Types of studies

We will include published and unpublished randomised controlled trials (RCTs), including cluster/group RCTs and cross‐over RCTs if they report outcome data at the end of the first treatment period prior to cross‐over. We will only include controlled clinical trials (CCTs) for a particular intervention in the absence of RCTs assessing effectiveness of that intervention. CCTs are quasi‐randomised trials in which an intervention (and appropriate control) are tested without strict randomisation. We will also include split‐site or split‐body trials, where one burn (or part of a burn) on a participant's body is randomised to different interventions. Trials assessing interventions where only a proportion of participants have pruritus at baseline (but are otherwise eligible for inclusion) will only be included if randomisation was stratified by pruritus status. In other words, if participants in a trial were first grouped into strata (i.e. pruritus versus no pruritus), and then patients within the pruritus stratum were randomised to treatment, we will include data from the pruritus stratum as this approach preserves randomisation. We will not impose any restriction on the basis of language, publication status, or date of publication.

Types of participants

We will include trials recruiting people of any age and socioeconomic background who have sustained any degree and any total body surface area (TBSA) of burn injury and who have experienced postburn pruritus on the burn site, grafted site, or on the donor site. Trials involving any type of burn injury (e.g. chemical, scald or flame burns) and managed in any care setting are eligible. As the definitions of 'burn injury' and 'pruritus' may vary, we will accept author definitions.

We will exclude studies recruiting people with pruritus originating from burn‐associated trauma (i.e. fractures). We will also exclude studies recruiting people at risk for postburn pruritus as prophylactic interventions are beyond the scope of this review which focuses on treatment rather than prevention.

Types of interventions

We will include published and unpublished trials that compare an intervention used as a treatment for postburn pruritus with any other intervention, placebo or sham intervention, or no intervention. Relevant interventions might include, but are not limited to:

• laser therapy;

• extracorporeal shockwave therapy;

• pharmacological agents (i.e. antihistamines);

• wound dressings;

• massage therapy;

• cooling agents;

• TENS.

Types of outcome measures

Electronic searches

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

• Cochrane Wounds Group Specialised Register (to present);

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

• Ovid MEDLINE (from 1946 onwards);

• Ovid Embase (from 1974 onwards);

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

We have devised a draft search strategy for CENTRAL which is displayed in Appendix 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 2019). We will combine the Embase search with the Ovid Embase filter terms developed by the UK Cochrane Centre (Lefebvre 2019). We will combine the CINAHL Plus search with the randomised trial filter developed by the Scottish Intercollegiate Guidelines Network (SIGN 2018). We will not impose any restrictions on the searches with respect to language, date of publication or study setting.

We will also search the following trial registries for unpublished and ongoing studies.

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

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

Searching other resources

We aim 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.

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

We will not perform a separate search for adverse effects of interventions used for the treatment of postburn pruritus. We will consider adverse effects described in included studies only.

Selection of studies

Two review authors (SS and WS) will independently assess titles and abstracts of the citations retrieved against the inclusion criteria. Following this preliminary assessment, we will obtain full‐text copies of all studies considered to be of potential interest. We will use these full‐text publications for detailed analysis and data collection.

Two review authors (SS and WS) will independently check the full papers for eligibility. Disagreements will be resolved by discussion and, where required, the input of other review authors (VG, DN, FGF) will be sought. If studies retrieved are reported through multiple publications, we will obtain and assess all publications. We will contact the corresponding authors of such studies by email to avoid double‐counting participants. We will report all reasons for exclusion of studies for which full copies were obtained. We will document and illustrate the study selection process in a PRISMA flow diagram (Liberati 2009).

Data extraction and management

Two reviewers will independently extract data from included studies. Any disagreements will be resolved by discussion and, if necessary, with the involvement of a third reviewer. Where necessary, the authors of included studies will be contacted to clarify data.

We intend to extract:

• bibliographic data including trial ID (if registered), authors, title of the publication, publication date, and periodical;

• country in which study was conducted;

• care setting in which study was conducted;

• study design details;

• number of participants randomised to each trial arm;

• inclusion/exclusion criteria;

• sample size;

• participants' age;

• pruritic site (i.e. burn site, grafted site, donor site);

• burn location;

• burn as percentage of total body surface area (TBSA);

• burn depth;

• details of all measurement tools/scales;

• primary and secondary outcome(s) with definitions and time points;

• unit of analysis and details of analysis;

• unit of randomisation (per participant) ‐ single burn or multiple burns on the same participant;

• intervention details including type, dosage, and duration;

• results;

• loss to follow‐up;

• length of follow‐up.

We will enter and combine the data using the latest version of Review Manager 5 software (Review Manager 2014).

