Studies were eligible if they were randomized controlled trials (RCTs) or clinical controlled trials (CCTs) with or without cross-over design, including adult patients (≥18 years) diagnosed with mental disorders as defined by ICD or DSM criteria or assessed through validated self-report measures. Due to the different diagnostic criteria that apply to children and adolescents, these samples were not considered. Studies were further included if prāṇāyāma techniques were applied as a standalone intervention, excluding studies that combined prāṇāyāma with other yoga components (except for relaxation) or other treatments that were not provided to both of the groups. There were no predefined criteria for intervention duration or frequency to capture a comprehensive range of the existing evidence. Eligible control interventions consisted of inactive and active comparators such as treatment as usual, wait list, attention control interventions, pharmacological treatments, or other non-pharmacological comparators. To be included, studies had to report at least one of the following outcomes: the primary outcome was symptom severity of the primary diagnosis, while secondary outcomes included health-related quality of life, depression, and safety. When multiple instruments were used to assess the same outcome in a study, preference was given to disease-specific over generic instruments, multi-item over single-item measures, and clinician-reported over patient-reported tools. Beyond that, the primary outcomes of the individual studies were favored over secondary ones. Safety was operationalized by the number of adverse events (AEs) or study withdrawals due to AEs. AEs were defined as any unfavorable medical event experienced by a participant, regardless of whether it was caused by the intervention. Events leading to death, life-threatening conditions, hospitalization, or substantial disability were classified as serious AEs (15).

We systematically searched PubMed, PsycINFO, and the Cochrane Central Register of Controlled Trials until April 2024 without language or date restrictions. The search strategy ( Table 1 ) included mesh and title/abstract searching for yoga and prāṇāyāma terms combined with those for CCTs and RCTs and was adapted for each of the databases. We also searched gray literature through ResearchRabbit and international trial registries of the National Institutes of Health (NIC) and World Health Organization (WHO). Following the PRISMA guidelines (13), two reviewers (CM and HH) independently screened titles and abstracts of studies and assessed full texts for eligibility. Any disagreements were rechecked with a third reviewer (DM) until consensus was reached.

Two reviewers (CM and DM) independently extracted data on study characteristics, including trial type, study origin, population characteristics, randomized sample size, mean age ± standard deviation (SD), percentage of female participants, treatment duration, intervention details, assessment points, outcomes included and not included in the meta-analysis, and funding sources. Discrepancies were rechecked by a third reviewer (HH) until consensus was reached. Missing study data were requested from the study authors by email.

The revised Cochrane risk-of-bias tool (RoB 2) (16) was used to assess the risk of bias in each included study across five domains: 1) bias arising from the randomization process, 2) bias due to deviations from intended interventions, 3) bias due to missing outcome data, 4) bias in the measurement of the outcome, and 5) bias in the selection of the reported result. Two reviewers (CM and DM) independently assessed each domain, and any discrepancies were resolved through discussion with a third reviewer (HH) to reach consensus. Each domain was rated as “low risk of bias”, “some concerns”, or “high risk of bias” according to the RoB 2 guidelines. An overall risk-of-bias judgment was derived based on domain-level ratings. Bias impact was visualized using the RoBvis tool (17).

We initially planned to evaluate the evidence of publication bias using Egger’s test. However, since the number of included studies for each meta-analysis was fewer than 10, it was not possible to assess publication bias.

The qualitative synthesis included a detailed comparison of study characteristics and risk of bias. As safety data were reported insufficiently, we decided against meta-analyzing data and reported AEs qualitatively.

The electronic database search revealed 2,973 articles ( Figure 1 ). Five additional articles were retrieved from ResearchRabbit. After removing duplicates and excluding articles by screening titles and abstracts, 16 full-text articles were assessed for eligibility. Nine full texts were excluded for the following reasons: six articles examined prāṇāyāma combined with other yoga elements or interventions (20–25), two articles lacked suitable control groups by including healthy adults or no control condition (26, 27), and one article included participants with burnout, which is not defined as a mental disorder (28). Thus, a final sample of seven articles on six individual datasets, including 517 patients, was included for qualitative and quantitative synthesis (29–35).

