Types of studies

Published and unpublished RCTs, including cluster‐RCTs, will be eligible for inclusion irrespective of language of report. Studies which used quasi‐randomised methods to allocate treatment (e.g. alternation or odd/even case numbers) will be excluded. Trials will be included if the application of compression is the only systematic difference between study arms.

Types of participants

Randomised controlled trials which recruited people of any age with venous leg ulceration (which may also be described as 'stasis' or 'varicose' ulceration) in any care setting will be eligible for inclusion. As the method of diagnosis of venous ulceration can vary between studies, we will apply no standardised definition, but each study must refer to the use of compression for venous ulcers.

We will include studies that recruited participants with a variety of wound types including venous leg ulcers if: a) the allocation of participants was stratified by wound type and included 'venous leg ulcer' as a group and results were presented (or available from the study authors) separately for this group; or b) studies included participants with non‐venous leg ulcers, but these made up a maximum of 25% of the total study population and we will assume that any treatment effect applies to people with venous ulcers. RCTs which only recruited people with non‐venous leg ulcers (e.g. arterial, or mixed) will be excluded from the review.

Types of interventions

We will include trials which compared the use of any compression bandage or stocking or any combination of compression with no compression (e.g. standard care, simple retention bandages, dressings alone) in participants with venous leg ulcers. We will exclude trials where intermittent pneumatic compression is the mode of compression being evaluated, as this is the focus of another Cochrane Review (Nelson 2014). 

Types of outcome measures

Electronic searches

We will search the following databases to retrieve reports of relevant clinical trials:

• the Cochrane Wounds Specialised Register (to present);

• the Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library (to latest issue);

• Ovid MEDLINE including In‐Process & Other Non‐Indexed Citations (from 1946 to present);

• Ovid Embase (from 1974 to present); and

• EBSCO CINAHL Plus (Cumulative Index to Nursing and Allied Health Literature; from 1937 to present).

We have devised a draft search strategy for CENTRAL which is presented in Appendix 1. We will adapt this strategy to search the Cochrane Wounds Specialised Register, Ovid MEDLINE, Ovid Embase and EBSCO CINAHL Plus. We will combine 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 will combine the Embase search with the Ovid Embase filter terms developed by the UK Cochrane Centre (Lefebvre 2011). We will combine the CINAHL Plus search with the trial filter developed by the Scottish Intercollegiate Guidelines Network (SIGN 2018). There will be no restrictions of the searches with respect to language, date of publication or study setting.

We will also search the following trials registries for ongoing trials or completed trials that have not been published.

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

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

Searching other resources

We will attempt to identify other potentially eligible trials or ancillary publications by searching the reference lists of retrieved included trials as well as relevant systematic reviews, meta‐analyses, and seven clinical practice guidelines for leg ulcers (Bolton 2014; Franks 2016; Marston 2016; O'Donnell 2014; SIGN 2010; Australian Wound Management Association 2011; Wittens 2015).

Selection of studies

Two review authors will independently assess the titles and abstracts of the citations retrieved by the searches for relevance. After this initial assessment, we will obtain full‐text copies of all studies considered to be potentially relevant. Two review authors will independently check the full papers for eligibility; disagreements will be resolved by discussion and, where required, the input of a third review author. Where the eligibility of a study is unclear we will attempt to contact study authors. We will record all reasons for exclusion of studies for which we obtain full‐text copies. We will complete a PRISMA flowchart to summarise this process (Liberati 2009).

Where studies are reported in multiple publications or reports, we will obtain all publications. Whilst the study will be included only once in the review, obtaining all publications will maximise the amount of data we can extract. We will also examine any relevant retraction statements and errata for information.

Data extraction and management

We will extract and summarise details of the eligible studies using a data extraction sheet. Two review authors will extract data independently and will resolve disagreements through discussion, consulting a third review author where required. Where data are missing from reports, we will attempt to contact the study authors to obtain this information.

