Studies were eligible for inclusion if they (i) followed an RCT protocol, (ii) used a wait-list, usual care, or attention-control group, (iii) included one or more aerobic, resistance, or mind-body exercise intervention arms, (iv) reported depressive symptoms as an outcome at baseline and during follow-up, (v) used one or more psychometrically validated depression questionnaires, (vi) recruited participants with a minimum mean sample age of 65 years. Studies were excluded when (i) the intervention condition used a multicomponent treatment including non-exercise components with the exercise condition, or (ii) the participants were diagnosed with clinical depression, defined by DSM or ICD criteria, or a clinical threshold on a questionnaire validated against a structured diagnostic interview prior to study enrollment. Eligibility was not restricted to specific years, languages, or publication status.

Studies were identified from computerised searches of the following databases: PubMed, Web of Science, Cumulative Index to Nursing and Allied Health Literature (CINAHL), Health Source: Nursing/Academic Edition, PsycARTICLES, PsycINFO, and SPORTDiscus. Databases were searched for key terms pertaining to four main concepts: older adults, exercise, depressive symptoms, and RCTs. Search terms were identified using text mining procedures and an example of a search strategy is presented in detail as Extended data. Published studies, systematic reviews, and meta-analyses ^{4, 15, 16, 33– 36} were also screened for additional articles. Databases were searched up to and including September 12 ^th, 2019.

All articles collated from the systematic search initially went through a title and abstract screening, followed by a full-text screening. Eligibility criteria were used to determine whether each article should be included or excluded. The screening process was performed concurrently for both the current review and a parallel review ²³ . Once the screening process was complete, the remaining studies were included in the systematic review and descriptively reported. Studies were only included in the quantitative analysis if they contained sufficient outcome data.

Detailed data extraction was undertaken independently by a minimum of two researchers (KJM, PA, and/or DH) in compliance with a data extraction form (see Extended data), with any inconsistencies being arbitrated by another researcher (CM). Study characteristics are presented in Table 1. Methodological characteristics of each study were used to evaluate the quality of evidence, which included publication status, intention-to-treat principle, use of a cluster design, and validated measure(s) of depressive symptoms used.

Control groups within each individual study were further categorised as either wait-list, usual care, or attention-control. Participants undergoing wait-list conditions received the exercise intervention following trial completion. Participants randomised to usual care were those in sole receipt of conventional treatment during the trial. Participants randomised to attention-control conditions (also known as attention placebo control or active control) received activities completely unrelated to physical activity and/or exercise during their respective trials (e.g., social activities, educational programs, etc.).

Important participant and intervention characteristics were used to verify whether potential effect modifiers were similarly distributed across comparisons within the network. Participant characteristics were coded according to sample size, age (mean and standard deviation), percentage of females, and place of residence (community-dwelling, residential care, clinical setting). Relevant inclusion criteria (e.g., sedentary, dementia, etc.) were further used to assess the risk of bias from equity considerations ¹¹⁷ .

Intervention characteristics were appropriately coded. Exercise types were categorised as aerobic, resistance, or mind-body exercise. Length of interventions were coded in weeks or months. Exercise intensities were coded according to ratings of perceived exertion ¹¹⁸ , heart rate maximum (HR _max; low = <50%, moderate = 50-70%, high = >70%), maximal oxygen uptake (VO _2max; low = <40%, moderate = 40-60%, high = >60%) or one-repetition maximum (1R _max; low = <50%, moderate = 50-74%, high = >74%) ¹¹⁹ , or where unavailable, this was estimated according to the assessment of the original author(s). Frequency was coded as total sessions per week. Duration was coded as the average number of minutes engaging in exercise per session. Format of program was dichotomously coded as exercise in a group or individual setting. Format of supervision was dichotomously coded as supervised or unsupervised exercise. Agreement between the three researchers was 91.3%.

Risk of bias of the included RCTs was assessed using the Cochrane Collaboration’s Tool for Assessing Risk of Bias ¹²⁰ , which were independently conducted by a minimum of two researchers (KJM, PA, and/or DH). Discrepancies were arbitrated by another co-author (CM). Appraisal for ‘other sources of bias’ were evaluated with consideration for small sample size ( n < 15), low adherence (less than 80%), cluster randomisation, and inequity in the selection of the sample.