The characteristics of the included studies are presented in Table 2 . All studies were RCTs conducted between 2000 and 2023 in the USA (29, 30, 33), India (32, 34, 35), and Germany (31). Patients were civilians (31, 32, 35), veterans (29, 33), and prisoners (34) suffering from various mental disorders, including PTSD (29–31, 33), depression (32), alcohol dependence disorder (35), and mixed non-psychotic mental disorders (34). Sample sizes varied from 21 to 232, with a median of 67 participants and a median of 6% female participants. The average age across studies was 40.2 years, ranging from 28.7 to 56.9 years. The duration and frequency of prāṇāyāma sessions varied by setting and population between 1 and 6 weeks, with an average of 17.5 sessions, while one study did not report duration in weeks but in sessions of 10 (31). Six out of the seven studies implemented Sudarśan Kriyā Yoga (SKY) as a standardized protocol (29, 30, 32–35), although the frequency and types of breathing exercises varied from low to fast/high frequency. The remaining study used a tailored protocol consisting of four specific prāṇāyāma exercises (31): one fast breathing technique of high frequency, two slow-breathing ones, and one breath-holding technique ( Table 3 ). Control conditions included passive ones such as wait list (33, 35) and attention control (34) as well as standard treatments such as cognitive processing therapy (29, 30), electroconvulsive therapy (32), and antidepressant drugs (32). In the latter study, the data of the two control groups were combined to avoid biasing the final sample size. Similarly, one study (31) provided two measurements for the same endpoint (physical and psychological quality of life) that were pooled to provide a single value.

Regarding data analysis, two studies presented findings for both PP and ITT populations: one applying the last observation carried forward method (29) and the other using fully conditional specification iterations (31). Four studies reported values that could be interpreted as ITT ones due to no (32, 35) or minimal dropout rates of n = 1 per group (33, 34), while one study (30) conducted only exploratory PP analysis.

RoB is summarized in Table 4 . Overall, RoB was high in four studies (29, 30, 32, 33, 35) and assessed with some concerns in two studies (31, 34). Regarding bias from the randomization process, only one study (31) provided a clear description of the allocation procedure. In contrast, one study (29, 30) excluded participants directly after randomization without explanation, potentially introducing bias. For the remaining studies (32–35), information was insufficient to adequately assess the entire randomization process.

Bias due to deviations from intended interventions was assessed as follows: due to the nature of the prāṇāyāma intervention, participants and providers were aware of assignments in all studies. However, one study (34) ensured scientific rigor by including a suitable attention control group, while one study (31) considered statistical adjustments for patient expectation, raising only some concerns. The other four studies were rated as high risk, as the authors deviated from the protocol by excluding participants after randomization with an incomprehensible explanation (29, 30), did not provide sufficient information (32), or possibly introduced nocebo effects by not offering any control intervention other than wait list (35).

Bias due to missing outcome data was rated low in three studies because of minimal dropout rates (33, 34) or ITT analysis with robust imputation methods of missing data (31). The remaining three studies were rated as high risk, as they did not provide sufficient information (32, 35) or excluded participants without justification (29, 30).

Measurement bias was generally low, as all studies used validated instruments with consistent methods and time points. However, in two studies (33, 35), the absence of active control conditions may have influenced outcome assessments, indicating a high risk of bias.

Finally, selective outcome reporting was low in only one study (31) that fully adhered to a registered protocol. Four studies raised some concerns, as they differed slightly from the published protocol without adequate explanation (29, 30) or did not report pre-registered protocols but reported comprehensible outcome selection, which do not seem to be biased (32–34). One study, however, reported using the Severity of Alcohol Dependence Questionnaire at baseline and follow-up, but only presented baseline values (35).

