Hydrogel dressings for donor sites of split‐thickness skin grafts

Abstract

This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:

To assess the effects of hydrogel dressings of donor site wounds following split‐thickness skin grafts (STSGs) for improving healing.

Background

Description of the condition

Skin grafting is a common surgical procedure for managing wounds to facilitate healing (Humrich 2018; Nanchahal 1992). The process involves removal of a tissue section from one part of the body, which is called the donor site, which is then used to cover healthy granulating surfaces of skin defects, such as ulcers or burns, that cannot be closed by bringing the two edges together. A skin graft is composed of two layers of the skin, the epidermis (the outermost layer of skin) and the dermis (the layer beneath the epidermis containing connective tissue, hair follicles and sweat glands). Split‐thickness skin grafts (STSGs) are obtained by harvesting the epidermis and part of the dermis of the skin and transplanting it to the area of skin defect after removal of tissue debris. There are many donor sites for STSGs, such as the upper and anterior thigh, buttocks, upper medial arm, back and scalp, depending on the recipient site (the area were the STSG will be transplanted to) and the thickness and texture of potential donor site skin (Francis 1998; Ratner 2003). Donor site wounds heal by re‐epithelization (restoration of the thin tissue forming the outer layer of the body’s surface) from the periphery of the wound to its centre and from the epithelium of the underlying sweat glands and hair follicles in the remaining dermis (Francis 1998; Ratner 2003). Re‐epithelization usually takes one to two weeks depending on many factors such as age and general health (e.g. smoking, diabetes and autoimmune diseases can slow the process) (Francis 1998; Rakel 1998; Ratner 2003). People with donor site wounds have a significant risk of morbidity and complications resulting from their wounds and these can have a considerable impact on their quality of life, as well as an increase in treatment costs (Humrich 2018).

Description of the intervention

Different types of dressings for people with donor site wounds are available and they come in varying forms (Voineskos 2009; Wiechula 2003). The British National Formulary for wound management products classifies dressings into basic, advanced, antimicrobial and specialised dressings (BNF 2017) (Appendix 1). The concept of optimal wound healing conditions was first introduced by Winter, who found faster re‐epithelization rates of animal experimental wounds covered with occlusive dressings compared with wounds exposed to air (Winter 1962). The optimal healing environment for donor site wounds is considered to be to keep the wound covered and moist until complete healing is achieved. Hydrogel dressings are classed as advanced wound dressings and they are thought to provide a moist environment for wound healing as they contain hydrophilic polymers (large, chain‐like molecules that contain polar or charged groups, rendering them soluble in water) with the ability to retain water in up to 90% of their content (Caló 2015; Jones 2005; Peppas 1993; Wichterle 1960). Hydrogels are available in two forms; flat sheets (e.g. ActiFormCool (Activa)), or amorphous hydrogel (e.g. Aquaflo (Covidien)). These dressings are usually applied by healthcare professionals (BNF 2017).

How the intervention might work

The ideal dressing should provide a moist environment for healing, protect against bacterial invasion, absorb exudate, and provide permeability to gases and oxygen (Gupta 2010; Lars 2013). As the donor site wound of an STSG is at risk of infection, fluid exudate and scarring, its management requires special care (Wiechula 2003). Hydrogels absorb wound exudate and promote moisture and oxygenation. Hydrogel dressings may also reduce pain, either by the process of cooling or providing analgesia to the wound (Trudgian 2000). Hydrogel dressings may be more effective than basic wound dressings in the treatment of diabetic foot ulcers (Dumville 2013).

Why it is important to do this review

The World Health Organization recognises wounds as a source of significant global morbidity; 5 to 7 million chronic or complex wounds occur annually in North America (Macdonald 2010). STSG is the most common surgical procedure used to cover skin defects (Kanapathy 2017). Dressing choice in the management of donor site wounds is crucial. A wide variety of dressings are used in wound management, including dry dressings, alginates, hydrocolloids and hydrogels (Voineskos 2009). However, there is a lack of evidence to support the efficacy and advantages of one dressing type over another in the management of donor site wounds (Uraloğlu 2012). The aim of this review is to assess the benefits and harms of hydrogel dressings compared with other dressing types in the management of donor site wounds of STSGs. This review is part of a suite of Cochrane Reviews currently being conducted to investigate the relative effectiveness of different dressing types for donor site wounds .

