Types of studies

We included randomised controlled trials (RCTs) and the first period of cross‐over RCTs. We excluded quasi‐randomised controlled trials (i.e. trials in which assignment to treatment was made using a non‐random method such as alternation) because the method of allocation may lead to biased estimates of effect. We did not restrict study eligibility by language or publication status.

We only included health economic studies conducted alongside studies that were included in the clinical component of this systematic review (Shemilt 2011).

Types of participants

We included studies with women aged 18 years or more who were diagnosed as having urinary incontinence on the basis of symptoms, signs or urodynamic evaluation (as defined by the trial authors). We only included trials that recruited both men and women if at least 90% of participants were women or if the trial provided demographic and outcome data separately for women. We included trials with women diagnosed as having stress, urgency or mixed urinary incontinence, as well as trials with participants who had mixed or unclassified types of urinary incontinence.

We included trials carried out on women who were experiencing urinary incontinence during the antenatal or postnatal period. Because this group has physiological differences from women who are not pregnant or postpartum, and the natural history of incontinence in this population differs from that in non‐pregnant women, the observed effects of the intervention may differ in this group. We therefore did not group this population with women who were not pregnant or postpartum and we planned to analyse the studies separately throughout the review.

We excluded studies of women who had urinary incontinence thought to be due to factors beyond the urinary tract such as neurological or psychiatric disorders, cognitive impairment, or mobility problems. We also excluded studies that focused on women who were experiencing nocturnal enuresis.

Types of interventions

We included studies of yoga as a treatment for urinary incontinence, where the study report specified that the intervention was 'yoga' provided at any dose, with any frequency and for any duration, because we believe these factors are likely to vary in practice.

We included interventions that belonged to any yoga tradition but excluded studies in which the yoga intervention did not include a physical practice component. We included studies that compared yoga to no treatment or to another active treatment. We also included studies that compared yoga as an adjunct to other treatments versus those same treatments without yoga. The types of included comparisons were as follows.

• Yoga versus no specific active intervention (e.g. usual care, waiting list).

• Yoga versus an active intervention (e.g. lifestyle intervention or pelvic floor muscle training), for which we considered different active comparators separately (e.g. yoga versus lifestyle advice, yoga versus pelvic floor muscle training).

• Yoga plus an intervention versus the same intervention without yoga (e.g. yoga as an add‐on intervention to pelvic floor training versus pelvic floor training alone), for which we considered different interventions separately.

We included studies in which co‐interventions were provided if they were similar between intervention groups (e.g. both the yoga and the comparison groups received advice on behavioural management techniques).

Studies that compare yoga to a sham yoga intervention do not appear to be common (Park 2014). However, we planned that we would consider such studies to represent an additional type of comparison (i.e. yoga versus sham yoga) and would analyse them separately.

We excluded studies of interventions based on yoga (e.g. exercises based on yoga postures) but not characterised as yoga, as well as studies of multimodal interventions in which yoga is only one component amongst others, such as mindfulness‐based stress reduction (MBSR).

Types of outcome measures

We used outcomes suggested by the Standardisation Committee of the International Continence Society (Bø 2017; Haylen 2010). The following five categories of outcomes are recommended for research investigating the effect of therapeutic interventions for women with urinary incontinence (Lose 2001):

• The woman’s observations (e.g. symptoms);

• Quantification of the woman's symptoms (e.g. urine loss);

• The clinician’s observations (anatomical and functional signs);

• The woman's quality of life (urinary incontinence ‐ specific and general);

• Economic measures.

In this review, we considered at least one outcome from each of the first four categories. We included specific outcomes that are commonly found in other Cochrane Incontinence reviews for urinary incontinence in women so that this review may produce results that are easily compared to or combined with those of other reviews of treatment for the same condition.

Electronic searches

Searching other resources

We checked the reference lists of all included studies and systematic reviews for additional references. We contacted experts in the field and authors of included studies to identify additional unpublished studies. We also checked the proceedings of the following conferences for relevant research:

• International Congress on Complementary Medicine Research (ICCMR) (2010 to 2017); and

• European Congress for Integrative Medicine (ECIM) (2009, 2011 to 2017).

Selection of studies

Two review authors independently screened the titles and abstracts of all retrieved references in Covidence (Covidence 2017). We retrieved the full‐text study reports for all citations that at least one review author considered potentially relevant. Two review authors independently screened the full‐text articles and identified studies for inclusion and identified and recorded reasons for excluded studies in the Characteristics of excluded studies. Any disagreements were resolved by discussion.