Outcome statistics including means ( M), standard deviations ( SD), and sample sizes ( n) for depressive symptoms were used to calculate the mean change in the primary outcome. Test statistics (i.e., t-, F-, and p-values) were used to estimate effect sizes when descriptive statistics were unavailable. Pairwise relative (head-to-head) treatment effects for depressive symptoms were estimated using Hedges’ g ¹²¹ , which corrects for overestimation biases due to small sample sizes ¹²² . Hedges’ g coefficients were interpreted according to Cohen’s conversions ¹²³ , whereby effects were considered small (0.2), medium (0.5), and large (0.8). Independent subgroups (e.g., males vs. females) within studies were treated as independent effect size estimates ¹²⁴ . When individual studies reported more than one post-treatment depression score for the same group of participants, only the initial post-treatment time-point was used. When studies reported depression scores on multiple outcome measures, the included depression measure was selected in compliance with clinical applicability ^{125, 126} .

Secondary outcome data were also extracted for study attrition, treatment adherence, and adverse events. Pairwise relative (head-to-head) treatment effects for study attrition were reported as odds ratios based on the pre-treatment sample size versus post-treatment dropout in the treatment and comparison conditions. Treatment adherence were reported as a percentage of total attendance in, or compliance to, the treatment condition. Adverse events were qualitatively reported according to the descriptive information provided in the transcript.

One notable assumption of network meta-analysis relates to comparison group estimates, which are derived from pooling studies with homogenous between-study effect modifiers ¹²⁷ . If the distribution of an effect modifier is heterogeneous across studies within a specific comparison group, the assumption of transitivity can be violated. In the context of this network meta-analysis, we separate exercise conditions (i.e., aerobic, resistance, mind-body) and control conditions (i.e., wait-list, usual care, attention-control) to account for the between-study variation of these effect modifiers. Given the intricacies of depression severity, a forest plot was generated to depict the juxtaposition of treatment effects between (i) participants in the present network meta-analysis with depressive symptomology but not clinically diagnosed and (ii) participants in a previous network meta-analysis with clinical depression ²³ .

Risk of bias assessment identified the potential for unit-of-analysis error within studies using a cluster design for treatment allocation. Thus, sample sizes were recalculated to account for error in cluster RCTs by determining a design effect ¹²⁸ with a conservative intracluster correlation coefficient of 0.05, in accordance with past studies ^{46, 129} . The certainty of evidence contributing to network estimates was assessed according to the Grading of Recommendations Assessment, Development and Evaluation (GRADE) approach ¹³⁰ .

Data were analysed and figures were generated using STATA/SE 15.1 ¹³¹ . Comparison-adjusted funnel plots were used to evaluate publication bias and small-study effects. Random-effects meta-regression was used to investigate modifying effects of age, gender, source of participants, length of intervention, exercise intensity, frequency, duration, and format of program, which have been identified as potential risks to transitivity in geriatric meta-analyses ^{4, 35, 132} .

A multivariate random-effects meta-analysis was conducted using the ‘mvmeta’ command ¹³³ . A random-effects model assumes variance both within and between studies, explaining the heterogeneity of treatment effects ¹³⁴ . A common heterogeneity parameter was assumed across comparisons. Heterogeneity was evaluated using tau-squared (τ ²), which estimates the deviation in effect sizes across the population of studies ¹²⁴ . The 95% prediction interval ( PrI) was also used to estimate the true dispersion of effect within two standard deviations of the mean effect size ¹²⁴ . The significance level was p < 0.05 for all analyses.

The initial systematic search yielded a total of 3,705 citations. When duplicate studies were removed ( n = 1,395), 2,310 eligible records were identified. Titles and abstracts were screened by two independent researchers (KJM and DCGB) with an agreement of 91.9%. Subsequently, 357 full-text articles were assessed for compliance with inclusion criteria and outcome data. Full-text screening was performed independently by two researchers (KJM and PA) with an agreement of 81.8%, where discrepancies were arbitrated and resolved by consensus with a third researcher (CM). Studies using duplicate sample sets ( n = 12) were identified, where the most informative publication with complete data being included in the quantitative analysis. Finally, 82 studies fulfilled all inclusion criteria to be included in the systematic review. In cases of missing data, authors were emailed by the first author (KJM). If authors failed to respond following two contact efforts, and there were insufficient data to calculate effect size estimates, the study was excluded from the quantitative analysis ( n = 9). Additionally, four studies ^{37, 61– 63} fulfilled all criteria but necessitated exclusion from the quantitative analysis due to control conditions being insufficiently defined, and the authors being unobtainable. Figure 1 outlines study selection and additional exclusion criteria.

