social Science (IBM SPSS, Inc., Chicago, IL, USA, version 26) was used. Statistical analyses were carried out using R (version 4.0.3) and RStudio (version 1.1.453). Descriptive statistics were used to analyze sample characteristics and dropout rates. Baseline differences between groups and between those that completed the study versus dropped out were analyzed using two-tailed t-tests for independent samples (continuous variables), Chi-scared tests or fisher’s exact tests (categorical variables).

Differences between groups on primary and secondary outcomes changes were analyzed as intention-to-treat (ITT) analysis with linear mixed models using the lme4 package [83] in R. Models used maximum likelihood as the estimation technique. Models included treatment group, time point and time point-by-treatment group interaction as fixed effects. Intercepts were included as random effects. An unstructured covariance matrix was assumed. Post-hoc tests for post-treatment-differences between groups were carried out using two-tailed t-test for independent samples. For post-hoc tests of the secondary outcome, a Bonferroni correction was used. Effect sizes for differences between groups (intermediate-, post-treatment-difference effects and interaction effects) were calculated according to Cohen’s d [84].

An additional analysis inspected clinically relevant changes of participants’ symptomatology. Clinically relevant changes were defined as a change on the GSI from pre-treatment to post-treatment assessment of at least 0.26 [58].

Sufficient statistical power enabled exploratory analyses that examined the efficacy of exercise on depression for subgroups of participants diagnosed with depressive disorders. Additional exploratory analysis (per-protocol analysis) tested the predictive value of the change of the amount of exercise on primary outcomes changes. Linear regressions were calculated with change of exercise (post-treatment assessment – pre-treatment assessment) as a predictor variable and primary outcomes changes (pre-treatment assessment – post-treatment assessment) as criterion variables.

In total, 106 individuals were assessed for eligibility. Of those assessed, 30.2% (n = 32) were excluded and 69.8% (n = 74) were eligible for participation. Those eligible were randomly assigned to the intervention group, 51.3% (n = 38), or control group, 48.7% (n = 36). 5.3% (n = 2) of participants of the intervention group were removed from the analysis due to a wrong diagnosis at pre-treatment assessment (comorbid lifetime eating disorder, 2.6% (n = 1), and a comorbid alcohol use disorder, 2.6% (n = 1) [79]. This led to an ITT efficacy group of N = 72 (50.0% (n = 36) of patients in the intervention group vs. 50.0% (n = 36) in the control group) (see Fig. 2).

Baseline characteristics of the studied sample are reported in Table 2. There were no significant baseline differences between intervention group and control group. Dropout rates of the control group were higher compared to the intervention group, but not statistically different. Compared to the intervention group, participants of the control group dropped out more frequently due to treatment change without reaching statistical significance (see Table 2 and Fig. 2). There were no significant baseline differences between study completers and dropouts (Additional file 1). There were no serious adverse events.

Missing data was missing completely at random (MCAR) (χ² (14) = 12.33, p = .580). 106 (14.7%) values of primary and secondary outcomes were incomplete. Per-protocol analyses for each primary and secondary outcome were conducted as sensitivity analyses, using linear mixed models (Additional file 2), to examine the robustness of the results.

Ten cases were detected as potential outliers in the linear mixed model with the GSI (SCL-90-R) as criterion variable and four cases in the linear mixed model with the global sleep quality score (PSQI) as criterion variable. No cases were detected as potential outliers in the mixed models with exercise (BSA questionnaire) as criterion variable. Excluding potential outliers did not change direction, nor significance of intervention effects (Additional file 4). Intervention effects on the global sleep quality score increased from moderate to large effect size (cohen’s d for post-treatment-difference between groups) when potential outliers were excluded. Therefore, potential outliers were not excluded from analyses.

Results of all primary and secondary outcomes and subgroup analysis, including effect sizes, are presented in Table 3. The interaction effect of group by time was significant for global symptom severity, F (1, 53) = 7.93, p = .007, 95%CI[− 0.50,- 0.08], depression, F (1, 55) = 6.30, p = .015, 95%CI[− 0.82, − 0.09], anxiety, F (1, 54) = 10.12, p = .002, 95%CI[− 0.36, − 0.08], and sleep quality, F (1, 58) = 11.24, p = .001, 95%CI[− 4.68, − 1.19], with larger decreases in the intervention group. Post-treatment difference effects were significant for depression, t (114) = 2.18, p = .031, and sleep quality, t (121) = 2.13, p = .035, with lower scores in the intervention group. Post-treatment difference effects for global symptom severity, t (105) = 1.68, p = .096, and anxiety, t (110) = 1.88, p = .063, were moderate, with lower scores in the intervention group, without reaching significance.

