5‐Fluorouracil for keloid scars

Abstract

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

To assess the effects of intralesional 5‐Fluorouracil for the treatment of keloid scars.

Background

Description of the condition

Keloid scarring is an abnormal healing response characterised by excessive localised growth of scar tissue in response to skin trauma, burns or infection (Seifert 2009). It is generally considered to be distinct from hypertrophic scarring, another type of abnormal scar, in that it grows outside the boundaries of the original wound and does not regress over time, as well as having microscopic differences in structure (McGrouther 1994).

The cause of keloid scarring is unknown but there is a genetic predisposition in individuals with darker skin types and an incidence of 16% in those from black and Hispanic backgrounds (Chike‐Obi 2009). The lesions appear more commonly in specific body locations such as the ears, face, chest and shoulders, have a greater prevalence in people aged between 10 to 30 years old and are reported to occur in 5% to 15% of all wounds (Bayat 2003; Berman 1995). Although not malignant, keloids can often cause symptoms such as pain and itching and are frequently unsightly, potentially resulting in significant social and psychological distress (Bayat 2003; Bock 2006). Other problems include functional difficulties, for example due to formation of tight bands, or contractures, over joints, or obstructive issues due to their proximity to the eyes, ears or mouth.

The condition is notoriously difficult to treat as surgical excision alone usually results in recurrence, occasionally with a more aggressive lesion (Berman 1995). As a result there are many treatment options available, including steroid injections directly into the scar, laser therapy, radiotherapy and combination therapies (Blit 2012). However, there is no gold standard of treatment and it can be challenging for the clinician to choose which therapy to use for large or recurrent lesions.

Description of the intervention

5‐Fluorouracil (5FU) is a drug that has numerous clinical applications and has been used in the treatment of gastrointestinal, breast and skin cancers, in addition to its use in improving the appearance and lowering the recurrence of scars (Nanda 2004; Wendling 2003). Fitzpatrick first reported its use as a therapeutic injection directly into the keloid scar over a decade ago (Fitzpatrick 1999).

When administered to keloids 5‐Fluorouracil is injected with a needle directly into the abnormal scar tissue. This is termed an intradermal or intralesional therapeutic method of treatment. In addition, 5FU has been used as a preventative measure on those who are at risk of keloids by injection into the healing scar within a surgical wound (Haurani 2009). In order to determine the benefits of the intralesional direct effects of 5FU on keloid tissue, this review will consider 5FU usage only as a therapeutic method of treating existing keloid scarring and not as a preventative measure.

The frequency and dose of administration for intralesional 5FU can be variable but usually consists of a series of weekly intradermal injections with doses ranging from 50 mg to 150 mg. These doses are far smaller than those used for intravenous chemotherapy. The duration of treatment may be dependent upon response or the practitioner's preference, or both, but the technique is reported to require between one to 16 sessions before showing improvement. In addition, some practitioners prefer to combine 5FU with other modalities such as intradermal steroid or surgical excision, which may make analysis of its individual effectiveness difficult (Goldan 2008; Gupta 2002; Haurani 2009; Khare 2012; Nanda 2004; Prabhu 2012; Saha 2012).

How the intervention might work

The precise mechanism of action of 5FU is not known, but experimental studies have shown it may prevent the production of type I collagen, the main structural protein in scar tissue, by fibroblasts (Bulstrode 2005; Haurani 2009). Fibroblasts are a type of cell found in abundance in connective tissue and have the role of making and organising the framework of scars in response to tissue injury.

When introduced to human tissue cells, 5FU acts as an inhibitor to the enzyme thymidylate synthase, which is another protein crucial in the production of cellular DNA (Longley 2003). It may also be broken down into smaller chemicals that mimic nucleosides, the building blocks of DNA and RNA (Bulstrode 2005). These are incorporated into chains of DNA and RNA and disrupt their function within the cell. Such actions affect the production of cellular proteins including TGF‐Beta, which is an important signalling protein involved in the manufacture and assembly of collagen by fibroblasts (Kontochristopoulos 2005).