Objectives

To assess the effects of hydrogel dressings of donor site wounds following split‐thickness skin grafts (STSGs) for improving healing.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised controlled trials (RCTs) irrespective of language and publication status. We will include cluster RCTs and split‐body designs, where treatment options are randomly assigned to different sites. We will include abstracts of eligible trial reports regardless of type or availability of data. In addition, the authors of these reports will be contacted if further information is required. We will exclude quasi‐randomised, cross‐over and split‐wound trials as we anticipate a high risk of carry‐over effect given the nature of the condition and interventions.

Types of participants

We will include people of any age with one or more donor site wounds who have had an STSG. This includes donor site wounds created during an emergency or an elective surgical procedure. Trials involving people with other types of wounds will be eligible only if the results for people with donor site wounds are presented separately and randomisation was stratified by wound type, or if the majority of wounds in the trial (75% or more) are the wound type relevant to this review.

Types of interventions

The intervention of interest will be any hydrogel dressing.

Comparisons for this review are likely to be:

• hydrogel dressings compared with no dressing;

• hydrogel dressings compared with other types of dressings;

• different types of hydrogel dressings compared with each other;

• hydrogel dressings compared with another therapy such as topical agents (a topical agent is a cream, an ointment or a solution that is applied directly to the wound);

• hydrogel and another therapy versus other therapy alone.

In case of the use of different trade names, we will resort to the generic and active ingredient and the type of dressing (flat sheets, amorphous hydrogel).

Types of outcome measures

If a trial is eligible for inclusion (i.e. it has the correct design, population and intervention/s) but does not report one of the eligible outcomes, we will contact the study authors to determine if that outcome was recorded but not reported. If the report is eligible, it will be included in the review regardless of the authors response, and the potential ‘selective outcome reporting’ will be discussed if relevant.

Some of the outcomes listed below may be recorded at multiple time points. We will group outcomes into specified intervals:

• short‐term: from 0 to 30 days;

• medium‐term: > 30 days to 6 months;

• long‐term: > 6 months.

Primary outcomes

• Complete wound healing, measured as 'time to event' (wound healing). The time (in days) from donor site wound creation until re‐epithelialization, as defined by study authors.

• Donor site pain (measured using any validated instrument, e.g. visual analogue scale (Hawker 2011)).

Secondary outcomes

• Health‐related quality of life (measured using any validated outcome measure such as the World Health Organization Quality of Life (WHOQOL‐BREF) (Kim 2014), 36‐Item Short Form Health Survey (SF‐36) (Lins 2016), European Quality of Life 5 dimensions (EQ‐5D) (Herdman 2011) or 12‐item Short Form Health Survey (SF‐12) (Ware 1996), measured at completion of the study.

• Number of people with wound infection (we will accept authors of definition of an infected wound).

• Cost of treatment (measured at completion of the study).

• Number of people with the following wound complications: over‐granulation, skin discolouration, and problematic scar formation. We will accept author definitions of these complications.

• Number of people with adverse events (non‐serious and serious) where the study provided a clear methodology for the collection of adverse event data. We will document whether events were reported at the participant level or, where multiple events per person were reported, that an appropriate adjustment was made for data clustering. This outcome does not include individual types of adverse events such as pain or infection, which require specific assessment, rather it covers the generic assessment of any event classed as adverse by the participant or health professional, or both, during the trial.

Search methods for identification of studies

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 (to latest issue);

• Ovid MEDLINE (from 1946 onwards);

• Ovid Embase (from 1974 onwards);

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

We have devised a draft search strategy for CENTRAL which is displayed in Appendix 2. 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 2019). We will combine the Embase search with the Ovid Embase filter terms developed by the UK Cochrane Centre (Lefebvre 2019). We will combine the CINAHL Plus search with the randomised trial filters 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 clinical trials registries for ongoing studies:

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

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

Searching other resources

We will search reference lists of all included studies and other relevant publications, such as systematic reviews and guidelines. We will contact experts in the field, and manufacturers of dressings used in the treatment of donor site wounds, to ask for information relevant to this review. We will also search trial registry databases and contact the authors of relevant publications to identify any ongoing or completed trials.

Data collection and analysis

Selection of studies

Two review authors will work independently to screen the titles and abstracts of the studies identified from the search strategy against the inclusion criteria and exclude irrelevant reports. We will retrieve the full texts of potentially eligible studies that appear to fulfil the inclusion criteria and assess them independently for inclusion. Disagreements will be resolved by discussion with a third review author. We will contact investigators to request missing information when the eligibility of the study is unclear. If we find more than one publication linked to the same study, all the papers will be included and one will be marked as the primary source of information.

We will complete a PRISMA flowchart to summarize this process (Liberati 2009). We will record all reasons for exclusion of studies for which we obtain full copies in the 'Characteristics of excluded studies' table.