The interaction effect of group by time was significant for the mean amount of exercise, F (2, 115) = 16.50, p < .001, 95%CI [1.41, 3.61], with larger increases in the intervention group. Bonferroni-corrected intermediate-treatment difference effect, t (167) = − 5.83, p < .001, and post-treatment difference effect, t (170) = − 5.04, p < .001, were significant, with higher scores in the intervention group.

Compared to participants of the control group, more participants of the intervention group revealed clinically significant changes of symptomatology, without reaching statistical significance (χ² (1) = 3.61, p = .058.

In a subgroup of participants with depressive disorders, the interaction effect was significant for depression, F (1, 37.48) = 5.74, p = .022, 95%CI[− 1.01, − 0.09], with larger decreases in the intervention group. The Post-treatment difference in this subgroup was significant, t (75) = 2.75, p = .008, with lower scores in the intervention group (see Table 3). Across both groups, the change of the mean amount of exercise from pre- to post-treatment assessment significantly predicted the change of global symptom severity, b = .35, t (49) = 2.61, p = .012]. Predictions from the change of exercise on the change of disorder-specific symptoms across both groups and for each group are displayed in Additional file 3.

Beneficial effects of the intervention on global symptom severity suggest that the exercise intervention efficaciously reduced symptoms across the included heterogenous sample. On the one hand, there are few studies that investigated the efficacy of exercise among outpatients with heterogenous psychiatric diagnoses [75]. On the other hand, the few existing studies assessed physical health, rather than mental health as primary outcomes [85]. Two RCTs assessed quality of life [86] and general mental health [87] as secondary outcome. Their results suggested improvements on quality of life (i.e., physical function score, social function, emotional role) [86] but not on general mental health (i.e., psychological distress and well-being) [87]. To the best of our knowledge, there exists no study investigating the effects of exercise among a sample with heterogenous diagnoses that include a clinical valid and reliable measure to assess global symptom severity. Whereas the intervention group revealed stronger improvements on global symptom severity, compared to the control group, the post-treatment effect between both groups was not significant. Since sample size calculation was based on large effects of exercise on disorder-specific symptoms among included disorders, power might have been to small to detect treatment effects on global symptom severity across disorders at post-treatment assessment.

Interaction effects of the current intervention on global symptom severity are similar to those of recent meta-analyses [27, 28, 29, 30, 31], evaluating the efficacy of transdiagnostic psychological treatments among patients with depressive disorders and/or anxiety disorders over comparison or control interventions (i.e., diagnosis-specific intervention control, treatment-as-usual, or a waitlist control). Results of these previous studies revealed moderate to large effects on clinical measures assessing symptom severity across included disorders (i.e., depression-anxiety scales, quality of life).

Supporting the assumption of the transdiagnostic efficacy of the intervention, our results demonstrated that the intervention improved one underlying process across included disorders with large effect size: poor sleep quality [21, 22]. This result is similar to a recent meta-analysis of RCTs [34] which demonstrated large beneficial effect of exercise on sleep quality among people with various psychiatric disorders. Nonetheless, the analysis included primarily RCTs assessing the effects of exercise on sleep quality among study samples with specific diagnoses. Only one RCT [88] included participants with a primary diagnosis of a depressive disorder with and without comorbid anxiety disorders. Similarly, another recent meta-analysis [89] that investigated the effects of exercise on various underlying processes across psychiatric disorders, mostly included participants with specific diagnoses or even non-clinical samples. Thus, the findings of our study therefore expand on the results of recent meta-analyses by demonstrating effects on one underlying process across a clinical sample with heterogenous psychiatric disorders.

Correspondingly, our results suggest disorder-specific efficacy by improving symptoms of depression, anxiety and insomnia. The moderate antidepressant effect of the intervention at post-treatment assessment is smaller compared to prior meta-analytical findings suggesting a large antidepressant effect of exercise, over non-active controls [36]. In contrast to our study, prior studies included samples with a primary diagnosis of a depressive disorder only [36]. Although the large antidepressant effect among patients with a primary depressive disorder have been consistently demonstrated in prior studies [35, 36], to the best of our knowledge, the antidepressant effect of exercise among anxiety disorders, insomnia, and ADHD has not been investigated yet. When analyzing the antidepressant efficacy of our exercise intervention among the subsample with a primary diagnosis of a depressive disorder, the effect size is comparable to prior studies [36]. The mean change of anxiety symptoms among the intervention group across the entire mixed sample was large, compared to the control group. Prior exercise trials have reported moderate interaction effects of exercise on anxiety symptoms among patients with anxiety disorders, over non-active controls [38]. This result may suggest that the current exercise intervention might have been more efficacious in reducing anxiety across heterogenous disorders than prior exercise trials that included only anxiety disorders [38]. However, this assumption needs to be considered with caution due to different sample characteristics and exercise modalities.

