Silicone gel sheeting for treating hypertrophic scars

Abstract

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

To assess the effectiveness of silicone gel sheeting in the treatment of hypertrophic scars compared with standard care or other therapies.

Background

Description of the condition

Each year, in high‐income countries alone, approximately 100 million people develop scars as a result of 55 million elective operations and 25 million operations following trauma (Sund 2000). Excessive scars form as a result of aberrations in the wound healing process, and may develop following any damage to the deep dermis, including burn injuries, lacerations, abrasions, surgery, piercings and vaccinations (Gauglitz 2011). Excessive scarring can cause pruritus (itching), pain, contractures (muscle shortening or spasm), and cosmetic disfigurement; and can dramatically affect people's quality of life, both physically and psychologically.

The physiology of wound healing can be divided into four stages: haemostasis (stopping of blood flow), inflammation, proliferation and tissue remodeling (Reinke 2012). The physiological process of normal wound healing will not result in hypertrophic scar formation. However, where chronic inflammation or infection occur this can prolong the wound healing process and lead to hypertrophic scar formation in part due to increased vessel and cell volume, as well as excessive collagen deposition (Gauglitz 2011).

Hypertrophic scars are defined as visible and elevated scars that do not spread into surrounding tissues and that often regress spontaneously (Rabello 2014). These scars are characterised by proliferation (rapid reproduction of cells) of the dermal tissue, with excessive deposition of fibroblast‐derived extracellular matrix proteins, particularly collagen, and by persistent inflammation and fibrosis (thickening and scarring of connective tissue) (Atiyeh 2007).

A review which identified 48 articles published since 1965, reported that the prevalence rate of hypertrophic scarring varied between 32% and 72% (Lawrence 2012). Other evidence shows that incidence rates of hypertrophic scarring vary from 40% to 70% following surgery to up to 91% following burn injury, depending on the depth of the wound (Lewis 1990). Despite this, there is surprisingly little literature regarding the incidence or potentially modifiable risk factors for this type of scarring. It is commonly accepted that hypertrophic scarring is much more likely with slower healing (e.g. burn wounds that take 3 weeks or more to heal) than those which heal more quickly (Chipp 2017). Additionally, there is a trend towards higher rates of hypertrophic scarring in darker skin types (Chipp 2017). Moreover, hypertrophic scars tend to recur after treatment (Cassuto 2010).

Differences between hypertrophic scars and keloid scars

Hypertrophic and keloid scars are both caused by abnormal wound healing and are characterised by pathologically excessive fibrosis in the skin (Arno 2014). Sometimes differentiating between hypertrophic scars and keloids can be difficult and lead to incorrect identification, which may result in inappropriate treatment (Arno 2014). Hypertrophic scars are mostly caused by trauma or burn injury to the deep dermis and do not extend beyond the boundary of the original injury (rarely wider than 1 cm). They usually occur around four weeks after the original injury, grow strongly for a few months, and tend to regress spontaneously within one year (Seifert 2009). Hypertrophic scars are red, raised and mostly linear scars occurring in any region of the body and can cause contracture when joint regions are affected (Rabello 2014).

Keloids can develop after minor injuries and may even spontaneously form on the sternal region without obvious injury. These scars can project beyond the original wound borders (Slemp 2006). Keloid scars can take years to develop, do not regress spontaneously and usually affect the sternal skin, shoulder, upper arms and earlobe, but rarely the palms of the hands and soles of the feet (Seifert 2009), and do not cause contracture. Keloids appear as pink to purple, shiny, rounded protuberances and are commonly seen in darker skinned populations and have never been reported in albino populations (Halim 2012).

Description of the intervention

The first documented use of silicone in gel form for the treatment of scars is from Australia's Adelaide Children's Hospital in 1981 (Perkins 1982). Silicone has since been produced in various forms, including: silicone cream compounds (Sawada 1992); silicone oil or gel with additives such as vitamin E (Palmieri 1995); in combination with other dressings (Davey 1991); and as custom made silicone applications. This particular review is solely concerned with commercially produced adhesive silicone gel sheeting.