Data from a total of 5,379 participants (2,815 treatment and 2,564 control) across 69 studies were pooled in the quantitative analysis. Each study reported pre- and post-treatment measures of depression symptoms, and data from 60 of the 69 studies were obtained for post-treatment attrition. Figure 2 illustrates the network of pairwise comparisons across all studies. Aerobic, resistance, and mind-body conditions had one or more direct comparison with each of the five comparison conditions. Direct comparisons for depressive symptoms were robustly characterised between intervention and corresponding control conditions (aerobic = 28, resistance = 22, mind-body = 32), with proportions being similar for study attrition (aerobic = 24, resistance = 21, mind-body = 25).

From the 69 included studies, 43 studies enrolled young-old samples (65–75 years) and 26 studies enrolled old-old samples (>75 years). Participants were identified as either community-dwelling ( n = 46), living in residential care ( n = 18), clinical ( n = 4), or uncategorised ( n = 1). Twelve studies enrolled participants with sedentary lifestyles, while the remainder enrolled participants with a range of active and sedentary lifestyles. Some studies recruited older adults that were either frail ( n = 5), wheelchair bound ( n = 3), or identified as presenting with a risk of falling ( n = 2). Participants with age-associated comorbidities were also recruited, including cardiovascular problems ( n = 6), dementia ( n = 3), cognitive impairment ( n = 3), cancer ( n = 2), and other chronic illness ( n = 6).

From 79 independent exercise interventions, the majority were supervised in group exercise classes ( n = 64). The remainder were either individually supervised ( n = 5), unsupervised in an individual format ( n = 2), supervised in an undisclosed format ( n = 1), or entirely undisclosed ( n = 1). The average exercise program length (weeks) was shorter for mind-body ( M = 13.67, SD = 6.77) than aerobic ( M = 19.76, SD = 14.44) or resistance ( M = 18.00, SD = 9.07). Average weekly exercise minutes (calculated as frequency multiplied by duration) were calculated for aerobic ( M = 107.78, SD = 40.88), resistance ( M = 126.90, SD = 50.28), and mind-body exercise ( M = 132.75, SD = 76.07). Treatment adherence ( n = 44) was comparable between aerobic ( M = 81.01, SD = 13.72), resistance ( M = 81.17, SD = 9.00), and mind-body exercise ( M = 79.34, SD = 14.73). Adverse events were observed during several of the included trials, which are presented in Table 2.

Risk of bias for each study is presented comprehensively as Extended data (see Figure S1). Both blinding of participants and personnel to treatment was implausible due to the implicit nature of exercise training interventions, and thus, the remaining six criteria were used to assess the overall risk of bias within each study. Methodological quality of included studies can be considered low-to-moderate ( M = 4.08/6, where low = 1, unclear, = 0.5, high = 0). Assessment of random sequence generation (selection bias), incomplete outcome data (attrition bias), and selective outcome reporting (reporting bias) may be considered adequate for most studies, whereas allocation concealment (selection bias) and blinding of outcome assessment (detection bias) were diverse. High ‘other sources of bias’ was due to low study adherence ( n = 14), small sample sizes ( n = 8), or both ( n = 1). See Figure 3 for a summary of the risk of bias in the included studies.

Inconsistency network models were used to test the global consistency of direct and indirect effects of pairwise and multi-arm comparisons. Assumption of consistency was satisfied for each treatment ( p > 0.05). Tests for inconsistency between direct and indirect estimates were not significant ( p > 0.05), thus indirect and direct estimates were not different to direct evidence. Inconsistency tables can be found as Extended data (see Tables S1 and S2).

Loop-specific heterogeneity was explored using inconsistency plots (see Extended data, Figure S7 and S8). Within the depressive symptoms network, inconsistency factors ( IF) did not indicate high inconsistency ( IF = 0.00 to 0.65) or loop-specific heterogeneity (τ ² = 0.05 to 0.28). The AER-MB-UC loop departed from the minimum lower-bound confidence interval ( CI), yet fell short of presenting risk for heterogeneity ( IF = 0.54, τ ² = 0.05, CI = 0.04, 1.03). Within the attrition network, the ratio of two odds ratios ( RoR) indicated a high degree of inconsistency for the AER-RES-UC ( RoR = 1.87) and MB-RES-UC ( RoR = 1.77) loops. Each were interpreted as presenting elevated risk for heterogeneity, which were subsequently downgraded during GRADE assessment. All remaining loops satisfied assumption of consistency.