The post-treatment difference effect between the intervention group and control group on anxiety was not statistically significant. As stated above, the power analysis was based on the median effect size for disorder-specific effects of exercise across depressive disorders, anxiety disorders, and insomnia. Beneficial effects of exercise on anxiety seem to be smaller than those for depression [35] and insomnia symptoms [39]. Furthermore, it appears that effect sizes differ across different anxiety disorders [37]. Therefore, the a-priori determined sample size might have been underestimated to detect treatment effects on anxiety across the heterogenous sample. The large post-treatment effect of exercise on sleep quality among the intervention group, compared to the control group, is comparable to prior meta-analytical findings investigating the effect of exercise on sleep quality in patients with insomnia, over non-active controls [40]. In comparison to meta-analytical findings investigating disorder-specific effects of CBT, over non-active controls, our results showed similar efficacy for depression among depressed participants [90] and sleep quality among the entire mixed sample [91].

The efficacy on global symptom severity and underlying mechanisms across the sample as well as disorder-specific efficacy of the current exercise intervention, suggests that exercise might be able treat a broad range of heterogenous diagnoses with and without comorbidities. Our study results further suggest, that exercise interventions do not necessarily be tailored to a specific psychiatric disorder referring to exercise modalities (i.e., type, frequency) to efficaciously treat disorder-specific symptoms or underlying processes across disorders. Rather, exercise modalities, that have shown therapeutic efficacy among single psychiatric disorders (i.e., two to three times per week, for 10 weeks, at a minimum of moderate intensity and a duration of 30 min, partially supervised or non-supervised, solely aerobic or aerobic combined with resistance training [33, 35, 37, 43]) seem to be adoptable to the treatment of heterogenous diagnoses with and without comorbidities. Similar to the efficacy of transdiagnostic psychological interventions, this may result in a faster and easier dissemination, compared to disorder-specific treatments, because there is no need to learn and apply multiple treatment protocols for different specific disorders [12]. Thus, exercise interventions may improve the existing treatment gap in mental health care [11] by offering an efficacious and effective treatment.

Study results demonstrated that the current exercise intervention was highly efficacious in increasing the amount of exercise, even when participants were not supervised. This is in line with a recent systematic review [46] and Editorial [48], suggesting that exercise interventions, combined with BCTs, are efficacious in increasing the amount of exercise. To date, there are only a few exercise interventions for individuals with psychiatric disorders integrating BCTs [46, 85] and only approximately one quarter of those seem to efficaciously increasing participant’s amount of exercise [85]. The frequent failure to increase exercise behavior among patients with psychiatric disorders may be related to a lack of motivation and exercise-related self-regulatory skills (i.e., volition) in this population [49]. A large proportion of outpatients in Germany do not exercise on a regular base [92]. Thus, the integrated BCTs in our intervention seem to be adequately tailored to outpatients to improve their deficiencies in motivation and volition regarding exercise.

Results of our explorative analyses demonstrated a prediction of symptom reduction by an increase of the performed amount of exercise, indicating that the change of exercise might indeed be one specific mode of action of the therapeutic effects. This moderation effect is often assumed in the exercise literature, however only very few trials do report such effects. As far as we know, only one of the recently published high quality RCTs [45] did show changes of exercise as the specific mode of action of the effects of exercise interventions. In addition to the increase of exercise, results suggest also a maintenance of exercise behavior because participants were still exercising even when they were not supervised. Since there is a lack of follow-up studies of exercise interventions or an absence of measures for exercise behavior, little is known about the maintenance of exercise behavior due to the conduction of exercise interventions combined or without BCTs [85]. As mentioned in the introduction, beneficial effects of exercise seem to be maintained only when exercise behavior has changed sustainably [45]. Since participants were still exercising during the non-supervised period of the intervention, participants might have integrated regular exercise into their daily life routines. Since the amount of exercise was assessed 5 weeks and 2 months after the supervised period, no general conclusions can be drawn about the long-lasting exercise behavior.

