Types of studies

Randomised controlled trials (RCTs). We will include studies reported as full‐text articles, those published as abstracts only, and unpublished data. There will be no language restrictions. Given the progressive nature of the disease, we will not consider cross‐over trials.

Types of participants

Patients aged 18 or over, with bilateral or unilateral, primary or secondary osteoarthritis (osteoarthritis), in one or more joints, diagnosed according to the American College of Rheumatology criteria (Altman 1986), or with clinically or radiologically confirmed osteoarthritis. We will conduct a subgroup analysis considering different diagnosis criteria.

Types of interventions

Types of outcome measures

We will include studies that assess at least one of the following outcomes.

Electronic searches

The Information Specialist of the Cochrane Musculoskeletal Group will conduct the searches of the following databases.

• The Cochrane Central Register of Controlled Trials (CENTRAL).

• Embase (Embase.com) (1974 to present).

• MEDLINE (1966 to present).

• Latin American and Caribbean Health Science Information Database (LILACS) (1982 to present).

• Physioterapy Evidence Database (PEDro) (1999 to present).

• ClinicalTrials.gov (www.clinicaltrials.gov).

• World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (apps.who.int/trialsearch).

See Appendix 1 for the MEDLINE search strategy.

Searching other resources

The electronic literature search will be complemented by searching the additional sources.

• Reference lists of all primary studies and review articles for additional references.

• Relevant manufacturers' websites for trial information (and contact the organisation by phone or email).

• We will contact experts and the main authors of included studies for additional unpublished or ongoing studies.

• Abstract archives of annual meetings of the American College of Rheumatology (ACR) (www.rheumatology.org/Learning‐Center/Publications‐Communications/Abstract‐Archives).

• Errata or retractions from included studies published in full‐text on PubMed (www.ncbi.nlm.nih.gov/pubmed). We will report the date we perform this in the review.

• Abstract archives of annual meetings of the European League Against Rheumatism (EULAR) (www.eular.org/abstracts.cfm).

• For assessments on adverse effects, we will search the websites of the following regulatory agencies: US Food and Drug Administration (FDA) MedWatch (www.fda.gov/Safety/MedWatch/default.htm), the European Medicines Agency (EMA) (www.ema.europa.eu/ema/), the Australian Adverse Drug Reactions Bulletin (http://www.tga.gov.au/) and the UK Medicines and Healthcare Products Regulatory Agency (MHRA) pharmacovigilance and drug safety updates (www.gov.uk/mhra)

Selection of studies

Two review authors (RR and ALCM) will independently screen titles and abstracts of all potentially‐relevant studies identified by the searches, and code them as either 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. We will retrieve the full‐text study reports/publication of the first group and two review authors (RR and ALCM) will independently read the full‐text articles and select those that fulfil the inclusion criteria. We will record the reasons for excluding ineligible studies. The two review authors will resolve any disagreement through discussion; if necessary, they will consult a third review author (VFMT). 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 (Moher 2009; http://prisma‐statement.org/PRISMAStatement/Default.aspx) and a 'Characteristics of excluded studies' table.

Data extraction and management

Two review authors (RR and ALCM) will independently review the selected RCTs and will use a standard form to extract information on study characteristics and outcome data. We will extract the following information from the included studies.

• Publication items (i.e. year, setting, country, authors).

• Design and methods: criteria for inclusion/exclusion of participants, characteristics of the design of the trial as outlined below in the 'Assessment of risk of bias in included studies' section (details on allocation generation, allocation concealment, and blinding).

• Participants' baseline characteristics (e.g. age, gender), severity of disease, type and anatomic site of osteoarthritis.

• Intervention (dose, regimen, duration, co‐interventions).

• Comparators (e.g. no intervention, placebo, active pharmacological intervention).

• Outcomes (effectiveness and safety outcomes, time point of measures).

• Dropouts (number and reasons).

• Follow‐up (length).

• Data analyses (i.e. per protocol, intention‐to‐treat, modified intention‐to‐treat).

• Funding and conflict of interest disclosure.

• Other potential risk of bias.

When necessary, we will discuss disagreements until we reach consensus and, if necessary, consult a third review author (VFMT) if necessary. Two review authors (RR and GJMP) will insert data into Review Manager (RevMan) (RevMan 2014). We will double‐check if the two review authors entered data properly into the software.

Assessment of risk of bias in included studies

Three review authors (RR, GJMP, and ALCM) will independently assess the quality of included RCTs using the criteria recommended by the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011c), which consider seven domains for judging the risk of bias.

• Sequence generation: was the allocation sequence adequately generated?

• Allocation concealment: was allocation adequately concealed?

• Blinding of participants and personnel: was knowledge of the allocated interventions adequately prevented during the study?

• Blinding of outcome assessors: was knowledge of the allocated interventions adequately prevented during the study?

• Incomplete outcome data: were outcome data adequately assessed and accounted for? (we will consider a loss to follow‐up rate greater than 15% as high risk).

• Selective reporting: were the reports of the study free of any suggestion of selective outcome reporting?

• Other potential threats to validity: was the study apparently free from other problems that could put it at risk of bias?

