Systemic interventions for treatment of Stevens‐Johnson syndrome (SJS), toxic epidermal necrolysis (TEN), and SJS/TEN overlap syndrome

Abstract

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

To assess the effects of all systemic therapies (medicinal compounds delivered orally, intramuscularly, or intravenously) for treatment of Stevens‐Johnson syndrome (SJS), toxic epidermal necrolysis (TEN), and SJS/TEN overlap syndrome.

Background

Please note that unfamiliar terms may be listed in Appendix 1.

Description of the condition

Stevens‐Johnson syndrome (SJS), toxic epidermal necrolysis (TEN), and SJS/TEN overlap syndrome are rare severe skin reactions most commonly triggered by medications. These three entities represent a spectrum of disease, with SJS the least and TEN the most severe, and the severity of SJS/TEN overlap syndrome in between. This spectrum of disease will henceforth be collectively referred to as SJS/TEN. Although the estimated incidence is only 1 to 2 per 1,000,000 individuals per year (Strom 1991), this condition is a potentially fatal dermatological emergency, with mortality ranging from 1% to 5% for SJS, and from 25% to 40% for TEN (Patel 2013).

Over 200 drugs have been associated with SJS/TEN, most frequently antibiotics, allopurinol, non‐steroidal anti‐inflammatory drugs, and anticonvulsants. The risk of SJS/TEN is greatest within weeks of the start of therapy (Roujeau 1995). Other risk factors include immunocompromised status, concomitant radiotherapy with anticonvulsant use, and a slow acetylator genotype (metabolise drugs slowly) (Dietrich 1995). Certain human leucocyte antigen (HLA) alleles are associated with development of SJS/TEN, including HLA‐B*15:02 in Asians and East Indians taking carbamazepine; HLA‐B*15:02 in Han Chinese taking carbamazepine, lamotrigine, or phenytoin; HLA‐B*58‐01 in Han Chinese taking allopurinol; and HLA‐A*31‐01 in Europeans taking carbamazepine (Cheung 2013; Chung 2004; Hsu 2016; Hung 2005; McCormack 2011). The pathogenesis of SJS/TEN is not entirely understood. It is hypothesised that SJS/TEN may be due to an immune response to an antigenic complex between the culprit drug and host tissue in predisposed individuals, whereby T lymphocytes, natural killer cells, and natural killer T cells secrete granulysin and Fas‐ligand, and this immune response induces apoptosis upon binding to the Fas‐ligand death receptor on keratinocytes (Figure 1) (Nickoloff 2008).

Figure 1.

Pathogenesis of SJS/TEN.

This spectrum of disease is characterised by widespread epidermal necrosis, which leads to separation of the epidermis from the underlying dermis. This separation causes erythema and erosion of both cutaneous and mucous membrane skin (< 10% body surface area for SJS, 10% to 30% for SJS/TEN overlap, and > 30% for TEN) (Bastuji‐Garin 1993). Acute effects of epidermal necrosis include abnormalities in the following: fluid and electrolyte balance, temperature regulation, and protection from infection. Significant secondary complications can be acute (sepsis, respiratory distress, hypothermia, fluid loss, electrolytic abnormalities) or chronic (ocular symblepharon, entropion, blindness, chronic pain and genital scarring with associated urethral stenosis and phimosis) (Revuz 1987).

Description of the intervention

No evidence‐based options other than tertiary level supportive care are available for the treatment of SJS/TEN. Various systemic therapies are used, in addition to supportive care including glucocorticoids, intravenous immunoglobulins (IVIGs), cyclosporine, N‐acetylcysteine, thalidomide, infliximab, etanercept, and plasmapheresis. Through various mechanisms (see How the intervention might work), these systemic therapies potentially function to halt the progression and lessen the severity of SJS/TEN. Supportive care measures include wound care; eye, mouth, and genital skin care; nutrition; fluid replacement; and care provided at a tertiary care centre. This review will examine systemic medical interventions only (not supportive care). Given the rarity of this spectrum of disease, evidence for efficacy of these treatments is limited, and most has been derived from retrospective, uncontrolled studies including few participants.

To the knowledge of the review authors, only two randomised controlled trials (RCTs) have examined systemic therapy for SJS/TEN. The first study, which compared thalidomide versus supportive care in patients with TEN, was stopped early owing to higher than predicted mortality (10 of 12 participants in the thalidomide group vs 3 of 10 in the placebo group). This is the only study that was included in a prior Cochrane Review of systemic therapies specifically for TEN, which was published in 2002 and was updated without changes in 2010 (Majumdar 2002). The authors of this review concluded that they found no reliable evidence to support treatment decisions for TEN. More recently, an RCT of 96 participants with SJS/TEN reported less than predicted mortality for patients treated with etanercept (8.3% observed vs 17.7% predicted deaths) based on severity of illness score or SCORe of Toxic Epidermal Necrolysis (SCORTEN) criteria; this mortality was less than that predicted for patients treated with corticosteroids (16.3%), and neither result was statistically significant (Wang 2018).

