Interventions for postburn pruritus

Abstract

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

To assess the effects of interventions for treating postburn pruritus in any care setting.

Background

Description of the condition

Burn injuries are a significant cause of morbidity and mortality for adults and children around the world. The World Health Organization (WHO) estimates that 11 million people annually are burned severely enough to require medical attention (WHO 2017). This results in approximately 18 million disability‐adjusted life years lost and more than 250,000 deaths worldwide. The global prevalence of burns is disproportionately higher amongst low socioeconomic populations, with low‐ and middle‐income countries accounting for 90% of all reported burns worldwide (Rybarczyk 2017; Smolle 2017). Different burn mechanisms generate unique injury patterns and require different management strategies. The three major burn mechanisms are thermal, electrical, and chemical injuries. Burns are categorised in order of severity as superficial epidermal, superficial dermal, deep dermal or partial thickness, and full thickness burns (NHS Inform 2018).

Development of specialised burn units, advances in acute care modalities, and burn prevention programmes have successfully reduced mortality rates of people with severe burns. These advancements, however, have introduced a new challenge: reintegrating people with significant physical and psychosocial complications from burn injury into their normal (pre‐injury) societal roles. There are many physical consequences of burn injury that interdisciplinary rehabilitation programmes seek to address. These include scar contractures (permanent shortening of inelastic scar tissue) leading to tightened skin, hypertrophic (raised) scarring, loss of muscle mass leading to fatigue and weakness, amputations, abnormal bone growth (heterotopic ossifications), damage to peripheral nerves resulting in neuropathy, pain, problems with regulation of body temperature, and issues with psychosocial adjustment (Esselman 2006; Esselman 2007; Procter 2010; Sinha 2018a; Tu 2017). Pruritus (itching) is a common long‐term consequence in healed burn scars and in healed skin graft donor sites from which grafts are harvested to treat burn injury. Pruritus has a significant negative impact on postburn quality of life (Ahuja 2016; Goutos 2009).

Pruritus (Latin for 'itch') is defined as an unpleasant sensation that elicits a desire or reflex to scratch (Weisshaar 2003). The incidence of postburn pruritus is estimated to be about 87% amongst discharged patients, varying with the anatomic area burned (Vitale 1991). For example, leg (100%) and arm (70%) burns are particularly prone to pruritus, whereas facial burns rarely cause itching. Postburn pruritus is often debilitating as it interferes with sleep, daily activities, and can complicate wound healing if scratching damages the newly formed epithelium and grafted skin (Bell 1988).

In origin, pruritus can be classified into one of five categories: cutaneous (originating in the skin), neuropathic (due to nerve damage), neurogenic (due to central neural damage), psychogenic (due to psychological disorders), or mixed (Twycross 2003). Although postburn pruritus is predominately cutaneous (originating in the skin), emerging evidence suggests neuropathic involvement as dysfunction in the sensory pathways may be involved in maintaining persistent itching (Goutos 2013). Many factors regulate burn‐induced pruritus; the most widely studied are histamines (Goutos 2009). Histamine, released by mast cells (a type of white blood cell) and keratinocytes (epidermal cells), stimulate histamine receptors 1 (H1) and 2 (H2) on nerve endings. This is thought to be the key mediator of pruritus across all phases of burn rehabilitation. Furthermore, the persistence of inflammatory factors (i.e. kinins, substance P, platelet activating factor) in the wound can further amplify the effects of histamine and exacerbate itch. Histamine‐induced increase in blood flow gives a pruritic wound its red (erythematous) appearance. As such, antihistamines have been the cornerstone for burn pruritus management (Bell 2009; Zachariah 2012).