Where possible we will extract the following data:

• country of origin;

• trial design (e.g. parallel, cluster);

• study population, including key related medical histories, diagnosis methods, the aetiology of leg ulcers (e.g. post‐thrombotic syndrome, varicose veins, chronic venous reflux), the onset or recurrence of leg ulcers, and the location of leg ulcers;

• care setting;

• eligibility criteria and key baseline participant data (total number of participants, age, sex, duration of leg ulcers, baseline leg ulcer area);

• details of the interventions, including compression devices used, and duration of interventions applied;

• descriptions of any co interventions or standard care;

• follow‐up period;

• unit of randomisation (e.g. leg ulcer, limb, or participant);

• numbers of participants randomised to each intervention;

• unit of analyses;

• number of ulcers per person;

• primary and secondary outcomes measured;

• data regarding time to complete wound healing: hazard ratio (HR) and its 95% confidence interval (CI), or any data that will allow its calculation (Parmar 1998; Tierney 2007);

• data regarding proportion of wounds completely healed during follow‐up: odds ratio (OR) and its 95% CI, or numbers of participants who have leg ulcers completely healed in each arm, both at the latest time point and (if different) at another time specified as of primary interest in the methods section;

• whether a Kaplan Meier plot is displayed;

• missing data rates per arm, and reasons for 'missingness', including the number of people who died;

• publication status of study; and

• source of funding for trial.

Assessment of risk of bias in included studies

Two review authors will independently assess each included study using the Cochrane tool for assessing risk of bias (Higgins 2011a). This tool addresses six specific domains: sequence generation, allocation concealment, blinding, incomplete data, selective outcome reporting, and other issues. In this review we will include unit of analysis issues under the domain of 'other issues', for example where a cluster‐randomised trial has been undertaken but analysed at the individual level in the study report. We will assess blinding of participants and personnel, blinding of outcome assessment, and incomplete outcome data for each of the review outcomes separately. We note that blinding of participants and personnel as to whether or not participants have been allocated to compression is impossible and therefore performance bias is a risk. Performance bias may be introduced when awareness of treatment allocation results in deviations from intended interventions and/or differential co‐interventions use or care between groups not specified in study protocol which may influence outcomes. We will scrutinise study reports and protocols (where available) to understand if, and how, studies attempted to minimise and document protocol deviations and differential care/co interventions compensated for this: for example, the study protocol might have been used to highlight the need to balance co interventions as well as potentially measuring and reporting this.

We will assess risk of bias for each domains as either: low risk, high risk or unclear risk. Since wound healing is a subjective outcome, unblinded outcome assessment represents a high risk of bias (Hróbjartsson 2012). We will therefore only record open intervention studies with blinded outcome assessment as being at low risk of detection bias.

All disagreements in 'Risk of bias' assessment will be resolved by discussion and, where required, the input of a third review author will be sought. Where possible, when a lack of reported information results in a judgement of unclear risk of bias, we will contact study authors for clarification. We will present our assessment of risk of bias using two 'Risk of bias' summary figures; one will be a summary of bias for each item across all studies, and the second will show a cross‐tabulation of each trial by all of the 'Risk of bias' items. We will classify studies with an assessment of high risk of bias for one or more of the following domains as being at high risk of bias overall for the specified outcome: sequence generation, allocation concealment or blinding of outcome assessment. 

For trials using cluster randomisation, we will consider the risk of bias in relation to: recruitment bias, baseline imbalance, loss of clusters, incorrect analysis and comparability with individually randomised trials (Higgins 2011a; Eldridge 2016) (Appendix 2).

Measures of treatment effect

For dichotomous outcomes (e.g. proportion of participants who have wounds completely healed during follow‐up), we will calculate the risk ratio (RR) with 95% CIs. For continuous outcomes we will use the mean difference (MD) with 95% CIs, for trials that used the same assessment scale. If trials that report continuous data used different assessment scales, we will use the standardised mean difference (SMD) with 95% CIs.

Time‐to‐event data (e.g. time to complete wound healing) will be reported as hazard ratios (HRs) where possible, in accordance with the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011). If studies reporting time‐to‐event data (e.g. time to healing) do not report a HR, then, when feasible, we will estimate this using other reported outcomes (such as numbers of events) through the application of available statistical methods (Parmar 1998; Tierney 2007). We will only consider median time to healing without survival analysis as a valid outcome if reports specify that all leg ulcers have healed (i.e. if the trial authors treat time‐to‐healing as a continuous measure as there is no censoring).