Silicone gel sheeting is a soft, self‐adhesive and semi‐occlusive sheet used with the aim of treating hypertrophic scars and preventing their return. It is made from medical grade silicone (cross‐linked polydimethylsiloxane polymer) and reinforced with a silicone membrane backing (Thomas 1997), thought to give it increased durability and make handling easier (Mustoe 2008; Williams 1996). Silicone gel sheeting is one of the most commonly used treatments for hypertrophic scars (Bleasdale 2015).

A typical treatment cycle recommended for optimal results is eight to 12 weeks. Silicone gel sheeting can be applied to the scar as soon as the wound has healed or the sutures have been removed from the incision. Immature scars that are younger than 12 to 18 months are perceived to be good candidates for silicone treatment, but use of this treatment for mature scars also occurs. Current gel sheet products have been designed to be worn for up to 24 hours and can be washed and reused (Bleasdale 2015).

How the intervention might work

The potential mechanism of action of silicone therapy has not been completely determined, but is suggested to involve occlusion (blockage or closing of blood vessels) and hydration of the outer layer of the epidermis (Mustoe 2008; Reish 2008). Studies have shown that silicone gel sheeting decreases evaporation of water from the skin and increases hydration of the outer layer of the epidermis (Musgrave 2002). Any beneficial effects of silicone sheets on scars are not thought to be mediated by pressure or by changes in oxygen tension. Similarly, the effects are not thought to be attributable to silicone entering the scar, because biopsies of scars treated with silicone gel sheeting have shown no evidence of a foreign body reaction (Mustoe 2008). However, an increase in skin surface temperature could be involved because the skin surface temperature of hypertrophic burn scars under silicone gel sheeting may be slightly increased (Musgrave 2002), which in turn may lead to more collagenase activity and affect scarring (Borgognoni 2002).

Why it is important to do this review

Hypertrophic scarring is not life‐threatening but its symptoms and appearance can result in significant physical and psychological morbidities which may severely affect an individual's quality of life (Chipp 2017). There is a general lack of evidence for proven safe and effective treatments for hypertrophic scars, and therefore informed decision making can be difficult. As a consequence, a person with hypertrophic scarring may need to undergo multiple attendances at outpatient clinics, need referrals to several different specialists and experience unnecessary complications from undergoing multiple interventions. Silicone gel sheeting is an option currently used in the treatment of hypertrophic scars (Bleasdale 2015), but there is no up‐to‐date systematic review assessing its effectiveness for scar type. An existing Cochrane Review of silicone gel sheeting (O'Brien 2013), highlighted a lack of robust evidence, low trial participant numbers and inadequate follow‐up data to enable a full assessment of the effectiveness of silicone gel sheeting to treat scarring. In addition, O'Brien 2013 grouped together hypertrophic and keloid scars, analysing silicone in combination with other therapies and assessing prevention over treatment as a therapeutic measure for silicone. There are many differences in the epidemiological, clinical and histological aspects of hypertrophic scars and keloids. A more recent review had similar methodological deficiencies (Hus 2017), and there were clinical heterogeneities (e.g. interventions, the nature of the products) which impacted on interpretation. A rigorous systematic review which takes into account the most recent data is required to guide clinicians, healthcare managers and people with hypertrophic scarring, regarding the effectiveness of silicone gel sheeting.

This review is the first in a suite of new reviews formed by splitting the existing review, 'Silicone gel sheeting for preventing and treating hypertrophic and keloid scars' (O'Brien 2013), into individual reviews looking separately at treatment and prevention of hypertrophic or keloid scars, respectively.

Objectives

To assess the effectiveness of silicone gel sheeting in the treatment of hypertrophic scars compared with standard care or other therapies.

