Types of studies

We included randomised controlled trials (RCTs) reported as full text, abstract only, or unpublished data. There was no language restriction.

Types of participants

We included studies in which participants were adults with venous leg ulcers, defined as ulcers in the lower leg or ankle due to underlying venous disease. We also included participants with venous leg ulcers that may have been complicated by other comorbidities such as diabetes. The rationale for this was to provide a result more representative of real‐patient population demographics, and ideally increase the generalisability of our review findings. We excluded participants with leg ulcers caused by other aetiologies unrelated to venous ulcers, such as arterial, diabetic, or mixed aetiologies. We included studies with mixed populations provided that separate data were available for participants with venous leg ulcers.

Types of interventions

The intervention was subfascial endoscopic perforator surgery (SEPS), either alone or in combination with another treatment method.

We accepted surgical and non‐surgical comparators, including but not limited to the following:

• conservative management alone (defined as compression bandaging or general wound care, or both);

• sham surgery (defined as a surgery that mimics the outward wound appearance of SEPS);

• another surgery for venous leg ulcer management that does not utilise SEPS (e.g. saphenous surgery, venous stripping);

• SEPS in conjunction with another surgical intervention (this was only accepted if the additional treatment method was applied to both intervention and comparator groups, that is as a co‐intervention in both groups);

• an alternative active intervention (e.g. debridement, zinc, mesoglycan, nutritional supplements, electromagnetic therapy, therapeutic ultrasound, topical agents).

It was expected that all treatment groups would have received compression bandaging, given that this is widely recognised as routine care for venous leg ulcers (Nelson 2014).

We excluded studies where SEPS in combination with another intervention was compared with a third intervention (e.g. SEPS + saphenous surgery versus conservative management), as the effects of SEPS could not be isolated.

Types of outcome measures

We did not limit study inclusion based on reporting of outcome measures.

Electronic searches

We searched the following electronic databases to identify reports of relevant clinical trials:

• the Cochrane Wounds Specialised Register (searched 4 March 2018);

• the Cochrane Central Register of Controlled Trials (CENTRAL; 2018, Issue 2) in the Cochrane Library (searched 4 March 2018);

• Ovid MEDLINE (including In‐Process & Other Non‐Indexed Citations (1946 to 4 March 2018);

• Ovid Embase (1974 to 4 March 2018);

• EBSCO CINAHL Plus (Cumulative Index to Nursing and Allied Health Literature) (1937 to 4 March 2018).

The search strategies for the Cochrane Wounds Specialised Register, CENTRAL, Ovid MEDLINE, Ovid Embase, and EBSCO CINAHL Plus can be found in Appendix 1. We combined the Ovid MEDLINE search with the Cochrane Highly Sensitive Search Strategy for identifying randomised trials in MEDLINE: sensitivity‐ and precision‐maximising version (2008 revision) (Lefebvre 2011). We combined the Embase search with the Ovid Embase filter developed by the UK Cochrane Centre (Lefebvre 2011). We combined the CINAHL Plus searches with the trial filters developed by the Scottish Intercollegiate Guidelines Network (SIGN 2018). We did not restrict studies with respect to language or date of publication.

We also searched the following clinical trials registries:

• US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (www.clinicaltrials.gov/) (searched 4 March 2018);

• World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (apps.who.int/trialsearch/Default.aspx) (searched 4 March 2018);

• EU Clinical Trials Register (www.clinicaltrialsregister.eu/) (searched 4 March 2018).

Search strategies for clinical trial registries can be found in Appendix 1.

Searching other resources

We checked the reference lists of all relevant publications identified by the database searches for additional eligible studies.

Selection of studies

Two review authors (ZCL, PL) independently assessed the titles and abstracts of all studies identified by the search and excluded any clearly irrelevant studies. Full‐text copies of potentially eligible studies were obtained and reviewed using the inclusion criteria. Any disagreements about inclusion were resolved by consensus or by consulting a third review author (RJ, MB, or CW) when necessary. The study selection process is summarised in a PRISMA flow diagram in Figure 1 (PRISMA 2009). See the Characteristics of excluded studies table for details of studies excluded after full‐text review. See the Characteristics of included studies table for details of included studies. We identified no ongoing studies or studies awaiting classification.

Figure 1

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PRISMA flow chart

Study flow diagram of the number of records identified, included, and excluded, and the reasons for exclusions.