Description of the intervention and how the intervention might work

Outside the central nervous system (CNS), histamine released by mast cells is the primary cause of pruritus. Burn wounds contain an overabundance of mast cells as they are thought to persist in the skin after healing and function as histamine secreting factories. Factors that decrease histamine release are effective antipruritic agents. There are several pharmacological and non‐pharmacological strategies which are routinely employed in clinical care. Interventions (and mechanisms underlying their antipruritic efficacy) are summarised below:

Pharmacological

• Antihistamines: the first‐line treatment for both adult and paediatric burn patients are antihistamines. Antihistamines bind and stabilise histamine receptors in the inactive state and block downstream signals. Since H1 and H2 receptors are preferentially expressed in the skin (O'Donoghue 2005), most postburn antipruritic protocols inhibit either H1 or H2 receptors. Two generations of antihistamines target the H1 receptor. The first‐generation antihistamines also bind non‐specifically to other receptors (e.g. muscarinic, adrenergic, serotonin), whereas second‐generation antihistamines (i.e. cetirizine) have minimal non‐specific effects. Second‐generation antihistamines also have a more sustained duration of action and less CNS penetration. Drugs that block the H1 receptor which have been proposed as antipruritic agents include diphenhydramine, hydroxyzine, cetrizine, chlorpheniramine, and pyrilamine (Ahuja 2011; Baker 2001; Vitale 1991). H2 receptor antagonists, such as cimetidine, have also been investigated (Baker 2001; Murphy 2005). Doxepin, a highly potent histamine receptor blocker, has also been proposed as a topical cream to avoid toxicity associated with oral dosing (Demling 2001).

• Gabapentin and pregabalin: although the precise mechanism of action of gabapentin (and its prodrug/precursor pregabalin) is not known, its primary site of action is in the spinal cord where it blocks the release of excitatory neurotransmitters (Bennett 2004). For pruritus, it is thought that gabapentin inhibits peptides that amplify pruritus (such as calcitonin gene‐related peptide) by increasing inhibitory neurotransmitter gamma‐aminobutyric acid (GABA). Pregabalin is similar to gabapentin but is a more potent drug (Bockbrader 2010). Both are mainly prescribed for managing epilepsy and neuropathic pain. Outside the CNS, they exert their effect on GABA‐sensitive nerve fibres that mediate pruritus. Within the CNS, they block calcium channels, which in turn, limits the release of excitatory neurotransmitter, glutamate. Both drugs have been proposed as antipruritic agents, administered either as monotherapy or in conjunction with antihistamines (Ahuja 2011; Ahuja 2013; Zachariah 2012).

• Serotonin receptor antagonists: in the wound, serotonin is thought to be released from platelet aggregates and not dermal mast cells. Since pruritus is conducted via nerve fibres whose stimulation can be enhanced by serotonin, inhibiting the serotonin receptor is an emerging therapeutic approach. As such, re purposed drugs, such as serotonin receptor antagonist, ondansetron (Gross 2007), and serotonin reuptake inhibitor, paroxetine (Zylicz 2003), have been assessed as antipruritic agents.

• Opiod antagonists: “itch specific” neurons in the spinal cord are typically maintained in an inactive state due to spontaneous firing of nociception‐specific and wide dynamic range neurons (Andrew 2001; Schmelz 2001). Opioid agonists, such as morphine sulfate, induce itch by decreasing activity of these two inhibitory neurons, thereby lifting inhibition on itch neurons (Ballantyne 1988; Fischer 1982). These observations have led Schmelz 2001 and others to propose that firing of ‘itch’ neurons is facilitated by opioids. While activation of opioid receptors induce pruritus, its inhibition may suppress pruritus. Pharmacological blockade of mu‐opioid receptors has been shown to be effective in suppressing scratching in rodents (Inagaki 2000). Following this, investigators have proposed opioid antagonists such as naltrexone as postburn antipruritic agents (LaSalle 2008). However, it is important to note that not all opioid receptors regulate itch similarly. In contrast to mu‐opioid receptors, κ‐opioid antagonists enhance itch and κ‐opioid agonists reduce itch (Kamei 2001).

Non‐pharmacological

• Cooling of the wound: common cooling agents, such as menthol, camphor, icilin, and showering/bathing can transiently mask the sensation of pruritus (Paul 2015). Application of topical coolants, such as menthol, activates the same fibres (A‐delta afferents) that are activated when skin is cooled by 2°C to 4°C (Bromma 1995). Activation of A‐delta fibres (thin, myelinated fibres carrying acute pain signals) activates an ion channel, called transient receptor potential cation channel subfamily M member 8 (TRPM8), and inhibits unmyelinated C‐fibres carrying itch signals (Biró 2005; Patel 2007). In addition, menthol selectively activates κ‐opioid receptors (Galeotti 2002), and this mechanism may further explain its efficacy as a coolant. Clinically, topical coolant application is typically effective at low concentrations (1% to 5% for menthol) as higher concentrations can cause irritation (Yosipovitch 2013).