The overall effect when injected into keloids is therefore considered to be a diminished activity of fibroblasts and thus a reduction in the manufacture and maintenance of scar tissue mass. Despite this understanding, however, it remains uncertain whether 5FU affects a number of other pathways involved in scarring and the optimal concentration, dose or method of administration for these effects to take place is unclear (Bulstrode 2005; Uppal 2001). Due to its potential toxicity to dividing human cells it is given only in low doses and is generally not indicated in children, those who are pregnant or who have haematological disorders.

Why it is important to do this review

Keloid 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 (Seifert 2009). There is a general lack of evidence for proven safe and effective treatments for keloids, and therefore informed decision‐making can be difficult. As a consequence, the patient may need to undergo multiple attendances at outpatient clinics, need referrals to several different specialists and experience unnecessary complications from undergoing multiple interventions.

Steroid intralesional injections are often reported to have similar beneficial effects to 5FU (Gupta 2002). However, steroids may not be indicated in all people with keloid scarring, and may cause localised complications including increased pigmentation, infection, indented (atrophic) scarring or the appearance of small blood vessels (telangectasia). In contrast, the long‐term side effects of intralesional 5FU are relatively unknown. However, potential injury to the central nervous system has been shown in 5FU animal studies and issues with heart function have been reported with high dose intravenous 5FU, used, for example, in chemotherapy (Carroll 2015; Han 2008).

In addition, when compared to laser therapy, radiotherapy or surgical interventions, intralesional injection of 5FU requires less practitioner training. specialised equipment or facilities. Other advantages include its easy portability, storage and relatively low cost of production. Therefore it may allow increased availability of a practical treatment option to those at‐risk individuals in more disadvantaged geographical regions or healthcare systems where sophisticated interventions might not be feasible.

Previous reviews of the literature have highlighted a lack of good‐quality evidence, low trial participant numbers and inadequate follow‐up data to enable a full assessment of the use of 5FU in keloid scarring, and the latest analyses are now in need of updating (Bijlard 2015, Carroll 2015). Other recent reviews have methodological deficiencies, such as a failure to distinguish between hypertrophic and keloid scars, analysing 5FU only in combination therapies and assessing prevention over treatment as a therapeutic measure for 5FU (Perdanasari 2015, Shin 2016). As a result a rigorous systematic review which takes into account the most recent data is required to guide clinicians, healthcare managers and people with keloid scarring regarding the effectiveness of 5FU alone or in combination with other treatment modalities, and the rate of adverse events.

Objectives

To assess the effects of intralesional 5‐Fluorouracil for the treatment of keloid scars.

Methods

Criteria for considering studies for this review

Types of studies

We will only consider randomised controlled trials (RCTs) or cluster‐randomised trials in this review. Due to the difficulty of blinding in clinical practice, included studies may be double‐blinded, single‐blinded or open trials. If we identify them, we will also include trials in which multiple lesions in the same participant are treated with different interventions. We will exclude cross‐over trials, as we would consider this intervention to have a significant carry‐over treatment effect if used in the same lesion.

Types of participants

Participants can be of any age, sex and pigmentation skin type as defined by Fitzpatrick (Fitzpatrick 1988). The keloid scar could have been diagnosed clinically but should not be classified as hypertrophic in nature.

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.

5FU is not indicated for use in those who are pregnant or with haematological disorders such as thrombocytopenia or leucopenia. It is therefore assumed that people falling into these categories will be excluded by the trial authors.

Types of interventions

We will include trials that compare the intralesional injection of 5FU as a therapeutic treatment of existing keloid scars with any other intervention, including placebo or no treatment. Expected comparative interventions would include:

• intralesional injection of steroid;

• laser therapy;

• topical application of imiquimod;

• cryotherapy;

• radiotherapy;

• dressings (e.g. those made from silicone);

• other intervention;

• no intervention;

• placebo (e.g. intralesional saline).