Retrospective cohorts from the EuroSCAR and RegiSCAR trials provide the most robust data on systemic therapies for SJS/TEN, with close to 1000 participants from these studies combined. These studies found no clear evidence of a survival benefit with corticosteroids versus supportive care. EuroSCAR found a non‐statistically significant reduction in disease‐specific mortality for corticosteroids versus supportive care (odds ratio (OR) 0.6, 95% confidence interval (CI) 0.3 to 1.0), and RegiSCAR showed no survival advantage. Likewise, data from these cohorts and from multiple other studies accounting for more than 1000 participants show no survival benefit for IVIG versus supportive care (Campione 2003; Faye 2005; Prins 2003; Stella 2001; Trent 2008; Tristani‐Firouzi 2002; Viard 1998). Data from the RegiSCAR cohort suggest a survival benefit for cyclosporine over supportive care, although this finding was not statistically significant (hazard ratio (HR) 0.26, 95% CI 0.06 to 1.06) (Sekula 2013).

Other case series and small cohorts and a phase 2 non‐randomised trial show efficacy of cyclosporine (3 to 5 mg/kg/d for one to two weeks) in halting the progression of SJS/TEN (Arevalo 2000; Jarrett 1997; Kirchhof 2014; Rai 2008; Reese 2011; Robak 2001; Sullivan 1996; Zaki 1995). Several retrospective studies have found a reduction in expected deaths of at least 50% based on SCORTEN criteria (González‐Herrada 2017; Kirchhof 2014; Robak 2001). A more recent retrospective study including 174 participants shows no benefit of cyclosporine over supportive care with the use of a propensity score matching analysis method that had not been previously reported in the literature, along with significantly increased risk of renal failure among patients receiving cyclosporine (Poizeau 2018).

Tumour necrosis factor inhibitors (anti‐TNF agents) are the newest agents under study for use in SJS/TEN. There are several reports of infliximab given as a single infusion of 5 mg/kg halted skin sloughing and induced rapid re‐epithelialisation (no erosions or active lesions) of denuded skin (Patmanidis 2012; Scott‐Lang 2014; Wojtkiewicz 2008; Zarate‐Correa 2013). A few case series have described similar results with a single 50 mg subcutaneous injection of etanercept (Famularo 2007; Gubinelli 2009; Paradisi 2014). The true benefit of anti‐TNF agents in SJS/TEN is difficult to ascertain because published studies on this topic are few.

In addition to mortality, time to complete re‐epithelialisation is an important and validated endpoint. A 20‐year retrospective study investigating a supportive care alone strategy at a tertiary dermatology centre found that average time to the beginning of re‐epithelialisation was 11.0 ± 2.8 days and noted no statistical differences for patients treated with supportive care versus corticosteroids or IVIG (Lalosevic 2015). Cyclosporine given for two weeks across multiple studies yielded a time to full re‐epithelialisation of 12.9 ± 1.1 days and disease stabilisation with the start of wound healing evident at 2.9 ± 0.4 days after initiation of therapy (Singh 2013; Valeyrie‐Allanore 2010). By indirect comparison, etanercept was superior, with time to complete re‐epithelialisation of 8.2 ± 1.8 days and time to disease stabilisation and wound healing of 2.0 ± 0.6 days (Famularo 2007; Napolitano 2013; Paradisi 2014). A recent RCT including 96 participants shows a statistically significant reduction in median time to skin healing for etanercept compared to systemic corticosteroids (14 vs 19 days; P = 0.01) (Wang 2018).

A recent meta‐analysis of 96 studies including 3248 participants shows survival benefit for cyclosporine and glucocorticoids but not for supportive care alone, IVIG, plasmapheresis, thalidomide, cyclophosphamide, anti‐TNF agents, haemoperfusion, or granulocyte colony‐stimulating factor (Zimmermann 2017). This is the only meta‐analysis to comprehensively evaluate treatments for SJS/TEN. Proposed strengths of our own review will include use of Cochrane methods that involve rigorous quality assessment of included studies and inclusion of only prospective studies (cohort and prospective patient registry studies) to ensure the highest quality of included data.

How the intervention might work

The interventions noted above involve several potential mechanisms. As the SJS/TEN disease spectrum is believed to be an immune response, researchers first explored steroids as therapy provided to reduce the immune response mounted against the exogenous agent (Yamane 2016). Dysregulation of Fas‐mediated apoptosis has also been implicated in SJS/TEN, and IVIG is thought to act via autoantibodies against Fas (Romanelli 2008). TNF‐alpha inhibitors are proposed to work by blocking TNF‐mediated apoptosis (Chave 2005). Other mechanisms of action include removal of pathogenic particles from blood (plasmapheresis) ‐ as investigated by Yamane 2016 ‐ and downregulation of NF‐kB (cyclosporine) ‐ as studied by Kohanim 2016.