Methods

Criteria for considering studies for this review

Types of studies

We will include all published and unpublished randomised controlled trials (RCTs) irrespective of language of report. This will also include cluster‐randomised trials. We will not include quasi‐randomised trials (i.e. trials where the method of allocating participants to different forms of care is not truly random, for example allocation by date of birth, day of the week, medical record number, month of the year, or the order in which participants were included in the study (alternation)). We will also include studies with the split‐body design where either people with two similar scars are enrolled and each is randomised to one of the interventions, or where one half of a scar is randomised to one treatment and the other half to a different treatment. These approaches are similar to the 'split‐mouth' approach (Lesaffre 2009). We will note the lack of clarity in the 'Risk of bias' assessment if these studies have not been analysed using paired data, which reflects the reduced variation in evaluating different treatments on the same person.

Types of participants

We will include people with hypertrophic scars only. We will accept study authors' definitions of what they classed as 'hypertrophic scars', but it will need to be clear that only hypertrophic scars are the focus of the study. There will be no restrictions regarding age, sex or ethnicity of participants. The scar itself may be located on any part of the body, may be caused by any form of skin injury and may have been treated with any previous therapeutic intervention, e.g. surgical excision.

We will include studies that recruited participants with hypertrophic scars alongside people with other types of scars (keloid scars) if the proportion of participants with hypertrophic scars is at least 75%. If this proportion is not clear, we will exclude the study. We will also include mixed scar studies if randomisation was stratified on scar type, and data for the hypertrophic scars are presented separately. We will exclude all other mixed scar trials.

We will include RCTs that evaluate treatment of scarring alongside prevention of scarring only when randomisation is stratified for this factor and results for prevention and treatment are given separately.

Types of interventions

We plan to include studies where the type or schedule of silicone gel sheeting is the only systematic difference between study arms. This review therefore aims to include comparisons of silicone gel sheeting with each other and/or placebo and/or treatment as usual or no intervention. We anticipate that we could include studies evaluating the following types of comparisons:

• silicone gel sheeting compared with no intervention or placebo;

• different types of silicone gel sheeting compared with each other;

• different schedules, timings, or doses of the same silicone gel sheeting compared with the same silicone gel sheeting applied in an alternative schedule/timing/dose.

All of these types of comparisons could potentially include silicone gel sheeting used as part of a bundle of interventions aimed at hypertrophic scar treatment as well as a single intervention. Cointerventions designed to reduce hypertrophic scars are expected, for example pressure therapy, or corticosteroid injections; however these co interventions have to be delivered similarly to all comparison groups as this review aims to determine the effect of silicone gel sheeting specifically.

Types of outcome measures

We list primary and secondary outcomes below. If a study is otherwise eligible (i.e. correct study design, population and intervention/comparator) but does not report a listed outcome, then we will contact the study authors where possible to establish whether an outcome of interest here was measured but not reported. If we remain unsure whether an outcome was measured or not, we will include the study and record these details. We will report outcome measures at the latest time point available (assumed to be length of follow‐up if not specified) and the time point specified in the methods as being of primary interest (if this was different from latest time point available). For all outcomes, we plan to class assessment of outcome measures from:

• less than eight weeks as short term;

• eight weeks to one year as medium term;

• more than one year as long term.

Primary outcomes

• Change in severity of hypertrophic scars as assessed by health professionals or other staff, measured using a specific scale (as defined by the authors): for example Vancouver Scar Scale (VSS), Manchester Scar Scale or Patient and Observer Scar Assessment Scale (POSAS) (Draaijers 2004; Idriss 2009).

• Change in severity of hypertrophic scars, validated by participant using a specific scale (as defined by the authors): for example POSAS (Draaijers 2004; Idriss 2009).

• Adverse events (measured using survey/questionnaire/data capture process or visual analogue scale (VAS)), where a clear methodology for the collection of adverse event data was provided. This would include making it clear whether (i) events were reported at the participant level or if multiple events per person were reported; and (ii) that an appropriate adjustment was made for data clustering. Where available, we will extract data on all serious and all non‐serious adverse events. We will not extract individual types of adverse events, such as pain or infection, which require specific assessment under this outcome, rather we will use the assessment of any event classed as adverse by the participant or health professional, or both, during the trial.