Any dose, frequency or duration of 5FU treatment would be acceptable although it must be administered directly into the lesion by injection.

We will exclude trials that assess 5FU as a preventative intervention; for example the injection of 5FU into a wound following surgical excision of a keloid.

Types of outcome measures

Primary outcomes

• Scar improvement as assessed by a clinician or participant

Assessment of scar improvement should ideally be by validated scales: for example Vancouver Scar Scale (VSS), Manchester Scar Scale or Patient and Observer Scar Assessment Scale (POSAS) (Draaijers 2004; Idriss 2009).

Where a validated scale is not used, any scale used by the trial authors will be considered but it would be expected to describe a change in a specific measure of scar quality at an appropriate time point in the trial. This is discussed in Timing of Outcome Assessment at the end of this section.

Acceptable criteria for such scales would include a graded description of any one of the following factors as included in the POSAS (Draaijers 2004):

• Observer‐reported:

  • vascularity or degree of blood vessel infiltration;

  • pigmentation;

  • thickness;

  • relief;

  • pliability or stiffness.

• Participant‐reported:

  • pain;

  • itching;

  • colour;

  • stiffness;

  • thickness;

  • irregularity.

Secondary outcomes

• Rate of recurrence of keloids determined by the need for further intervention due to continued growth of scar, unacceptable appearance or continuation of symptoms. This should be assessed at an appropriate time interval (see Timing of Outcome Assessment below).

• Adverse events including infection, ulceration or malignancy. Scar pain and pigmentation are included as participant‐reported outcomes in validated scar scales and therefore would be considered as graded components of the primary outcome, that is, scar improvement.

• Improvement in quality of life, ideally reported by a validated scale such as SF‐36 (Anderson 1993).

Timing of outcome assessment

The assessment of outcomes should take place at an appropriate time for the intervention to have taken effect and will be considered in the following periods:

• short term: less than three months;

• medium term : three to six months;

• long term: more than six months.

This will allow pooling of results and therefore more accurate assessment and analysis of the efficacy of the intervention.

Search methods for identification of studies

Electronic searches

We will search the following electronic databases for relevant RCTs:

• the Cochrane Wounds Specialised Register;

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

• Ovid MEDLINE (1946 to date);

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

• Ovid Embase (1974 to date);

• EBSCO CINAHL Plus (1937 to date).

The draft search strategy for CENTRAL may be viewed below in Appendix 1.

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 developed by the UK Cochrane Centre (Lefebvre 2011). We will combine the CINAHL Plus search with the trial filters developed by the Scottish Intercollegiate Guidelines Network (SIGN 2017). There will be no restrictions with respect to language, date of publication or study setting. We will also search the following clinical trials registries:

• Clinical trials.gov

• WHO International Clinical Trials Registry Platform

• EU Clinical Trials Register

Searching other resources

We will handsearch associated reference lists from relevant textbook chapters and published reviews, conference abstracts such as those from international plastic surgery or dermatological meetings, and dissertation databases to identify any suitable studies.

Data collection and analysis

Selection of studies

Two of the review authors (NR and SG) will independently carry out literature searching using criteria agreed on prior to commencement of the selection process. We will identify appropriate studies by means of their title and abstract using search strategies designed with the assistance of the Cochrane Wounds Information Specialist.

Both review authors will discuss titles and abstracts to identify and reach agreement on studies suitable for further analysis with any disagreements being decided with the assistance of the third senior author (RP) and, if required, Cochrane Wounds advisors. We will use the full‐text published report for detailed analysis and data collection, with missing information being clarified by contacting the trial authors when required. We will record all reasons for exclusion of studies for which we had obtained full copies and will summarise this process by means of a PRISMA diagram (Liberati 2009).

