Types of studies

We will consider all randomised controlled trials (RCTs) for inclusion. Non‐randomised and quasi‐randomised studies will be excluded to minimise the risk of patient selection bias. There will be no language restrictions on included studies and we will translate non‐English articles.

Types of participants

We will include studies of adults (aged 18 years and over) with arthritis of the shoulder joint, confirmed by radiographic examination. We will include participants with primary osteoarthritis and osteoarthritis secondary to rotator cuff tear arthropathy (RCTA).

We will exclude studies of adults undergoing surgery for inflammatory arthritis such as rheumatoid arthritis, benign or malignant tumours, adhesive capsulitis, shoulder instability or fractures.

Types of interventions

We will include studies that compare any type of shoulder arthroplasty (replacement) surgery to any other treatment modality. We will specifically include studies that compare shoulder arthroplasty to placebo (i.e. sham surgery), other surgical modalities (e.g. arthroscopic debridement), non‐surgical modalities (e.g. intra‐articular corticosteroid injections, physiotherapy, acupuncture, etc.) or no treatment. In addition, we will include studies that compare one type of shoulder arthroplasty to another type of shoulder arthroplasty (e.g. conventional total shoulder arthroplasty (TSA) versus reverse total shoulder arthroplasty (RTSA)) or one type of arthroplasty surgical technique to another (e.g. cemented TSA versus uncemented TSA).

Types of outcome measures

Based on the preliminary core domain set described by the OMERACT (Outcome Measures in Rheumatology) Special Interest Group (Buchbinder 2017), we will measure the following major outcomes.

Electronic searches

We will search the following databases, from inception, with no date or language restrictions:

1. The Cochrane Central Register of Controlled Trials (CENTRAL), via the Cochrane Library, Wiley InterScience (www.thecochranelibrary.com);

2. MEDLINE (1966 to present)

3. EMBASE (1988 to present)

4. CINAHL (1937 to present)

5. SportDiscus (1985 to present)

6. Web of Science (1945 to present)

We will also conduct searches of ClinicalTrials.gov (www.ClinicalTrials.gov) and the WHO International Clinical Trials Registry Platform (www.who.int/ictrp/en/).

See Appendix 1, Appendix 2, Appendix 3, Appendix 4, Appendix 5, Appendix 6, Appendix 7, and Appendix 8 for detailed search strategies.

Searching other resources

We will check reference lists of all primary studies and review articles for additional references. In addition, we will search for published congress abstracts from, but not limited to, the American Academy of Orthopedic Surgeons (AAOS), the British Orthopaedic Association (BOA), the American Society of Shoulder and Elbow Surgeons, the British Elbow and Shoulder Society (BESS), the European Society of Shoulder and Elbow Surgery (SECEC) and the European Federation of National Associations of Orthopaedics and Traumatology (EFORT), using the available archives on the relevant society websites. We will search relevant manufacturers' websites for trial information and contact individuals or organisations where appropriate. We will search for errata or retractions from included studies.

Selection of studies

Independently, two review authors (RC, HG) will review the titles and abstracts of studies identified by the searches according to the 'Criteria for considering studies for this review', and discard those that are clearly not relevant. We will then retrieve the full text of those remaining potentially eligible studies. Independently, the same authors (RC, HG) will repeat the selection process by screening the full text versions of these studies, to determine which studies should be included and have data extracted. We will resolve any disagreements by consensus. Where consensus is not achieved initially, a third author (SH or JR) will act as an adjudicator.

We will identify and exclude duplicates and collate multiple reports of the same study 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 a PRISMA flow diagram (PRISMA Group 2009), and 'Characteristics of excluded studies' table.

Data extraction and management

We will use the online review manager 'Covidence' to create a data collection form for study characteristics and outcome data, which will be piloted on at least one study in the review ( Covidence). Independently, two review authors (RC, HG) will extract study characteristics from included studies. Consensus for the final data extraction will be reached by discussion. We will extract the following study characteristics.

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

2. Participants: N, mean age, age range, sex, sociodemographics, ethnicity, disease duration, severity of condition, diagnostic criteria, important condition‐specific baseline data; inclusion criteria, and exclusion criteria.

3. Interventions: the total number of intervention groups within each trial, specific details of each intervention and comparator (e.g. details of the surgery including number of surgeons in the trial, their experience and duration of operation, descriptions of the procedure for tailoring the interventions to individual participants), any co‐interventions and details of rehabilitation following surgery.