Secondary outcomes

• Pain (including pain at dressing change). We will include pain only where mean scores with a standard deviation were reported using a scale validated for the assessment of pain levels, such as a VAS.

• Adherence to treatment, measured by physician and/or patient report.

• Participant health‐related quality of life/health status, measured using a standardised generic questionnaire (e.g. EQ‐5D, SF‐36, SF‐12 or SF‐6), or scar‐specific questionnaires at noted time points. We will not include ad hoc measures of quality of life that were not likely to be validated and would not be common to multiple trials.

• Within‐trial cost‐effectiveness analysis comparing mean differences in effects with mean cost differences between the two arms: data extracted will be incremental mean cost per incremental gain in benefit (incremental cost‐effectiveness ratio (ICER)).

Search methods for identification of studies

Electronic searches

We will search the following electronic 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, MEDLINE Daily and Epub Ahead of Print) (1946 to present);

• Ovid Embase (from 1974 to present);

• EBSCO CINAHL Plus (from 1937 to present).

We have devised a draft search strategy for CENTRAL which is displayed 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). We will not impose any 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 and unpublished studies;

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

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

Searching other resources

We will try 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 health technology assessment reports. We will also search conference abstracts manually or electronically through a search of conference proceedings.

Data collection and analysis

Selection of studies

Two review authors (ZL and QJ) 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 (ZL and QJ) will independently check the full papers for eligibility; disagreements will be resolved by discussion and, where required, the input of a third review author (JC). Where required and possible, we will contact study authors where the eligibility of a study is unclear. We will record all reasons for exclusion of studies for which we have obtained full copies. We will complete a PRISMA flowchart to summarise this process (Liberati 2009).

Where studies have been reported in multiple publications/reports, we will obtain all publications. Data extraction will be performed at the level of the study rather than the report.

Data extraction and management

We will extract and summarise details of the eligible studies using a data extraction sheet. Two review authors (ZL and QJ) will extract data independently and will resolve disagreements by discussion, drawing on a third review author (JC) where required. Where data are missing from reports, we will attempt to contact the study authors to obtain this information. Where a study with more than two intervention arms is included, we will only extract data from intervention and control groups that meet the eligibility criteria.

We will extract the following data, where possible, by treatment group for the prespecified interventions and outcomes in this review. We will collect outcome data for relevant time points, as described in Types of outcome measures.

• Country of origin

• Type of wound preceding scar (e.g. surgical, burn, trauma)

• Unit of randomisation (e.g. participant or wound)

• Unit of analysis (e.g. participant or wound)

• Trial design (e.g. parallel; cluster)

• Number of participants randomised to each trial arm

• Eligibility criteria and exclusion criteria

• Details of treatment regimen received by each group

• Duration of treatment

• Details of any co interventions

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

• Outcome data for primary and secondary outcomes (by group)

• Duration of follow‐up

• Number of withdrawals (by group)

• Publication status of study

• Source of funding for trial

Assessment of risk of bias in included studies

Two review authors (ZL and QJ) will independently assess included studies using the Cochrane approach for assessing risk of bias as detailed in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). We will resolve disagreements through discussion or by consulting a third review author (JC). The Cochrane tool for assessing risk of bias addresses specific domains: sequence generation, allocation concealment, blinding of participants and personnel, blinding of outcome assessors, incomplete data, selective outcome reporting, and other issues. In this review we will record issues with unit of analysis, for example, where a paired or cluster trial has been undertaken but analysed at the individual level in the study report (Appendix 2). 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 to treatment will be difficult in open trials, and therefore performance bias is a risk. However, where open studies have aimed to minimise performance bias by design and activities such as documenting protocol deviations and active minimisation of differential care/co‐interventions they may not be considered at high risk of bias. We will present our assessment of risk of bias using two 'Risk of bias' summary figures; one that is a summary of bias for each item across all studies, and a second that shows a cross‐tabulation of each trial by all of the risk of bias items.

