Types of studies

We will include randomized controlled trials (RCTs) or controlled clinical trials (CCTs). We will include studies reported as full text, those published as abstract only, and unpublished data. There will be no language restriction. We will include trials irrespective of whether measured outcome data are reported in a ‘usable’ way.

Types of participants

We will include adults over the age of 18 years with a diagnosis of osteoporosis, as defined by the World Health Organization (WHO) as a T‐score of less than −2.5 (Kanis 1994; WHO study group report 1994). We will also include participants from studies using osteoporosis definitions other than that of the WHO. We will exclude participants with the following co‐morbidities/characteristics: untreated hyperthyroidism or hypothyroidism; hypercalcemia or hypocalcemia; substantially impaired renal function or bone marrow transplantation. We will exclude participants who received therapeutic doses of systemic corticosteroids, fluoride, strontium or parathyroid hormone, systemic oral or transdermal estrogen, selective estrogen receptor modulators, bisphosphonates, denosumab, or with a known allergy to monoclonal antibody. Participants from both primary and secondary fracture prevention studies will be included.

Types of interventions

We will include trials in which the treatment arm includes anti‐sclerostin antibodies (romosozumab 210 mg or blosozumab 270 mg) versus placebo. We will pool trials in which the treatment arm includes anti‐sclerostin antibodies and the control arm includes placebo. All other comparisons (e.g. anti‐sclerostin antibodies versus bisphosphonates or any other active comparison) will be considered secondary and will be part of the appendices.

Types of outcome measures

Electronic searches

We will search the Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library, MEDLINE, Embase, Web of Science, and PubMed. We will also conduct a search of ClinicalTrials.gov (www.ClinicalTrials.gov) and the WHO trials portal (www.who.int/ictrp/en/). We will search all databases from their inception to the present, and we will impose no restriction on language of publication.

For assessments on adverse effects, we will search the web sites of the regulatory agencies.

• US Food and Drug Administration‐MedWatch (www.fda.gov/Safety/MedWatch/default.htm).

• European Medicines Evaluation Agency (www.emea.europa.eu).

• Australian Adverse Drug Reactions Bulletin (www.tga.gov.au/publication/australian‐adverse‐drug‐reactions‐bulletin).

• UK Medicines and Healthcare products Regulatory Agency (MHRA) pharmacovigilance and drug safety updates (www.mhra.gov.uk).

See Appendix 1 for the MEDLINE search strategy

Searching other resources

We will check reference lists of all primary studies and review articles for additional references. We will search relevant manufacturers' web sites for trial information. We will search for errata or retractions from included studies published in full text on PubMed (www.ncbi.nlm.nih.gov/pubmed), and report the date this was done within the review.

Selection of studies

Two review authors (XP and HL) will independently screen titles and abstracts for inclusion of all the potential studies we identify as a result of 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 and two review authors (XP and HL) will independently screen the full text and 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 (MSA). 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 and 'Characteristics of excluded studies' table.

Data extraction and management

We will use a data collection form, which will be piloted on at least one study in the review, for study characteristics and outcome data. Two review authors (XP and HL) will independently extract study characteristics and data from included studies. We will resolve disagreements by consensus or by involving a third reviewer (MSA). We will extract the following study characteristics.

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

2. Participants: N, mean age, age range, sex, disease duration, severity of condition, diagnostic criteria, important osteoporosis‐specific baseline data (e.g. BMD, body mass index etc.); inclusion criteria, and exclusion criteria.

3. Interventions: intervention, comparison, and concomitant medications. Data on dosage and treatment schedules of anti‐sclerostin antibodies and the comparative medications.

4. Outcomes: primary and secondary outcomes specified and collected, and time points reported. 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 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. If both unadjusted and adjusted values for the same outcome are reported, we will report on the unadjusted values. We will note in the 'Characteristics of included studies' table if outcome data were not reported in a usable way and when data were transformed or estimated from a graph.

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.

Two review authors (XP, MLO) will transfer data into the Review Manager 5 (RevMan 5) file (Review Manager 2014). We will double‐check that data is entered correctly by comparing the data presented in the systematic review with the study reports.

• If both final values and 'change from baseline' values are reported for the same outcome, the final value will be used.

• If data are analyzed based on an intention‐to‐treat (ITT) sample and another sample (e.g. 'per protocol', 'as treated'), only the ITT will be used.

• If multiple time points are present, information on all time points will be extracted.

Assessment of risk of bias in included studies

Two review authors (XP and HL) will independently assess risk of bias for each study using the criteria outlined in theCochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). We will resolve any disagreements by discussion or by involving another author (MSA). 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.

5. Incomplete outcome data.

6. Selective outcome reporting.

7. Other bias (baseline imbalance, selective subgroup reporting, supplementation for dropouts by providing additional recruits, recruitment of additional participants from a subgroup showing more or less benefit and deviation from the study protocol in a way that does not reflect clinical practice, and other sources of bias not covered in other domains of bias).

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 judgment in the 'Risk of bias' table. We will summarize the risk of bias judgments across different studies for each of the domains listed. We will consider blinding separately for different key patient‐reported subjective outcomes including improvement in skeletal pain (back pain), quality of life, and tolerability of treatment. In addition, 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 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. The primary analysis for our reviews for self‐reported outcomes (e.g. outcomes such as skeletal pain, health‐related quality of life), will be restricted to trials with low risk of detection and selection bias.

Measures of treatment effect

We will analyse dichotomous data as risk ratios (RRs) or Peto odds ratio when the outcome is a rare event (approximately less than 10%), and use 95% confidence intervals (CIs). Continuous data will be analyzed as mean difference (MD) or standardized mean difference (SMD), depending on whether the same scale is used to measure an outcome, with 95% CIs. 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 (e.g. quality of life), SMDs will be calculated instead, with corresponding 95% CIs. SMDs will be back‐translated to a typical scale (e.g. 0 to 10 for skeletal pain) by multiplying the SMDs by a typical among‐person standard deviation (e.g. the standard deviation of the control group at baseline from the most representative trial) (Schünemann 2011b).

