Types of studies

We will include randomised controlled trials (RCTs). We will include studies reported as full text, those published as abstract only, and unpublished data. There will be no language or time restriction.

Types of participants

We will include trials of adults with a diagnosis of patella tendinopathy.

Types of interventions

We will include trials comparing surgery with nonoperative interventions or placebo surgery.

Arthroscopic and open debridement will be pooled for comparison to nonoperative measurements. The reason for pooling is that the active component of the surgery (debridement) and the overall goal of the surgery are the same.

Nonoperative therapies/interventions include placebo, injections, physiotherapy, or no treatment. The outcomes of nonoperative therapies will be pooled and will be grouped by treatment type where two or more studies are available.

Types of outcome measures

Electronic searches

We will search the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, and Embase.

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.

See Appendix 1 for the MEDLINE search strategy; Appendix 2 for CENTRAL and Appendix 3 for Embase.

Searching other resources

We will check reference lists of all primary studies and review articles for additional references. We will search relevant manufacturers' websites for trial information.

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

Selection of studies

Two review authors (MD, AP) will independently screen titles and abstracts for inclusion of all of the potentially relevant studies from the search, and code them as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. We will retrieve the full‐text reports and two review authors (MD, AP) 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 (IH). 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, prisma‐statement.org/PRISMAStatement/Default.aspx) and 'Characteristics of excluded studies' table.

Data extraction and management

We will use a data collection form for study characteristics and outcome data, which has been piloted on at least one study in the review. Data will be independently extracted by two authors (MD and AP) and disagreements settled by discussion or referal to the senior author (IH). 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, location, study setting, withdrawals, and year of study.

2. Participants: N, mean age, age range, sex, socioeconomic status, disease duration, severity of condition, diagnostic criteria, important condition‐specific and general health baseline data, inclusion criteria, and exclusion criteria.

3. Interventions: intervention, comparison, concomitant medications, concomitant physical treatments, and excluded treatments.

4. Outcomes: primary and secondary outcomes specified and collected, 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.

Two review authors (MD, AP) will independently extract outcome data from included studies. 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 if 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 (IH). One review author (MD) will transfer data into the Review Manager (RevMan 2014) file. We will confirm data accuracy by comparing the data presented in the systematic review with the study reports.

We will use PlotDigitizer to extract data from graphs or figures. These data will also be extracted in duplicate.

We will apply the following a priori decision rules to select which data to extract in the event of multiple outcome reporting;

• Knee functional outcome scores: VISA is preferred, followed by Lysholm Knee Score, KOOS (Knee injury and Osteoarthritis Outcome score), WOMAC (Western Ontario and McMaster Universities Osteoarthritis Index) and Oxford Knee scores;

• Pain: overall pain will be selected preferentially over pain related to activity, followed by pain at rest. We will preferentially select pain on a VAS scale over pain reported on numerical or categorical rating scales, over pain reported on other scales, such as a subscore of a knee score;

• If both final values and change from baseline values are reported for the same outcome, we will preferentially extract change from baseline values;

• If both unadjusted and adjusted values for the same outcome are reported, we will preferrentially extract adjusted values;

• As per CONSORT(CONsolidated Standards Of Reporting Trials) guidelines, we will report on both intention‐to‐treat and per‐protocol analysis, using the per‐protocol to explore 'efficacy' of the intervention versus intention‐to‐treat to reflect the 'effectiveness' of the intervention.

• If there are multiple time points, we will extract outcomes reported up to six and up to 12 months.

Assessment of risk of bias in included studies

Two review authors (MD, AP) will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Intervention (Higgins 2017). We will resolve any disagreements by discussion or by involving another author (IH).

We will consider blinding separately for different key outcomes, where necessary (e.g. for unblinded outcome assessment, risk of bias for tendon rupture may be different than for a participant‐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 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 (CIs). Continuous data will be analysed as mean difference (MD) or standardised mean difference (SMD), 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 different scales are used to measure the same conceptual outcome (e.g. disability), SMDs will be calculated, with corresponding 95% CIs. SMDs will be back‐translated to a typical scale (e.g. 0 to 10 for pain) by multiplying the SMD by a typical among‐person standard deviation (e.g. the standard deviation of the control group at baseline from the most representative trial) as per Chapter 12 of theCochrane Handbook (Schünemann 2017b).

If return to sport is measured at intervals outside the three, six, or 12 month mark, we will analyse time‐to‐event data as hazard ratios. Rate data will be analysed 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 additonal beneficial outcome (NNTB), or number needed to treat for an additonal harmful outcome (NNTH) (the NNTB or NNTH will be provided only when the outcome shows a statistically significant difference).

For dichotomous outcomes, the NNTB or NNTH will be calculated from the control group event rate and the relative risk using the Visual Rx NNT calcultor (Cates 2008). The NNTB or NNTH for continuous measures will be calculated using the Wells calculator (available at the CMSG Editorial office).

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

The relative per cent change for dichotomous data will be calculated as the risk ratio ‐ 1 and expressed as a percentage. For continuous outcomes, the relative difference in the change from baseline will be calculated as the absolute benefit divided by the baseline mean of the control group, expressed as a percentage.

Unit of analysis issues

Where multiple trial arms are reported in a single trial, we will include only the relevant arms. W will halve the control group if two comparisons (e.g. arthrocopic surgery versus placebo and open surgery versus placebo) are combined in the same meta‐analysis.

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.

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. We will use the number of randomised patients in each group at baseline, if the number of patients analysed is not presented for each time point.

Where possible, we will compute missing standard deviations 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 2011). If we cannnot calcuate standard deviations, we will impute them (e.g. from other studies in the meta‐analysis) (Higgins 2011).

Assessment of heterogeneity

Clinical and methodological diversity will be assessed in terms of participants, interventions, outcomes, and study characteristics for the included studies to determine whether a meta‐analysis is appropriate. This will be conducted by observing these data from the data extraction tables. Statistical heterogeneity will be assessed 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 by Deeks 2017, 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% may represent 'considerable' heterogeneity. As noted in the Cochrane Handbook, 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 as follows: a P value ≤ 0.10 will indicate evidence of statistical heterogeneity.

If we identify substantial heterogeneity (greater than 50%), we will report it and investigate possible causes by following the recommendations in Deeks 2017.

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 by Sterne 2017. 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 of Sterne 2017.

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 Organisation (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 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.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses.

1. open surgery versus arthroscopic surgery;

2. subgroup analysis of different nonoperative comparators; we will compare injectables to physiotherapy alone.

We will use the following outcomes in subgroup analyses.

1. major outcomes as previously reported.

We will use the formal test for subgroup interactions in Review Manager (RevMan 2014) and will use caution in the interpretation of subgroup analyses as advised by Deeks 2017.

Sensitivity analysis

We plan to carry out sensitivity analyses to investigate the robustness of the treatment effect for pain and function to selection and detection biases.

1. Selection bias: assess potential influence of selection bias on pain and function by removing trials at risk of selection bias (i.e. with inadequate or unclear allocation concealment) from the meta‐analysis; and

2. Detection bias: assess influence of detection bias on pain and function by removing trials with unclear or inadequate blinding of the participants from the meta‐analysis.