Types of studies

We will include randomised controlled trials. We will include parallel and cross‐over trials (only data from before cross‐over), and cluster‐randomised trials. We will include studies reported as full text, those published as abstract only, and unpublished data.

Types of participants

We will include studies that recruited participants with traumatic or non‐traumatic multidirectional instability (as defined by trialists) with any symptom duration. We will include studies with participants with various shoulder disorders only if the results for participants with multidirectional instability are presented separately.

We will exclude studies that included participants with systemic inflammatory conditions, such as rheumatoid arthritis, osteoarthritis, and hemiplegic shoulders.

Types of interventions

We will include any type of exercise therapy for multidirectional instability. Eligible interventions include supervised or unsupervised exercises, individual exercises, or combinations of various types. Exercise can be land‐ or water‐based, but should consist of shoulder‐specific exercises rather than general activities (e.g. swimming or running). We will accept trials with any content, duration, frequency, or intensity of exercise.

Comparisons

1. Exercise therapy versus placebo

2. Exercise therapy versus no treatment, waiting list, or usual care

Co‐interventions (e.g. electrotherapy and taping) will be allowed as long as they are applied equally to all study groups.

Types of outcome measures

Electronic searches

We will search the following databases, without restrictions on language or date of publication.

1. The Cochrane Central Register of Controlled Trials (CENTRAL; current issue)

2. MEDLINE Ovid (1946 to current; Appendix 1)

3. Embase Ovid (1974 to current)

We will also search the US National Institutes of Health Ongoing Trials Register, ClinicalTrials.gov (www.ClinicalTrials.gov), and the World Health Organization Clinical Trials Registry Platform (ICTRP; www.who.int/ictrp/en/) for ongoing or unpublished trials.

Searching other resources

We will check the reference lists of all included studies and review articles identified in the database searches for additional references. We will also contact experts in the field to ask whether they know about ongoing or unpublished trials.

Selection of studies

Two review authors (MK and TI) will independently screen the titles and abstracts we identify through the search, and code them as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. We will retrieve the full‐text study reports/publication of those we identify as 'retrieve', and two review authors (MK and TI) will independently screen the full text to identify studies for inclusion, and identify and record reasons for exclusion of the ineligible studies. We will resolve any disagreement through discussion, or if required, we will consult a third person (JK).

We will identify and exclude duplicates and collate multiple reports of the same study under a single reference ID so that each study, rather than each report, is the unit of interest in the review. We will record the selection process in sufficient detail to complete the characteristics of excluded studies table, and a PRISMA flow diagram (Page 2021).

Data extraction and management

We will use a data collection form for study characteristics and outcome data, which has been piloted on at least one study from the review.

1. Methods: study design, total duration of study, details of any 'run‐in' period, number of study centres and location, study setting, withdrawals, and date of study

2. Participants: the number of people randomised, the number of people completing treatment, the number of people who withdrew or were lost to follow‐up, mean age, age range, sex, disease duration, diagnostic criteria, inclusion criteria, and exclusion criteria

3. Interventions: type of exercise, supervised or unsupervised, individually or in a group, measurement and reporting of adherence to exercise, setting in which exercises were performed, qualifications of the exercise instructor, exercise content (frequency, intensity, total number of treatment sessions, duration of each session of treatment, length of program), comparisons, and co‐interventions. We will use the Consensus on Exercise Reporting Template (CERT) to extract the characteristics of exercise interventions (Slade 2016).

4. Outcomes: major and minor outcomes as specified and collected; time points when reported, including a description of the measurement tool (i.e. direction of scale)

5. Characteristics of the design of the trial, as outlined in the Assessment of risk of bias in included studies section

6. Notes: funding for the trial, notable declarations of interest of trial authors, intervention adherence (expressed as percentages or number of participants), information about missing data, and contact with study authors

Two review authors (MK and TI) will independently extract the outcome data from the included studies. We will resolve disagreements by consensus, or by involving a third review author (JK). One review author (MK) will transfer the data to Review Manager Web (RevMan Web 2023). We will double‐check that data are entered correctly by comparing the data with the study reports.

We will follow these decision rules to extract data in the event of multiple outcome reporting in trials.

1. If both final values and changes from baseline values are reported for a continuous outcome, we will extract the final values.

2. If both unadjusted and adjusted values are reported for the same outcome, we will extract adjusted values.

3. If data are analysed on the basis of both an intention‐to‐treat (ITT) sample and another sample (e.g. per‐protocol, as‐treated), we will extract the ITT‐analysed data.

