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Cochrane Database of Systematic Reviews Protocol - Intervention

Hyaluronate for shoulder osteoarthritis

Authors' declarations of interest

Version published: 27 March 2017 Version history

https://doi.org/10.1002/14651858.CD012617
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Abstract

This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:

To assess the benefits and harms of hyaluronate injections for treating people with OA of the glenohumeral joint in the shoulder.

Background

Description of the condition

Osteoarthritis (OA) is a common joint disease that affects cartilage and bone (Bellamy 2006). Shoulder pain affects up to 20% of the general population in the United States and in Western countries (Chard 1991; Miller 1993). Shoulder OA is the final diagnosis in 5% of those who report shoulder pain (Meislin 2005). Although the pain is not as great as in other joints, shoulder OA, or glenohumeral OA, causes considerable discomfort (Millett 2008). Shoulder OA is characterised by gradual wear and breakage of the articular surface of the glenoid rim and humeral head. As the cartilage becomes worn, friction within the joint is increased, gradually diminishing the normal load‐bearing cartilage. Patients usually have progressive pain, stiffness and disability over the involved shoulder joint with disease progression (Millett 2008). Loss of shoulder function leads to problems in motion, labouring activity and working performance (Kerr 1985). Causes of shoulder OA can be classified simply into two categories: primary and secondary. Primary OA has no specific known aetiology but is more prevalent than secondary OA and is not limited to the elderly (Memel 2000). Secondary OA has a known cause or predisposing factor, such as major trauma (fracture or instability), inflammatory arthropathy, congenital malformation, genetic predisposition or chronic rotator cuff tear (Kerr 1985).

Description of the intervention

Non‐surgical treatments for patients with shoulder OA include non‐pharmacological and pharmacological therapies. Non‐pharmacological therapies consist of physical therapy, aerobic exercise and muscle strengthening (Page 2014a; Page 2014b; Van der Windt 2003). The most common pharmacological therapies include oral analgesics, non‐steroidal anti‐inflammatory drugs (NSAIDs), corticosteroids and nutritional supplements (e.g. glucosamine, chondroitin) (Derry 2016; Hochberg 2012; Shamoom 2000; Towheed 2006). In fact, the efficacy of most conservative interventions for shoulder OA has not been confirmed (Green 2006; Zhang 2004). Similar to other therapies, intra‐articular steroid injection may provide benefit for pain (Bloom 2012; Buchbinder 2003). In knee OA, intra‐articular corticosteroids may lead to moderate improvement in pain and small improvements in physical function (Jüni 2015). Intra‐articular platelet‐rich plasma injection is another treatment option for patients with OA, but its value and efficacy in treating shoulder OA remain unclear (Di Matteo 2016).

In 1997, the US Food and Drug Administration (FDA) approved viscosupplementation with hyaluronate (HA) and its derivatives for treatment of patients with OA (Lo 2003). HA has provided pain relief and functional improvement for people with knee OA (Bellamy 2006). Studies on HA injected into the shoulder have described benefit for pain relief (Itokazu 1995; Silverstein 2007; Valiveti 2006). In 2007, the European Medicines Agency (EMEA) extended approval of HA to treatment of patients with ankle and shoulder OA (EMEA 2007).

A systematic review reported that HA injection may be effective in treating patients with chronic painful shoulder, but as participants were not limited to people with glenohumeral OA, assessment of risk of bias in this systematic review was limited, and benefits of HA injection for glenohumeral OA remain unclear (Saito 2010). One randomised placebo‐controlled trial in people with chronic shoulder pain due to various disorders, including but not limited to glenohumeral joint OA, reported improved pain relief with HA therapy (Blaine 2008); a second trial restricted to those with glenohumeral OA did not report any benefit of intra‐articular HA therapy (Kwon 2013).

How the intervention might work

The primary role of synovial fluid consists of lubricating the joints and providing nutrition to the cartilage. Synovial fluid is a filtrate from plasma that includes a large amount of hyaluronic acid, a polysaccharide that contributes to the elastoviscosity of synovial fluid and protects surrounding joint tissues (including cartilage, synovial tissue, capsule and ligament) from mechanical damage (Balazs 1985). With progression of OA, the concentration and molecular weight of HA are decreased, making synovial fluid less viscous (Altman 1992). Changes in synovial fluid decrease its protective effects and make articular cartilage susceptible to injury (Balazs 1982).