Data extraction and management

Two review authors (ZCL, PL) independently extracted data from eligible trials including source of funding, study population, interventions, analyses, and outcomes using standardised data extraction forms. We included data from trials published in duplicate only once. Where necessary, we sought additional information from the principal investigator of the study concerned.

We extracted the following study characteristics.

• Methods: study design, total duration of study, number of study centres and location, study setting.

• Participant characteristics: age, gender, comorbidities, ulcer size and duration, number of ulcers, severity of ulcers as defined by trialists, associated pain, quality of life, inclusion criteria, and exclusion criteria.

• Interventions: intervention, comparison, standard therapies, concomitant therapies, and excluded therapies.

• Outcomes: the measurement scale, direction of the scale, the mean and standard deviation, number of participants per treatment group for continuous outcomes (such as mean pain and quality of life), number of events and number of participants per treatment group for dichotomous outcomes (such as number healed, number with recurrence, adverse events), and hazard ratios and associated 95% confidence intervals for time‐to‐event outcomes (time to complete healing) as outlined in Types of outcome measures and time points reported.

• Risk of bias of the trial as outlined below in Assessment of risk of bias in included studies.

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

Some outcome data was not reported in suitable form for meta‐analysis. Where possible, missing data were calculated or estimated from a graph or imputed; this was noted in the Characteristics of included studies tables.

Assessment of risk of bias in included studies

Two review authors (ZCL, PL) independently assessed the risk of bias of each included study against key criteria recommended by Cochrane (Higgins 2011a). The domains were as follows:

• random sequence generation

• allocation concealment

• blinding of participants, personnel, and outcome assessors

• incomplete outcome data

• selective outcome reporting

• other sources of bias (e.g. if groups were similar at baseline for important prognostic indicators such as wound size and duration of ulcer; and if co‐interventions were monitored or similar between the treatment and control groups).

We explicitly judged each of these criteria as low, high, or unclear risk of bias (either lack of information or uncertainty over the potential for bias) and recorded this information in the 'Risk of bias' table for each included study, see Appendix 2. Any disagreements were resolved by consensus for by consulting a third review author (CW) when necessary. Based on the overall risk of bias of each study and its likely effect on a given outcome, we downgraded the certainty of outcome results for studies where there is a high risk of bias through the GRADE approach.

Measures of treatment effect

The results of each included study were plotted as point estimates, that is risk ratio (RR) with corresponding 95% confidence interval (CI) for dichotomous outcomes (number healed, recurrence); mean difference (MD) and 95% CI for continuous outcomes (e.g. pain, quality of life); and hazard ratio (HR) and 95% CI for time‐to‐event outcomes (e.g. time to complete healing).

When the results could not be presented in this way, we described the results in the Characteristics of included studies table and reported them within the narrative of text in the review. For dichotomous outcomes with a statistically significant difference between groups, we calculated the number needed to treat for an additional beneficial outcome of healing and number needed to treat for one additional adverse event using the Cates online calculator (Cates 2008).

For continuous measures, we calculated MD for ease of interpretation. We did not have to compare any continuous outcomes across trials and as such did not calculate standardised mean differences (SMD) (Schünemann 2011b).

Unit of analysis issues

None of the included RCTs randomised or allocated clusters (e.g. clinics), hence we did not have to re‐analyse such studies by calculating effective sample sizes according to the methods outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b). There was no need to incorporate an estimate of the intracluster coefficient (ICC) using external estimates obtained from similar studies (Higgins 2011b). Consequently, no studies were excluded from the main analysis.

We noted that in studies where people were randomised and received treatment in two legs, a separate outcome was measured from each leg, and the number of legs was used as the denominator in the analysis without adjustment for the non‐independence. In such cases there was a potential unit of analysis error. In these studies, we extracted outcomes using the number of people randomised as the denominator (e.g. if we could extract the outcome for just one leg, or if the trialists adjusted their analysis to account for the two legs). Since the studies had been adjusted to account for two legs, there were no exclusions from the primary analyses.

Where multiple trial arms were reported in a single trial, we included only the two relevant arms in a single meta‐analysis. For trials presenting outcomes at multiple time points, we extracted data at all time points (0 to 6 months, 6 to 12 months, 12 to 24 months, and latest time point) as subgroups.

Dealing with missing data

We attempted to contact the trial authors to obtain information that was missing from trial reports.