4. Outcomes: relevant primary and secondary outcomes specified and collected in the trials, and time points reported.

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

6. Notes: funding for trial, and notable declarations of interest of trial authors.

Independently, two review authors (RC, HG) will extract outcome data from included studies using Covidence. We will extract the number of events and number of participants per treatment group for dichotomous outcomes, and means and standard deviations and number of participants per treatment group for continuous outcomes. We will note in the 'Characteristics of included studies' table whether outcome data were not reported in a usable way and when data were transformed or estimated from a graph. We will resolve disagreements by consensus or by involving a third person (SH or JR). One review author (RC) will transfer data into Review Manager 5 (RevMan 5) (RevMan 2014). We will double‐check that data are entered correctly by comparing the data presented in the systematic review with the study reports.

For numerical data presented only in figures or graphs, we will contact the authors of the original report and request data. Where this is not possible, we will use software for extraction from graphs (e.g. PlotDigitizer) to extract data from the graphs or figures. These data will also be extracted in duplicate.

Where both final and change from baseline values are reported for a given outcome, we will extract the final value; if both unadjusted and adjusted values for the same outcome are reported, we will extract the unadjusted value. If more than one outcome measure is reported in a trial, we will prioritise outcomes based on the hierarchy of major outcomes listed above. Where possible, we will extract data based on intention‐to‐treat analysis.

Assessment of risk of bias in included studies

Independently, two review authors (RC, HG) will assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). We will resolve any disagreements by discussion or by involving another author (SH). We will assess the risk of bias according to the following domains.

1. Random sequence generation

2. Allocation concealment

3. Blinding of participants and personnel

4. Blinding of outcome assessment ‐ self‐reported outcomes

5. Blinding of outcome assessment ‐ physician‐reported outcomes

6. Incomplete outcome data

7. Selective outcome reporting

8. Major baseline imbalance

9. Differences in rehabilitation regime

We will grade each potential source of bias as high, low or unclear, and provide a quote from the study report together with a justification for our judgement in the 'Risk of bias' table. We will summarise the 'Risk of bias' judgements across different studies for each of the domains listed. In addition, we will consider the impact of missing data by key outcomes.

Where information about risk of bias relates to unpublished data or correspondence with a trialist, we will note this in the 'Risk of bias' table. When considering treatment effects, we will take into account the risk of bias for the studies that contribute to that outcome. We will present the figures generated by the 'Risk of bias' tool to provide summary assessments of the risk of bias.

Measures of treatment effect

We will analyse dichotomous data as risk ratios or Peto odds ratios when the outcome is a rare event (approximately less than 10%), and use 95% confidence intervals (CI).

We will analyse continuous data as mean difference (MD) or standardised mean difference (SMD), with 95% CIs, depending on whether the outcome is measured using the same scale or different scales. We will enter data presented as a scale with a consistent direction of effect across studies. When different scales are used to measure the same conceptual outcome, we will back‐translate SMD to a typical scale (e.g. 0 to 10 for pain) as described in Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2011a).

In the 'Effects of intervention' results section and the 'Comments' column of the 'Summary of findings' table, we will provide the absolute per cent difference, the relative per cent change from baseline, and the number needed to treat for an additional beneficial outcome (NNTB). We will provide the NNTB only when the outcome shows a statistically significant difference.

For dichotomous outcomes, such as serious adverse events, we will calculate the NNTB and number needed to treat for an additional harmful outcome (NNTH) from the control group event rate and the risk ratio using the Visual Rx NNT calculator (Cates 2008). We will calculate the NNTB for continuous measures using the Wells calculator (available at the Cochrane Musculoskeletal Group (CMSG) Editorial office, musculoskeletal.cochrane.org). The minimal clinical important difference (MCID) will be used in the calculation of NNTB or NNTH for continuous outcomes; we will assume an MCID of 1.5 points in a 10‐point scale for pain; and 10 points on a 100 ‐point scale for function or disability for input into the calculator.

For dichotomous outcomes, we will calculate the absolute risk difference using the risk difference statistic in RevMan 5 and express the result as a percentage. For continuous outcomes, we will calculate the absolute benefit as the improvement in the intervention group minus the improvement in the control group, in the original units.