Injections of HA may replace synovial fluid with low viscoelasticity with solutions of higher viscosity (Balazs 1993). Meanwhile, HA can protect the tissue from free radical damage and may have anti‐inflammatory effects (Tammi 1988; Wisnienski 1997). Some reports show that HA supplementation may improve pain and function in patients with OA, probably as the result of modulation of early inflammatory responses (Ghosh 2002).

Why it is important to do this review

Use of hyaluronate has been accompanied by a substantial economic burden for healthcare systems. For example, in 2012, US Medicare paid $287 million for the hyaluronic acid product and associated joint injection (Schmajuk 2014). Thus, HA treatment in shoulder OA is potentially costly; results from limited trials in people with glenohumeral OA are conflicting (Blaine 2008; Kwon 2013), and systematic review evidence is lacking for people with chronic shoulder pain due to glenohumeral OA as opposed to a variety of shoulder disorders (Saito 2010).

Another Cochrane review has separately considered different surgical interventions for shoulder OA (Singh 2010). Total shoulder arthroplasty seems to offer an advantage in terms of shoulder function and provides no clinical benefit over that provided by hemiarthroplasty. Additional randomised trials are warranted to compare shoulder surgery versus sham, placebo and other non‐surgical treatments.

To explore this uncertainty, we plan to conduct a systematic review to evaluate the benefits and harms of HA injection in treating patients with shoulder OA. We will conduct this review according to guidelines provided by the Cochrane Musculoskeletal Group Editorial Board (Ghogomu 2014).

Objectives

To assess the benefits and harms of hyaluronate injections for treating people with OA of the glenohumeral joint in the shoulder.

Methods

Criteria for considering studies for this review

Types of studies

We will include all randomised and quasi‐randomised studies (using a method of participant allocation to treatment that is not strictly random, e.g. date of birth, hospital record number, alternation). We will include studies reported as full text, those published as abstract only and unpublished data. We will apply no language restrictions.

Types of participants

We will include participants younger than 18 years of age with a diagnosis of primary shoulder OA. We will also include participants with unspecified chronic shoulder pain, provided inclusion and exclusion criteria are compatible with a diagnosis of primary OA. The diagnosis of OA should reflect symptoms and radiological appearances characteristic of OA (Weinstein 2000) and should be confirmed by a physician.

We will exclude individuals with a history of significant injury or fracture and those with systemic inflammatory conditions other than OA (such as rheumatoid arthritis or polymyalgia rheumatica).

If trials report shoulder OA and OA elsewhere or other shoulder disorders, we will include only trials that provide separate data for participants with shoulder OA.

Types of interventions

We will include intra‐articular glenohumeral HA injection of any dose, composition and frequency.

Comparator interventions will include placebo; intra‐articular (glenohumeral) HA injections of different dose, composition and frequency; and other available treatments, such as analgesics, nutritional supplements, physiotherapy, steroids, platelet‐rich plasma injection and surgery.

We will allow the following co‐interventions as long as they are used by all treatment groups equally: analgesics, nutritional supplements, physiotherapy, steroids, platelet‐rich plasma (PRP) injections and surgery.

Main planned comparisons

We will examine the following main comparisons if relevant data are available.

  • Hyaluronate therapy (any dose) versus placebo.

  • Hyaluronate therapy versus steroid injection.

  • Hyaluronate therapy versus analgesics.

  • Hyaluronate therapy versus exercise or physiotherapy.

  • Hyaluronate therapy versus PRP.

  • Hyaluronate therapy of various doses.

  • Hyaluronate therapy versus surgery.

Types of outcome measures

Major outcomes

  • Overall pain measured by visual analogue scale (VAS), verbal rating score (VRS), numerical rating scale (NRS), descriptive scales such as the short‐form McGill Scale (Melzack 1987; range 0 to 45; higher denotes worse pain) or other validated instruments used to measure pain.

  • Function or disability, assessed by upper limb functional outcome measures instruments, including but not limited to:

    • Western Ontario Osteoarthritis of the Shoulder Index (WOOS) (Lo 2001);

    • American Shoulder and Elbow Surgeons (ASES) Shoulder Score (Richards 1994);

    • Shoulder Pain and Disability Index (SPADI) (Breckenridge 2011);

    • University of California at Los Angeles (UCLA) Shoulder Scale (Amstutz 1981);

    • Constant score: contains both subjective and objective elements (Constant 1987);

    • Neer rating (Neer 1982); and

    • Disability of the Arm, Shoulder and Hand (DASH) (Hudak 1996).