• Transcutaneous electrical nerve stimulation (TENS): transcutaneous high‐frequency, low‐intensity electrical impulses generated by a device can be carried along large diameter afferent nerves. Given TENS use is well tolerated, it has been assessed as an antipruritic treatment for conditions such as atopic dermatitis (Nilsson 2004), macular amyloidosis (Yüksek 2011) and lichen simplex (Engin 2009, Yüksek 2011, Mohammad Ali 2015). This has provided an impetus to evaluate its efficacy for postburn pruritus. Low voltage pulsed electric currents generated in TENS are passed through the itchy skin to stimulate large diameter afferent nerves. This stimulation blocks A‐delta and C‐fibres carrying pain and pruritus signals, respectively (Mohammad Ali 2015). Short duration (150 seconds) of TENS at a high frequency (180 Hz) yields nonpainful tingling sensations with no muscle contraction (Hettrick 2004).

• Extracorporeal shock wave therapy (ESWT): ESWT is a sequence of sound waves that are generated by a vibration source and are subsequently dispersed throughout the skin. Scar ESWT is adapted from extracorporeal shock wave technology originally used to break up kidney stones noninvasively (Chaussy 1980). Here, high‐energy shock waves transmitted through a coupling gel mechanically disintegrate the scar tissue by fragmenting the collagenous matrix. This is thought to trigger production of growth factors (i.e. endothelial nitric oxide synthase, vessel endothelial growth factor) that form new blood vessels and improve blood supply in the scar tissue, leading to reduced pain and pruritus (Joo 2017; Wang 2003). Recently, investigators have assessed a shock wave dose of 100 impulses/cm² at 0.05 to 0.20 mJ/mm2 with a total of 1000 to 2000 impulses as an adjunct to postburn antipruritic protocols (Joo 2017).

• Massage therapy: lubricants, such as cocoa butter and petroleum jelly, are commonly used in clinical trials assessing massage therapy where they are typically administered by trained burn therapists (Field 2000; Roh 2007). The Gate Control Theory of pain posits that activation of fibres, which compete with pain pathways, can "close the gate" and preclude central processing of pain (Melzack 1965). Consistent with this view, application of pressure through massage may trigger action potentials in large myelinated fibres with a quicker transit time to the CNS and outcompete signals from less myelinated, slow conducting C‐fibres, carrying pruritic signals.

• Laser therapy: the advent of ablative fractional lasers has made it possible to purposefully generate large arrays of microscopic thermal wounds within mature burn scars without injuring the surrounding skin (Geronemus 2006; Manstein 2004). Similar to how a surgical blade breaks apart disorganised collagen in scar tissue during Z‐plasty (a surgical technique that relieves tension on a contracted scar), fractional lasers break apart disorganised collagen fibres with patterned columns of microthermal wounds. This is thought to elicit wound repair programmes that allow wound tissue to heal in an organised fashion, thereby mitigating pathological scar symptoms, such as itch and pain. Recent molecular profiling of laser‐treated scars have reported changes in collagen types, matrix metalloproteinases, transforming growth factor family proteins, Wnt proteins, heat shock proteins, as well as small noncoding microRNA expressions that may underlie a laser's efficacy in mitigating pathological scar symptoms (Kim 2013; Qu 2012). Among the ablative lasers, high‐energy pulsed dye and fractional CO₂ lasers have shown efficacy in reducing itch, pain, and restoring normal pigmentation in burn scars (Levi 2016; Waibel 2008).

• Wound dressing: dressings can be impregnated with biologically active compounds (such as silver bound to activated charcoal; Aziz 2012), that can impact on postburn pruritus. Since dressings can be impregnated with different biologically active compounds, there's no universal mechanism common to all dressings. In the example of silver‐coated dressings, it is thought that sustained release of silver ions into the wound reduces postburn pruritus by preventing bacterial growth, thereby reducing inflammatory cytokines, such as tumour necrosis factor and interleukin‐12 protein (Dunn 2004). While some wound dressings like Acticoat are specifically marketed to treat pruritis (Brooks 2007), most wound dressing trials identify change in pruritus as an outcome measure.