For trials using cluster‐randomisation, we will also consider the risk of bias considering: recruitment bias, baseline imbalance, loss of clusters, incorrect analysis, and comparability with individually‐randomised trials (Higgins 2011b; Appendix 3).

Measures of treatment effect

For dichotomous outcomes, we will calculate the risk ratio (RR) with 95% confidence intervals (CIs). For continuous outcomes we will use the mean difference (MD) with 95% CIs, if all trials use the same or a similar assessment scale. If trials use different assessment scales, we will use the standardised mean difference (SMD) with 95% CIs.

Unit of analysis issues

Where studies randomised at the participant level and measured outcomes at the scar level (e.g. scar improvement), we will treat the participant as the unit of analysis when the number of scars assessed appeared equal to the number of participants (e.g. one scar per person).

Where there are instances of clustered data, that is where a proportion of individually‐randomised trial participants had outcome data collected and reported on multiple scars, this is not treated as a cluster trial since not all participants would have multiple scars. Rather it is a trial that incorrectly includes a mixture of individual and clustered data. We will note these trials and record the issue in the 'Risk of bias' assessment. Data will be extracted and presented but will not be the subject of any further analyses.

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

• the number of clusters (or groups) randomised to each intervention group; or the average (mean) size of each cluster;

• the outcome data ignoring the cluster design for the total number of participants (e.g. number or proportion of participants with events, or means and standard deviations (SD)); and

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

Where multiple trial arms are reported in a single trial, we plan to include only the relevant arms. If two or more interventions are compared with the control and are eligible for the same meta‐analysis, we plan to pool the intervention arms and compare them with the control. If the study data cannot be analysed correctly, we will extract outcome data and present them but will not analyse them further.

We will also include studies with split‐body design, where either people with two eligible scars were enrolled and each scar was randomised to one of the interventions, or where one half of a scar was randomised to one treatment and the other half to a different treatment. These approaches are similar to the 'split‐mouth' approach (Lesaffre 2009). These studies should be analysed using paired data which reflects the reduced variation in evaluating different treatments on the same person. Although trial authors may have analysed paired data, poor presentation may make it impossible for review authors to extract paired data. We will adopt a pragmatic but conservative approach to analyses including clustered and paired data in an included study. We plan to include such studies in meta‐analyses where possible (where unadjusted clustered data would produce too narrow CIs and unadjusted paired data too wide CIs). We will undertake sensitivity analyses to explore the impact of including data that had been inappropriately unadjusted. Where the sensitivity analysis produced a materially different result to the primary analysis, we will use these analyses as the basis for the GRADE assessment and the 'Summary of findings' tables.

Dealing with missing data

It is common to have data missing from trial reports. 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. If it is thought that study authors might be able to provide some missing data, we will attempt to contact them; however, data are often missing because of loss to follow‐up. When a trial did not specify participant group numbers before dropout, we plan to present only complete case data.

For continuous variables, we will present all analyses on as a complete case analysis and will not conduct an imputation. The amount of attrition and the potential for introduction of bias will be assessed and reported as part of the 'Risk of bias' assessment process. Where there are missing data, such as standard deviations, we will aim to calculate these using all available data, wherever possible (Higgins 2011a). If calculation is not possible, we will contact the study authors. Where these measures of variation remain unavailable and we would not be able to calculate them, we will exclude the study from any relevant meta‐analyses that we conduct.

Assessment of heterogeneity

Assessment of heterogeneity can be a complex, multifaceted process. Firstly, we will consider clinical and methodological heterogeneity: that is, the degree to which the included studies vary in terms of participant, intervention, outcome, and characteristics such as duration of follow‐up. We will supplement this assessment of clinical and methodological heterogeneity by information regarding statistical heterogeneity, assessed using the Chi² test (we will consider a significance level of P < 0.10 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). In general, I² values of 30%, or more, may represent moderate heterogeneity (Higgins 2003), and values of 75% or more, indicate considerable heterogeneity (Deeks 2011). However, these figures are only a guide, and it has been recognised that statistical tests and metrics may miss important heterogeneity. Thus, whilst these will be assessed, the overall assessment of heterogeneity will assess these measures in combination with the methodological and clinical assessment of heterogeneity. See Data synthesis for further information about how we will deal with potential heterogeneity in the data analyses.