Data extraction and management

Two review authors will independently extract data from eligible studies, using an offline electronic form that will be piloted. We will resolve discrepancies through discussion and consensus and if no agreement is achieved we will consult a third review author. We will try to obtain missing or unclear data by contacting the study authors. Where a study with more than two intervention arms is included, we will only extract data from relevant intervention and control groups that meet the eligibility criteria. We will enter data into Review Manager 5 software (Review Manager 2014) and check them for accuracy.

In accordance with the methods described in the Cochrane Handbook for Systematic Reviews of Interventions, we will extract the following information (Li 2019).

• Study ID and year of publication

• Methods

  • Study design

  • Total study duration

  • Country of origin

  • Study setting

  • Unit of investigation (per person): single donor site wounds or multiple donor site wounds on the same person

  • Duration of follow‐up

• Participants

  • Inclusion and exclusion criteria

  • Total number

  • Participant demographic data (gender, age, ethnicity); relevant past history (such as diabetes, vascular disease, etc.)

  • Donor site wound size and site

  • Recipient site

• Intervention

  • Number of participants randomised to each treatment group

  • Details of the dressing/treatment regimen received by each group

  • Details of any co‐interventions

• Outcomes

  • Outcomes and time points (i) collected; (ii) reported

  • Primary and secondary outcome(s) (with definitions)

  • Unit of measurement (if relevant)

  • Unit of analysis (participant or wound)

  • For scales: upper and lower limits, and whether a high or low score is favourable

• Results

  • Number of participants allocated to each intervention group

  • For each outcome: sample size; missing participants; summary data for each intervention group (e.g. 2 × 2 table with proportions for dichotomous data; means and standard deviations (SDs) for continuous data); number of withdrawals (by group, with reasons)

• Notes

  • Source of funding

  • Key conclusions of the study authors

  • Citation and contact details

Assessment of risk of bias in included studies

Two review authors will independently assess the methodological quality of included studies using the Cochrane 'Risk of bias' tool, as described in theCochrane Handbook (Higgins 2011). We will resolve any discrepancies by discussion; if consensus is not achieved, disagreements will be resolved by consulting with a third review author. The 'Risk of bias' tool includes the following domains:

• sequence generation;

• allocation concealment;

• blinding of participants and personnel;

• blinding of outcome assessors;

• incomplete outcome data;

• selective outcome reporting;

• other bias, e.g. incorrect study analysis for unit of analysis issues.

A detailed description of criteria for a judgement of 'low risk’, 'high risk’ or 'unclear risk’ of bias is available (see Appendix 3).

If there are trials using cluster randomisation we will consider additional 'Risk of bias' domains: recruitment bias, baseline imbalance, loss of clusters, incorrect analysis, and comparability with individually randomised trials (Higgins 2019a; 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

Dichotomous data

For dichotomous data, we will calculate risk ratios (RRs) with 95% confidence intervals (CIs).

Continuous data

For continuous data, we will calculate the mean difference with 95% CIs, if outcomes are measured in the same way between trials. We will use the standardized mean difference (SMD) to combine trials that measured the same outcome but used different scales.

For data on wound healing, we will record 'time to event (wound healing)' as the time (in days) from donor site wound creation until re‐epithelialization, as defined by each study author. Time‐to‐event data (e.g. time‐to‐complete wound healing) will be expressed as hazard ratios (HRs) where possible, in accordance with the methods described in the Cochrane Handbook (Deeks 2019).

Unit of analysis issues

We will consider 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 would not be a cluster‐randomised 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 will not be the subject of any further analyses.

We will only incorporate well conducted cluster‐randomised trials that provide complete reports of the randomisation process and performed the meta‐analyses adequately. Where a cluster‐randomised trial has been conducted but incorrectly analysed, we will record this in the 'Risk of bias' assessment. If possible we will follow the guidance in the Cochrane Handbook (Higgins 2019a) and approximate estimates of the correct analyses, 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 intra‐cluster correlation coefficient (ICC).

In studies with multiple intervention arms, only the arms related to our review topic will be analysed. In the presence of multiple related arms, two or more equal size groups will be created from the shared group and compared with similar groups as a control.

We will include studies with a split‐body design where either people with two similar donor site wounds were enrolled and each wound was randomised to one of the interventions. These studies will be analysed using paired data which reflects the reduced variation in evaluating different treatments on the same person. However, if it is not clear whether such analysis has been undertaken this lack of clarity will be noted in the 'Risk of bias' assessment and in the notes in the 'Characteristics of included studies' table. Studies where one half of a wound was randomised to one treatment and the other half to a different treatment (split‐wound) will be excluded as there will be high carry across effect and diffusion of treatment effects.