Unit of analysis issues

We will note whether trials present outcomes at the level of the leg ulcer, the limb or the participant and whether there may have been multiple ulcers reported for the same participant. Where trials randomise at the participant level and outcomes are measured at the wound level, e.g. leg ulcer healing, we will treat the participant as the unit of analysis when the number of leg ulcers assessed appears to be equal to the number of participants (e.g. one leg ulcer per person).

A particular unit of analysis issue may occur in trials if randomisation was carried at the participant level, with the allocated treatment used on multiple leg ulcers per participant, but data are presented and analysed per leg ulcer (clustered data). We will note whether data regarding multiple ulcers on a participant were (incorrectly) treated as independent within a study, or were analysed using within‐participant analysis methods. If clustered data were incorrectly analysed, we will record this as part of the 'Risk of bias' assessment. For an individually randomised trial, such data on multiple leg ulcers may be collected and analysed:

• only in a proportion of participants (in this case, we will only extract and present relevant data but not treat the trial as a cluster trial to seek for an analysis because the trial incorrectly includes a mixture of individual and clustered data); or

• in all participants (in this case, we will treat the trial as a cluster trial and will incorporate relevant data in meta‐analyses if the trial was analysed correctly). Where a cluster trial was not incorrectly analysed, we will record this in the 'Risk of bias' assessment. Where possible we will approximate the correct analyses based on guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b).

Useful information for approximating the correct analyses include:

• the number of clusters randomised to each arm or the average size of each cluster;

• the outcome data ignoring the cluster design; and

• an estimate of the intracluster correlation coefficient (ICC).

Dealing with missing data

It is common for there to be data missing from trial reports. Excluding participants from the analysis post‐randomisation or ignoring participants who are lost to follow‐up compromises the randomisation and potentially introduces bias into the trial. If it is thought that study authors might be able to provide some missing data, we will attempt to contact them; however, it is likely that data will often be missing because of loss to follow‐up.

In individual studies, when data for the proportion of leg ulcers healed are presented, we will assume that randomly assigned participants not included in an analysis had an unhealed leg ulcer at the end of the follow‐up period (i.e. they will be considered in the denominator but not in the numerator). We will examine the impact of this assumption through doing a sensitivity analysis (see Sensitivity analysis) in which we will assume participants with missing data had a healed leg ulcer (i.e. they will be included in both the numerator and the denominator). When a trial does not specify participant group numbers before dropout, we will present only complete case data. For the time‐to‐healing analysis using survival analysis methods, dropouts should be accounted for as censored data. Hence all participants would contribute to the analysis. We acknowledge that such analysis assumes that dropouts are missing at random and there is no pattern of 'missingness'.

We will present data for all categorical secondary outcomes as a complete case analysis. For continuous secondary outcome variables, e.g. length of hospital stay, we will present available data from the study reports/study authors and will not impute missing data. We will calculate measures of variance when these are missing (Deeks 2011) or we will contact study authors, where possible. Where these measures of variation remain unavailable, we will exclude the study from any relevant meta‐analyses.

Assessment of heterogeneity

Assessment of heterogeneity can be a complex, multi‐faceted process. Firstly, we will consider clinical and methodological heterogeneity: that is the degree to which the included studies vary in terms of participants' characteristics (e.g. mean age, proportion of participants by sex, methods of diagnosing leg ulcers), interventions (e.g. delivery approaches of compression systems), outcome definitions and other characteristics such as duration of follow‐up. This assessment of clinical and methodological heterogeneity will be supplemented by information regarding statistical heterogeneity. We will assess statistical heterogeneity using the Chi² test (a significance level of P value less than 0.10 will be considered to indicate statistically significant heterogeneity) in conjunction with the I² measure (Higgins 2003). I² examines the percentage of total variation across RCTs that is due to heterogeneity rather than chance (Higgins 2003). Very broadly, we will consider that I² values of 25%, or less may not indicate important heterogeneity and values of more than 75% indicate considerable heterogeneity (Deeks 2011; Higgins 2003).

