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

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.

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

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.