Dealing with missing data

For included studies, we will note levels of attrition. Excluding participants post‐randomisation from the analysis, or ignoring those participants who are lost to follow‐up, compromises the randomisation and potentially introduces bias into the trial. Where possible, we will contact named corresponding study authors to request these data if details are not provided.

Where data remain missing for the 'proportion of wounds healed' outcome, for analysis we will assume that if randomised participants were not included in an analysis, their wound did not heal (i.e. they will be considered in the denominator but not the numerator). We will test the impact of this assumption by performing a sensitivity analysis in which we assume those with missing outcome data had the outcome of interest; that is they are included in both the numerator and the denominator (see Sensitivity analysis).

For continuous variables (e.g. change in wound area or length of hospital stay), we will present available data from the study reports/study authors and do not plan to impute missing data. Where measures of variance are missing, we will calculate these wherever possible. If calculation is not possible, we will document this but exclude the study from any relevant meta‐analyses that are conducted.

Assessment of heterogeneity

We will explore clinical or methodological heterogeneity by examining the following factors: care setting, participant characteristics, methods, interventions and outcomes of studies. We will supplement this assessment of clinical and methodological heterogeneity with information regarding statistical heterogeneity. We will inspect forest plots visually to consider the direction and magnitude of effects and the degree of overlap between confidence intervals. We will assess statistical heterogeneity in each meta‐analysis using Tau², the I² statistic, and the Chi² statistic (Higgins 2003). For the Chi² test, we will consider a significance level of P <0.10. For the I² test, we will use the following thresholds: 0% to 40%: might not be important; 30% to 60%: may represent moderate heterogeneity; 50% to 90%: may represent substantial heterogeneity; 75% to 100%: considerable heterogeneity. Collectively, we will regard heterogeneity as substantial if Tau² is greater than zero and either I² is ≥50% or the P value in the Chi² test for heterogeneity is <0.1.

Where there is evidence of considerable heterogeneity we will explore this further (see Data synthesis and Subgroup analysis and investigation of heterogeneity).

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 (Page 2019). We plan to present funnel plots for meta‐analyses using Review Manager 5 (Review Manager 2014) if 10 or more RCTs are available for inclusion in any single meta‐analysis.

Data synthesis

Data synthesis will be conducted using Review Manager 5 software. We will use a fixed‐effect meta‐analysis for combining data where it is reasonable to assume that studies are estimating the same underlying treatment effect, that is where trials are examining the same intervention, and the trials’ populations and methods are judged to be sufficiently similar. In case of substantial heterogeneity that cannot be explained clinically or methodologically, we will use a random‐effects meta‐analysis to produce an overall summary where an average treatment effect across trials is considered clinically meaningful. We will treat the random‐effects summary as the average range of possible treatment effects, and we will discuss the clinical implications of treatment effects differing between trials. If the average treatment effect is not clinically meaningful, we will not combine trials. If we use random‐effects analyses, we will present the results as the average treatment effect with its 95% CI and the estimates of Tau² and the I² statistic (Deeks 2019). We will pool dichotomous outcomes using Mantel‐Haenszel analysis for the fixed‐effect model or DerSimonian and Laird for a random‐effects model.

For continuous outcomes, we will calculate the difference in means with corresponding 95% CIs. If pooling is possible across studies, we plan to present a pooled difference in means with corresponding 95% CIs for continuous outcomes. If studies measure the same outcome using different instruments, we will combine data using a SMD estimate. For time to healing, we plan to plot estimates of HRs with 95% CIs from study reports using the generic inverse method in Review Manager 5 (Review Manager 2014).

We will present the results of the individual trials and meta‐analyses in the form of forest plots. If data are insufficient or unsuitable for meta‐analysis, a summary of results will be collated to summarize the findings in a narrative way.

'Summary of findings' tables and GRADE assessment of the certainty of the evidence

We will assess the certainty of the evidence using the GRADE approach (Schünemann 2013) related to the following main outcomes, which are important for decision‐making:

• complete wound healing;

• donor site pain;

• health related quality of life;

• number of people with wound infection;

• number of people with adverse events;

• number of people with the following wound complications: over‐granulation, skin discolouration, and problematic scar formation.