Comparison-adjusted funnel plots were used to detect publication bias and small-study effects. Funnel plots were roughly symmetrical for both depressive symptoms and attrition, indicative of low risk of publication bias and no presence of small-study effects. See Figure 4 for the depressive symptoms network and Extended data for the attrition network (see Figure S9).

In order to test transitivity across networks, potential effect modifiers were tested with meta-regression sensitivity analyses for the entire pool of studies and separately for each exercise comparison (aerobic vs. resistance vs. mind-body). No significant modifying effects were observed for the pool of studies or any separate exercise comparison for age, gender, source of participants, length of intervention, format of program, exercise intensity, frequency, duration, adherence, year of study, risk of bias, publication status, intention-to-treat analysis, nor cluster design, indicating that the assumption of transitivity was upheld. Full analyses are presented as Extended data (see Tables S6– S8).

Data pooled from 69 eligible studies provided a total of 88 individual comparisons for depressive symptoms and 76 individual comparisons for study attrition. Table 3 presents the network meta-analysis of depressive symptoms and attrition. Network estimates were calculated to establish relative effectiveness between pairs of comparisons.

Each exercise type effectively reduced depressive symptoms compared with control conditions (see Figure 5). Ranking of treatments for depressive symptoms are presented on surface under the cumulative ranking curve (SUCRA) plots of ranked mean values, which can be found as Extended data (see Figure S11 and Table S3). Ranked order of quantitative values determined mind-body exercise to be the most effective type of exercise to mitigate depressive symptoms, followed closely by resistance and aerobic exercise, respectively. The magnitude of study effect did not reach statistical threshold to favour any individual exercise treatment.

Resistance exercise demonstrated the highest study compliance compared with each of the other comparison groups, but the dispersion of effect estimates presented a level of heterogeneity that confounded any substantive differences. Comprehensive reporting of study attrition can be found as Extended data (see Figure S10) in addition to SUCRA plots and ranked order (see Figure S12 and Table S4).

A two-dimensional clustered ranking plot was employed to illustrate the average reduction in depressive symptoms for each comparison, relative to average attrition rate. Figure 6 presents the ranking of the exercise conditions with respective control conditions in conjunction with SUCRA values for depressive symptoms (effectiveness) and attrition. The three exercise conditions amalgamated a single cluster and were more effective than control conditions.

The certainty of evidence was assessed with the GRADE approach ¹³⁰ . All control comparisons in the depressive symptoms network were rated as high or moderate certainty, which were downgraded due to small sample size or potential risks of bias (i.e., attrition bias, detection bias, or bias resulting from low adherence). Comparisons between exercise interventions were moderate-to-low certainty, resulting from imprecision in confidence intervals and small sample sizes. Detailed summary of the depressive symptoms network is presented in Table 4. Estimates of the attrition network were downgraded due to inconsistency and imprecision, which reflect moderate to very low confidence this outcome (see Extended data, Table S5).

Figure 7 presents collective representation for all adults aged ≥ 65 years. This comparison employs scaled distribution (Hedges’ g) for the present data and that of clinically depressed older adults ²³ .

Behavioural and physiological research ^{24, 25, 27, 28} coalesce to provide ample reasoning to separate participant cohorts with existing clinical depression from those without diagnosis. This study is no different. In agreement with findings from previous research ^{13, 14, 35} , aerobic and resistance exercise demonstrated similar treatment effectiveness in older samples aged ≥ 65 years (Hedges’ g = -0.06, PrI = -0.91, 0.79). Exercise characteristics (i.e., intensity, frequency, duration, etc.) are often similar between aerobic and resistance exercise, representing two sides of the same coin. Meta-analytical data ¹⁵ on older adults with existing clinical depression observed that exercise programs incorporating a combination of aerobic and resistance training were most beneficial. Although the synergistic effects of combined exercise types were beyond the scope of the current review, it is conceivable that aerobic and resistance exercise may complement one another in an exercise intervention.