By excluding studies with a high risk of overall bias, only comparisons against passive controls remain in the analyses. For symptom severity, pooling effects of ITT samples no longer revealed significant group differences, and statistical heterogeneity increased (SMD = −0.22, 95% CI = [−0.57, 0.13], I² = 48%, N = 304) (31, 34). By pooling the effects of PP samples, differences remain significant (SMD = −0.33, 95% CI = [−0.56, 0.10], I² = 0%, N = 295) (31, 34). For quality of life, all main analyses were based on studies without a high risk of bias. Depression analyses are all based on studies with a high risk of bias, with one exception (31). Comparing the results of this individual study with the pooled effects, all revealed no significant difference between prāṇāyāma and passive controls on depression.

Substantial statistical heterogeneity was observed in meta-analyses of quality of life and depression. As most analyses included only two studies, reducing heterogeneity by excluding studies was only possible for the comparison of prāṇāyāma versus passive controls on depression. Here, statistical heterogeneity could only be reduced by excluding the study with the best quality and the highest number of patients, resulting in significant group differences within the ITT and PP samples. However, as these results are likely subject to substantial bias, the data were not shown.

The systematic search revealed seven RCTs on six samples investigating the effectiveness of prāṇāyāma in patients diagnosed with mental disorders. Based on analyses of studies with overall some concerns of risk of bias, the evidence suggests that prāṇāyāma may have small-to-medium short-term effects on symptom severity and quality of life when compared to passive controls. However, sensitivity analysis showed that when high-risk trials are excluded, the effects remain significant only for PP data, not ITT ones. Moreover, we did not find any effects of prāṇāyāma on depression. Comparable effects of prāṇāyāma against standard psycho- or pharmacotherapy should be interpreted with caution, as they were based on single or pooled high-risk studies. The same is true for long-term effects. Safety was reported insufficiently. Based on the reported data, prāṇāyāma, in particular fast breathing, was associated with adverse events.

These findings align with a comprehensive systematic review and meta-analysis of 26 RCTs on breathwork and mental health in mixed populations of healthy individuals and somatically and mentally ill patients who revealed small-to-medium effects of modern and traditional forms of breathwork on self-reported stress, anxiety, and depression compared to non-breathwork active and passive controls (12). Likewise, our meta-analyses did not find any effects on depression. However, due to substantial heterogeneity in all of the analyses, this conclusion should be considered preliminary. The review further reported comparable effect sizes for different breathing techniques, in particular slow and fast breathing exercises, but only slow breathing resulted in significant pooled effects and was therefore recommended to patients. In our analyses, we were not able to differentiate between slow and fast prāṇāyāma techniques because of the overall low number of studies and the combination of low and fast techniques in all of the included studies. However, we detected higher AEs of fast breathing techniques, especially kapālabhātī, which strengthened the prior recommendation. Another scoping review on breathwork for clinically diagnosed anxiety disorders also found significant symptom improvements, particularly with slow diaphragmatic breathing, while the results for fast hyperventilation techniques were contradictory (36). This can be explained by evidence showing that slow breathing enhances parasympathetic activity, improves vagal tone, and regulates emotional responses by modulating brain regions such as the prefrontal cortex and amygdala (37). Furthermore, slow breathing has been associated with increased alpha power in the electroencephalogram (EEG), reflecting states of relaxation and focused attention (38). These physiological mechanisms likely underpin the reductions in anxiety and stress observed following slow breathing interventions and suggest that prāṇāyāma protocols emphasizing slow and controlled breathing techniques could improve therapeutic outcomes while minimizing adverse events associated with fast practices such as kapālabhātī. Nonetheless, fast breathing techniques have shown interesting effects as well. Although they did not lower cortisol levels initially but increased them, fast breathing showed a better long-term stabilization of cortisol levels and was discussed to act as a training impulse to the autonomic nervous system, similarly to physical exercises (39). By communicating possible AEs of fast breathing techniques to patients and adequately accompanying them, patients may equally or even better benefit from fast breathing techniques.