We will calculate the relative per cent change for dichotomous data as the risk ratio − 1 and express this as a percentage. For continuous outcomes, we will calculate the relative difference in the change from baseline as the absolute benefit divided by the baseline mean of the control group.

Unit of analysis issues

Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons (e.g. surgical intervention A versus non‐surgical intervention and surgical intervention B versus non‐surgical intervention) are combined in the same meta‐analysis, we will halve the control group to avoid double‐counting.

If multiple time points are reported, we will group them into short‐ (less than one year), intermediate‐ (one to three years), and long‐term (more than three years) follow‐up. If a single trial reports multiple time points within one of these groups, then we will extract the data that relate to the latest time point.

Dealing with missing data

We will contact investigators or study sponsors in order 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). Where 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 by a sensitivity analysis. We will describe any assumptions and imputations we make to handle missing data clearly, and we will explore the effect of imputation by 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 mean difference 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.

Where possible, we will compute missing standard deviations from other statistics such as standard errors, confidence intervals or P values, according to the methods recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b). If standard deviations cannot be calculated, they will be imputed (e.g. from other studies in the meta‐analysis).

Assessment of heterogeneity

We will assess clinical and methodological diversity in terms of participants, interventions, outcomes and study characteristics for the included studies to determine whether a meta‐analysis is appropriate. We will conduct this by observing these data from the data extraction tables. We will assess statistical heterogeneity by visual inspection of forest plots to assess for obvious differences in results between the studies, and using the I² and Chi² statistical tests.

As recommended in theCochrane Handbook for systematic Reviews of Interventions (Deeks 2011), the interpretation of an I² value of 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% represent 'considerable' heterogeneity. As noted in the Cochrane Handbook for systematic Reviews of Interventions, we will keep in mind that the importance of I² depends on: 1) magnitude and direction of effects; and 2) strength of evidence for heterogeneity.

We will interpret a Chi² test P value ≤ 0.10 as indicative of statistical heterogeneity.

If we identify substantial heterogeneity we will report it and investigate possible causes by following the recommendations in section 9.6 of the Cochrane Handbook for systematic Reviews of Interventions (Deeks 2011).

Assessment of reporting biases

We will create and examine a funnel plot to explore possible small study biases. In interpreting funnel plots, we will examine the different reasons possible for funnel plot asymmetry as outlined in section 10.4 of the Cochrane Handbook for systematic Reviews of Interventions and relate this to the results of the review. If we are able to pool more than 10 trials, we will undertake formal statistical tests to investigate funnel plot asymmetry, and will follow the recommendations in section 10.4 of the Cochrane Handbook for systematic Reviews of Interventions (Sterne 2011).

To assess outcome reporting bias, we will check trial protocols against their published reports. For studies published after 1 July 2005, we will screen the Clinical Trial Register at the International Clinical Trials Registry Platform of the World Health Organization (apps.who.int/trialssearch) for the a priori trial protocol. We will evaluate whether selective reporting of outcomes is present.

Data synthesis

We will undertake meta‐analyses only where this is meaningful, that is, if the treatments, participants and the underlying clinical question are similar enough for pooling to make sense. For clinically homogeneous studies, we will pool outcomes in a meta‐analysis using the random‐effects model as a default. We will also examine the results from the fixed‐effect model as sensitivity analyses, to evaluate any bias from smaller studies.

We will restrict the primary analysis for our main outcome measures reported in the 'Summary of findings' table to trials at low risk of detection and selection bias.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses, where data are available, for the following factors thought to influence outcomes (Muh 2013; Simone 2014):

1. age of participant divided into groups: < 55 years, 55 to 64 years, 65 to 74 years, 75 to 84 years, ≥ 85;

2. presence or absence of significant rotator cuff tear.

We will use our seven main outcomes ('Types of outcome measures') in the sub‐group analyses.

We will use the formal test for subgroup interactions in RevMan 5 (RevMan 2014), and will use caution in the interpretation of subgroup analyses as advised in section 9.6 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011).

Sensitivity analysis

We plan to carry out the following sensitivity analyses to investigate the robustness of the treatment effect of pain, disability and function.

1. Inclusion of missing data

2. Inclusion of trials identified at risk of selection bias

3. Inclusion of trials with unclear or inadequate blinding of the outcome assessor

4. The choice of statistical method for pooled data (fixed‐effect versus random‐effects model)