We collated multiple reports of the same study so that each study, rather than each report, was the unit of interest in the review. We recorded the selection process in sufficient detail to complete a PRISMA flow diagram (Moher 2009).

Data extraction and management

We used a standardised piloted data collection form in Microsoft Excel 2018 for Mac Version 16.20 and extracted the following study characteristics and outcome data.

• Methods: study design.

• Participants: number randomised, number with each type(s) of incontinence and how incontinence was diagnosed, if participants were pregnant or postpartum, how many were pregnant and how many were postpartum, severity and duration of urinary incontinence if reported, study participant mean age or age range, study location and setting, recruitment methods and inclusion and exclusion criteria.

• Interventions: description of yoga intervention characteristics, dose and duration of yoga intervention, description of comparison intervention characteristics, adherence to the yoga and comparison interventions, description of any co‐interventions, length of follow‐up, number of withdrawals and reasons for withdrawal.

• Outcomes: description of primary and secondary outcomes in the review that were reported in the trial, and listing of other outcomes collected in the trial.

• Notes: funding for trial and notable conflicts of interest of trial authors.

• 'Risk of bias' assessment.

Two review authors independently extracted outcome data from the included studies into Microsoft Excel 2018 spreadsheets and compared the data to identify any discrepancies in data entry. Any disagreements were resolved by consensus. We noted in the Characteristics of included studies if a trial did not report outcome data in a usable way. We transferred all outcome data into Cochrane’s Review Manager 5 software (Review Manager 2014).

In addition to extracting data from included studies as described above, we planned to include an appendix of bibliographic detail of any identified economic studies. As such, we did not conduct a further review of potential economic studies.

Assessment of risk of bias in included studies

Two review authors (LSW, ZSL) independently assessed the risk of bias for each included trial using Cochrane's 'Risk of bias' tool (Higgins 2011a). Any disagreements were resolved by discussion. We assessed the risk of bias for the following domains: random sequence generation (selection bias), allocation concealment (selection bias), blinding of participants and personnel (performance bias), blinding of outcome assessment for each outcome (detection bias), incomplete outcome data (attrition bias), selective outcome reporting (reporting bias) and other bias (such as validity of outcome measure and baseline comparability).

We assessed each potential source of bias as either high, low, or unclear and provided a quotation from the study report together with a justification for our judgement in the 'Risk of bias’ tables. We summarised the judgements across different studies for each of the domains listed.

The participants and personnel in most yoga trials are not blinded. As the primary outcomes of this review depended upon the perception and reporting of the study participant, we have not included blinding of personnel, participants or outcome assessors in our dichotomising of trials into higher versus lower risk of bias. Instead, for our sensitivity analyses of the primary outcomes by higher versus lower risk of bias, we classified studies as having a relatively lower risk of bias if they had a low risk of bias for random allocation, allocation concealment and incomplete outcome assessment, and did not have a high risk of bias for selective outcome reporting or other bias (see Sensitivity analysis).

Measures of treatment effect

We uploaded the outcome data for each study into the data tables in Review Manager 5 to calculate treatment effects (Review Manager 2014). We used the risk ratio (RR) for dichotomous outcomes related to benefit of treatment (e.g. cure). We used the absolute risk difference (RD) for adverse events. We used the mean difference (MD) for continuous outcomes reported on the same scale, and the standardised mean difference (SMD) for continuous outcomes measured on different scales in different trials included in the same meta‐analysis. We expressed the uncertainty with 95% confidence intervals (CIs) for all effect estimates.

If the included studies only reported effect estimates and their CIs, standard errors or exact P values, we uploaded these data into Review Manager 5 in order to apply the generic inverse variance method (Review Manager 2014). We ensured that higher scores for continuous outcomes had the same meaning for a given outcome and explained the direction to the reader. When we were unable to enter the results in either of the above ways, we described them in the Characteristics of included studies or entered the data into the Additional tables.

Unit of analysis issues

Where appropriate, we planned to include the first period of cross‐over studies. We also planned to include cluster‐randomised studies if they were suitable according to the guidance in Chapter 16 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b).