  • Participant‐rated global assessment of success. We will accept both dichotomous measures (such as participant reporting success or not, or score improvement above 30% indicating success) and continuous measures (e.g. VAS global).

  • Health‐related quality of life measures, such as Short Form‐36 (SF‐36) (Ware 1992) and EuroQoL (EQ‐5D) (Linde 2008).

  • Proportion of participants proceeding to surgery.

  • Proportion of participants with adverse events.

    • Local adverse events, such as shoulder stiffness, instability, infection, injection site pain, skin peeling and nerve damage.

    • Systemic adverse events, such as thromboembolism; other pulmonary, cardiac and gastrointestinal events; and others.

  • Proportion of participants with serious adverse events (i.e. leading to hospitalisation, disability or death).

Minor outcomes

  • Functions assessed by range of motion (active and passive), muscle strength or recurrence of symptoms (portion and time to recurrence).

  • Numbers of participants returning to previous activities (work, sport, activities of daily living, etc.), including time to return.

  • Radiographic structural change of the glenohumeral joint (Weinstein 2000): stage 1: normal radiograph; stage 2: minimal joint space narrowing with a concentric head and glenoid; stage 3: moderate joint space narrowing with early inferior osteophyte formation; and stage 4: loss of joint space with osteophyte formation and loss of concentricity between humeral head and glenoid.

  • Withdrawals due to adverse events.

Time points

If outcomes are reported at multiple time points, we will extract endpoint data at the following time periods: short‐term follow‐up (up to three months following treatment) ‐ the primary time point for this review; intermediate follow‐up (longer than three months and up to one year after completion of treatment); and long‐term follow‐up (longer than one year after completion of treatment).

Search methods for identification of studies

Electronic searches

We will search databases including the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, Embase, the Cumulative Index to Nursing and Allied Health Literature (CINAHL), Ovid SPORTdiscus and Science Citation Index (Web of Science) for relevant randomised and quasi‐randomised trials.

We will search trial registers including ClinicalTrials.gov (www.clinicaltrials.gov) and the World Health Organization International Clinical Trials Registry Platform (WHO ICTRP) (www.who.int/ictrp/en/).

For adverse events, we will conduct a separate search of websites of regulatory agencies, including the US Food and Drug Administration‐MedWatch (www.fda.gov/Safety/MedWatch/default.htm), the European Medicines Evaluation Agency (www.emea.europa.eu), the Australian Adverse Drug Reactions Bulletin (www.tga.gov.au/publication/australian‐adverse‐drug‐reactions‐bulletin) and the UK Medicines and Healthcare products Regulatory Agency (MHRA), for drug safety updates (www.gov.uk/drug‐safety‐update).

We will search all databases from their inception to the present, and we will impose no restrictions on the language of publication.

See Appendix 1 for the search strategy applied for MEDLINE.

Searching other resources

We will check the reference lists of all included studies and relevant review articles for additional relevant trials. We will search relevant manufacturers' websites for trial information, including Hylan GF‐20 (Synvisc) ‐ Sanofi‐Aventis (http://www.sanofi.us/l/us/en/index.jsp), Gel‐One ‐ Zimmer (http://www.zimmer.com/medical‐professionals/products/biologics‐sports‐medicine/gel‐one.html), SUPARTZ ‐ Bioventus LLC (http://supartzprofessional.com/index.cfm), EUFLEXXA ‐ Ferring Pharmaceuticals (http://www.euflexxa.com) and Orthovisc ‐ DePuy Mitek (https://www.orthovisc.com).

We will search for errata or retractions from included studies published in full text on PubMed (www.ncbi.nlm.nih.gov/pubmed) and will report in the review the date this was done.

Data collection and analysis

Selection of studies

Two review authors (LTK and YSL) will independently screen the titles and abstracts of items found during the search to identify potentially eligible trials, and will code them as 'retrieve' (potentially eligible) or 'do not retrieve'. We will retrieve the full texts of potentially eligible studies; two review authors (LTK and YSL) will independently examine these full texts to determine if the trial should be included and will record reasons for exclusion of ineligible studies. We will resolve disagreements by discussion and, when necessary, through adjudication by a third review author (CCC).