Why it is important to do this review

Given the rarity of this disease, evidence of treatment efficacy is limited, and most patients are still being treated according to institutional experience. In a practice survey of 147 North American centres treating patients with SJS/TEN (130 burn centres and 17 academic dermatology centres), only 54% of physicians reported that they followed treatment guidelines or an institutional standard of care for SJS/TEN, and only a minority of these physicians used professionally published guidelines (Dodiuk‐Gad 2015). IVIG was the first choice at more than 80% of sites, followed by systemic corticosteroids, cyclosporine, anti‐TNF medications, and supportive care alone (provided at 14% of centres). This pattern of practice is markedly different from published expert opinion at the iSCAR meeting in 2013 ‐ as reported by Dodiuk‐Gad 2015 ‐ and from our preliminary review of the literature, which yielded evidence that non‐pulsed corticosteroids and IVIG are not beneficial for treatment of individuals with SJS/TEN. It appears that personal experience and comfort with these agents have resulted in their continued use.

The topic of this review was covered in part by the Cochrane Review titled "Interventions for toxic epidermal necrolysis" (Majumdar 2002).

Objectives

To assess the effects of all systemic therapies (medicinal compounds delivered orally, intramuscularly, or intravenously) for treatment of Stevens‐Johnson syndrome (SJS), toxic epidermal necrolysis (TEN), and SJS/TEN overlap syndrome.

Methods

Criteria for considering studies for this review

Types of studies

This review will include randomised controlled trials (RCTs), cohort studies, and prospectively designed patient registries. Hence, we shall include only prospective studies.

Types of participants

We will include patients of any age with a clinical diagnosis of SJS, TEN, or SJS/TEN overlap syndrome. Given the rarity of SJS/TEN and the limited number of studies to date, we will include studies in which participants with SJS/TEN represent a subset of the population, but we will include in our review only data for these patients. When only aggregate data are available, we will contact study authors for separate data. If we are unable to obtain these data, we will not include the study. We will classify SJS/TEN as per published criteria (Bastuji‐Garin 1993), but we will include all studies reporting a clinical diagnosis of SJS/TEN.

Types of interventions

We will include all systemic therapies studied to date, including corticosteroids, IVIG, cyclosporine, N‐acetylcysteine, thalidomide, infliximab, plasmapheresis, and etanercept. We will include comparisons between each of the therapies outlined when data are available (28 possible comparisons). In addition, we will include comparisons of some therapies versus placebo (supportive care alone vs the intervention with supportive care) when these data are available.

Types of outcome measures

See definitions below.*

Primary outcomes

• SJS/TEN‐specific mortality

• Adverse effects leading to discontinuation of SJS/TEN therapy

*We will classify SJS/TEN as per published criteria (Bastuji‐Garin 1993), but we will include all studies reporting a clinical diagnosis of SJS/TEN.

Secondary outcomes

• Time to complete re‐epithelialisation

• Intensive care unit (ICU) length of stay

• Total hospital length of stay

• Chronic mucocutaneous morbidity (illness sequelae ‐ see below)

• Other adverse effects attributed to systemic therapy

We will include these outcomes because literature review and clinical experience indicate that they are important considerations for patients with SJS/TEN. Besides reducing mortality, the purpose of treating SJS/TEN is to increase the spread of skin healing to minimise the potential for illness sequelae. Length of stay in hospital including the ICU is an important determinant of healthcare costs. Furthermore, minimising time spent in hospital reduces the risk of hospital‐acquired illness among these patients. Included studies will collect data on these measures at any and all outcome time points.

Pre‐specified confounders and co‐interventions for observational studies

Confounders include disease duration (first day of illness to hospitalisation), disease severity (as determined by SCORTEN; Bastuji‐Garin 2000), use of diagnostic criteria (as published in Table 1; Bastuji‐Garin 1993), baseline comorbidities, age distribution, and duration of follow‐up. These variables may confound the relationship between SJS/TEN treatment and disease‐specific mortality, as they are related to these variables and, when not adjusted for, may impact the measure of treatment effect. For example, if treatment X is used only for patients who have better disease prognosis (present to hospital early in their disease, have less severe disease, are younger, have fewer baseline comorbidities), the effect of treatment X on reducing mortality may be overestimated. Similarly, studies that do not use diagnostic criteria may include other diseases that are less severe than SJS/TEN (such as erythema multiforme), which may lead to overestimation of treatment effects. Duration of follow‐up is also important, as studies with shorter follow‐up (i.e. < 1 month) may underestimate SJS/TEN mortality, which again would lead to overestimation of the treatment effect. We will include non‐randomised studies in the analysis only when researchers adjust for these pre‐specified confounders. Similarly, adjustments must be made for the use of co‐interventions (i.e. supportive care, other systemic medical treatments).

Table 1.