For dichotomous outcomes, we used the number randomised as the denominator, assuming that any participants at the end of treatment did not have a positive outcome (e.g. for the outcome of recurrence, we assumed any missing participants had recurrence; for the outcome of healing, we assumed missing participants did not heal).

For continuous outcomes (e.g. mean pain), we calculated the MD or SMD based on the number of participants analysed at that time point. Where the number of participants analysed was not presented for each time point, and the trialists did not report imputed data for missing outcomes, we used the number of randomised participants in each group at baseline.

There were no missing standard deviations that could be computed from other statistics such as standard errors, confidence intervals, or P values, nor did we impute any standard deviations (e.g. from other studies in the meta‐analysis). We used this method per the recommendations in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011c).

For time‐to‐event data (e.g. time to complete healing), we extracted HR and 95% CI if this information was reported in the individual trials. If HR and 95% CI were not reported, we obtained estimates of log hazard ratios and their standard errors from other data reported in the trial, as recommended by Parma and Tierney (Parmar 1998; Tierney 2007).

Assessment of heterogeneity

We assessed clinical and methodological diversity in terms of participants, interventions, outcomes, and study characteristics for the included studies to determine whether a meta‐analysis was appropriate by observing data from the data extraction tables. We were able to conduct a meta‐analysis for one outcome as detailed in later sections.

We assessed statistical heterogeneity between the two studies that examined the same intervention by visual inspection of a forest plot. We used the I² statistic to quantify the possible magnitude of and the Chi² statistic to assess the statistical significance of heterogeneity.

As recommended in the Cochrane Handbook (Deeks 2011), we considered 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% to represent considerable heterogeneity.

We interpreted the Chi² statistic such that a P value ≤ 0.10 indicates evidence of statistical heterogeneity.

In the single meta‐analysis conducted, we were unable to investigate the cause of heterogeneity due to the poor design of the RCTs and data provided.

Assessment of reporting biases

We planned to create funnel plots to explore the possible presence of small‐study biases, provided we were able to pool data from more than 10 trials for meta‐analysis of a primary outcome (Sterne 2011). However, due to the small number of eligible studies this was not possible.

We planned to compare trial protocols against published reports to assess outcome reporting bias. For studies published after 1 July 2005, we screened the WHO ICTRP (apps.who.int/trialsearch/Default.aspx) and the US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (www.clinicaltrials.gov/) for the a priori trial protocol. However, as we identified no protocols for the included trials, we performed no comparison.

Data synthesis

For clinically homogeneous studies with similar participants and comparators and using the same outcome measure, we pooled outcomes in a meta‐analysis, using the random‐effects model as the default. We planned to use the fixed‐effect model in a sensitivity analysis to assess the possibility of small‐sample bias, however this was not required.

For time‐to‐event data (e.g. time to complete healing), we intended to enter log HR and standard error into Review Manager 5 and use generic inverse‐variance meta‐analysis to pool the HRs (Deeks 2011). However, this was not possible, as there were no two studies with the same intervention and comparator reporting these outcomes.

For dichotomous outcomes, the absolute risk difference was calculated using the risk difference statistic in Review Manager 5 (RevMan 2014), and the result expressed as a percentage. For continuous outcomes, the absolute benefit or change and the relative difference in the change from baseline was calculated, and the absolute benefit divided by the baseline mean of the control group, expressed as a percentage.

Subgroup analysis and investigation of heterogeneity

There were insufficient data (e.g. stratified data presented in the trials) to perform subgroup analyses to determine whether ulcer healing and recurrence are influenced by the following factors:

• participants with type 1 and 2 diabetes mellitus as a comorbidity (versus no diabetes);

• severity of ulcers at baseline determined by size (> 5 cm² or ≤ 5 cm²) and/or ulcer duration (> 6 months or ≤ 6 months).

We therefore did not use the formal test for subgroup interactions in Review Manager 5 (RevMan 2014). The magnitude of the effects if present would have been compared between the subgroups by means of assessing the overlap of the confidence intervals of the summary estimate. Non‐overlap of the confidence intervals may indicate statistically significant differences between subgroups.

Sensitivity analysis

There were insufficient data to perform sensitivity analysis. We had planned to assess the robustness of effect estimates for ulcer healing and ulcer recurrence to selection bias (excluding trials with inadequate or unclear allocation concealment); detection bias (excluding trials with unclear or inadequate blinding of outcome assessors); and attrition bias (excluding trials with incomplete outcome data). However, as all trials were subject to these biases, we could not limit analyses to studies at low risk of bias.