We will identify and exclude duplicates and will collate multiple reports of the same study, so that each trial, 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 (Preferred Reporting Items for Systematic Reviews and Meta‐Analyses) study flow diagram and a 'Characteristics of excluded studies' table.

Data extraction and management

We will use a data collection form that has been piloted on at least one trial included in the review to document study characteristics and outcome data. One review author (LTK) will extract the following study characteristics from included studies. A second review author (YSL) will spot‐check study characteristics for accuracy against the trial report.

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

  • Participants: number, mean age, age range and sex of participants; disease duration, severity of condition, diagnostic criteria and important baseline characteristics; inclusion and exclusion criteria of participants.

  • Interventions: intervention, comparison, co‐interventions and prohibited co‐interventions. We will extract details including HA injection dose, frequency, molecular weight, generic name and manufacturer's name.

  • Outcomes: major and minor outcomes specified and collected, time points when outcomes were measured.

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

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

Two review authors (LTK and YSL) will independently extract outcome data from the included trials. We will extract number of events and participants per treatment group for dichotomous outcomes; and means, standard deviations and number of participants per treatment group for continuous outcomes. We will note in the 'Characteristics of included studies' table if outcome data were not reported in a useable way, and when data have been transformed or estimated from a graph. We will resolve disagreements by consensus with a third review author (CCC). One review author (LTK) will enter data into the Review Manager (RevMan 2014) file. We will double‐check whether data have been entered correctly by comparing data presented in the systematic review against the study reports. We will contact the authors of included trials to obtain more information if needed.

If more than one measure for an outcome is reported within or across trials, we will extract information according to the following rules.

  • For pain, we choose VAS as the preferred measure over other measures such as NRS or the McGill Scale. We will combine different measures using the methods described under Measures of treatment effect. If studies report different types of pain, we will extract overall pain preferentially over unspecified pain, pain on motion, rest pain or night pain.

  • If multiple measures of function are reported, we will combine them in the following hierarchy: WOOS; ASES score; SPADI; UCLA score; Constant score; DASH; others.

  • For quality of life (QoL), we choose SF‐36 as the preferred measure over other measures, such as EQ‐5D or other scales.

  • In the case of multiple outcome reporting in single trials, we will adopt the following decision rules to select which data to extract.

    • If both final values and change from baseline values (and corresponding standard deviations) are reported for the same outcome, we will preferentially extract change from baseline values.

    • If both unadjusted and adjusted for baseline values are reported for the same outcomes, we will extract adjusted values.

  • When possible, we will extract outcomes based on intention‐to‐treat (ITT) analyses.

  • If outcomes are reported at multiple time points, we will extract the time point nearest but not exceeding three months following treatment; one year following treatment; and the latest time point after one year following treatment.

Assessment of risk of bias in included studies

Two review authors (LTK and YSL) will independently assess the risk of bias for each included trial using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). We will resolve disagreements by discussion with a third review author (CCC), and we will assess risk of bias in the following domains.

  • Random sequence generation.

  • Allocation concealment.

  • Blinding of participants and personnel.

  • Blinding of outcome assessment: We will assess risk of bias separately for self‐reported subjective outcomes (pain, function, quality of life, global success) and objective outcomes (proportion proceeding to surgery, adverse events, serious adverse events).

  • Incomplete outcome data.

  • Selective outcome reporting.

  • Other bias: any other possible concerns about bias, such as major imbalances in baseline characteristics (e.g. age, gender, concomitant rotator cuff tear) and performance bias resulting in major differences in care programmes, including route of HA injection, size of syringes and image‐guided injection.

We will rate each potential source of bias as high, low or unclear and will provide a quote from the study report together with a justification for our judgement in the 'Risk of bias' table. We will summarise risk of bias judgements across different studies for each domain listed. We will consider blinding separately for different key outcomes when necessary (e.g. for unblinded outcome assessment, risk of bias for proportion having surgery may be different than for a participant‐reported pain scale). As well, we will consider the impact of missing data by key outcomes.

When information on risk of bias is related 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 studies that contributed to that outcome.

We will present figures generated by the risk of bias tool to provide summary assessments of risk of bias.

We will conduct this review according to this published protocol and will report deviations from it in the 'Differences between protocol and review' section.