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). We plan to present funnel plots for meta‐analyses comprising 10 RCTs or more using Review Manager 5 (Review Manager 2014).

Data synthesis

We will combine details of included studies in a narrative review according to type of comparator, where appropriate by type of surgical wound, and then by outcomes and time period. We will consider clinical and methodological heterogeneity, and undertake pooling when studies appear appropriately similar in terms of wound type, intervention type, duration of follow‐up, and outcome type.

In terms of meta‐analytical approach, 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 CIs. We will only use a fixed‐effect approach when clinical heterogeneity is thought to be minimal, and statistical heterogeneity is not statistically significant for the Chi² value and 0% for the I² assessment (Kontopantelis 2013). We will adopt this approach as it is recognised that statistical assessments can miss potentially important between‐study heterogeneity in small samples, hence the preference for the more conservative random‐effects model (Kontopantelis 2012). Where clinical heterogeneity is thought to be acceptable, or of interest, we may meta‐analyse even when statistical heterogeneity is high, but we will attempt to interpret the causes behind this heterogeneity, and will consider using meta‐regression for that purpose, if possible (Thompson 1999).

We will present data using forest plots, where possible. For dichotomous outcomes, we will present the summary estimate as a RR with 95% CI. Where continuous outcomes are measured in the same way across studies, we plan to present a pooled MD with 95% CI; we plan to pool SMD estimates where studies measure the same outcome, but use different scales.

We will obtain pooled estimates of treatment effect using Review Manager 5 software (Review Manager 2014).

Subgroup analysis and investigation of heterogeneity

Studies about the mechanism of scar development report that scar formation is affected by wound healing (Yordanov 2014). Where feasible, we will consider whether there is potential heterogeneity in treatment outcomes based on the wound type which preceded the scar, i.e. burn, surgery, trauma etc.

Sensitivity analysis

We will assess the impact on results of removing from meta‐analyses studies classed as having a high or unclear risk of bias for any domain. We will also assess the impact of not including studies with incorrectly analysed paired or clustered data in meta‐analyses.

'Summary of findings' tables and assessment of the quality of the evidence using the GRADE approach

We will present the main results of the review in 'Summary of findings' tables. We plan to use the principles of the GRADE system to assess the certainty of the body of evidence associated with specific outcomes (Guyatt 2008), and construct 'Summary of findings' tables using GRADEpro GDT software (GRADEpro GDT 2015).

These tables will present key information concerning the certainty of the evidence, the magnitude of the effects of the interventions examined and the sum of available data for the main outcomes (Schünemann 2011a). The 'Summary of findings' tables also include an overall grading of the evidence related to each of the main outcomes using the GRADE approach, which defines the certainty of a body of evidence as the extent to which one can be confident that an estimate of effect or association is close to the true quantity of specific interest. The certainty of a body of evidence involves consideration of within‐trial risk of bias (methodological quality), directness of evidence, heterogeneity, precision of effect estimates and risk of publication bias (Schünemann 2011b). We plan to include the following main outcomes in the 'Summary of findings' tables:

• change in severity of hypertrophic scars reported by health professionals

• change in severity of hypertrophic scars reported by participant

• adverse events

• adherence to treatment

• health‐related quality of life

• cost‐effectiveness.

For relevant outcomes reported for comparisons not listed above, we will present a GRADE assessment without a 'Summary of findings' table.