We will use the GRADEpro Guideline Development Tool (GRADEpro GDT) to import data from Review Manager 5 in order to create 'Summary of findings' tables. We will produce a summary of the intervention effect and a measure of certainty for each of the above outcomes, using the GRADE approach (Schünemann 2013). This uses the following five considerations to assess the certainty of the body of evidence for each outcome: study limitations, inconsistency of effect, imprecision, indirectness, and publication bias. We will downgrade the certainty of the evidence if we have concerns about each factor (from high confidence to moderate, low or very low confidence) using the guidelines developed by Rubinstein and colleagues (Rubinstein 2013). We will downgrade the certainty of the evidence if more than 25% of the participants providing data for an outcome are from studies with a high risk of bias (see Sensitivity analysis). Also, if significant heterogeneity is identified or there are large differences between studies in magnitude or direction of effects (or both), the level of evidence will be downgraded further. Lastly, we will downgrade the evidence if more than 50% of the participants are unrepresentative of the target group, and if single studies include less than 400 participants for continuous outcomes or 300 participants for dichotomous outcomes. The level of evidence will be downgraded from 'high certainty' by one level for serious limitations, or by two or more levels for very serious limitations, depending on assessments for risk of bias, indirectness of evidence, inconsistency, and imprecision of effect estimates or potential publication bias (Rubinstein 2013; Schünemann 2013).

Subgroup analysis and investigation of heterogeneity

If we identify substantial heterogeneity, we will check the data for accuracy, and then check for methodological or clinical explanations for the heterogeneity.

We will perform the following subgroup analysis for the primary outcomes if there are a minimum of 10 studies included in the meta analysis:

• people with diabetes, both type 1 and type 2 (Dumville 2013)

Sensitivity analysis

We will perform a sensitivity analysis for all outcomes by excluding studies at high risk of bias; that is, any study that is assessed as being at high risk of bias in any of the following domains:

• generation of the randomisation sequence;

• allocation concealment;

• blinding of outcome assessor;

• incomplete outcome data.

We will also perform a sensitivity analysis if split‐body studies are included in the analysis and remove these studies if there is evidence that the results differ substantially from those of parallel group studies.

Appendices

Appendix 1. British National Formulary Wound Dressings Classification, based on BNF 2017

Basic wound contact dressings

Low‐adherence dressings and wound contact materials

These dressings are usually cotton pads that are placed directly in contact with the wound. They can be either non‐medicated (e.g.
 paraffin gauze dressing) or medicated (e.g. containing povidone iodine or chlorhexidine). Examples include paraffin gauze dressing, BP
 1993 and Xeroform (Covidien) dressing ‐ a non‐adherent petrolatum blend with 3% bismuth tribromophenate on fine mesh gauze.

Absorbent dressings

These dressings are applied directly to the wound and may be used as secondary absorbent layers in the management of heavily exuding

wounds. Examples include Primapore (Smith & Nephew), Megapore (Molnlycke) and absorbent cotton gauze (BP 1988).

Advanced wound dressings

Hydrogel sheet and amorphous dressings

These dressings consist of a starch polymer and up to 96% water. They can absorb wound exudate or rehydrate a wound, depending

on the wound moisture levels. They are supplied in either flat sheets or amorphous hydrogel. Examples of hydrogel sheet dressings

include: Actiformcool (Activa) and Aquaflo (Covidien). Examples of amorphous hydrogel dressings include: Purilon Gel (Coloplast)

and NuGel (Systagenix).

Films: permeable film and membrane dressings

These dressings are permeable to water vapour and oxygen, but not to liquid water or micro‐organisms. Examples include Tegaderm

(3M); Opsite (Smith & Nephew).

Soft polymer dressings

These dressings are composed of a soft silicone polymer held in a non‐adherent layer. They are moderately absorbant. Examples include:

Mepitel (Molnlyckye) and Urgotul (Urgo).

Hydrocolloid dressings

These dressings are usually composed of an absorbant hydrocolloid matrix on a vapour‐permeable film or foam backing. Examples

include: Granuflex (Conva Tec). NU DERM (Systagenix). Fibrous alternatives have been developed that resemble alginates and are

not occlusive: Aquacel (Conva Tec).

Foam dressings

These dressings contain hydrophilic polyurethane foam and are designed to absorb wound exudate and maintain moist wound surface.

There are various versions; some include additional absorbent materials, such as viscose and acrylate fibres, or particles of superabsorbent

polyacrylate, while some are silicone‐coated for non traumatic removal. Examples include: Allevyn (Smith & Nephew); Biatain

(Coloplast); Tegaderm (3M).

Alginate dressings

These dressings are highly absorbent and consist of calcium alginate or calcium sodium alginate, which can be combined with collagen.