We will classify each domain as having a high, low, or unclear risk of bias and we will include a quote from the study report and the reason 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. We will consider blinding separately for different key outcomes where necessary (e.g. for unblinded outcome assessment, risk of bias for all‐cause mortality may be different than for a patient‐reported pain scale). As well, we will consider the impact of missing data by key outcomes. Where information on risk of bias relates to unpublished data or correspondence with a trial author, 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 (CIs). We will analyse continuous data as mean difference (MD) or standardised mean difference (SMD) values, depending on whether the same scale is used to measure an outcome, and 95% CIs. We will enter data presented as a scale with a consistent direction of effect across studies.

When the included studies use different scales to measure the same conceptual outcome (e.g. disability), we will calculate the SMD values instead, with corresponding 95% CIs. We will then back‐translate the SMDs to a typical scale (e.g. zero to 10 for pain) by multiplying the SMD by a typical among‐person standard deviation (SD) (e.g. the SD of the control group at baseline from the most representative trial) (Schünemann 2011b).

In the 'Effects of interventions' results section and 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 number needed to treat for an additional harmful outcome (NNTH). We will only provide the NNTB or NNTH value when the outcome shows a statistically significant difference.

For dichotomous outcomes, we will calculate the NNTB or NNTH from the control group event rate and the relative risk using the Visual Rx NNT calculator (Cates 2008). We will determine the NNTB or NNTH for continuous measures using the Wells calculator (available at the Cochrane Musculoskeletal Group editorial office).

For dichotomous outcomes, we will calculate the absolute risk difference using the risk difference statistic in RevMan (RevMan 2014), and will express the result as a percentage. For continuous outcomes, we will determine the absolute benefit as the improvement in the intervention group minus the improvement in the control group, in the original units, expressed as a percentage.

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

Unit of analysis issues

The unit of analysis will be the individual.

Where multiple trial arms are reported in a single trial, we will include only the relevant trial arms. If two comparisons (e.g. drug A versus placebo and drug B versus placebo) are combined in the same meta‐analysis, we will halve the control group to avoid double‐counting. In this case, we will clearly state in the ‘Characteristics of included studies’ table that more than two intervention groups were present in the study.

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 we identify a study as an abstract only or when data are unavailable 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 clearly describe any assumptions and imputations to handle missing data 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 patients 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 patients analysed at that time point. If an included trial does not present the number of patients analysed for each time point, we will use the number of randomised patients in each group at baseline.

Where possible, we will compute the missing SD values 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. If we cannot calculate SDs, we will impute these values (e.g. from other studies in the meta‐analysis) (Higgins 2011b).

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 the forest plot 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 statistic 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% represents 'considerable' heterogeneity. As noted in the Cochrane Handbook for Systematic Reviews of Interventions, we will keep in mind that the importance of I² statistic depends on: (i) magnitude and direction of effects and (ii) strength of evidence for heterogeneity.

We will interpret the Chi² test where a P value ≤ 0.10 indicates evidence of statistical heterogeneity.

If we identify substantial or considerable 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). We will investigate possible causes of heterogeneity by subgroup and sensitivity 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 the different possible reasons for funnel plot asymmetry as outlined in Section 10.4 of the Cochrane Handbook 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 Handbook (Sterne 2011).

To assess outcome reporting bias, we will check trial protocols against published reports. For studies published after 1 July 2005, we will screen the clinical trial register of the WHO ICTRP (http://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 by using RevMan (RevMan 2014), and only where this is meaningful, i.e. if the treatments, participants, and the underlying clinical question are similar enough for pooling to make sense.

We will use a random‐effects model and perform a sensitivity analysis with fixed‐effect model.

We will restrict the primary analysis for self‐reported outcomes (e.g. outcomes such as pain, function, health‐related quality of life, the results that go in the 'Summary of findings' table and thus the Abstract and Plain Language Summary) to trials at low risk of detection and selection bias.

Subgroup analysis and investigation of heterogeneity

We plan to perform the following subgroup analyses.

• Different doses of strontium ranelate (2 g/day (usual dose), less than 2 g daily, more than 2 g/day).

• Different joints (e.g. shoulder, hip, knee, spine, hands).

• Severity of disease (i.e. Kellgreen‐Lawrence scale for knee, I, II, III, and IV) (Kellgren 1957).

• Sedentary or physically active participant (participants will be considered sedentary if they did not practice any type of physical exercise during the last three months; those who did will be considered physically active).

• Different time points: short term (up to three months, inclusive) or long term (more than three months).

• Participants with a history of, or those who are currently suffering from VTE, or those who are bedridden for the short term or long term versus those without these characteristics.

We will use the following outcomes in subgroup analyses.

• Pain.

• Physical function.

• Proportion of patients experiencing a serious adverse event.

We will use the formal test for subgroup interactions in RevMan (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. We will compare the magnitude of the effects between the subgroups by assessing the overlap of the CIs of the summary estimate. Non‐overlap of the CIs indicates statistical significance.

Sensitivity analysis

We will use sensitivity analyses to determine the robustness of the review findings. We plan to undertake the following sensitivity analyses for the primary outcome overall pain.

• Inclusion of all trials regardless of the risk of bias for detection and selection bias.

• Random‐effects model versus fixed‐effect model.