Data collection and analysis

After removal of duplicates, two review authors (JMP and AKV) will independently screen the abstract and title of every record retrieved by the searches. We will obtain the full‐text of all potentially eligible relevant records, and will screen them for eligibility. We will resolve any disagreements through consensus or by recourse to a third review author (RS). If we cannot resolve a disagreement, we will categorise the trial as a 'study awaiting classification' and will contact the trial authors for clarification. We will present an adapted PRISMA flow diagram to show the process of trial selection (Liberati 2009). We will list all articles excluded after full‐text assessment in a 'Characteristics of excluded studies' table and will provide the reasons for exclusion.

Two review authors (JMP and RS) will independently extract the data from trials that fulfil our inclusion criteria to identify key participant and intervention characteristics. We will describe interventions by use of the 'template for intervention description and replication' (TIDieR) checklist (Hoffmann 2014; Hoffmann 2017).

We will report data on efficacy outcomes and adverse events using standardised data extraction sheets from the CMED Group. We will resolve any disagreements by discussion or, if required, we will consult a third review author (AKV).

We will provide information about potentially relevant ongoing trials, including the trial identifiers, in the table 'Characteristics of ongoing trials' and in a joint appendix 'Matrix of trial endpoint (publications and trial documents)'. We will try to find the protocol for each included trial and we will report primary, secondary and other outcomes in comparison with data in publications in a joint appendix.

We will email all authors of included trials to enquire whether they would be willing to answer questions regarding their trials. We will present the results of this survey in an appendix. We will thereafter seek relevant missing information on the trial from the primary trial author(s), if required.

In the event of duplicate publications, companion documents or multiple reports of a primary trial, we will maximise the information yield by collating all available data, and we will use the most complete data set aggregated across all known publications. We will list duplicate publications, companion documents, multiple reports of a primary trial, and trial documents of included trials (such as trial registry information) as secondary references under the study ID of the included trial. Furthermore, we will also list duplicate publications, companion documents, multiple reports of a trial, and trial documents of excluded trials (such as trial registry information) as secondary references under the study ID of the excluded trial.

If data from included trials are available as study results in clinical trials registers, such as ClinicalTrials.gov or similar sources, we will make full use of this information and will extract the data. If there is also a full publication of the trial, we will collate and critically appraise all available data. If an included trial is marked as a completed study in a clinical trial register but no additional information (study results, publication or both) is available, we will add this trial to the 'Characteristics of studies awaiting classification' table.

Two review authors (JMP and IML) will independently assess the risk of bias of each included trial. We will resolve any disagreements by consensus or by consulting a third review author (AKV). In the case of disagreement, we will consult the rest of the review author team and we will make a judgement based on consensus. If adequate information is unavailable from the publications, trial protocols or other sources, we will contact the trial authors for more detail to request missing data on 'Risk of bias' items.

We will use the Cochrane 'Risk of bias' assessment tool (Higgins 2017), assigning assessments of low, high or unclear risk of bias (for details see Appendix 2; Appendix 3). We will evaluate individual bias items as described in the Cochrane Handbook for Systematic Reviews of Interventions according to the criteria and associated categorisations contained therein (Higgins 2017).

We will present a 'Risk of bias' graph and a 'Risk of bias' summary figure.

We will distinguish between self‐reported, investigator‐assessed and adjudicated outcome measures.

We will consider the following self‐reported outcomes.

Health‐related quality of life

Adverse events of surgery

We will consider the following outcomes to be investigator‐assessed.

Cure of PHPT

Morbidity related to PHPT

All‐cause mortality

Adverse events of surgery

Hospitalisation with hypercalcaemia or renal impairment

Socioeconomic effects

Some risk of bias domains, such as selection bias (sequence generation and allocation sequence concealment), affect the risk of bias across all outcome measures in a trial. In the case of high risk of selection bias, we will mark all endpoints investigated in the associated trial as being at high risk. Otherwise, we will not perform a summary assessment of the risk of bias across all outcomes for a trial.

We will assess the risk of bias for an outcome measure by including all entries relevant to that outcome (i.e. both trial‐level entries and outcome‐specific entries). We consider low risk of bias to denote a low risk of bias for all key domains, unclear risk to denote an unclear risk of bias for one or more key domains and high risk to denote a high risk of bias for one or more key domains.

These are the main summary assessments that we will incorporate into our judgments about the certainty of evidence in the 'Summary of findings' tables. We will define outcomes as at low risk of bias when most information comes from trials at low risk of bias, unclear risk when most information comes from trials at low or unclear risk of bias, and high risk when a sufficient proportion of information comes from trials at high risk of bias.

When at least two included trials are available for a comparison and a given outcome, we will try to express dichotomous data as a risk ratio (RR) or odds ratio (OR) with 95% confidence intervals (CIs). For continuous outcomes measured on the same scale (e.g. weight loss in kg), we will estimate the intervention effect using the mean difference (MD) with 95% CIs. For continuous outcomes that measure the same underlying concept (e.g. health‐related quality of life) but use different measurement scales, we will calculate the standardised mean difference (SMD). We will express time‐to‐event data as a hazard ratio (HR) with 95% CIs.

We will take into account the level at which randomisation occurred, such as for cross‐over trials, cluster‐randomised trials and multiple observations for the same outcome. If more than one comparison from the same trial is eligible for inclusion in the same meta‐analysis, we will either combine groups to create a single pair‐wise comparison or appropriately reduce the sample size so that the same participants do not contribute data to the meta‐analysis more than once (splitting the 'shared' group into two or more groups). While the latter approach offers some solution to adjusting the precision of the comparison, it does not account for correlation arising from the same set of participants being in multiple comparisons (Higgins 2011).

