Types of studies

We will include all randomised controlled trials (RCTs), irrespective of language and publication status. We will exclude quasi‐randomised studies (studies where the allocation of participants to interventions is not truly random e.g., alternate allocation, allocation by date of birth, or allocation by medical record number).

Types of participants

We will include people of any age in any setting who have a donor site wound created as a result of harvesting a split‐thickness skin graft. The donor site wound may be created as an elective or an emergency procedure. Only studies involving human participants will be considered. Split‐thickness skin grafts harvested for any cause will be considered (e.g. burns, trauma, pressure ulcers). We will exclude full thickness skin grafts donor site wounds, since these require alternative closure methods.

Types of interventions

We will include studies in which any alginate dressing is applied to donor site wounds with a view to promoting healing.

We anticipate that likely comparisons in this systematic review may include:

• comparisons of alginate dressings as a primary dressing with other dressings, or topical agents

• different types of alginate dressings compared with each other.

Types of outcome measures

If a trial is eligible for inclusion (i.e. has the correct design, population and intervention/s) but does not report a listed outcome we will contact the study authors, if possible, to determine if a listed outcome was recorded but not reported.

Some of the outcomes listed below may be recorded at multiple time points. An example of this might be itch or pain and during and after healing of the donor site wound. Another example is scar appearance at 3, 6, and 12 months. We anticipate grouping outcomes by the following time points:

• short‐term: from donor site wound creation to 30 days;

• medium‐term: > 30 days after donor site wound creation to 6 months;

• long‐term: > 6 months after donor site wound creation.

Electronic searches

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

• the Cochrane Wounds Specialised Register;

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

• Ovid MEDLINE (from 1946 onwards);

• Ovid MEDLINE (In‐Process & Other Non‐Indexed Citations);

• Ovid Embase (from 1974 onwards);

• EBSCO CINAHL Plus (from 1946 onwards).

We have devised a draft search strategy for CENTRAL which is displayed in Appendix 2. We will adapt this strategy to search 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 searches with the randomised trial filter developed by the Scottish Intercollegiate Guidelines Network (SIGN 2017). There will be no restrictions of the searches with respect to language, date of publication or study setting.

We will search the following clinical trials registries for ongoing studies:

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

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

• EU Clinical Trials Register (www.clinicaltrialsregister.eu/ctr‐search/search).

We will also search the following databases to identify reports of relevant trials published in conference abstracts and theses:

• ProQuest COS Conference Papers Index (from 1982 onwards);

• ProQuest Dissertations & Theses Global (from 1861 onwards).

Searching other resources

We aim to identify other potentially eligible trials or ancillary publications by checking the reference lists of retrieved included trials, as well as relevant systematic reviews, meta‐analyses, and health‐technology assessment reports.

When necessary, we will contact experts in wound care and pharmaceutical companies to enquire about unpublished, ongoing and recently published trials.

We will not perform a separate search for adverse effects of alginate dressings for donor sites of split‐thickness skin grafts. We will consider adverse effects described in included studies only.

Selection of studies

Two review authors (CM and BP) will independently screen titles, abstracts, and keyword or descriptor terms of the retrieved articles for potential relevance. We will obtain full‐text copies of studies if initial assessment suggests potential inclusion. We will retrieve full articles in ambiguous cases, and in cases where a single author has identified a study for potential inclusion. Two review authors will then independently further assess the retrieved articles for final selection. Discrepancies will be resolved by discussion and consensus. If no consensus is reached we will use a third author to make a casting decision. Depending on the number of potentially relevant articles retrieved, this task may be shared amongst the entire review authorship. In all cases at least two authors will independently check studies for final selection. All authors have clinical experience in burns, and/or experience in prior systematic reviews. We will record reasons for exclusion of those studies where full‐text was retrieved. We will complete a PRISMA flowchart to summarise this selection (Liberati 2009).

Data extraction and management

Each author will be assigned a share of the included studies, such that each study has two review authors extracting data. We will use a data extraction sheet to summarise each study. Duplicated studies will have their data recorded once only, but all study reports will be used to maximise data extraction. Where there are missing data from reports, we will contact the study authors to request this information. Discrepancies will be resolved by discussion and consensus amongst all authors. If there is no consensus the majority opinion will apply. Where studies have intervention arms that are not eligible, we will only extract data from intervention and control arms that meet eligibility criteria.

We will extract the following data, by treatment group and for relevant time points where appropriate:

• year of publication, or publication status if unpublished;

• country of origin and care setting;

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

• study registration;

• pre published protocol;

• randomisation method, and unit of randomisation (patient or wound);

• allocation method;

• blinding of allocation and/or outcome assessment;

• duration of follow‐up;

• funding source/s;

• declarations of potential conflicts of interest;

• number of participants or wounds randomised to each trial arm;

• unit of analysis (patient or wound);

• type of wound being grafted (e.g. burn, venous ulcer);

• primary and secondary outcome/s, with definitions and time points;

• outcome data for primary and secondary outcomes (by group);

• measurement scales used for outcomes, and rationale for use;

• number of withdrawals (by group);

• intervention received by each group;

• duration of treatment; and

• concurrent interventions.