The alginate forms a gel when in contact with wound surface. This gel can be lifted off at dressing removal, or rinsed away with sterile

saline. Bonding to a secondary viscose pad increases absorbency. Examples include: Curasorb (Covidien); SeaSorb (Coloplast); Sorbsan

(Unomedical).

Capillary‐action dressings

These dressings consist of an absorbant core of hydrophilic fibres held between two low‐adherent contact layers. Examples include:

Advadraw (Advancis); Vacutx (Protex).

Odour‐absorbent dressings

These dressings contain charcoal and are used to absorb wound odour. Often this type of dressing is used in conjunction with a

secondary dressing to improve absorbency. Examples include: CarboFLEX (Conva Tec).

Anti‐microbial dressings

Honey‐impregnated dressings

These dressings contain medical‐grade honey, which is supposed to have antimicrobial and anti‐inflammatory properties, and can be

used for acute or chronic wounds. Examples include: Medihoney (Medihoney) and Activon Tulle (Advancis).

Iodine‐impregnated dressings

These dressings release free iodine, which is thought to act as a wound antiseptic, when exposed to wound exudate. An example is

Iodozyme (Insense).

Silver‐impregnated dressings

These dressings are used to treat infected wounds, as silver ions are thought to have antimicrobial properties. Silver versions of most

dressing types are available (e.g. silver foam, silver hydrocolloid, etc). Examples include: Acticoat (Smith & Nephew) and Urgosorb

Silver (Urgo).

Other antimicrobial dressings

These dressings are composed of a gauze or low‐adherent dressing impregnated with an ointment thought to have antimicrobial

properties. Examples include: chlorhexidine gauze dressing (Smith & Nephew) and Cutimed Sorbact (BSN Medical).

Specialist dressings

Protease‐modulating matrix dressings

These dressings alter the activity of proteolytic (protein‐digesting) enzymes in chronic wounds. Examples include: Promogran (Systagenix) and Sorbion (H & R).

Silicone keloid dressing

These dressings reduce or prevent hypertrophic or keloid scarring. Examples include: Cica‐Care (Smith & Nephew) and Ciltech (Sumed).

Appendix 2. The Cochrane Central Register of Controlled Trials (CENTRAL) draft search strategy

#1 MeSH descriptor: [Skin Transplantation] explode all trees

#2 MeSH descriptor: [Transplantation, Autologous] explode all trees

#3 MeSH descriptor: [Transplant Donor Site] explode all trees

#4 (((split next thick*) or split‐thick* or "split skin" or split‐skin or "partial dermal" or partial‐dermal or (partial next thick*) or partial‐thick*) near/3 graft*):ti,ab,kw

#5 ((skin or derm*) next transplant*):ti,ab,kw

#6 STSG:ti,ab,kw

#7 donor site:ti,ab,kw

#8 {or #1‐#7}

#9 MeSH descriptor: [Hydrogels] explode all trees

#10 MeSH descriptor: [Bandages] explode all trees

#11 hydrogel*:ti,ab,kw

#12 ("Askina Transorbent" or "Cutimed Sorbact" or "Intrasite Comformable" or "Xtrasorb HCS" or ActivHeal or Aquaform or Askina or Cutimed or Granugel or Intrasite or "Nu Gel" or "Nu‐Gel" or Prontosan or Octenillin or "Actiform cool" or ActiformCool or Hydrosorb or Iodozyme or Kerralite or Novogel or Oxyzyme or Hyiodine or Flexigran or Purilon or Aquaflo or Coolie or "Gel FX" or Geliperm or Novogel or SanoSkin or Vacunet or curafil or dermagran or duoderm or hypergel or normlgel or "suprasorb gel" or hypligel or "elasto‐ gel" or tegagel or curasol or curate):ti,ab,kw

#13 {or #9‐#12}

#14 #8 and #13 in Trials

Appendix 3. The Cochrane tool for assessing risk of bias

1) Random sequence generation (checking for possible selection bias)

We will describe the method used to generate the allocation sequence in each study in sufficient detail to allow an assessment of whether it should produce comparable groups.

• Low risk of bias: the investigators describe a random component in the sequence generation process such as: referring to a random number table; using a computer random number generator; coin tossing; shuffling cards or envelopes; throwing dice; drawing of lots.

• High risk of bias: the investigators describe a non‐random component in the sequence generation process. Usually, the description would involve some systematic, non‐random approach, for example: sequence generated by odd or even date of birth; sequence generated by some rule based on date (or day) of admission; sequence generated by some rule based on hospital or clinic record number.

• Unclear risk of bias: insufficient information about the sequence generation process to permit judgement of low or high risk of bias.