In order to obtain all the relevant data from a single trial, we will collate multiple reports of the same study, which will be included only once in the review. Where data are incomplete or contradictory, we will contact the trial authors for clarification.

Data extraction and management

Two review authors (NR and SG) will independently collect all data from the relevant RCTs and record them on a data collection form, which has been designed and agreed upon by all review authors with assistance from Cochrane Wounds editorial base. Where data are absent we will attempt to contact the report authors.

Key data to be recorded would include:

• author ID, study ID, trial ID, title, publication date, journal, country of origin;

• trial design (e.g. group allocation criteria, concealment or blinding methods);

• participant numbers, unit of analysis, co‐morbidities and inclusion criteria (e.g. ethnicity, age, keloid aetiology and anatomical location, previous interventions);

• intervention and comparator details including care setting, dose, frequency and duration of administration;

• outcome and adverse event assessment methods, use of validated scales, timing of outcome assessment;

• methods of data collection, analysis and outcome reporting of both beneficial and adverse effects;

• results, level of participant compliance, duration of follow‐up;

• author conclusion summary;

• source of funding.

Assessment of risk of bias in included studies

Two review authors (NR and SG) will use the Cochrane 'Risk of bias' tool independently to assess bias (Higgins 2011a). This tool reports on the following risks of bias:

• selection bias;

• performance bias;

• detection bias;

• attrition bias;

• reporting bias;

• other bias, (i.e. potential source of bias related to the specific study design, claims of fraudulent data or other problem not addressed by the other domains).

We will use the data collection form mentioned above to record the analysis and discuss any disagreements. We will report the agreed outcomes on a table for each included study. The criteria on which we will base our judgements can be seen in Appendix 2.

Measures of treatment effect

Primary outcome

When a validated scar scale is reported we would expect the data to be presented as continuous data. If the reported scales are the same or similar we will use the mean difference (MD) with 95% confidence intervals (CIs). When the scales are different we will make comparisons using standardised mean differences (SMDs) with 95% CIs.

Occasionally the keloid scar assessment data may be presented as a short ordinal data scale, for example poor, moderate, good or excellent. In these cases we would convert into dichotomous data for analysis by means of risk ratios (RRs) and 95% CIs (Deeks 2011).

Secondary outcomes

• The rate of recurrence and specific adverse events will be reported as dichotomous data and we can therefore compare them by means of RRs with 95% CIs.

• We will analyse quality‐of‐life scales as continuous data and we will use MDs with 95% CIs when the scales are the same or similar, and SMDs with 95% CIs when the scales are sufficiently different.

Unit of analysis issues

We expect that the unit of analysis in most cases will be an individual with one keloid scar subjected to one intervention. There may be some trials, however, that subject multiple keloids on the same individual to the same or different interventions. This would increase the likelihood of a unit‐of‐analysis error due to the use of each treatment event, not the number of participants, as the denominator leading to an incorrect standard error and large CIs in the review comparison.

In such cases of multiple treatment sites per participant, we will aim to minimise the error by identifying these studies and grouping them into those receiving either the same or different interventions. We will then extract the summary statistic for each study and combine with other parallel trials using the 'generic inverse‐variance method' (Higgins 2011b). Such data would enable comparison across trial designs but may hide heterogeneity (i.e. study variability) effects and increase risk of bias. We will therefore document all instances of this in our report and carry out sensitivity analyses on trials of similar design in order to highlight any differences. This will also be noted during our 'Risk of bias' analyses.

Further unit of analysis issues may arise from reporting outcomes following repeated observations on participants at different points in time. When this occurs we will report participant data according to the time periods already stated, that is, short, medium and long term, and perform separate analyses on each.

Dealing with missing data

We will attempt to contact the authors of the appropriate trials for any missing data. Should we be unable to obtain the required information we shall detail this in the review along with any assumptions made in order to help with our analyses. Such assumptions would include population means for continuous data and the exclusion of unavailable dichotomous data. We will carry out sensitivity analyses in order to test the effects of these assumptions and document them in the report (Deeks 2011).