These data will be used to populate results tables for individual studies, and to facilitate risk‐of‐bias assessments for each study.

Separate searches will be performed for pre‐published protocols. In addition, the text of published articles will be searched for mention or citation of a pre‐published protocol and/or trial registration. Any available published version of a protocol will be considered for data extraction regarding trial design.

Assessment of risk of bias in included studies

Two review authors will independently apply the Cochrane tool for assessing risk of bias to the included studies (Higgins 2011a; see Appendix 3). This tool assesses six domains: sequence generation, allocation concealment, blinding, incomplete outcome data, selective outcome reporting, other issues (e.g. source of funding). Blinding and the completeness of outcome data will be assessed for each outcome separately. It is difficult to blind participants and personnel to particular dressings, as many are uniquely recognisable. Therefore this domain of the 'Risk of bias' assessment will be weighted 'low' accordingly. We will focus instead on blinding for outcome assessment, and use this for assessment of risk of bias from blinding for these studies. We will construct and present a 'Risk of bias' table from the available data for each eligible study. Any disagreement will be discussed until a consensus is reached. If there is no consensus we will involve a third author as a casting vote. We will present the data as two tables. The first will be a summary of risk of bias for each domain across all studies, and a second which will cross‐tabulate each study across all 'Risk of bias' items.

It is possible trials may have been conducted by industry or agents that produce or have close ties to the products under investigation. This creates a duality of interest at least, and conflicts of interest are possible in such cases. Declarations of such dualities or conflicts become important, as they contribute to judgements on whether methodological decisions may have been influenced by possible vested interests. Studies funded by industry are more likely to have outcomes favouring the funder, when compared against studies with other sponsors (Lundh 2012). Studies authored by principal investigators with ties to industry are similarly more likely to have favourable outcomes (Ahn 2017). Declarations within the published manuscript will be used to determine author/industry affiliations and will be extracted into the 'Characteristics of included studies' table.

The presence of a pre‐published protocol allows assessment of outcome switching once data become available within the trial (Category 5 ‐ selective outcome reporting).

If there are trials using cluster randomisation we will apply further 'Risk of bias' considerations: recruitment bias, baseline imbalance, loss of clusters, incorrect analysis, and comparability with individually randomised trials (Higgins 2011b; see Appendix 4). If cluster randomised trials have been analysed incorrectly, we will extract and present data but perform no further analyses.

Measures of treatment effect

We will calculate treatment effects for dichotomous outcomes using relative risk (RR) and risk difference (RD) with 95% confidence intervals (CI). The numbers needed to treat for an additional beneficial or harmful outcome (NNTB or NNTH, respectively) will be estimated if RD is statistically significant.

For wound healing data we will record 'time to event (wound healing)' as the time (in days) from donor site wound creation until re‐epithelialisation, as defined by each study's authors. Time to healing will be expressed as a Hazard Ratio.

For continuous outcomes, we will use the mean difference (MD) with 95% CI to describe the data if all trials use the same or similar assessment scales, and final scores will be chosen over change scores. Where trials use different assessment scales, we will use standardised mean difference (SMD) with 95% CIs. We may back‐transform SMD data into a common scale (e.g. Patient Observer Scar Assessment Scale/POSAS) for the purposes of presentation. Where this is done we will present a justification for our choice of scale, and will use the pooled baseline SD of studies using that scale. For multiple studies using that scale, we will present a range from lowest to highest SD.

Unit of analysis issues

Some studies randomise by participant, but analyse outcomes by wound. Where this occurs, and the numbers of participants and wounds are equal (i.e. one wound per participant) we will treat the participant as the unit of analysis. There may be instances of clustered data, where a proportion of trial participants have outcome data collected and reported on multiple wounds. Since not all participants will have multiple wounds this is not a cluster trial per se but rather a trial that incorrectly includes a mixture of individual and clustered data. Such trials will be noted and the issue will be recorded in the risk of bias assessment. Data will be extracted and presented but not the subject of any further analyses.

We will only incorporate clearly conducted fully cluster trials into meta‐analyses if the trial has been analysed correctly. Where a cluster‐randomised trial has been conducted but incorrectly analysed we will record this in the 'Risk of bias' assessment. If it is possible, we will approximate the correct analyses with guidance from the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b), using information on:

• the number of clusters randomised to each intervention, or the mean size of each cluster;

• outcome data ignoring cluster design for the total number of individuals; and

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

If we cannot analyse the study data correctly, we will extract and present the data without further analysis.

We will ensure there are no unit of analysis issues with double counting of controls when using studies with multiple intervention arms.

Where repeated observations are recorded on the same participant (e.g. pain or scar scales over time), we will define time points and analyse accordingly. Where multiple recordings are available within these time points we will incorporate all available data for an overall mean where possible.