Pooled direct and indirect estimates marginally favoured treatment with mind-body exercise over either aerobic (Hedges’ g = -0.12, PrI = -0.95, 0.72) or resistance exercise (Hedges’ g = -0.06, PrI = -0.90, 0.79). However, it must be noted that the magnitude of effect falls short of being statistically different between groups and should be considered equivalent. Certainty of evidence is moderate, due to the dispersion in effect size estimates resulting in imprecision. Direct comparisons from multi-arm RCTs have offered mind-body exercise to be more effective than aerobic ⁹² or resistance ⁴⁵ exercise. Moreover, subgroup analyses ¹⁶ have indicated that clinically depressed older adults respond more favourably to mind-body exercise, but this hypothesis has not be substantiated ⁴ .

Since mind-body exercise engages low intensity muscular activity (i.e., yoga, Tai Chi, qigong), the novel evidence in the current systematic analysis challenges the perception that exercise intensity is the primary mechanism for the antidepressive effect of exercise. Rather, mind-body exercise combines the mental and physical aspects of exercise, which may result in similar antidepressive effects to higher intensity exercise ^{135, 136} . Critical to these mental aspects is interoceptive sensations such as an internally directed focus on breathing and proprioception, which have previously been linked to the resilience of depressive states ^{137, 138} . Thus, it is plausible that mind-body exercise allows older adults to regulate negative mood states, though the relative contribution of mindfulness per se remains to be elucidated ¹³⁹ .

Other important determinants of successful programming include study attrition, adherence rate, and adverse events. Here, we anticipated that each exercise condition would demonstrate lower compliance to treatment than wait-list, usual care, and attention-control comparisons. Contrary to expectations, pooled direct and indirect estimates indicated that study attrition was comparable for all comparisons apart from resistance exercise, which offered a higher degree of compliance. However, on deeper scrutiny of absolute sample size, any differences observed in attrition become abrogated due to relatively smaller participant numbers within the resistance exercise studies ( n = 705) compared with aerobic ( n = 1,143) or mind-body ( n = 1,005). Thus, in consideration of the wide dispersion in effect size estimates and a moderate risk of bias in individual studies, there are limitations in the certainty to confidently conclude substantive difference in study attrition between any comparisons.

Each of the three types of exercise had similar adherence rates and time spent per week (calculated as frequency multiplied by duration). Interestingly, mind-body exercise had relatively shorter intervention length than either aerobic or resistance exercise ( M _diff = 6.09 and 4.33 weeks, respectively) despite having a greater reduction in depressive symptoms. This could be explained by (i) mind-body exercise having the same antidepressive effects in a shorter time than aerobic and resistance exercise, or (ii) a potential plateau effect whereby the antidepressive effects reach a maximum threshold during the first 10–15 weeks of an exercise program and are then maintained during the remaining weeks. Either way, it seems plausible that mind-body exercise provides a slightly more effective intervention against depressive symptoms in older populations without clinical depression, but that these treatment effects are not substantive enough to constitute statistical difference (we direct the reader to the Extended data for further discussion relating to potential mechanisms for the antidepressant effects of exercise in older adults).

With consideration to projected population estimates over the next decade and the consequential demand on healthcare services ^{1, 8} , the findings from this network meta-analysis offer a message of support for exercise prescription to promote mentally healthy ageing. When considering the collective findings of the present review in conjunction with the recent network meta-analysis in clinically depressed adults aged ≥ 65 years ²³ , stakeholders in healthy ageing and exercise prescription have encouraging pooled RCT evidence for the antidepressant effects of either aerobic, resistance, or mind-body exercise for older adults across the mental health continuum.

Treatment safety is a matter of ongoing importance in gerontological health, and exercise treatment programs are no different. Systematic scrutiny of the included RCTs found that study participants reported no major adverse events and only a few minor somatic complaints ( n = 28). Taken together, this provides encouraging support for personnel wanting to safely prescribe exercise-based intervention programs in older populations. Of course, there is always a possibility of underreporting adverse events in clinical trials, and the present review was no exception. Therefore, the importance of reporting event outcomes, adverse or otherwise, cannot be understated. In fact, there is a known phenomenon in geriatric exercise research whereby adverse events are often underreported because authors do not consider minor adverse events to be noteworthy and/or essential to the primary purpose of the trial ¹⁴⁰ , giving rise to an ongoing issue that will not be corrected until all studies routinely report event outcomes.