2) Allocation concealment (checking for possible selection bias)

We will describe for each included study the method used to conceal allocation to interventions prior to assignment and assess whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment. We will assess the methods as being at:

• low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);

• high risk of bias (open random allocation; unsealed or non‐opaque envelopes);

• unclear risk of bias (insufficient information to permit judgement of low or high risk of bias. This is usually the case if the method of concealment is not described or not described in sufficient detail to allow a definite judgement).

3.1) Blinding of participants and personnel (checking for possible performance bias)

We will describe for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We will consider that studies are at low risk of bias if they were blinded, or if we judge that the lack of blinding would be unlikely to affect results. We will assess blinding separately for different outcomes or classes of outcomes. We will assess the methods as:

• low, high or unclear risk of bias for participants;

• low, high or unclear risk of bias for personnel.

3.2) Blinding of outcome assessment (checking for possible detection bias)

We will describe for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We will assess blinding separately for different outcomes or classes of outcomes. We will assess methods used to blind outcome assessment as:

• low risk of other bias;

Either of the following.
 • No blinding of outcome assessment, but the review authors judge that the outcome measurement is not likely to be influenced by lack of blinding.
 • Blinding of outcome assessment ensured, and unlikely that the blinding could have been broken.

• high risk of other bias;

Either of the following.
 • No blinding of outcome assessment, and the outcome measurement is likely to be influenced by lack of blinding.
 • Blinding of outcome assessment, but likely that the blinding could have been broken, and the outcome measurement is likely to be influenced by lack of blinding.

• unclear risk of bias;

• Insufficient information available to permit a judgement of 'low risk' or 'high risk'.

4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)

We will describe for each included study, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We will state whether attrition and exclusions were reported and the numbers included in the analysis at each stage (compared with the total randomised participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. Where sufficient information is reported, or can be supplied by the trial authors, we will re‐include missing data in the analyses. We assessed methods as being at:

• low risk of bias (e.g. no missing outcome data; missing outcome data balanced across groups; ≦ 20% participants missing);

• high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis done with substantial departure of intervention received from that assigned at randomisation; more than 20% participants missing);

• unclear risk of bias.

5) Selective reporting (checking for reporting bias)

We will describe for each included study how we investigated the possibility of selective outcome reporting bias. We will assess the methods as being at:

• low risk of bias (where it is clear that all of the study’s pre‐specified outcomes and all expected outcomes of interest to the review have been reported);

• high risk of bias (where not all the study’s pre‐specified outcomes have been reported; one or more reported primary outcomes were not pre‐specified; outcomes of interest are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported);

• unclear risk of bias.

6) Other bias (checking for bias due to problems not covered by 1 to 5 above)

We will consider other risk of bias issues as follows: comparability of treatment groups in relation to donor site wound surface area;
 choice of analysis where participant(s) with multiple donor site wounds are studied; and choice of analysis in cluster‐randomised trials. For trials using cluster randomisation we planned to assess the risk of bias using the following domains: recruitment bias, baseline imbalance, loss of clusters, incorrect analysis and comparability with individually randomised trials (Higgins 2019a). We will assess whether each study was free of other problems that could put it at risk of bias:

• low risk of other bias;

The study appears to be free of other sources of bias.

• high risk of other bias;

There is at least one important risk of bias. For example, the study:

• has extreme baseline imbalance; or
 • had a potential source of bias related to the specific study design used;
 • had an inappropriate influence of funders due to industry initiated protocols;
 • has been claimed to have been fraudulent; or
 • had some other problem.

Or in cluster‐randomised trials there is:
 • recruitment bias (differential participant recruitment in clusters for different interventions);
 • baseline imbalance; or
 • loss of clusters.

• unclear whether there is risk of other bias;

There may be a risk of bias, but there is either:
 • insufficient information to assess whether an important risk of bias exists; or
 • insufficient rationale or evidence that an identified problem will introduce bias.

7) Overall risk of bias

We will make explicit judgements about whether studies were at high risk of bias, according to the criteria given in the Cochrane Handbook (Higgins 2019a). With reference to 1 to 6 above, we will assess the likely magnitude and direction of the bias and whether we will consider it likely to impact on the findings. We will explore the impact of the level of bias through undertaking sensitivity analyses.

We will present our assessment of risk of bias using a ’Risk of bias’ summary figure which will present the judgements in cross tabulation. This display of internal validity indicates the weight the reader may give to the results of each study.