Why it is important to do this review

Postburn pruritus is a common, well‐recognised chronic condition which impairs quality of life and inflicts a substantial burden on healthcare systems. Although several reviews have been conducted to synthesise evidence from available treatments (Ahuja 2014; Goutos 2010; Zachariah 2012), only one was a systematic review (Bell 2009). Considering that this systematic review was published nearly a decade ago, the synthesised summary of the evidence needs to be updated. Furthermore, no review thus far has performed a thorough risk of bias, assessment of trial heterogeneity, subgroup analysis, or meta‐analytic pooling of evidence. The production of a robust and current systematic review can identify, appraise, and synthesise evidence for clinical decision making.

Objectives

To assess the effects of interventions for treating postburn pruritus in any care setting.

Methods

Criteria for considering studies for this review

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

Primary outcomes

• Change in burn‐related pruritus, defined by a change recorded on itch severity scales (i.e. 5D‐Itch Scale (Elman 2010), Leuven Itch Scale (Haest 2011)), pan burn scales, which include itch severity (i.e. Burn Specific Health Scales (Blades 1979; Blades 1982; Blalock 1994; Kildal 2001; Munster 1987), or culturally adapted variants of the two (Ahuja 2016; Mulay 2015). We will also accept measurements of burn‐related pruritus, recorded on any scale, where mean or median with a measure of variance is either calculable or directly reported.

• Adverse events (number of participants in each group with an event). We will report events defined and grouped as 'adverse events' by study authors, where methods for the collection of adverse event data is provided. The study authors should make it clear whether: 1) events were reported at the participant level; or 2) if multiple events per person were reported. We anticipate study authors will specify adverse events specific to the treatment modality being assessed. For example, adverse events for gabapentin could include dizziness, somnolence, sedation and fatigue.

Secondary outcomes

• Cost‐effectiveness: 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).

• Pain, measured either as a continuous outcome using a visual analogue scale (such as a Simple Descriptor Scale), or reported as a dichotomous outcome.

• Patient perception (i.e. level of satisfaction with the application of intervention).

• Wound healing, measured as time‐to‐event (survival) outcome and proportion of wounds that healed completely.

• Participant health‐related quality of life. We will analyse data on health‐related quality of life if reported using a standardised scale, such as the 36‐Item Short Form Health Survey (SF‐36) or EuroQol Group's EQ‐5D. We will not include measures of quality of life that are not validated and would not be common across multiple trials.

If a study is otherwise eligible for inclusion, but does not report a listed outcome, we will contact the trial authors to establish whether an outcome of interest was measured but not reported.

We will report outcomes at the latest time point available (assumed to be length of follow‐up) and the time point specified by the authors as being of primary interest (if different from the latest time point). It is possible that some of the specified outcomes may be recorded at multiple time points. We anticipate grouping outcomes by the following time points as proposed by Van Loey 2008.

• 'Acute' pruritus: wound closure to six months.

• 'Chronic' pruritus: more than six months from wound closure.

Search methods for identification of studies

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.

Data collection and analysis

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.

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

The goal of ‘Summary of findings’ tables is to present the main findings of a systematic review in a transparent and tabular format. These tables report key information regarding the quality of available evidence, the magnitude of the effects of examined interventions, comparative risks versus effect estimates, and numbers of participants and trials included to arrive at these determinations (Schünemann 2011a). This table also includes an overall assessment of the quality of the evidence related to each outcome using the GRADE approach. The GRADE approach, developed by the GRADE Working Group, defines the quality of a body of evidence regarding 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 quality 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). The quality of evidence varies in rating, ranging from high, moderate, low, or very low. For reference, RCTs start as high quality, whereas observational studies start as low quality.