Diagnostic criteria for SJS/TEN as proposed by Bastuji et al (1993)

Classification	Types of lesions	Distribution	Percentage of BSA detached/detachable
Bullous EM	Typical or atypical raised targets	Acral	< 10
SJS	Spots ± flat atypical targets	Generalised	< 10
Overlap SJS/TEN	Spots ± flat atypical targets	Generalised	≥ 10‐30
TEN with spots	Spots ± flat atypical targets	Generalised	≥ 30
TEN without spots	No spots or targets	Generalised	≥ 10

Typical targets: lesions < 3 cm with well‐defined borders and regular round shape with three separate zones of colour; atypical targets: flat or palpable lesions with two zones of colour and poorly defined borders.

Outcome definitions and criteria

• Disease‐specific mortality: mortality within one month of onset of SJS/TEN that is not clearly attributed to another cause

• Adverse effects leading to discontinuation of SJS/TEN therapy: events that occur within one month following administration of therapy that are listed as potential adverse effects in the product monograph and lead to discontinuation of therapy

• Other adverse effects: events that occur within one month following administration of therapy that are listed as potential adverse effects in the product monograph and do not lead to discontinuation of therapy

• Chronic mucocutaneous morbidity (illness sequelae): sequelae that clinically make sense as possible outcomes of SJS/TEN including cutaneous (scarring, dyspigmentation, loss of nails), ocular (cicatricial conjunctivitis, corneal perforation/ulceration/epithelial defects, entropion/ectropion, chronic dry eye, symblepharon, blindness), gastrointestinal (ulceration, perforation, strictures), genitourinary (vaginal stenosis, phimosis, urethral strictures), and respiratory (bronchiolitis, bronchiectasis, obstructive lung disease) events, and chronic pain (all of these measures will be collected as dichotomous variables ‐ yes/no)

• All‐cause mortality: death due to any cause

• Hospital/ICU length of stay: time during which patient is admitted to hospital or ICU ward, as reported when available

Search methods for identification of studies

We aim to identify all relevant prospective trials including RCTs, cohort studies, and those using prospective data from patient registries. We aim to identify studies regardless of language or publication status (published, unpublished, in press, in progress).

Electronic searches

The Cochrane Skin Information Specialist will search the following databases for relevant trials with no restriction by date.

• Cochrane Skin Specialised Register.

• Cochrane Central Register of Controlled Trials (CENTRAL), in the Cochrane Library.

• MEDLINE via Ovid (from 1946 onwards).

• Embase via Ovid (from 1974 onwards).

The Information Specialist has devised a draft search strategy for MEDLINE (Ovid), which we have displayed in Appendix 2. We will use this as the basis of search strategies for the other databases listed.

Trial registers

We (AL and MT) will search the following trials registers using the following terms: Stevens‐Johnson syndrome, toxic epidermal necrolysis, SJS, and Lyell’s syndrome or Lyell’s disease.

• International Standard Randomized Controlled Trials Number (ISRCTN) register (www.isrctn.com).

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

• Australian New Zealand Clinical Trials Registry (www.anzctr.org.au).

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

• EU Clinical Trials Register (www.clinicaltrialsregister.eu).

Searching other resources

Reference lists

We will check the reference lists of all primary studies and key review articles for additional references to relevant trials.

Relevant individuals or organisations

We will search relevant manufacturers' websites for trial information; if found, will contact these organisations to request relevant data.

Errata or retractions

We will search for errata or retractions from included studies published in full text on PubMed and will report the date this was done (www.ncbi.nlm.nih.gov/pubmed).

Adverse effects

We will not perform a separate search for adverse effects of interventions used for treatment of SJS, TEN, and SJS/TEN overlap syndrome. We will consider only adverse effects described in included studies.

Data collection and analysis

Selection of studies

We will merge all search results into Covidence reference management software and will remove the duplicates (Covidence 2018). Two review authors (AL and MT) will independently review and select abstracts based on relevancy to the research question. A third review author (BW) will resolve discrepancies in study selection. We will obtain full texts for the final selected articles and will store them in Covidence. We will produce a PRISMA flow diagram to outline study selection and will create a 'Characteristics of excluded studies' table (Eden 2011). We will collate multiple reports of the same study, so that each study, rather than each report, is the unit of interest in the review.

Data extraction and management

We will extract data for each included study (Table 2). We will use a data collection form that has been piloted on at least one study in the review to record study characteristics and outcome data. Two review authors (AL and MT) will independently extract the following study characteristics from reports of included studies.

Table 2.

Data collection

Study information	Methods	Participants	Interventions	Outcomes
Citation	Study design	Number randomised	Description of intervention	Mean time to initial skin healing
Date of study	Total duration of study	Mean age, range	Description of comparison	Mean time to full skin healing
Funding	Details of any run‐in period	Sex	Concomitant medications	Mean hospital length of stay
Notable declaration of interest of study authors	Number of study centres	Ethnicity	Excluded medications	Mean ICU length of stay
	Study locations	Inclusion criteria		All‐cause mortality
	Study setting	Exclusion criteria		Disease‐specific mortality
		Diagnostic criteria		SMR
		Disease severity		Adverse effects of treatment
		Disease duration		Illness sequelae (chronic mucocutaneous morbidity)
		Mean day of illness at which treatment was initiated

SMR: The standardized mortality ratio (SMR) is a ratio of the observed number of deaths to the number of deaths expected for a standard population of known age and sex distribution.