Dealing with missing data

Missing data from trial reports potentially compromises outcome measures by introducing bias into the trial. Where data are missing we will contact authors of included studies for clarification. A partially filled data extraction form (with data from their own study) will be supplied, along with an open‐ended request for more data. Where data are missing, this will be described in the Results section and also in the 'Characteristics of included studies' section.

Participants with missing data will be described. Data will be analysed on an available case basis. We will substitute means for medians if a study has reported medians. If measures of variance are missing, we will calculate these where possible using standard Cochrane methodology. If we are unable to calculate these measures, then those studies will be excluded from any relevant meta‐analyses.

Assessment of heterogeneity

Where appropriate, and depending on their clinical and statistical heterogeneity, we will pool data (Higgins 2003). Assessment of heterogeneity is complex and multifaceted. We will assess the clinical and methodological heterogeneity of included studies by considering them in terms of participants, dressing types, and outcome parameters. We will assess heterogeneity by visual examination of the forest plots, and assess statistical heterogeneity using the Chi² test and I² measure. We will consider a Chi² significance of P > 0.10 as representing statistically significant heterogeneity. I² examines the percentage of total variation across RCTs that is due to heterogeneity rather than chance. (Higgins 2003). Generally, I² values of 40% or less might not be important when assessing the level of heterogeneity. Values of 75% or more indicate considerable heterogeneity. We will use a combination of these measures to assess heterogeneity. If we judge data to be too heterogeneous (e.g. Chi² test with P > 0.10, and I² values of 75% or greater), then results will be presented narratively only. We address how we will deal with potential heterogeneity further in Data synthesis.

Assessment of reporting biases

Assymetry will be assessed by visual inspection of funnel plots. We will present funnel plots for meta‐analyses comprising at least 10 RCTs using Review Manager 5 to assess publication bias (RevMan 2014). The funnel plot is essentially a scatter plot of outcome estimates from RCTs against some measure of a trial's precision or (more commonly) size (Egger 1997; Sterne 2011). Smaller studies commonly over‐estimate positive effects, in what is known as the 'small study effect', and can lead to biases in meta‐analyses. Negative studies are less likely to be submitted, published, and cited. Assymetry in funnel plots is commonly taken to reflect publication bias, but there are other causes of such asymmetry (Egger 1997). Other possible reasons are true heterogeneity, data irregularities, artefactual, or simply chance.

Publication bias is only one form of reporting bias. Others include time lag, duplicate publication, location, citation, language and/or outcome reporting biases. Since trial registries are being searched, we will have a list of trials registered but not published at the time of this review. These will be identified for future updates of this review. Multiple publication may be identified by noting similarities in published data from the same centre or authors. In such situations we will check with the authors, and use all publications to derive a single data set such that individual patients' data are not included twice. Our strategy for searching multiple databases and languages should mitigate location, citation, and language biases. Comparison of the registered trial with its outcome data may allow us to detect any outcome reporting bias. If such bias exists we will highlight this in our results.

Data synthesis

We will provide a descriptive summary of included studies according to comparators, combining details according to primary and secondary outcomes. We will consider both clinical and methodological heterogeneity. Where studies appear appropriately similar we will pool results. Where studies are not similar enough for pooling, results will be presented narratively. Data pooling may not be possible where populations are widely dissimilar (such as the elderly versus children).

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. Chi‐squared and I‐squared 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. We will report any evidence that suggests that the use of a particular model might not be robust. We may meta‐analyse even when there is thought to be extensive heterogeneity. We will attempt to explore the causes behind this using meta‐regression, if possible (Thompson 1999).

We will use forest plots to present data. We will present summary estimates of each effect, along with 95% confidence intervals (CI). For dichotomous outcomes we will present relative risk (RR). For continuous outcomes we will present pooled MD and 95% CI where studies report the same scale or method, or pooled SMD and 95% CI where studies measure the same outcome using different methods. For time to event data (such as days to re‐epithelialisation) we will plot (and pool if appropriate) estimates of hazard ratios and 95% CIs, using the generic inverse variance method in Review Manager 5 (RevMan 2014).

Subgroup analysis and investigation of heterogeneity

If numbers and data permit, we will conduct subgroup a analysis confined to paediatric patients. The definition of a paediatric patient varies, with cut‐offs determined by local hospital practices somewhere in the 14 to 18 year range. This may limit our ability to determine any differences in outcomes between paediatric and adult patients, or in varying age ranges. We will limit this subgroup analysis to patients 0‐18 years of age.

Subgroup analyses for paediatric patients will be performed for each dressing type, following the British National Formulary wound dressing classification (BNF 2017). If data permit, further subgroup analyses will be performed for individual dressings.

Subgroup analyses will be performed using the same methodologies as outlined above to determine if any treatment effects observed hold true in children.

Sensitivity analysis

We will perform a sensitivity analysis to examine the sensitivity of the results to excluding high risk of bias studies; that is any study that is assessed as being high risk of bias in any of the following domains:

• generation of the randomisation sequence;

• allocation concealment;

• blinding of outcome assessment.

Parts of the Methods section are based on the standard Cochrane Wounds Protocol Template.