The first limitation is the small number of included studies with limited follow-up data. Conclusions, especially from meta-analyses that include only two RCTs, should therefore be considered preliminary. Substantial heterogeneity in some of the analyses suggests that additional studies are urgently needed to make precise and robust conclusions about the effectiveness of prāṇāyāma, especially as a single intervention against standard care. Moreover, the absence of long-term data in all but two studies (29, 33) limits the conclusions regarding the sustainability of the effects. In addition, given the limited number of studies, we were unable to assess the risk of publication bias, which cannot be excluded and should be considered in the interpretation of the findings.

A second limitation includes the risk of bias profile of the included studies. Although it was comparable with the profile of studies on conventional breathing interventions (12), only 33.3% of the domains could be assessed as low risk, and 27.8% raised some concerns, potentially impacting the internal validity of the studies as well as the generalization of the pooled results.

The third limitation refers to possible placebo effects that cannot be excluded because therapists cannot be blinded to treatment allocation, and analyses contained patient-reported outcomes, which may have been influenced by subjective perceptions and expectations. Only one study (31) controlled for patient expectations in statistical analyses. In contrast, none of the studies addressed other non-specific treatments and therapist effects, such as the therapeutic alliance, which can be controlled, for example, by using validated questionnaires (40).

Additional limitations include the insufficient reporting of adverse events and more favorable effects in small, high-risk studies from India (41), which may bias conclusions regarding the risk–benefit ratio. Moreover, the predominance of male participants (94%) limits the generalizability of findings to female populations.

Future studies should investigate both the efficacy and specific mechanisms of prāṇāyāma in treating various psychological disorders in detail. Systematic reporting of AEs is essential to improve comparability and ensure a comprehensive understanding of prāṇāyāma’s safety in the treatment of mental disorders. Future studies should therefore include reporting of AEs according to the Consolidated Standards of Reporting Trials (CONSORT) extension for harms to ensure the standardized reporting of adverse events (42). The sustainability of treatment outcomes should also be evaluated by examining long-term effects. Recommendations further include the need for larger sample sizes, rigorous study designs, and the reporting of methodologies in accordance with CONSORT (43) to minimize the risk of bias. In addition, the Checklist Standardising the Reporting of Interventions For Yoga (CLARIFY) checklist (44) provides researchers with a minimum reporting template for yoga studies. If blinding of therapists is not feasible, attention effects could be controlled by asking patients about their perception of the therapeutic alliance using validated questionnaires. Moreover, further research should include diverse demographic groups. In this review, women were severely underrepresented, with a median of only 6%. Given the higher prevalence of mental health disorders in women (27.2%) than in men (18.1%) (45), this proportion should be accounted for in future studies. Moreover, future research should include more diverse populations beyond the currently studied groups (e.g., Indian clinical samples and U.S. veterans) to improve generalizability across cultural and demographic contexts. Future studies should also aim to clarify specific mechanisms of action by examining factors such as type of prāṇāyāma (e.g., slow versus fast), session duration, intensity, and frequency. Additionally, future trials may directly compare prāṇāyāma with established treatment approaches such as cognitive behavioral therapy or pharmacotherapy to determine comparative effectiveness. Together, these implications will contribute to drawing better conclusions about the efficacy, effectiveness, and safety of prāṇāyāma for patients with mental disorders.

prāṇāyāma, in particular slow breathing techniques, may decrease symptom severity and improve quality of life of non-psychotic mental disorders when integrated in out- and inpatient care. To date there is no robust evidence that prāṇāyāma programs has comparable effects to standard treatments such as Cognitive Behavioral Therapy or Antidepressants and should therefore not be used instead of these therapies. Due to the considerable variability in the duration and frequency of prāṇāyāma interventions across studies, no evidence-based recommendation regarding an optimal length or intensity of prāṇāyāma can be made yet. Therapists should also be aware of possible side effects of fast breathing techniques, especially in patients with PTSD or anxiety disorders who might perceive these techniques as additional stressors or even trigger. Nevertheless, they might be useful to increase stress tolerance equally to the use of breath-holding tasks (46).