• Methods: study design, total duration of study, details of any 'run‐in' period, number of study centres and locations, study setting, withdrawals, study dates.

• Participants: number of participants, mean age, age range, sex, ethnicity, disease duration, severity of condition, diagnostic criteria, baseline comorbidities, inclusion criteria, exclusion criteria.

• Interventions: interventions, comparisons, concomitant medications, supportive care measures, excluded medications.

• Outcomes: primary and secondary outcomes specified and collected, time points reported (both adjusted and unadjusted measures of treatment effect will be collected).

• Characteristics of the design of the study as outlined below under Assessment of risk of bias in included studies.

• Notes: funding for trial, notable declarations of interest of trial authors.

We will use these study characteristics to create a 'Characteristics of included studies' table for each trial. We will compare each study against the PRISMA checklist for inclusion of information reported in the study protocol.

Two review authors (AL and MT) will independently extract outcome data from included studies. We will extract the number of events and the number of participants per treatment group for dichotomous outcomes, and means and standard deviations and number of participants per treatment group for continuous outcomes. For our pre‐specified outcomes, we do not anticipate that values would be described as change from baseline. If both final values and change from baseline values happen to be reported for the same outcome, we will extract final values. Furthermore, for our pre‐specified outcomes, we do not anticipate that data will be provided at multiple time points (but if it is, we will use data from the longest time point from treatment initiation). We will note in the 'Characteristics of included studies' table if outcome data were not reported in a usable way and when data were transformed or estimated from a graph. We will resolve disagreements by consensus or by involving a third review author (BW). One review author (AL) will transfer data into the Review Manager file (Review Manager 2014). We will double‐check that data are entered correctly by comparing data presented in the systematic review against the study reports.

Assessment of risk of bias in included studies

Two review authors (AL and MT) will independently assess risk of bias for each randomised study. We will assess risk of bias in RCTs using Cochrane's 'Risk of bias' tool (criteria are outlined in the Cochrane Handbook for Systematic Reviews of Interventions Version 5.1.0) (Higgins 2011). We will resolve disagreements by discussion or by consultation with another review author (BW). We will assess risk of bias as low, high, or unclear, according to the following domains.

• Random sequence generation (selection bias).

• Allocation concealment (selection bias).

• Blinding of participants and personnel (performance bias).

• Blinding of outcome assessment (detection bias).

• Incomplete outcome data (attrition bias).

• Selective outcome reporting (reporting bias).

• Other bias.

We will systematically assess non‐randomised studies for bias using the ROBINS‐I tool as developed by members of the Cochrane Non‐Randomized Studies Methods Group (Sterne 2016). We will apply this tool to cohort studies and prospective patient registries. We will complete separate ROBINS‐I tables to generate an overall risk of bias for each study. We will assess bias as it relates to confounding, selection bias, bias in the measurement of interventions and outcomes, bias due to missing data, and bias in selection of the reported result. We will score each of these domains as having low, moderate, serious, or critical risk bias; based on these scores, we will determine an overall risk of bias for each study. If any domain is graded as serious, we will deem the overall risk of bias as serious.

When information on risk of bias relates to unpublished data or correspondence with a trialist, we will note this in the 'Risk of bias' table.

When considering treatment effects, we will take into account the risk of bias for studies that contribute to each outcome. We will present the figures generated by the 'Risk of bias' tool to provide summary assessments of the risk of bias.

Measures of treatment effect

We will collect effect estimates from each study. Based on a preliminary review of the literature, these will consist of standardised mortality ratios (SMRs) comparing the actual number of deaths versus the number of deaths predicted by SCORTEN, hazard ratios, and odds ratios. When researchers provide both adjusted and unadjusted measures of treatment effect, we will collect both. 'Adjusted measures' refers to those produced from multi‐variate analyses that adjust for the confounding effects of co‐variates. Although adjusted data will be preferred for the analysis, collection of unadjusted data will allow us to perform a sensitivity analysis for inclusion of these data in the results.

We will analyse dichotomous data as risk ratios and will use 95% confidence intervals (CIs). We will analyse continuous data as mean differences (MDs) or standardised mean differences (SMDs), depending on whether the same scale is used to measure an outcome, and 95% CIs. We will enter data presented as a scale with a consistent direction of effect across studies.

When different scales are used to measure the same conceptual outcome (e.g. disability), we will calculate SMDs instead, along with corresponding 95% CIs. We will convert SMDs back to MDs on a typical scale (e.g. 0 to 10 for pain) by multiplying the SMD by a typical among‐person standard deviation (e.g. standard deviation of the control group at baseline from the most representative trial), as per Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (Schunermann 2011b).