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); (the NNTB will be provided only when the outcome shows a statistically significant difference).

For dichotomous outcomes, such as serious adverse events, we will calculate the NNTB from the control group event rate and the relative risk using the Visual Rx NNT calculator (Cates 2008). We will calculate the NNTB for continuous measures using the Wells calculator (available at the CMSG Editorial office, musculoskeletal.cochrane.org/).

For dichotomous outcomes, we will calculate the absolute risk difference using the risk difference statistic in RevMan 5 software and express the result as a percentage (Review Manager 2014). 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, and express as a percentage.

We will calculate the relative per cent change for dichotomous data as (RR − 1) and express 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, and express as a percentage.

Unit of analysis issues

The participants will be the unit of analysis. Where multiple trial arms are reported in a single trial, we will include our main comparison: anti‐sclerostin antibodies versus placebo. Other comparisons will be analysed and reported separately in the appendices. 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 (Higgins 2011b). We will prioritize comparison of anti‐sclerostin antibodies in combination with calcium and vitamin D versus placebo in combination with calcium and vitamin D. We will make it clear in the 'Characteristics of included studies' table that more than two intervention groups were present in the study, where applicable.

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 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 to handle missing data clearly; and explore the effect of imputation using sensitivity analyses.

For dichotomous outcomes, the withdrawal rate will be calculated using the number of patients randomized 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 analyzed at that time point. If the number of patients analyzed is not presented for each time point, the number of randomized patients in each group at baseline will be used.

Where possible, missing standard deviations (SDs)will be computed 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 2011c). Where SD is not presented for follow‐up, or cannot be calculated from other statistics, we will use the baseline SD instead if available (Fu 2015). When the mean is not presented, we will use the median if reported. We will use the interquartile range (IQR) to calculate the SD as recommended in the Cochrane Handbook for Systematic Reviews of interventions (SD = IQR/1.35), when necessary (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 examine data from the data extraction tables to assess clinical and methodological diversity in terms of participants, interventions, outcomes and study characteristics for the included studies; and from these we will determine whether a meta‐analysis is appropriate. We will assess statistical heterogeneity by visual inspection of the forest plot to assess for obvious differences in result between the studies, and by using the I² and Chi² statistical tests.

As recommended in the Cochrane 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% 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 (i) magnitude and direction of effects and (ii) strength of evidence for heterogeneity.

The Chi² test will be interpreted where a P value less than or equal to 0.10 will indicate evidence of statistical heterogeneity. If we detect significant heterogeneity (I² > 40%), we will examine the included studies for sources of heterogeneity, including differences in participant characteristics and other potential reasons for differences in effect sizes.

Assessment of reporting biases

If there are at least 10 trials, we will create and examine a funnel plot to explore possible publication 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 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 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 (www.who.int/ictrp/en/) 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, 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 for analysis. We will perform a sensitivity analysis by performing analyses using the fixed‐effect model as an alternate approach. We will combine the data from included trials in a meta‐analysis if two or more studies report on the same outcomes (anti‐sclerostin antibodies in combination with calcium; and vitamin D versus placebo in combination with calcium and vitamin D).

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses to investigate the robustness of the treatment effect of anti‐sclerostin antibodies in combination with calcium, and vitamin D versus placebo in combination with calcium and vitamin D.

1. Gender (men versus women). Prevalence of osteoporosis and fractures maybe different in women and men and potentially respond differently to osteoporosis treatment interventions.

2. Menopausal status (premenopausal versus postmenopausal). Prevalence of osteoporosis and fractures may be higher in postmenopausal women in comparison to premenopausal women and potentially respond differently to osteoporosis treatment interventions.

3. Definition of osteoporosis. The World Health Organization defines osteoporosis as a T‐score of less than −2.5 (Kanis 1994, WHO study group report 1994). However, it is possible for research studies to use other definitions such as a T‐score of less than −2.0, and others.

4. Categorization of osteoporosis such as steroid‐induced osteoporosis versus post‐menopausal osteoporosis. The mechanisms of bone loss and osteoporosis may differ by the implicated causal variable.

5. By dose. There may be differences in benefits and harms at different doses of the intervention and this needs to be explored.

6. Primary versus secondary fracture prevention.

We will use the formal test for subgroup interactions in Review Manager 5 (Review Manager 2014); and we will use caution in the interpretation of subgroup analyses as advised in section 9.6 of the Cochrane Handbook for Systematic Reviews of interventions. The magnitude of the effects will be compared between the subgroups by means of assessing the overlap of the CIs of the summary estimated. Non‐overlap of the CIs indicates statistical significance. We plan to analyse the outcome of clinical vertebral fractures in the subgroup analyses, and if not reported, subgroup analysis will not be conducted.

Sensitivity analysis

We will perform sensitivity analysis by assessing 'high‐quality' studies versus 'low‐quality' studies. We will define 'high quality' as those studies with adequate concealment of allocation, proper blinding of outcome assessor for subjective outcomes including improvement in skeletal pain report (back pain), quality of life and tolerability of treatment, and a drop‐out rate of less than 15%. In addition, we will perform a sensitivity analysis on those trials receiving funding from a pharmaceutical company versus those trials that do not receive such funding. We will also do a sensitivity analysis based on the fixed‐effect model and random‐effects model of meta‐analysis, as described under 'Data collection and analysis' above. We plan to include clinical vertebral fractures and non‐vertebral fractures in the sensitivity analyses, when data are available.