We will attempt to re‐analyse cluster‐RCTs that have not appropriately adjusted for potential clustering of participants within clusters in their analyses. The variance of the intervention effects will be inflated by a design effect. Calculation of a design effect involves estimation of an intracluster correlation coefficient (ICC). We will obtain estimates of ICCs by contacting trial authors or by imputing the ICC values by using either estimates from other included trials that report ICCs or external estimates from empirical research (e.g. Bell 2013). We plan to examine the impact of clustering using sensitivity analyses.

If possible, we will obtain missing data from the authors of the included trials. We will carefully evaluate important numerical data such as screened, randomly assigned participants as well as intention‐to‐treat, and as‐treated and per‐protocol populations. We will investigate attrition rates (e.g. dropouts, losses to follow‐up, withdrawals), and we will critically appraise issues concerning missing data and use of imputation methods (e.g. last observation carried forward).

In trials where the standard deviation (SD) of the outcome is not available at follow‐up or we cannot recreate it, we will standardise by the mean of the pooled baseline SD from those trials that reported this information.

Where included trials do not report means and SDs for outcomes and we do not receive the necessary information from trial authors, we will impute these values by estimating the mean and variance from the median, range and the size of the sample (Hozo 2005).

We will investigate the impact of imputation on meta‐analyses by performing sensitivity analyses, and we will report for every outcome which trials had imputed SDs.

In the event of substantial clinical or methodological heterogeneity, we will not report trial results as the pooled effect estimate in a meta‐analysis.

We will identify heterogeneity (inconsistency) by visually inspecting the forest plots and by using a standard Chi² test with a significance level of α = 0.1 (Deeks 2017). In view of the low power of this test, we will also consider the I² statistic, which quantifies inconsistency across trials to assess the impact of heterogeneity on the meta‐analysis (Higgins 2002; Higgins 2003).

When we find heterogeneity, we will attempt to determine the possible reasons for it by examining individual trial and subgroup characteristics.

If we include 10 or more trials that investigate a particular outcome, we will use funnel plots to assess small‐trial effects. Several explanations may account for funnel plot asymmetry, including true heterogeneity of effect with respect to trial size, poor methodological design (and hence bias of small trials) and publication bias (Sterne 2017). Therefore we will interpret the results carefully (Sterne 2011).

We plan to undertake (or display) a meta‐analysis only if we judge participants, interventions, comparisons and outcomes to be sufficiently similar to ensure an answer that is clinically meaningful. Unless good evidence shows homogeneous effects across trials of different methodological quality, we will primarily summarise low risk of bias data using a random‐effects model (Wood 2008). We will interpret random‐effects meta‐analyses with due consideration to the whole distribution of effects and present a prediction interval (Borenstein 2017a; Borenstein 2017b; Higgins 2009). A prediction interval needs at least four trials to be calculated and specifies a predicted range for the true treatment effect in an individual trial (Riley 2011). For rare events such as event rates below 1%, we will use the Peto's odds ratio method provided that there is no substantial imbalance between intervention and comparator group sizes and intervention effects are not exceptionally large. In addition, we will perform statistical analyses according to the statistical guidelines presented in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2017).

We expect the following characteristics to introduce clinical heterogeneity, and we plan to carry out the following subgroup analyses including investigation of interactions (Altman 2003).

Different surgical techniques

Severity of PHPT

Difference in the demographics of trial population such as gender, age and ethnic differences

We plan to perform sensitivity analyses to explore the influence of the following factors (when applicable) on effect sizes by restricting analysis to the following.

Published trials.

Effect of risk of bias, as specified in the 'Assessment of risk of bias in included studies' section.

Very long or large trials to establish the extent to which they dominate the results.

Using the following filters: diagnostic criteria, imputation, language of publication, source of funding (industry versus other) or country.

We will also test the robustness of results by repeating the analyses using different measures of effect size (RR, OR, etc.) and different statistical models (fixed‐effect and random‐effects models).

We will present the overall certainty of evidence for each outcome specified below, according to the GRADE approach, which takes into account issues related not only to internal validity (risk of bias, inconsistency, imprecision, publication bias) but also to external validity, such as directness of results. Two review authors (JMP and IML) will independently assess the certainty of evidence for each outcome. We will resolve any differences in assessment by discussion or consulting a third review author (RS).

We will include an appendix entitled 'Checklist to aid consistency and reproducibility of GRADE assessments', to help with standardisation of the 'Summary of findings' tables (Meader 2014). Alternatively, we will use the GRADEpro Guideline Development Tool (GDT) software and will present evidence profile tables as an appendix (GRADEpro GDT 2015). We will present results for the outcomes as described in the 'Types of outcome measures' section. If meta‐analysis is not possible, we will present the results in a narrative format in the 'Summary of findings' table. We will justify all decisions to downgrade the quality of trials using footnotes, and we will make comments to aid the reader's understanding of the Cochrane Review where necessary.

We will present a summary of the evidence in a 'Summary of findings' table. This will provide key information about the best estimate of the magnitude of the effect, in relative terms and as absolute differences, for each relevant comparison of alternative management strategies, numbers of participants and trials addressing each important outcome and a rating of overall confidence in effect estimates for each outcome. We will create the 'Summary of findings' table based on the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2017) using Review Manager 5 (RevMan 5) table editor (RevMan 2014). We will report the following outcomes, listed according to priority.

Cure of PHPT

Morbidity related to PHPT

All‐cause mortality

Adverse events of surgery

Health‐related quality of life

Hospitalisation with hypercalcaemia or renal impairment

Socioeconomic effects.