We will analyse time‐to‐event data as hazard ratios and rate data using Poisson methods (Lawless 1986).

For dichotomous outcomes, we will calculate the absolute risk difference using the risk difference statistic in RevMan software (Review Manager 2014), and we will express the result as a percentage. For continuous outcomes, we will calculate the absolute benefit as improvement in the intervention group minus improvement in the control group, in original units, expressed as a percentage.

We will calculate the relative percent change for dichotomous data as 'Risk ratio ‐ 1' and will express this as a percentage. For continuous outcomes, we will calculate the relative difference in the change from baseline as the absolute benefit divided by the baseline mean of the control group, expressed as a percentage.

We will analyse all data using SAS software (SAS Institute Inc. 2015).

Unit of analysis issues

The unit of analysis for studies completed to date is the individual patient. When possible, we will attempt to obtain patient‐level data for studies deemed appropriate for data pooling.

When multiple study arms are reported in a single study, we will include only the relevant arms. If two comparisons (e.g. drug A vs placebo and drug B vs placebo) are combined in the same meta‐analysis, we will halve the control group to avoid double‐counting.

We will include cluster and cross‐over RCTs; however, we anticipate the number of studies to be minimal or none. As for cluster RCTs, we will account for within‐cluster participant correlation in the analysis (Higgins 2011). For cross‐over RCTs, we will use data only up to the point of cross‐over to avoid contamination of treatment effects. Within‐participant (split‐body) RCTs are not relevant to this topic, which pertains to systemic therapies only, and we will therefore exclude them.

For this review, we will obtain data from RCTs and non‐RCTs. We will undertake meta‐analyses only when this is meaningful (i.e. if treatments, participants, and the underlying clinical question are similar enough for pooling to make sense based on heterogeneity assessment) (see Assessment of heterogeneity). We will analyse studies by grouping them according to study design; we will provide a global estimate in the context of analysis of each study design. If data from RCT versus non‐RCT studies are sufficiently similar with minimal heterogeneity, we will cautiously consider a pooled meta‐analysis.

Dealing with missing data

We will contact investigators or study sponsors to verify key study characteristics and to obtain missing numerical outcome data when possible (e.g. when a study is identified as abstract only, when data are not available for all participants). We will create a table to present contact details and other information received. When this is not possible and missing data are thought to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results by performing a sensitivity analysis. We will clearly describe any assumptions and imputations used to handle missing data and will explore the effect of imputation by performing sensitivity analyses.

For dichotomous outcomes (e.g. number of withdrawals due to adverse events), we will calculate the withdrawal rate using the number of participants randomised in the group as the denominator.

For continuous outcomes (e.g. mean change in pain score), we will calculate the MD or the SMD based on the number of participants analysed at that time point. If the number of participants analysed is not presented for each time point, we will use the number of randomised participants in each group at baseline.

When possible, we will compute missing standard deviations from other statistics such as standard errors, CIs, or P values, according to methods recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). If standard deviations cannot be calculated, we will impute them (e.g. from other studies in the meta‐analysis).

Assessment of heterogeneity

We will assess clinical and methodological diversity in terms of participants, interventions, outcomes, and study characteristics for the included studies to determine whether a meta‐analysis is appropriate. We will do this using data from the data extraction tables. We will assess statistical heterogeneity by visually inspecting the forest plot to assess for obvious differences in results between studies, and by performing I² and Chi² statistical tests.

As recommended in Chapter 9 of theCochrane Handbook for Systematic Reviews of Interventions (Deeks 2011), we will interpret the I² value as follows: 0% to 40% might 'not be important'; 30% to 60% may represent 'moderate' heterogeneity; 50% to 90% may represent 'substantial' heterogeneity; and 75% to 100% may represent 'considerable' heterogeneity. As noted in the Cochrane Handbook for Systematic Reviews of Interventions, we will keep in mind that the importance of I² depends on (1) the magnitude and direction of effects and (2) the strength of evidence for heterogeneity. We will interpret the Chi² test with P ≤ 0.10 as indicating evidence of statistical heterogeneity. If we identify substantial heterogeneity, we will report this and will investigate possible causes by following the recommendations provided in Section 9.6 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011).

Assessment of reporting biases

We will create and examine a funnel plot to explore possible small‐study biases. In interpreting funnel plots, we will examine different possible reasons for funnel plot asymmetry as outlined in Section 10.4 of the Cochrane Handbook for Systematic Reviews of Interventions, and will relate this to review results. If we are able to pool more than 10 trials, we will undertake formal statistical tests to investigate funnel plot asymmetry and will follow the recommendations provided in Section 10.4 of the Cochrane Handbook for Systematic Reviews of Interventions (Sterne 2011).