Measures of treatment effect

We will analyse dichotomous data (e.g. proportion of participants proceeding to surgery, proportion of participants with adverse events, proportion of participants with serious adverse events) as risk ratios or Peto odds ratios with 95% confidence intervals (CIs) when the outcome is a rare event (approximately < 10%). We will analyse continuous data (e.g. pain score, functional score, QoL score) as mean differences with 95% CIs when the same scale is used to measure the outcome.

When primary studies express the same variable using different instruments and different units of measure, we will use standardised mean differences (SMDs) with 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. standard deviation of the control group at baseline from the most representative trial) (Schünemann 2011b). We will analyse time‐to‐event data (e.g. time to recurrence of symptoms, time to return to prior activities) as hazard ratios. We will analyse rare data by using Poisson methods.

In the 'Effects of interventions' 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) with 95% CIs and the number needed to treat for an additional harmful outcome (NNTH) with 95% CIs (NNTB otr NNTH will be provided only when the outcome shows a statistically significant difference between treatment groups).

For dichotomous outcomes, such as adverse events, we will calculate the NNTB or 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 by using the Wells calculator (available at the CMSG Editorial Office).

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

We will calculate the relative percent change for dichotomous data as the risk ratio ‐ 1 and will 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

The unit of analysis will be all participants in included trials.

Cluster‐randomised trials

For cluster‐randomised trials, if clustering is not accounted for in primary studies, we will present data in a table and will use a (#) symbol to indicate the presence of a probable unit of analysis error. We will seek to contact first authors of trials to obtain intraclass correlation coefficients (ICCs) for clustered data and to adjust for this by using accepted methods (Gulliford 1999). When clustering has been incorporated into the analysis of primary studies, we will present these data as if from a non‐cluster‐randomised trial but will adjust for the clustering effect.

We will present binary data as divided by a 'design effect'. We will calculate this by using the mean number of participants per cluster (m) and the ICC as follows: [Design effect = 1 + (m ‐ 1) * ICC] (Donner 2002). If the ICC is not reported, we will assumed that it is 0.1 (Ukoumunne 1999).

If cluster studies have been appropriately analysed with consideration of ICCs and relevant data documented in the report, synthesis with other trials would be feasible with use of the generic inverse variance technique.

Cross‐over trials

For cross‐over trials, a major concern is the carry‐over effect. The carry‐over effect occurs if the effect (e.g. medical, physical, mental) of treatment in the first phase is carried over to the second phase. As a consequence, on entry to the second phase, participants can differ systematically from their initial state despite a wash‐out phase (Elbourne 2002). The carry‐over effect is very likely to occur in cases of shoulder OA; therefore, we will use only data from the first phase of cross‐over studies.

Studies with multiple treatment groups

When a single trial with multiple treatment arms is included, we will include only the relevant arms. If two comparisons (e.g. higher‐molecular‐weight HA injection vs placebo and lower‐molecular‐weight HA injection vs placebo) are combined in the same meta‐analysis, we will halve the control group to avoid double‐counting. If a three‐arm trial compares, for example, HA versus steroid injection versus placebo, we will include HA versus steroid injection in one meta‐analysis and HA versus placebo in another.

We will record the details of multiple trial arms in the 'Characteristics of included studies' tables for trials that included multiple treatment arms.

Dealing with missing data

We will contact investigators or study sponsors to obtain missing data when possible (e.g. when a study is identified as abstract only, when data are not reported for all participants). When this is not possible and missing data are thought to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results by performing a sensitivity analysis. We will clearly describe any assumptions and imputations needed to handle missing data, and we will explore the effect of imputation by performing sensitivity analyses.

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

For continuous outcomes (e.g. mean change in pain score), we will calculate MD or SMD according to 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.

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

Assessment of heterogeneity

First, we will assess clinical homogeneity across included trials regarding participants, interventions, outcomes and study characteristics. For studies assessed to be clinically heterogeneous, we will describe them separately and will not combine them to perform a meta‐analysis. Second, we will assess statistical heterogeneity by calculating I² statistics.

As recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011), an I² value of 0% to 40% suggests that heterogeneity 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. As noted in the Cochrane Handbook for Systematic Reviews of Interventions, we will keep in mind that the importance of I² depends on the magnitude and direction of effects and the strength of evidence for heterogeneity.