Assessment of heterogeneity

Given the variable nature of the intervention and participant characteristics there may be potentially significant clinical and methodological heterogeneity between trials. Intervention differences such as the dose, duration and method of 5FU administration, participant differences such as genetic background and age, and individual trial methodological and reporting differences could all have an effect on the observed effects. We will identify such disparities during selection of the trials and report them in the results of the review.

We will use the Chi² test to analyse the overall degree of statistical heterogeneity between studies and groups, as recommended by the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011) and include the results in the statistical analysis software Review Manager 5 (RevMan 5) (RevMan 2014). These results act as a guide to whether the observed differences in data could be due to chance alone, but must also be considered in conjunction with the number of participants in the trials and the assessment of methodological and clinical heterogeneity.

To assess the extent of statistical heterogeneity we will visually inspect of the forest plots and degree of overlap of CIs and Chi² tests, as well as considering the I² measure. We will consider a significant degree of heterogeneity exists when the Chi² test P is less than 0.10, I² is greater than 50% and there is poor graphical overlap of CIs. Such findings would lead us to seek an explanation by investigating potentially incorrectly entered data, problems with effect measures or issues with included trials. This may highlight the need for further sensitivity analyses (see the Data synthesis section below) or for us to consider the possibility that a meta‐analysis or assessment of heterogeneity might not be suitable for the collected data (Deeks 2011).

Assessment of reporting biases

If there are 10 or more studies included in the review, we will use a funnel plot of intervention effect versus intervention standard error to identify any potential reporting bias effect on the data. This will be carried out using RevMan 5 software tools (RevMan 2014). We will assess asymmetry by visual inspection in accordance with the guidelines in the Cochrane Handbook of Systematic Reviews of Interventions (Sterne 2011). Possible sources of asymmetry, such as publication bias or small‐study effects, would be discussed amongst all review authors and detailed in the report. If necessary, and with consultation with Cochrane Wounds' editorial base, we will carry out further tests for funnel plot asymmetry.

Data synthesis

We will consider trials to be of sufficient homogeneity if there is agreement between all review authors after analysis of clinical, methodological and statistical heterogeneity. Such determinants would include the correlation of intervention administration, participant characteristics and reporting of outcomes. Where we determine heterogeneity to be absent, we will use a fixed‐effect model to pool data, with the number of studies required for this taken as more than three.

Where clinical and methodological heterogeneity are minimal, but statistical heterogeneity is of moderate or substantial significance, we will explore the heterogeneity by re‐reviewing the data and using subgroup analysis or meta‐regression when there are ten or more studies. When no specific cause can be found, we will use a random‐effects model for the pooling of data. This method takes into account that the reported effects may not be identical, but that they do follow the same distribution (Deeks 2011).

If the heterogeneity between trials is such that no meaningful data synthesis can be made, we will analyse the results narratively.

We will use data tables with accompanying forest plots to represent pooled data and present continuous data in terms of MDs for similar intervention trial designs or SMDs for different designs with their corresponding 95% CIs. We will report dichotomous data in terms of RRs with 95% CIs. Where dichotomous and continuous data for the primary outcome are combined for purposes of comparison, we will convert odds ratios (ORs) to SMDs by means of the product of (ln OR) and (√3/π) with the same conversion made to the standard error (Deeks 2011).

Subgroup analysis and investigation of heterogeneity

If enough data are available, we will carry out subgroup analyses in order to determine potentially important differences in intervention characteristics and, if appropriate, to investigate heterogeneity. We will consider the following intervention subgroups:

• 5FU treatment dose

• Frequency of 5FU treatment

• Duration of 5FU treatment.

Sensitivity analysis

If the number of studies permits, we aim to carry out sensitivity analyses. These repeat the primary analysis of the collected data using alternate ranges of values in order to test the robustness of the review conclusions. We will analyse the following criteria.