To assess outcome reporting bias, we will check trial protocols against published reports. When a protocol is not available, we will request access from study authors. If this is not possible, we will list these studies as "reporting bias cannot be ruled out". For studies published after 1 July 2005, we will screen the Clinical Trials Register at the International Clinical Trials Registry Platform of the World Health Organization (http://apps.who.int/trialssearch) for the a priori trial protocol. We will evaluate whether selective reporting of outcomes is present.

Data synthesis

We will undertake meta‐analyses only when this is meaningful (i.e. if treatments, participants, and the underlying clinical question are similar enough for pooling to make sense). We will analyse studies by grouping them according to study design; we will provide a global estimate in the context of the analysis of each study design. We will not pool together different measures of effect (e.g. OR and RR).

If meta‐analyses are possible, we will use a random‐effects model using RevMan software (Review Manager 2014). If they are not possible, we will summarise results narratively.

We will report data from non‐comparative studies in a narrative summary table to provide a comprehensive report.

When results are estimated for individual studies with low numbers of events (< 10 in total), or when the total sample size is less than 30 participants and a risk ratio is used, we will report the proportion of events in each group together with a P value from Fisher’s exact test.

'Summary of findings' tables and GRADE assessments

We will create 'Summary of findings' (SoF) tables using the following outcomes.

• Disease‐specific mortality.

• Time to complete re‐epithelialisation.

• ICU length of stay.

• Total hospital length of stay.

• Withdrawal due to adverse events.

We will create an SoF table for the following comparisons, which we have identified as the most clinically important: (1) etanercept versus cyclosporine, (2) etanercept versus IVIG, (3) IVIG versus cyclosporine, and (4) cyclosporine versus corticosteroids.

Two review authors (AL and MT) will independently assess the quality of the evidence, and a third review author (BW) will resolve potential discrepancies. We will use the five Grading of Recommendations Assessment, Development and Evaluation (GRADE) considerations (study limitations, consistency of effect, imprecision, indirectness, and publication bias) to assess the quality (certainty) of a body of evidence as it relates to studies that contribute data to meta‐analyses for the pre‐specified outcomes, and we will report the certainty of evidence as high, moderate, low, or very low. Evidence from RCTs is automatically assessed as high quality, and we can downgraded the quality for any of the factors listed above by one level (serious concerns) or two levels (very serious concerns). Evidence from observational studies is first classified as low quality but can be upgraded. We will consider the following criteria for upgrading the certainty of evidence, if appropriate: large effect, dose‐response gradient, and plausible confounding effect. We will use methods and recommendations as described in Sections 8.5 and 8.7, and in Chapters 11 and 12, of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011; Dijkers 2013; Higgins 2011; Schunermann 2011a; Schunermann 2011b). We will use GRADEpro software to prepare the SoF tables (GRADEpro 2015). We will justify all decisions to downgrade or upgrade the certainty of evidence using footnotes, and we will provide comments to aid the reader's understanding of the review when necessary.

Subgroup analysis and investigation of heterogeneity

When data permit, we will perform subgroup analysis by category of disease severity (SCORTEN ≥ 3), body surface area (≥ 30%), advanced age (≥ 75 years), and co‐interventions.

Sensitivity analysis

We will conduct sensitivity analyses to assess the robustness of data analysis, specifically, to test the impact of the following.

• Treatment effect estimates that are unadjusted (because we believe this will help to support our decision to exclude studies that do not adjust for important pre‐specified confounding variables by showing that the results may potentially change when this confounding is not accounted for).

• Missing data that require assumptions and/or imputations.

• Studies with brief (< 1 month) follow‐up.

• Quality assessment of included studies (removing studies that are at high risk of bias).

Appendices

Appendix 1. Glossary

Apoptosis: programmed cell death.

Cutaneous: skin.

Epidermal: top‐most layer of the skin.

Exogenous: external to the body.

Fas‐mediated apoptosis: fas‐ligand belongs to a group of proteins called "tumour necrosis factor (TNF) transmembrane proteins", which are molecules present on the surfaces of skin cells. These proteins bind (connect) with receptors, which causes the skin cells to apoptose (die).

IVIG: intravenous immunoglobulin; a medical therapy that consists of concentrated antibodies extracted from the blood of healthy donors.

Mucous membrane: skin that lines internal body cavities such as the oral cavity and the vagina.

Necrosis: tissue death.

NF‐kB: nuclear factor kappa‐light chain enhancer of activated B cells (NF‐kB) is a protein that influences DNA transcription, thereby regulating cellular responses to various stimuli.

Pathogenesis: the mechanism (process) of a disease.

Re‐epithelialisation: the process of skin re‐growing its outermost layer (epidermis).