When evaluating the 'Risk of bias' domain, we plan to downgrade the GRADE assessment only when we classify a study as being at high risk of bias for one or more domains, or when the 'Risk of bias' assessment for selection bias is unclear (that is, classified as unclear for the generation of randomisation sequence domain and the allocation concealment domain). We will downgrade the GRADE assessment when the 'Risk of bias' assessment for blinding is unclear (classified as unclear for the performance bias domain and the detection bias domain) as well as at high risk of bias. We will not downgrade for unclear 'Risk of bias' assessments in other domains.

Following GRADE guidance (GRADE 2013), in assessing the precision of effect estimates we will assess the size of CIs, downgrading twice for imprecision when there are very few events and CIs around effects include both appreciable benefit and appreciable harm. We will consider the CI to be especially fragile where there are fewer than 50 participants; event rates will be also considered in determining fragility.

Appendices

Appendix 1. The Cochrane Central Register of Controlled Trials (CENTRAL) draft search strategy searched via the Cochrane Register of Studies

1 MESH DESCRIPTOR Cicatrix EXPLODE ALL AND CENTRAL:TARGET

2 MESH DESCRIPTOR Hypertrophy EXPLODE ALL AND CENTRAL:TARGET

3 hypertrophic OR cicatrix OR scar OR scars OR scarred OR scarring AND CENTRAL:TARGET

4 #1 OR #2 OR #3

5 MESH DESCRIPTOR Silicones EXPLODE ALL AND CENTRAL:TARGET

6 MESH DESCRIPTOR Silicone Elastomers EXPLODE ALL AND CENTRAL:TARGET

7 silicone* AND CENTRAL:TARGET

8 (cica‐care or silastic or (advasil NEXT conform) or bapscarcare or ciltech or dermatix or mepiform or (scar NEXT FX) or silgel) AND CENTRAL:TARGET

9 #5 OR #6 OR #7 OR #8

10 #4 AND #9

Appendix 2. 'Risk of bias' assessment (individually‐randomised controlled trials)

1. Was the allocation sequence randomly generated?

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

Insufficient information about the sequence generation process to permit judgement of low or high risk of bias.

2. Was the treatment allocation adequately concealed?

Low risk of bias

Participants and investigators enrolling participants could not foresee assignment because one of the following, or an equivalent method, was used to conceal allocation: central allocation (including telephone, web‐based and pharmacy‐controlled randomisation); sequentially numbered drug containers of identical appearance; sequentially numbered, opaque, sealed envelopes.

High risk of bias

Participants or investigators enrolling participants could possibly foresee assignments and thus introduce selection bias, such as allocation based on: use of an open random allocation schedule (e.g. a list of random numbers); assignment envelopes without appropriate safeguards (e.g. envelopes were unsealed, non‐opaque, or not sequentially numbered); alternation or rotation; date of birth; case record number; any other explicitly unconcealed procedure.

Unclear

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, for example if the use of assignment envelopes is described, but it remains unclear whether envelopes were sequentially numbered, opaque and sealed.

3. Blinding ‐ was knowledge of the allocated interventions adequately prevented during the study?

Low risk of bias

Any one of the following.

• No blinding, but the review authors judge that the outcome and the outcome measurement are not likely to be influenced by lack of blinding.

• Blinding of participants and key study personnel ensured, and unlikely that the blinding could have been broken.

• Either participants or some key study personnel were not blinded, but outcome assessment was blinded and the non‐blinding of others unlikely to introduce bias.

High risk of bias

Any one of the following.

• No blinding or incomplete blinding, and the outcome or outcome measurement is likely to be influenced by lack of blinding.

• Blinding of key study participants and personnel attempted, but likely that the blinding could have been broken.

• Either participants or some key study personnel were not blinded, and the non‐blinding of others likely to introduce bias.

Unclear

Either of the following.

• Insufficient information to permit judgement of low or high risk of bias.

• The study did not address this outcome.

4. Were incomplete outcome data adequately addressed?

Low risk of bias

Any one of the following.

• No missing outcome data.

• Reasons for missing outcome data unlikely to be related to true outcome (for survival data, censoring unlikely to be introducing bias).