If we identify substantial heterogeneity, we will report this and will investigate possible causes by conducting subgroup analyses.

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 different possible reasons for funnel plot asymmetry as outlined in Section 10.4 of the Cochrane Handbook for Systematic Reviews of Interventions and will relate this to review results. If more than 10 trials are available for a primary outcome, we will undertake formal statistical tests to investigate funnel plot asymmetry and will follow the recommendations provided 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 published reports. For studies published after 1 July 2005, we will obtain the a priori trial protocol from the International Clinical Trials Registry Platform of the World Health Organization (http://apps.who.int/trialsearch/) and will evaluate whether selective reporting of outcomes has occurred.

Data synthesis

We will undertake meta‐analyses only when this is meaningful (i.e. when treatments, participants and the underlying clinical question are similar enough for pooling to make sense).

When we expect some heterogeneity across studies, we will perform a random‐effects meta‐analysis as the default.

'Summary of findings' table

We will create a 'Summary of findings' table using the following outcomes.

  • Overall pain.

  • Function or disability, measured by upper limb functional outcome measures.

  • Participant global assessment of success.

  • Health‐related quality of life.

  • Proportion of participants proceeding to surgery (joint replacement or arthroscopic debridement).

  • Total adverse events.

  • Serious adverse events (i.e. leading to hospitalisation, disability or death).

We will use outcome data at three months to create respective 'Summary of findings' tables for each of the following comparisons if data are available.

  • Hyaluronate therapy (any dose) versus placebo.

  • Hyaluronate therapy versus steroid injection.

  • Hyaluronate therapy versus analgesics.

  • Hyaluronate therapy versus exercise or physiotherapy.

  • Hyaluronate therapy versus PRP.

  • Hyaluronate therapy of various doses.

  • Hyaluronate therapy versus surgery.

Two review authors (LTK and YSL) will independently assess the quality of the evidence. We will use the five GRADE considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of a body of evidence as it relates to studies that contribute data to meta‐analyses for prespecified outcomes. We will use methods and recommendations as described in Sections 8.5 and 8.7 and in Chapter 11 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a; Schünemann 2011a). We will justify all decisions to downgrade the quality of studies by using footnotes, and we will make comments to aid the reader's understanding of the review when necessary.

In the Comments column of the 'Summary of findings' table, we will provide the absolute percent difference, the relative percent change from baseline and the number needed to treat for an additional beneficial outcome (NNTB) or the the number needed to treat for an additional harmful outcome (NNTH) (we will present NNTB or NNTH only when the outcome shows a statistically significant difference).

For dichotomous outcomes, such as treatment success or adverse events, we will calculate the NNTB or the 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 by using the Wells calculator (available at the CMSG Editorial Office; http://musculoskeletal.cochrane.org/).

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

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

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses, if data are available, to determine whether outcomes differ for the following factors.

  • Age of participants (e.g. age ≤ 60 years vs age > 60 years).

  • Presence or absence of significant rotator cuff disease.

We will assess the following outcomes in subgroup analyses if data are available.

  • Overall pain.

  • Function or disability, measured by upper limb functional outcome measures.

We will conduct the formal test for subgroup interactions in Review Manager (RevMan 2014) and will use caution in interpreting subgroup analyses, as advised in Section 9.6 of the Cochrane Handbook for Systematic Reviews of Interventions. We will compare the magnitude of effects between subgroups by assessing overlapping of the confidence intervals of summary estimates. Non‐overlapping of the confidence intervals indicates statistical significance.

Sensitivity analysis

We will carry out the following sensitivity analyses, if sufficient data are available, to assess whether results for pain and function are robust to selection and detection biases.

  • Restricting analysis to studies at low risk of selection bias (i.e. with adequate allocation concealment).

  • Assessing the effect of including only studies at low risk of detection bias (i.e. with adequate blinding of outcome assessors, in this case, participants).

Interpreting results and reaching conclusions

We will follow the guidelines provided in the Cochrane Handbook for Systematic Reviews of Interventions, Chapter 12 (Schünemann 2011b), when interpreting results and will be aware of distinguishing lack of evidence of effect from lack of effect. We will base our conclusions only on findings from the quantitative or narrative synthesis of studies included in this review. We will avoid making recommendations for practice, and our implications for research will suggest priorities for future research and will outline remaining uncertainties in this area.