• Type of scar scale used

• Using an alternate cut‐off point for the dichotomisation of ordinal scales

• Excluding studies considered to be at high risk of bias for one or more of the following; selection, attrition or detection bias.

• If applicable, excluding studies that use more than one treatment site per patient

• If applicable, excluding studies for which we have had to make statistical assumptions due to incomplete data.

'Summary of findings' tables

We will present the main outcomes in the 'Summary of findings' table. This table will contain the important findings of the review, including key statistics relating to the magnitude of intervention effects, the number of participants and included trials and the quality of the evidence found (Schünemann 2011a).

The outcomes which will be represented are:

• scar improvement;

• rate of recurrence;

• adverse events.

We will also include in the table an assessment of the quality of evidence by means of a GRADE assessment (GRADEPro GDT 2015). The GRADE approach permits an evaluation of the quality of evidence for each individual outcome by considering methodological quality, directness of evidence, heterogeneity, precision of effect estimates and risk of publication bias (Schünemann 2011b).

If analysis of an outcome is not possible, for example because of lack of data, we will clearly present the reasons for this in the table under the appropriate heading.

Appendices

Appendix 1. CENTRAL search strategy

#1 MeSH descriptor: [Cicatrix] explode all trees #2 (keloid* or cicatrix):ti,ab,kw #3 (hypertrophic next (scar or scars or scarred or scarring)):ti,ab,kw #4 {or #1‐#3} #5 MeSH descriptor: [Fluorouracil] explode all trees #6 (Fluorouracil or FU or 5FU or 5‐FU or FFU):ti,ab,kw #7 (Carac or Fluroplex or Efudex):ti,ab,kw #8 {or #5‐#7} #9 {and #4, #8} in Trials

Appendix 2. Criteria for 'Risk of bias' judgements

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 provided to permit a 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 provided to permit a 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 are unlikely to be related to true outcome (for survival data, censoring unlikely to be introducing bias).

• Missing outcome data are 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 the observed event risk is not enough to have a clinically relevant impact on the intervention effect estimate.

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

• Missing data have been imputed using appropriate methods.

High risk of bias

Any one of the following:

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

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

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

• 'As‐treated' analysis done with a 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 a 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 is/are reported using measurements, analysis methods, or subsets of the data (e.g. subscales) that were not prespecified.

• One or more reported primary outcomes was/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 is/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 provided to permit a 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.

Contributions of authors

Nicholas Rabey: conceived the review question; developed the protocol; co‐ordinated 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.

Stephen Goldie: developed the protocol; contributed to writing or editing the protocol; and made an intellectual contribution to the protocol.

Richard Price: conceived the review question; contributed to writing or editing the protocol; made an intellectual contribution to the protocol; and approved the final version of the protocol prior to submission.

Contributions of the editorial base

Joan Webster (Editor): edited the protocol; advised on methodology, interpretation and protocol content; approved the final protocol prior to submission.

Gill Rizzello (Managing Editor): co‐ordinated the editorial process; advised on content; edited the protocol.

Zipporah Iheozor‐Ejiofor (Methodologist): advised on content and the methodology, edited the protocol.

Reetu Child and Naomi Shaw (Information Specialists): designed and edited the search strategy and search methods sections.

Ursula Gonthier (Editorial Assistant): edited the reference section of the protocol.

Sources of support

Internal sources

• No sources of support supplied

External sources

• National Institute for Health Research (NIHR), UK.

  This project was supported by the NIHR via Cochrane Infrastructure funding to Cochrane Wounds. The views and opinions expressed herein are those of the authors and do not necessarily reflect those of the Systematic Reviews Programme, NIHR, NHS or the Department of Health.

Declarations of interest

Nicholas Rabey: no conflicts of interest to declare. Stephen Goldie: no conflicts of interest to declare. Richard Price: no conflicts of interest to declare.

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