Assessment of risk of bias in included studies

Two reviewers will independently assess risk of bias of each of all included RCTs using the Cochrane's Risk of Bias tool (see Appendix 2). This tool has six specific domains:

• Sequence generation (selection bias)

• Allocation concealment (selection bias)

• Blinding

• Incomplete data (attrition bias)

• Selective outcome reporting (reporting bias)

• Other issues (Higgins 2011a)

We will assess blinding of participants and personnel (performance bias), blinding of outcome assessment (detection bias), and incomplete outcome data (attrition bias) for each of the review outcomes separately (Higgins 2011a). We note that it is often impossible to blind participants and personnel in trials. In this case, performance bias may be introduced if knowledge of treatment allocation results in deviations from intended interventions and/or differential co‐interventions use or care between groups not specified in study protocols which may influence outcomes. We will attempt to understand if, and how, included studies compensated for challenges in blinding, e.g. implementing strict protocols to maximise consistency of co‐interventions between groups to reduce the risk of performance bias. We also note that non‐blinded assessment of subjective outcomes tends to be associated with more optimistic effect estimates of experimental interventions in RCTs (Hróbjartsson 2012). Therefore, we will judge non‐blinded outcome assessment as high risk of detection bias. In this review we will include issues around unit of analysis under the domain of “other issues”. For example unit of analysis will occur where a cluster‐randomised trial has been undertaken but analysed at the individual level in the study report.

We will judge the domain risk of bias assessment using the high, low, or unclear risk of bias category. Any discrepancy between two reviewers will be resolved by discussion and a third reviewer where necessary. Where possible, when a lack of reported information results in a judgement of unclear risk of bias, we will contact study authors for clarification.

We will present our assessment of risk of bias using two “Risk of bias” summary figures; one will be a summary of bias for each item across all studies, and the second will show a cross‐tabulation of each trial by all of the “Risk of bias” items. Once judgements have been given for all risk of bias domains, the overall risk of bias for each study will be judged as:

• Low risk of bias if all domains are judged to be at low risk of bias;

• Unclear risk of bias if at least one domain is judged to be unclear risk of bias, but no domain is at high risk of bias; or

• High risk of bias if at least one domain is judged as being at high risk of bias or all domains have unclear risk of bias judgements as this can substantially reduce confidence in the result.

Any discrepancy between two reviewers will be resolved by discussion and a third reviewer where necessary.

For trials using cluster‐randomisation, we will also consider the following five risks of bias identified by Higgins 2011b (full descriptions of each provided in Appendix 3).

• Recruitment bias

• Baseline imbalance

• Loss of clusters

• Incorrect analysis

• Comparability with individually‐randomised trials

Measures of treatment effect

For dichotomous outcomes, we will calculate the risk ratio (RR) with 95% confidence intervals (CIs). For continuously distributed outcome data, we will use the mean difference (MD) with 95% CIs if all trials use the same or similar assessment scale. When a validated pruritus scale is used, we would expect the data to be presented as continuous data. When clinical scales employed are different, we will make comparisons using standardised mean differences (SMDs) with 95% CIs. We will report time‐to‐event data as hazard ratios (HRs) where possible, in accordance with the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011). If studies reporting time‐to‐event data (e.g. time to pruritus severity reduction) do not report HRs, then, if feasible, we will estimate this using other reported outcomes by applying available statistical methods (Parmar 1998; Tierney 2007).

Unit of analysis issues

We expect that the unit of analysis in most trials will be one participant with one pruritic anatomical region subjected to one intervention. For such trials, we will treat the participant as the unit of analysis when the number of pruritic sites assessed appears equal to the number of participants (e.g. pruritic site per participant). However, we anticipate the following two types of unit of analysis issues.

Firstly, there may be trials where multiple wounds are associated with one or more participants. Here, the participant is randomised to an intervention (where all of their wounds receive this intervention), and instead of focusing on the individual, the analysis is conducted at the level of the wound. Such a trial would generate clustered data. However, many cluster‐randomised trials are incorrectly analysed as if randomisation was performed on individuals rather than clusters. We will record where a cluster‐RCT has been conducted but incorrectly analysed. This will be recorded as part of the 'Risk of bias' assessment. If possible, we will approximate the correct analyses based on guidance in theCochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b), using information on:

• the number of clusters (or groups) randomised to each intervention group, or the 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); and

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

If we cannot analyse the trial data correctly, we will extract and present outcome data but not analyse it further.

Secondly, there may be trials where individuals have multiple wounds/wound areas and wounds are randomised to different interventions. When this is the case, we will note that randomisation has been undertaken at the wound level and will assess whether correct paired analysis was performed. If an incorrect analysis was performed, and if the required data can be accessed by contacting the study authors, we will try and approximate a correct analysis. If this is not possible, we will extract and present the relevant outcome data but not analyse or pool them further (Lesaffre 2009).

Dealing with missing data

It is common to have data categories missing from burn trial publications (Sinha 2018b). Of particular concern are missing data due to exclusion of participants postrandomisation, or exclusion of participant records who are lost to follow‐up. We anticipate the latter being a potential concern since most pruritic trials are of lengthy duration and can span several months. Since such exclusions compromise randomisation and can introduce bias in our analysis, we will contact corresponding authors to confirm no patient records were excluded due to loss to follow‐up if the authors do not mention this in the paper. We will also contact the corresponding authors if review‐relevant data fields are missing. If data remains missing for the 'change in burn‐related pruritus' (primary outcome), we will assume no change in pruritus for that patient in our analysis. For all secondary outcomes, we will synthesise the data available without imputing missing data.