Appendix 2. Draft MEDLINE (Ovid) search strategy

1. exp Stevens‐Johnson Syndrome/ 2. Stevens Johnson Syndrome$.mp. 3. sjs.mp. 4. (toxic and epidermal and necrolys$).mp. 5. (Lyell$ and (syndrome$ or disease$)).mp. 6. or/1‐5 7. cyclosporine.mp. or CYCLOSPORINE/ 8. STEROIDS/ 9. (steroid$ or corticosteroid$).mp. 10. Adrenal Cortex Hormones/ 11. corticoid$.mp. 12. dexamethasone.mp. or DEXAMETHASONE/ 13. prednisolone.mp. or PREDNISOLONE/ 14. METHYLPREDNISOLONE/ or methylprednisolone.mp. 15. Immunoglobulins/ 16. (immunoglobulin$ or IVIG).mp. 17. enbrel.mp. 18. etanercept.mp. or ETANERCEPT/ 19. Tumor Necrosis Factor‐alpha/ 20. anti‐tumo?r necrosis factor$.mp. 21. anti‐tnf.mp. 22. TNF‐alpha inhibitor$.mp. 23. anti‐interleukin$.mp. 24. infliximab.mp. or INFLIXIMAB/ 25. remicade.mp. 26. exp PLATELETPHERESIS/ 27. Plateletpheres$.mp. 28. (platelet and rich and pheres$).mp. 29. PLASMAPHERESIS/ 30. plasmapheres$.mp. 31. THALIDOMIDE/ 32. Thalidomid$.mp. 33. ACETYLCYSTEINE/ 34. Acetylcystein$.mp. 35. N?acetylcystein$.mp. 36. NAC.mp. 37. systemic immunomodulating therap$.mp. 38. Glucocorticoids/ 39. (glucocorticosteroid$ or glucocorticoid$).mp. 40. cyclophosphamide.mp. or CYCLOPHOSPHAMIDE/ 41. granulocyte stimulating factor$.mp. 42. hemoperfusion.mp. or HEMOPERFUSION/ 43. or/7‐42 44. 6 and 43 45. exp animals/ not humans.sh. 46. 44 not 45

*Note, there is no restriction by study design as we aim to identify RCTs, cohort studies, and those studies using prospective data from patient registries.

What's new

Last assessed as up‐to‐date: 29 May 2018.

Date	Event	Description
10 July 2018	Amended	Revisions made based on post‐peer review editorial queries; changes tracked
29 May 2018	Amended	Requested revisions from external peer review incorporated with tracked changes

Contributions of authors

Annie Langley was the contact person with the editorial base. Annie Langley co‐ordinated the contributions from the co‐authors and wrote the final draft of the protocol. Annie Langley, Jordi Pardo Pardo, and Peter Tugwell worked on the methods sections. Annie Langley, Brandon Worley, Jennifer Beecker, and Arturo Saavedra drafted the clinical sections of the background and responded to clinical comments of the referees. Annie Langley and Jordi Pardo Pardo responded to the method and statistics comments of the referees. Annie Langley and Jordi Pardo Pardo contributed to writing the protocol. Jean Farrell‐McCawley was the consumer co‐author who checked the protocol for readability and clarity. She also ensured that the outcomes are relevant to consumers. Annie Langley is the guarantor of the final review.

Sources of support

Internal sources

• No sources of support supplied

External sources

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

  The NIHR, UK, is the largest single funder of the Cochrane Skin Group.

Declarations of interest

Annie Langley: none known. Brandon Worley: none known. Jordi Pardo Pardo: none known. Jennifer Beecker: none known. Timothy Ramsay: none known. Arturo Saavedra: none known. Jean Farrell‐McCawley: none known. Peter Tugwell: [unpaid] Chair of the Management Executive Committee of the OMERACT Board of Governors. OMERACT receives unrestricted educational grants from several sources, including the American College of Rheumatology, the European League of Rheumatology, and several pharmaceutical companies (names follow) which are used to support fellowships, international patient advocacy groups, and a major international biennial conference. This organisation and biennial conferences have produced many seminal peer‐reviewed publications since their inception. The list of past and current participating pharmaceutical companies includes Amgen, AstraZeneca, Bristol Myers Squibb, Celgene, Eli Lilly, Genentech/Roche, Genzyme/Sanofi, Horizon Pharma Inc., Merck, Novartis, Pfizer, PPD, Quintiles, Regeneron, Savient, Takeda Pharmaceuticals, UCB Group, Vertex, Forest, and Bioiberica. In addition, an independent Committee Member for several clinical trial Data Safety Monitoring Boards for FDA‐approved trials involving UCB Biopharma SPRL, ReSearch Pharma Services Inc., and PRA Health Sciences. Also, a member of the Independent Expert Committee of the Canadian Reformulary Group Inc., a company that reviews the evidence for health insurance companies' employer drug plans.

Editor Laurence Le Cleach: one of the authors of a study that might be included in this review (Poizeau 2018).

Disclaimer

This project was supported by the National Institute for Health Research, via Cochrane Infrastructure funding to the Cochrane Skin Group. The views and opinions expressed therein are those of the review authors and do not necessarily reflect those of the Systematic Reviews Programme, NIHR, NHS, or the Department of Health.

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