Assessment of risk of bias in included studies

Two review authors (MK and TI) will independently assess the risk of bias for each study using the RoB 2 tool (Sterne 2019), outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2023b). We will resolve disagreements by discussion, or by involving another author (TA).

We will assess the risk of bias according to the following domains:

1. bias arising from the randomisation process;

2. bias due to deviations from intended interventions;

3. bias due to missing outcome data;

4. bias in measurement of the outcome;

5. bias in selection of the reported result.

We will use the signalling questions in RoB 2 and rate each domain as low risk of bias, some concerns, or high risk of bias.

We will summarise the risk of bias judgements for each outcome across different studies for each of the domains listed; the overall risk of bias for the outcome will be the least favourable assessment across the domains of bias.

For the results of an outcome to be judged at low risk, all domains must be rated at low risk of bias. We will assess an outcome as having some concerns if we rate the risk of bias as having some concerns in at least one domain, and rate none of the domains at high risk of bias. We will assess an outcome at high risk if we identify at least one domain at high risk of bias. We will also classify an outcome at high risk if we judge several domains as having some concerns, as we consider confidence in such an outcome to be considerably reduced (Higgins 2023b).

We will assess the risk of bias for the major outcomes, with a focus on the effect of the assignment to the intervention (the ITT effect).

Measures of treatment effect

If continuous outcomes are measured on the same scale across studies, we will use the mean difference (MD) and 95% confidence intervals (CIs). If different scales are reported across trials, we will use the standardised mean difference (SMD) and 95% CIs. We will back‐translate SMDs to a typical scale (e.g. 0 to 10 for pain) by multiplying the SMD by a typical among‐person standard deviation (e.g. the standard deviation (SD) of the control group at baseline from the most representative trial (Higgins 2023a)). For dichotomous outcomes, we will use risk ratio (RR) and 95% CI.

We will assume a minimal clinically important difference (MCID) of 1.5 points on a 10‐point scale for pain, and 10 points on a 100‐point scale for function or disability (Tubach 2012).

Unit of analysis issues

When multiple trial arms are reported in a single trial, we will include only the relevant arms. When a trial includes multiple relevant treatment arms, we will combine groups to perform a single pairwise comparison. If this results in the identification of potential heterogeneity, we will analyse each group separately against a common control group. However, to ensure that a common control group is not included multiple times in a meta‐analysis that includes several interventions from the same trial, we will divide the control group by the number of intervention groups to avoid double‐counting. In trials that collected data at different time points within each category, we will use the data at the end of the intervention.

Dealing with missing data

We will contact investigators or study sponsors to verify key study characteristics and obtain missing numerical outcome data where possible (e.g. when a study is identified as an abstract only, or when data are not available for all participants). If this is not possible, and the missing data are thought to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results through a sensitivity analysis. We will clearly describe any assumptions and imputations used when handling missing data, and we will explore the effect of imputation through sensitivity analyses.

For dichotomous outcomes (e.g. number of withdrawals due to adverse events), we will calculate the withdrawal rate using the number of participants randomised in the group as the denominator.

For continuous outcomes (e.g. mean change in pain score), we will calculate the MD or SMD based on the number of participants analysed at that time point. If the number of participants analysed is not presented for each time point, we will use the number of randomised participants in each group at baseline.

If necessary, and when possible, we will compute missing SDs from other statistics, such as standard errors, CIs or P values, according to the methods recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2023a). If we cannot calculate the SDs, we will impute them (e.g. from other studies in the meta‐analysis).

Assessment of heterogeneity

We will assess the clinical and methodological diversity of participants, interventions, outcomes, and study characteristics (e.g. study design and outcome measurement tools) of the included studies to determine whether a meta‐analysis is appropriate. We will assess statistical heterogeneity by visually inspecting the forest plots for obvious differences between study results, and using I² and Chi² statistics. We will interpret the I² statistic as recommended in the Cochrane Handbook for Systematic Reviews of Interventions: 0% to 40% might not be important; 30% to 60% may represent moderate heterogeneity; 50% to 90% may represent substantial heterogeneity; and 75% to 100% represents considerable heterogeneity (Deeks 2023). We will keep in mind that the observed value of I² depends on: (i) the magnitude and direction of effects, and (ii) the strength of evidence for heterogeneity.

When the Chi² has a P value ≤ 0.10, we will interpret this as evidence of statistical heterogeneity.

If we identify substantial heterogeneity (at least 50%), we will report it and investigate the possible causes by following the recommendations in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2023).

Assessment of reporting biases

We will create funnel plots to explore possible small study biases if we have at least 10 studies in a meta‐analysis. If we are able to pool more than 10 trials, we will undertake formal statistical tests to investigate funnel plot asymmetry (Egger 1997), and follow the recommendations in section 13.3 of the Cochrane Handbook for Systematic Reviews of Interventions (Page 2023).