• Missing outcome data balanced in numbers across intervention groups, with similar reasons for missing data across groups.

• For dichotomous outcome data, the proportion of missing outcomes compared with observed event risk not enough to have a clinically relevant impact on the intervention effect estimate.

• For continuous outcome data, plausible effect size (difference in means or standardised difference in means) among missing outcomes not enough to have a clinically relevant impact on observed effect size.

• Missing data have been imputed using appropriate methods.

High risk of bias

Any one of the following.

• Reason for missing outcome data likely to be related to true outcome, with either imbalance in numbers or reasons for missing data across intervention groups.

• For dichotomous outcome data, the proportion of missing outcomes compared with observed event risk enough to induce clinically relevant bias in intervention effect estimate.

• For continuous outcome data, plausible effect size (difference in means or standardised difference in means) among missing outcomes enough to induce clinically relevant bias in observed effect size.

• 'As‐treated' analysis done with substantial departure of the intervention received from that assigned at randomisation.

• Potentially inappropriate application of simple imputation.

Unclear

Either of the following.

• Insufficient reporting of attrition/exclusions to permit judgement of low or high risk of bias (e.g. number randomised not stated, no reasons for missing data provided).

• The study did not address this outcome.

5. Are reports of the study free of suggestion of selective outcome reporting?

Low risk of bias

Either of the following.

• The study protocol is available and all of the study’s prespecified (primary and secondary) outcomes that are of interest in the review have been reported in the prespecified way.

• The study protocol is not available but it is clear that the published reports include all expected outcomes, including those that were prespecified (convincing text of this nature may be uncommon).

High risk of bias

Any one of the following.

• Not all of the study's prespecified primary outcomes have been reported.

• One or more primary outcomes are reported using measurements, analysis methods or subsets of the data (e.g. subscales) that were not prespecified.

• One or more reported primary outcomes were not prespecified (unless clear justification for their reporting is provided, such as an unexpected adverse effect).

• One or more outcomes of interest in the review are reported incompletely so that they cannot be entered in a meta‐analysis.

• The study report fails to include results for a key outcome that would be expected to have been reported for such a study.

Unclear

Insufficient information to permit judgement of low or high risk of bias. It is likely that the majority of studies will fall into this category.

6. Other sources of potential bias

Low risk of bias

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

High risk of bias

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

• had a potential source of bias related to the specific study design used; or

• has been claimed to have been fraudulent; or

• had some other problem.

Unclear

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.

Appendix 3. 'Risk of bias' assessment (cluster‐randomised controlled trials)

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

• recruitment bias;

• baseline imbalance;

• loss of clusters;

• incorrect analysis; and

• comparability with individually‐randomised trials.

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

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 randomisation of clusters. Reporting of the baseline comparability of clusters, or statistical adjustment for baseline characteristics, can help reduce concern about the effects of baseline imbalance.

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.

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.

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. 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 (which were often 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

Qingling Jiang: conceived the review question; developed and advised on the protocol; coordinated the protocol development; contributed to writing and editing the protocol; made an intellectual contribution to the protocol; approved the final version of the protocol prior to submission; and is a guarantor of the protocol.

Junjie Chen: made an intellectual contribution to the protocol; advised on the protocol.

Zhenmi Liu: conceived the review question; developed and advised on the protocol; coordinated the protocol development; produced the first draft of the protocol; contributed to writing and editing the protocol; made an intellectual contribution to the protocol; approved the final version of the protocol prior to submission; and is a guarantor of the protocol.

Contributions of the editorial base

Jo Dumville (Coordinating 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.

Naomi Shaw and Sophie Bishop (Information Specialists): designed the search strategy and edited the search methods section.

Ursula Gonthier (Editorial Assistant): proof read the protocol and edited the reference sections.

Sources of support

Internal sources

• West China School of Public Health, West China Hospital, Sichuan University, China.

External sources

• 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

Qingling Jiang: none known

Junjie Chen: none known

Zhenmi Liu: none known

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