We plan to present the following outcomes in our 'Summary of findings' tables:

• change in pruritus

• adverse events

• pain

For outcomes reported in comparisons but not included above, we will present GRADE assessments narratively within the Results section, without including these in the 'Summary of findings' table. For GRADE assessment, when assessing studies for 'Risk of bias', we will consider downgrading the evidence quality only when studies are assessed to be at a high risk of bias for one or more domains. We will not downgrade for unclear risk of bias assessments. In assessing the precision of effect estimates, we will also follow GRADE guidance (GRADE 2013). When there are very few events, and CIs around both relative and absolute estimates of effect include appreciable benefit and appreciable harm, we will downgrade the quality of evidence by two levels.

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.

Appendices

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

#1 MeSH descriptor: [Burns] explode all trees #2 (burn or burns or burned or scald* or postburn* or post‐burn*):ti,ab,kw #3 (thermal near/5 injur*):ti,ab,kw #4 #1 or #2 or #3 #5 MeSH descriptor: [Pruritus] explode all trees #6 (pruritus or pruritis or itch*):ti,ab,kw #7 (antipruritic* or anti‐pruritic*):ti,ab,kw #8 #5 or #6 or #7 #9 #4 and #8

Appendix 2. Cochrane tool for assessing risk of bias

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.

• Reason 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.

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

In cluster‐randomised controlled trials (RCTs), five particular biases to consider include: recruitment bias; baseline imbalance; loss of clusters; incorrect analysis and comparability with individually‐randomised trials.

1. Recruitment bias: can occur when participants 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.

2. Baseline imbalance: cluster‐RCTs 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 participants. 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.

3. Loss of clusters: occasionally complete clusters are lost from a trial, and have to be omitted from the analysis. Just as for missing outcome data in individually‐RCTs, this may lead to bias. In addition, missing outcomes for participants within clusters may also lead to a risk of bias in cluster‐RCTs.

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

5. Comparability with individually‐randomised trials: in a meta‐analysis including both cluster‐ and individually‐RCTs, or including cluster‐RCTs 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 everyone in a community would be expected to be more effective than if the vaccine were applied to only half of the people. Another example is provided by a Cochrane Review of hip protectors (Hahn 2005). The cluster‐RCTs showed large positive effect, whereas individually‐RCTs did not show any clear benefit. One possibility is that there was a 'herd effect' in the cluster‐RCTs (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

Sarthak Sinha: conceived the review question; developed the protocol; co‐ordinated the protocol development; produced the first draft of the protocol; contributed to writing or editing the protocol; advised on the protocol; approved the final version of the protocol prior to submission and is guarantor of the protocol.

Vincent Gabriel: conceived the review question; developed the protocol; co‐ordinated the protocol development; contributed to writing or editing the protocol; advised on the protocol; approved the final version of the protocol prior to submission.

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

Frankie Fraulin: advised on the protocol; approved the final version of the protocol prior to submission.

Wisoo Shin: contributed to writing or editing the protocol; advised on the protocol; approved the final version of the protocol prior to submission.

Waleed Rahmani: contributed to writing or editing the protocol; advised on the protocol; approved the final version of the protocol prior to submission.

Pallab Chatterjee: contributed to writing or editing the protocol; advised on the protocol; approved the final version of the protocol prior to submission.

Rajeev Ahuja: developed the protocol; contributed to writing or editing the protocol; advised on the protocol; approved the final version of the protocol prior to submission.

Jeff Biernaskie: contributed to writing or editing the protocol; advised on the protocol; approved the final version of the protocol prior to submission.

Contributions of the editorial base

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

Sources of support

Internal sources

• No sources of support supplied

External sources

• National Institute for Health Research, UK.

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

Declarations of interest

Sarthak Sinha: none known.

Vincent Gabriel: none known.

Duncan Nickerson: none known.

Frankie Fraulin: none known.

Wisoo Shin: none known.

Waleed Rahmani: none known.

Pallab Chatterjee: none known.

Rajeev Ahuja: I have performed prospective randomised controlled trials assessing efficacy of cetirizine, gabapentin (Ahuja 2011), and pregabalin (Ahuja 2013), for postburn pruritus. These trials will potentially be eligible for inclusion in this review. 'Risk of bias' assessment, decision to include or exclude, data extraction, and checking will be performed by members of the review team not associated with this trial.

Jeff Biernaskie: I hold the Calgary Firefighters Burn Treatment Society Chair in Skin Regeneration. Funds from this have been used to support trainee stipends during the course of this review.

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