To assess outcome reporting bias, we will check trial protocols against published reports. For studies published after 1 July 2005, we will screen clinical registers at ICTRP and ClinicalTrials.gov for the trial protocols. We will evaluate whether selective reporting of outcomes is present.

Data synthesis

We will undertake meta‐analyses only when this is meaningful, i.e. if the treatments, participants, and underlying clinical questions are similar enough for pooling to make sense. We will consider the following comparisons.

Comparisons

1. Exercise therapy versus placebo

2. Exercise therapy versus no treatment, waiting list, usual care

We will analyse the data using Review Manager Web (RevMan Web 2023). We will use a random‐effects model in the meta‐analysis, based on the assumption that clinical diversity and methodological heterogeneity is likely to exist, and have an impact on the results. We will include all studies in the primary analysis, regardless of the risk of bias.

Subgroup analysis and investigation of heterogeneity

We will undertake subgroup analyses for two of the major outcomes, pain and shoulder instability, at the primary time point (end of intervention), if data are available.

1. Age (≤ 18 years or > 18 years)

Younger people may not fare as well as older people, because multidirectional instability usually improves with age (Misamore 2005). A previous study examined the recurrence rate in participants with shoulder instability under the age of 18 years, and reported that young people aged 14 to 18 years were more likely to experience recurrent instability. Considering populations with different skeletal maturity, it is expected that age will also affect treatment efficacy in multidirectional instability (Olds 2016).

2. Athletes or non‐athletes (as defined by the trial authors)

Athletes may be more prone to overuse syndromes, with an increased risk of converting generalised capsular laxity to symptomatic instability (Beasley 2000). Therefore, shoulder instability may be more severe in athletic participants with multidirectional instability.

3. Duration of exercise therapy (≤ 12 weeks or > 12 weeks)

The duration of exercise therapy is expected to affect treatment effectiveness. Positive changes in shoulder instability, pain, and muscle strength have been observed in participants with multidirectional instability who received 12 weeks of exercise therapy (Watson 2018).

4. Traumatic or non‐traumatic (as defined by the study authors)

A previous study showed that participants with traumatic multidirectional instability had a higher rate of poor exercise outcomes (Burkhead 1992).

5. Exercise adherence (≤ 80％ or > 80％)

An association between exercise adherence and improved clinical outcomes has been suggested in people with musculoskeletal diseases (Patterson 2021; Pisters 2010).

Sensitivity analysis

We will conduct sensitivity analyses to investigate the robustness of the treatment effect for two of the major outcomes, pain and shoulder instability, if data are available.

1. Risk of bias: we will remove studies that we judged at an overall risk of bias of having some concerns, or at high risk.

2. The impact of excluding studies in which we imputed values for missing data during the review process

3. The impact of excluding studies with poorly or inadequately described comparisons, classified as placebo or no treatment groups

Summary of findings and assessment of the certainty of the evidence

We will follow the guidelines in the Cochrane Handbook for Systematic Reviews of Interventions, Chapters 14 and 15 for interpreting results (Schünemann 2023a; Schünemann 2023b). We will take care to distinguish between a lack of evidence of effect and a lack of effect. We will base our conclusions only on the findings from the quantitative or narrative synthesis of the included studies. We will avoid making recommendations for practice; our implications for research will suggest priorities for future research, and outline the remaining uncertainties in the area.

We will create two summary of findings (SoF) tables at the primary time point (end of intervention); one for the main comparison, exercise versus placebo; and another for the comparison, exercise versus no treatment, waiting list, or usual care. We will create a SoF table using the following outcomes. We will use methods and recommendations described in the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2023a).

1. Overall pain

2. Shoulder instability

3. Participant's global assessment of treatment success

4. Health‐related quality of life (HRQoL)

5. Number of participant withdrawals due to adverse events

6. Number of participants who experienced an adverse event

Two review authors (MK and TI) will independently assess the certainty of the evidence, with disagreements resolved by discussion, or by involving a third review author (TA). We will use the five GRADE considerations (study limitations (risk of bias), consistency of effect, imprecision, indirectness, and publication bias) to assess the certainty of a body of evidence as it relates to the studies that contribute data to the analyses for each outcome. We will report the certainty of evidence as high, moderate, low, or very low.

We will use GRADEpro GDT software to prepare the SoF tables (GRADEpro GDT). We will justify all decisions to downgrade the certainty of evidence for each outcome in footnotes, and we will provide comments to aid the reader's understanding of the results, when necessary.