Appendix 4. Risk of bias assessment for cluster‐randomised trials

In cluster‐randomised trials, particular biases to consider include:

• recruitment bias;

• baseline imbalance;

• loss of clusters;

• incorrect analysis;

• comparability with individually randomised trials.

1) Recruitment bias can occur when individuals are recruited to the trial after the clusters have been randomised, as knowledge of whether each cluster is an 'intervention' or 'control' cluster could affect the types of participants recruited.

2) Cluster‐randomised trials often randomise all clusters at once, so lack of concealment of an allocation sequence should not usually be an issue. However, because small numbers of clusters are randomised, there is a possibility of chance baseline imbalance between the randomised groups, in terms of either the clusters or the individuals. Although not a form of bias as such, the risk of baseline differences can be reduced by using stratified or pair‐matched randomization of clusters. Reporting the baseline comparability of clusters, or statistical adjustment for baseline characteristics, can help reduce concern about the effects of baseline imbalance.

3) Occasionally, complete clusters are lost from a trial, and have to be omitted from the analysis. Just as for missing outcome data in individually randomised trials, this may lead to bias. In addition, missing outcomes for individuals within clusters may also lead to a risk of bias in cluster‐randomised trials.

4) Many cluster‐randomised trials are analysed by incorrect statistical methods, not taking the clustering into account. Such analyses create a 'unit of analysis error' and produce over‐precise results (the standard error of the estimated intervention effect is too small) and P values that are too small. They do not lead to biased estimates of effect. However, if they remain uncorrected, they will receive too much weight in a meta‐analysis.

5) In a meta‐analysis including both cluster‐ and individually‐randomised trials, or including cluster‐randomised trials with different types of clusters, possible differences between the intervention effects being estimated need to be considered. For example, in a vaccine trial of infectious diseases, a vaccine applied to all individuals in a community would be expected to be more effective than if the vaccine was applied to only half of the people. Another example is provided by a Cochrane Review of hip protectors (Santesso 2014). The cluster trials showed large positive effect, whereas individually randomised trials did not show any clear benefit. One possibility is that there was a 'herd effect' in the cluster‐randomised trials (many of which were performed in nursing homes, where compliance with using the protectors may have been enhanced). In general, such 'contamination' would lead to underestimates of effect. Thus, if an intervention effect is still demonstrated despite contamination in those trials that were not cluster‐randomised, a confident conclusion about the presence of an effect can be drawn. However, the size of the effect is likely to be underestimated. Contamination and 'herd effects' may be different for different types of cluster.

Contributions of authors

Ahmed Younis and Ashraf Nabhan conceived the review question; developed the protocol; co‐ordinated the protocol development; produced the first draft of the protocol; contributed to writing or editing the protocol; advised on the protocol; approved the final version of the protocol prior to submission; and are guarantors of the protocol.

Ibrahim Abdelmonem, Yasser Mohamed and Hamdy Alnaggar conceived the review question; developed the protocol; co‐ordinated the protocol development; produced the first draft of the protocol; contributed to writing or editing the protocol; advised on the protocol; and approved the final version of the protocol prior to submission.

Gemma Villanueva conceived the review question; developed the protocol; contributed to writing or editing the protocol; advised on the protocol; approved the final version of the protocol prior to submission.

Haitham El‐Dessokey, Jacqueline Thompson and Carlos Areia conceived the review question; developed the protocol; contributed to writing or editing the protocol; advised on the protocol; and approved the final version of the protocol prior to submission.

Contributions of the Editorial Base

Jo Dumville (Co‐ordinating Editor): edited the protocol; advised on methodology, interpretation and content; approved the final version of the protocol prior to submission.
 
 Gill Rizzello (Managing Editor): coordinated the editorial process; advised on content; edited the protocol.
 
 Sophie Bishop (Information Specialist): designed the search strategy and edited the search methods section.
 
 Tom Patterson (Editorial Assistant): edited the reference sections.

Sources of support

Internal sources

• No sources of support supplied

External sources

• Egyptian Center for Evidence Based Medicine, Egypt.

  Author training.

• National Institute for Health Research, UK.

  This project was supported by the National Institute for Health Research, via Cochrane Infrastructure funding to Cochrane Wounds. The views and opinions expressed are those of the authors and not necessarily those of the NIHR, NHS or the Department of Health and Social Care

Declarations of interest

Ahmed Younis: none known

Ibrahim Abdelmonem: none known

Yasser Mohamed: none known

Hamdy Alnaggar: none known

Gemma Villanueva: none known

Jacqueline Thompson: none known

Haitham El‐Dessokey: none known

Carlos Areia: none known

Ashraf Nabhan: none known

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