Nevertheless, participants engaging in aerobic exercise reported the least adverse events ( n = 3), including minor medical attention and hip pain. Amongst studies included in this meta-analysis, aerobic exercise predominantly involved walking and stationary cycling, which may reflect a safe and natural form of exercise for older adults. Resistance exercise was typically associated with participants experiencing mild muscular pain and falls ( n = 16), which may be explained by the progressive overloading of resistance-based training. Notably, incidents of falling were reported in an unsupervised exercise program. Finally, mind-body exercise was typically associated with different types of muscular pain and body strain ( n = 9). It is speculated that the higher rates of injury in mind-body exercise are predominantly because it incorporates flexibility, balance, and stability movements, which may be unique to older bodies. In general, exercise seems to be a relatively safe intervention for older adults living in both the local community and residential aged care, although intensity and supervision, particularly for resistance training, should be monitored to ensure falls and injury do not occur.

The present review has some notable advantages above a traditional pairwise meta-analysis. RCTs with considerable non-exercising components, such as those using a multicomponent exercise intervention, were excluded because they may have overestimated the magnitude of the true effect in past reviews. Specifically, it is likely that multicomponent exercise interventions such as laughter therapy ¹⁴¹ , depression awareness training ¹²⁹ , or self-efficacy training ¹⁴² may have introduced a risk of bias by inflating the observed effectiveness of the exercise program on depressive symptoms through a secondary, complementary treatment effect. Pairwise meta-analysis also assumes that all control groups are the same, which is not always the case ¹⁸ . To manage heterogeneity from this assumption, control groups were separated into individual network comparisons. Taken together, the current findings provide a more accurate estimate of the true effects of exercise on depressive symptoms in adults aged ≥ 65 years.

The present network meta-analysis is not without limitations. As study participants and personnel cannot be successfully blinded, there is an inherent risk of performance bias. It is also believed that many exercise-based interventions have a small number of participants, shorter follow-up, and do not adequately conceal randomisation ¹⁴³ , which are all likely to reduce the quality of RCTs and increase the risk of bias. However, we mitigated the impact of this by comparing relative effects with multiple control groups in order to increase reliability and specificity. This, combined with the relatively low risk of bias in individual RCTs, were extremely important in minimising overall risk of bias and achieving accurate effect comparisons in the present review.

Since most RCTs did not explicitly describe the exclusion of participants with ongoing diagnosis of clinical depression, there was potential contamination with data from participants with existing clinical diagnosis and medical treatment that may have been underreported. Here, this was managed by explicitly separating (i) participants without clinically diagnosed depression from (ii) participants with clinical depression as described in another recent network meta-analysis ²³ . Within this review, we further mitigated this effect modifier by only including RCTs, where this risk would be counter balanced with respective control participants. Similarly, in the absence of evidence to the contrary, and confirmed by separate analysis (see Extended data), we selected to include a small number of trials where participants met existing criteria in the presence of co-morbidity (i.e., cognitive decline, Parkinson’s disease, dementia). Despite a lack of impact here, we offer this as a cautionary note should evidence of differential antidepressant response to exercise become available for these subgroups, and encourage researchers to report all ongoing pharmacological regimens and co-morbidities in RCTs recruiting older participants.

Although modifying effects were explored using meta-regression, potential compounding effects from exercise modifiers (e.g., fitness improvements, length of program, session frequency and duration, exercise intensity, supervision, group format) were outside the scope of our network meta-analysis. There has been a modicum of such exploration in subgroup and meta-regression analyses of previous reviews ^{4, 16, 35} , providing researchers with an encouraging opportunity in their planning of future similar work. Future meta-analyses with extensive subgroup analyses should explain the heterogeneity of effect sizes between similar exercise intervention studies in older persons.

Figshare: Aerobic, resistance, and mind-body exercise are equivalent to mitigate symptoms of depression in older adults: A systematic review and network meta-analysis of randomised controlled trials (extended data). https://doi.org/10.6084/m9.figshare.12998549.v3 ³² .

This project contains the following underlying data:

Figshare: Aerobic, resistance, and mind-body exercise are equivalent to mitigate symptoms of depression in older adults: A systematic review and network meta-analysis of randomised controlled trials (extended data). https://doi.org/10.6084/m9.figshare.12998549.v3 ³² .

This project contains the following extended data:

Figshare: PRISMA-NMA checklist for “Aerobic, resistance, and mind-body exercise are equivalent to mitigate symptoms of depression in older adults: A systematic review and network meta-analysis of randomised controlled trials (extended data). https://doi.org/10.6084/m9.figshare.12998549.v3 ³²

Data are available under the terms of the Creative Commons Attribution 4.0 International license (CC-BY 4.0).