Dealing with missing data

We contacted investigators or study sponsors in order to verify key study characteristics and to obtain missing numerical outcome data where possible. If numerical outcome data such as standard deviations (SDs) or correlation coefficients were missing, we attempted to calculate them from other available statistics, such as P values, according to the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). If we were unable to obtain a full report even after contacting the study authors, we listed the study as 'awaiting classification'.

Assessment of heterogeneity

We assessed clinical heterogeneity (i.e. differences in study populations, interventions and outcomes) between studies qualitatively. For studies that we judged to have sufficient clinical homogeneity to combine in a meta‐analysis, we planned to assess heterogeneity in three ways: visual examination of the forest plots; the Chi² test (P ≤ 0.10) for heterogeneity; and the I² statistic, which describes the per cent of the variability in the estimate that is due to clinical or methodological heterogeneity rather than to chance. We planned to consider the implications of the observed value of the I² statistic as follows:

• 0% to 40%: might not be important;

• 30% to 60%: may represent moderate heterogeneity;

• 50% to 90%: may represent substantial heterogeneity;

• 75% to 100%: considerable heterogeneity (Deeks 2011).

We planned to assess the importance of the value of the I² statistic in light of the range and direction of effects as observed from the forest plots and the strength of the evidence for heterogeneity based upon the Chi² test (Deeks 2011). We planned to seek and discuss plausible explanations for observed statistical heterogeneity. We planned to investigate causes of heterogeneity between trials, qualitatively assessing any differences between individual trials in the populations and interventions. We also planned to explore heterogeneity through the use of subgroup and sensitivity analyses.

Assessment of reporting biases

We searched study registries of prospectively registered trials to identify completed, but not published, trials. We planned to use a funnel plot and Egger's test to assess the potential for publication bias in meta‐analyses with more than 10 trials (Egger 1997; Sterne 2011).

Data synthesis

Where trials were clinically comparable (i.e. clinical comparability of population, intervention, comparison, outcome and timing of measurement), we planned to combine the outcome data from the individual trials in a meta‐analysis using Review Manager 5 (Review Manager 2014). We planned to analyse pregnant and postpartum women separately in call cases. However, for non‐pregnant, non‐postpartum populations, we planned to group together women with SUI, UUI, MUI and mixed or unclear urinary incontinence diagnoses in the primary analysis, and examine different types of urinary incontinence diagnoses using subgroup analyses (see Subgroup analysis and investigation of heterogeneity).

As yoga is a complex intervention with variations in practice components and implementation and we expected some between‐study variation due to these factors, we planned to use the random‐effects model for meta‐analysis.

When outcome data from individual trials were not sufficiently similar to be combined quantitatively, we planned to narratively describe the results from clinically comparable trials.

Subgroup analysis and investigation of heterogeneity

As the mechanisms of SUI and UUI are different, the effects of yoga may vary across types of urinary incontinence. We planned that if there were sufficient data, we would carry out subgroup analyses by type of urinary incontinence in the following groups:

• SUI;

• UUI;

• MUI; and

• a range of urinary incontinence diagnoses, where data are not reported separately by urinary incontinence subgroup.

If sufficient data become available, we also plan to conduct subgroup analyses of trials conducted in older (mean age 65 years or greater) versus younger populations, as populations from different age groups may vary in their ability to perform yoga. Among women who are pregnant or postpartum, we plan to perform subgroup analyses of trials conducted in women who are pregnant versus postpartum, as the natural history of incontinence is different in the two states. We also intend to carry out subgroup analyses by style (e.g. Iyengar yoga, Viniyoga, Yin yoga), dose and duration of yoga intervention to determine whether type of yoga, amount of yoga or duration of yoga modifies the effect of the yoga intervention.

Sensitivity analysis

When both endpoint and change data were available, we used endpoint data for our primary analysis and carried out a sensitivity analysis to check whether the results varied according to endpoint versus change data. In cases where study participants were lost to follow‐up and intention‐to‐treat analyses were conducted using imputation alongside available‐case analyses, we used the observed data for our primary analysis and performed a sensitivity analysis to check whether the results varied according to imputed versus available‐case data. In cases where both unadjusted and adjusted data were available, we used the unadjusted data for our primary analysis and performed a sensitivity analysis to check whether the results varied according to adjusted versus unadjusted data.

If sufficient data become available, we plan to assess the robustness of our conclusions by excluding studies that we judge to have a high risk of bias from our meta‐analyses for the primary outcomes.