Results of this study not only suggest efficacy of the current exercise intervention but also its feasibility in a realistic outpatient setting. First, the study sample included a realistic outpatient sample, waiting for psychotherapeutic treatment, with heterogenous, highly prevalent psychiatric disorders with and without comorbid diagnoses. Second, approximately half of the participants of the intervention group revealed clinically relevant changes of global symptom severity, compared to less than one quarter of the control group. Third, the dropout quote among participants of the intervention group was low. Additionally, only 5.2% (n = 2) of the intervention group dropped out due to lost to follow up. Hence, a strong acceptance and few adherence issues regarding the intervention can be assumed. The dropout rate is similar to prior exercise interventions [38, 93] and lower than other health behaviour change interventions (e.g., exercise, health education) for individuals with psychiatric disorders, in which the medium average dropout rate was 45% [94]. The current dropout rate was lower than those of individual and group CBT interventions (35%). Most dropouts were reported in outpatient settings [95]. The lower dropout rate in the current exercise intervention over CBT, might suggest equivalent acceptance of exercise than CBT among outpatients. Forth, the latency between pre-treatment assessment and initiation of the intervention was low, compared to waiting times for psychotherapy of approximately 5 months in Germany [10]. As stated in the introduction, prolonged waiting times for treatment are associated with worsening and chronicity of symptoms and the development of comorbid diagnoses. Consequently, the current intervention could be conducted to improve negative consequences of delayed treatment in Germany. Lastly, in comparison to an average duration of 19 weeks of prior exercise intervention for patients with psychiatric disorders [96], the current exercise intervention was short (12 weeks), including a very short supervised period of 4 weeks. The total number of 12 supervised sessions is equivalent to the average treatment duration of CBT among depressive disorders and anxiety disorders [97, 98].

Hence, in addition to the suggested transdiagnostic and disorder-specific efficacy of the intervention, current results demonstrated that the exercise intervention might be feasible treatment among outpatients, that were waiting for psychotherapeutic treatment in German health care settings in outpatient units and practices.

One limitation of the current study is the use of a passive control group, which does not allow to control for non-specific effects of therapy, such as relationship building or social support. However, the results of our explorative analyses demonstrated a prediction of symptom reduction by an increase of the performed amount of exercise, indicating that the change of exercise might indeed be one specific mode of action of the therapeutic effects. Second, the measure for global symptom severity symptoms was comprised of symptoms that were not characteristic for all included disorders (e.g., aggression). Therefore, the validity of this metric to assess global symptom severity among the current sample is disputable. However, the GSI is a reliable and valid instrument to assess clinical global symptom severity across heterogenous psychiatric disorders and allows to rate clinically relevant changes of symptomatology [99]. Therefore, the use of this measure was reasonable in this study because of the inclusion of heterogenous and highly comorbid psychiatric disorders. Furthermore, the internationally widespread use of this measure [58] allows to compare study results with international publications on the effect of various treatments on symptom severity. Third, eligibility criteria of the current study allowed for a wide age range. However, participants had a low average age, which might limit the generalizability of results to older individuals. Large standard deviations around the mean value, a large age range (19–63 years) of the current sample as well as a similar average age of prior exercise trials [36] might increase the generalizability of results to older individuals. Forth, although the SCID was conducted at pre-treatment and post-treatment assessment, we did not include results of the SCID from post-treatment assessment in our analyses. We intended to assess clinically relevant changes of symptomatology. If a diagnosis, that was present at pre-treatment assessment, had still been present at post-treatment assessment, relevant changes on symptomatology would not have been able to assess. Therefore, we considered self-reported outcomes (GSI of the SCL-90-R) as a more valid measure to assess clinically relevant changes of symptomatology. Moreover, one eligible participant could meet multiple inclusion diagnoses. Thus, the comparison of the number of inclusion diagnoses between pre-treatment and post-treatment assessment did not seem as a valid indicator of treatment responders vs. non-responders. Alternative indicators of treatment responders vs. non-responders, resulting from analyses of the SCID (e.g., counting of symptom criteria for depressive disorders) seem to be an arbitrary and not valid approach.

First, the high methodological standard is an important strength of the study. The study involved an RCT design with stratified block-randomization, which is considered as the gold standard to evaluate intervention efficacy [100]. Equal treatment arms and allocation maximized internal validity [101]. Strict inclusion and exclusion criteria controlled for factors that may obfuscate outcome measures [102]. Second, the inclusion of a heterogeneous sample with a broad age range and various psychiatric disorders allowed for a high generalizability of the results. The conduction of the intervention in a realistic outpatient setting, the large number of included patients with severe, clinically raised symptoms and comorbid presentations of psychiatric disorders suggest a valid representation of the clinical reality [12].