Assessment of heterogeneity

Assessment of heterogeneity is a multifaceted process. First, we will consider clinical and methodological heterogeneity. Given the variable nature of burns, there may be significant clinical and methodological heterogeneity between included burn trials (Sinha 2017). We will assess clinical and methodological heterogeneity of included studies by considering them in terms of participant characteristics (i.e. burn severity as indicated by percentage TBSA and burn depth), intervention, anatomical site of the burn, and outcome parameters reported. In addition, interventional differences, such as the dose, duration, and route of administration could all affect the observed effects. We will identify such disparities during selection of the trials and report them in the results of the review. This assessment of clinical and methodological heterogeneity will be supplemented by analysis regarding statistical heterogeneity, assessed using the Chi² test (a significance level of P < 0.10 will be considered to indicate statistically significant heterogeneity) in conjunction with the I² measure (Higgins 2003). The I² measure examines the percentage of total variation across RCTs that is due to heterogeneity rather than chance alone (Higgins 2003). For reference, I² values of 25% or less suggest a low level of heterogeneity (Higgins 2003), and more than 75% indicate very high heterogeneity (Deeks 2011). Where there is evidence of high heterogeneity, we will explore this further: see Data synthesis for how we will deal with potential heterogeneity in the data analyses.

Assessment of reporting biases

Reporting biases arise when dissemination of trial findings is influenced by the nature and direction of results. Publication biases arise from withholding negative results from publication. Publication bias is one of many plausible causes of 'small study effects', 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 if a minimum of 10 trials are available for the meta‐analysis of the primary outcome (Sterne 2011). If a funnel plot is presented, the bias will be assessed by plotting trial size against treatment effect and visually inspecting the asymmetry in the resultant plot (Egger 1997). We will also use the linear regression method described by Egger 1997 to calculate the funnel plot asymmetry.

Data synthesis

We will first synthesise a narrative overview from all studies included.

Although we are unable to pre specify the extent of heterogeneity in the included studies, our previous review synthesis experience suggests that it may be extensive (Sinha 2017). We will perform a meta‐analysis if included studies do not demonstrate substantial heterogeneity. We will consider trials to be of sufficient homogeneity if there is a unanimous agreement between review authors after analysis of clinical (i.e. wound type), methodological (i.e. intervention type, duration of follow‐up, outcome measures), and statistical (i.e. P value generated from Chi² test, I² statistic) heterogeneity. If a meta‐analysis is warranted, our default approach will be to use a random‐effects model. This method assumes that the reported treatment effects may not be identical, but follow the same distribution (Deeks 2011). Additionally, a fixed‐effect model might generate inaccurate confidence intervals in the presence of even minor heterogeneity. We will only use a fixed‐effect model if heterogeneity is assessed to be minimal and the assumption that a single treatment effect is being estimated holds. We will utilise Cochrane Review Manager 5 software to combine data and calculate pooled estimates of treatment effect (Review Manager 2014). We will present pooled data using forest plots and accompanying data tables, where possible. For dichotomous outcomes, we will present the summary estimate as a RR with 95% CI. For continuous outcomes, if the outcome is measured in the same way across multiple studies, we will calculate a pooled MD with 95% CI. If the outcome is measured differently between studies, we will pool SMD estimates. Where dichotomous and continuous outcomes need to be combined to enable comparison, we will convert odds ratios (ORs) to SMDs, as described in Deeks 2011. For time‐to‐event data, we will pool estimates of HR with 95% CI.

If we find substantial heterogeneity between trials, which precludes meaningful data pooling, we will analyse the results narratively. If we do not perform a meta‐analysis, we will present unpooled results graphically to allow readers to appreciate treatment effect sizes and heterogeneity in the included trials.

Subgroup analysis and investigation of heterogeneity

If enough data are available, we will consider potential sources of heterogeneity by carrying out subgroup analyses to elucidate potentially important differences in response to the intervention. When possible, we will consider performing prespecified subgroup analyses to determine if the size of treatment effects are influenced by:

• adult versus paediatric burn populations;

• anatomical site of the burn (e.g. legs versus arms versus face);

• percentage TBSA of burn (e.g. < 10%, 10% to 20%, > 20%) as percentage TBSA‐burn and percentage TBSA‐grafted are both correlated to itch intensity (Carrougher 2013);

• pruritic site (e.g. grafted site versus donor site).

Sensitivity analysis

Sensitivity analyses seek to answer whether findings obtained in primary analysis are robust to the decisions made in the process of obtaining them. If there are an adequate number of studies, we plan to carry out sensitivity analyses for each comparison where primary analysis was conducted. We will explore the effect of:

• using alternate cut‐off points, if quantification of pruritus is performed on a dichotomised ordinal scale;

• removal of studies classed at 'high risk of bias' for any domain.