These statistical tests are recognised to be underpowered and should be only used as an indicator of heterogeneity. Therefore the clinical, methodological and statistical heterogeneity should be considered together for the overall assessment of heterogeneity. Where there is no clinical or statistical heterogeneity, we will use a fixed‐effect model. In the absence of clinical heterogeneity and in the presence of some statistical heterogeneity (I² over 50%), we will use a random‐effects model; however, we will not anticipate pooling data across studies where heterogeneity is considerable (I² over 75%). Where there is evidence of considerable heterogeneity we will explore this further if required: see Data synthesis.

Assessment of reporting biases

Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results. Publication bias is one of a number of possible causes of small‐study effects, that is, a tendency for estimates of the intervention effect to be more beneficial in smaller RCTs. Funnel plots allow a visual assessment of whether small‐study effects may be present in a meta‐analysis. A funnel plot is a simple scatter plot of the intervention effect estimates from individual RCTs against some measure of each trial’s size or precision (Sterne 2011). Funnel plots are only informative when there are a substantial number of studies included in an analysis; we will present funnel plots for meta‐analyses that include at least 10 RCTs, using Review Manager 5 (RevMan 2014).

Data synthesis

We will summarise details of included studies in a narrative review according to the comparison between intervention and comparator, the participants, and the outcome measurement including the follow‐up duration. We will consider clinical and methodological heterogeneity and will undertake pooling if studies appear appropriately similar in terms of participants, intervention comparison, and outcome assessment including follow‐up duration. Where studies are not similar enough for pooling, we will present the results of included studies narratively.

We are unable to pre specify the amount of clinical, methodological and statistical heterogeneity in the included studies but it might be extensive. Thus, we anticipate using a random‐effects approach for meta‐analysis. Conducting meta‐analysis with a fixed‐effect model in the presence of even minor heterogeneity may provide overly narrow confidence intervals. We will only use a fixed‐effect approach when clinical and methodological heterogeneity is assessed to be minimal, and the assumption that a single underlying treatment effect is being estimated holds. Chi² and I² will be used to quantify heterogeneity but will not be used to guide choice of model for meta‐analysis. We will exercise caution when meta‐analysed data are at risk of small‐study effects because a random‐effects model may be unsuitable. In this case, or where there are other reasons to question the selection of a fixed‐effect or random‐effects model, we will assess the impact of the approach using sensitivity analyses to compare results from alternate models (Thompson 1999). We will report any evidence that suggests that the use of a particular model might not be robust.

We will produce pooled estimates of the treatment effect using Review Manager 5 (RevMan 2014) and present data using forest plots where possible. For time‐to‐event data, we will plot (and, if appropriate, pool) estimates of HRs and 95% CIs as presented in the study reports, using the generic inverse variance method in Review Manager 5 (RevMan 2014). Where time‐to‐healing is analysed as a continuous measure, but it is not clear if all wounds healed, we will document use of the outcome in the study, but will not summarise or use the data in any meta‐analysis.

We will include only the relevant arms where a trial involves multiple arms. If two or more arms in comparison with control are eligible for the same meta‐analysis, we will pool data on the two or more arms and compare them with control.

Subgroup analysis and investigation of heterogeneity

When there appears to be considerable between‐study heterogeneity we will attempt to explore the causes using the steps proposed by Cipriani 2013:

• check the data extraction and data entry for errors and possible outlying studies;

• if outliers exist, perform sensitivity analysis by removing them; and

• if heterogeneity is still present, perform subgroup analyses/meta‐regression for study‐level characteristics (see below) in order to explain heterogeneity as much as possible (Thompson 1999).

For subgroup analysis/meta‐regression, we will consider four study‐level characteristics: funding sources (binary: non‐for‐profit versus other/unclear); overall risk of bias (binary: low and unclear risk of bias versus high risk of bias); study designs (binary: parallel versus other designs); and follow‐up duration (continuous).

Sensitivity analysis

For pooled analyses, where possible, we will undertake sensitivity analyses to explore the impact of the following:

• assuming participants with missing data had a healed leg ulcer (i.e. they will be included in both the numerator and the denominator) followed by the analysis with the assumption that participants with missing data had unhealed leg ulcers;

• removing unpublished data (i.e. abstracts and dissertations) from the analysis; and

• changing effects model (i.e. using random‐effects model for the main analysis, followed by a repeated analysis with fixed‐effect model).