Thymosin‐ɑ1 for people with chronic hepatitis B

Objectives

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

To assess the benefits and harms of thymosin‐α1 in people with chronic hepatitis B, regardless of their age, sex, and ethnicity

Background

Description of the condition

Hepatitis B virus (HBV) is a DNA virus of the Hepadnaviridae family (Schaefer 2007). Viral hepatitis is a necro‐inflammatory disease of the liver, which can present with acute or chronic viral hepatitis, or both (Rutherford 2016; WHO 2021). Acute viral hepatitis is usually asymptomatic, but with its progression, people may present with jaundice, pruritus, dark urine, and scleral icterus (Rutherford 2016). Most people with chronic HBV infection can also be asymptomatic. The diagnosis is usually made incidentally, or when the disease progresses to a clinically evident hepatic dysfunction (e.g. to cirrhosis, hepatocellular carcinoma (HCC), or end‐stage liver disease) (Anstee 2018; Mast 2006; Rutherford 2016).

Despite global vaccination programmes, HBV infection remains a public health challenge. Chronic HBV infection is a leading cause of chronic liver diseases worldwide (Anstee 2018). According to World Health Organization (WHO) estimates, 1.1 million people were newly infected with chronic HBV infection during 2019 (WHO 2019). A total of 1.4 million people died from infection with any of the viral hepatitis viruses during 2016 (WHO 2019). The prevalence of hepatitis B surface antigen (HBsAg)‐positive chronic HBV infection was highest among the Western Pacific region (6.2%), followed by the African region (6.1%), the Eastern Mediterranean region (3.3%), the South‐East Asia region (2.0%), the European region (1.6%), and the region of the Americas (0.7%) (WHO 2017).

Diagnosis of HBV infection is based on the presence of serological markers (antigens and antibodies) in plasma or serum. Serological testing encompasses detection of HBV antigens (i.e. HBsAg, hepatitis B e antigen (HBeAg), hepatitis B core antigen (HBcAg)), and antibodies (i.e. anti‐HBs, anti‐HBe, anti‐HBc) (Anstee 2018). Viral load for HBV DNA can be measured using polymerase chain reaction (PCR) in peripheral blood (Anstee 2018). HBsAg and HBV DNA may not be detectable in serum, but HBV DNA is detectable in the liver (Marianna 2018). Other laboratory investigations such as liver enzymes (aminotransferase levels), bilirubin, albumin, and prothrombin time can be used to measure the hepatic decompensation status (Rutherford 2016). Imaging techniques such as ultrasound, computed tomography (CT), and magnetic resonance imaging (MRI) are used to evaluate liver parenchyma and to detect any associated complications (Rutherford 2016). Liver biopsy and histological evaluation are useful for evaluation of the disease stages (Rutherford 2016).

According to the new nomenclature from the European Association for the Study of the Liver (EASL) in 2017, HBV infection has five phases based on the HBeAg status, HBV DNA levels, alanine aminotransferase (ALT) values, and the presence or absence of liver inflammation (EASL 2017; Sarin 2016). The clinical course of HBV infection varies and may include acute and self‐limiting stage, fulminant hepatic failure, inactive carrier state, chronic hepatitis with further complication to cirrhosis, and HCC. Table 1 presents a summary of the five phases and the associated serological markers, enzyme levels, and liver histology findings (Kim 2021; McHugh 2011).

1. Phases of chronic hepatitis B virus infection and associated serological markers, enzyme levels, and liver histology.

	HBeAg positive		HBeAg negative		HBsAg negative
	Chronic infection	Chronic hepatitis	Chronic infection	Chronic hepatitis	Phase 5
	Phase 1	Phase 2	Phase 3	Phase 4
HBsAg	High	High/intermediate	Low	Intermediate	Negative
Anti‐HBs	—	—	—	—	Positive or negative
HBeAg	Positive	Positive	Negative	Negative	—
Anti‐HBe	—	—	Detectable	Detectable	—
Anti‐HBc	—	—	—	—	Positive
HBV DNAa	Very high > 107 IU/mL	High 104–107 IU/mL	Undetectable or low < 2000 IU/mL	> 2000 IU/mL	May be undetectable
ALT	Normal limit or ULN	Elevated	Normal	Elevated	Normal
Liver inflammation status	Minimal or no necroinflammation and fibrosis	Moderate‐to‐severe necroinflammation and fibrosis	None or minimal necroinflammation and low fibrosis	Moderate/severe necroinflammation and fibrosis	—
Old terminology	Immune tolerant phase	Immune reactive HBeAg‐positive phase	Inactive HBsAg carrier phase	HBeAg‐negative chronic hepatitis B	Occult HBV infection

Adapted from EASL 2017; Kim 2021; and McHugh 2011.
ALT: alanine aminotransferase; anti‐HBc: antibody to HBcAg; anti‐HBe: antibody to HBeAg; anti‐HBs: antibody to HBsAg; HBeAg: hepatitis B e‐antigen; HBsAg: hepatitis B surface antigen; HBV: hepatitis B virus; HBV DNA: hepatitis B virus DNA (a measure of the viral load of the hepatitis B virus in the blood); ULN: upper limit of normal.
^aFor HBV DNA: 2000 IU/mL = 104 copies/mL; 20,000 IU/mL = 105 copies/mL; ULN = upper limit of normal.

Treatment consideration for chronic HBV infection is based mainly on three criteria: serum HBV DNA level, serum ALT level, and severity of the liver disease (EASL 2017). According to the global strategy advocated by WHO, elimination of HBV infection requires a synergy across five core actions: (i) immunisation against hepatitis B; (ii) prevention of mother‐to‐child transmission (PMTCT) of HBV; (iii) blood and injection safety; (iv) harm reduction services for people who inject drugs, and (v) increased testing and treatment (WHO 2016a). Hence, an effective antiviral treatment is one of the core interventions for the elimination of chronic HBV (WHO 2019). Since one of the WHO strategies is to eliminate hepatitis by 2030, 80% of HBV‐infected people need to receive eligible treatment to achieve the target (WHO 2016a).

The main goal of treatment of people with chronic HBV infection is to decrease mortality and improve quality of life by preventing disease progression to cirrhosis and HCC (EASL 2017). In treatment guidelines of HBV, pegylated interferon‐α (PEG‐IFN‐α) and nucleos(t)ide analogues are recommended treatments (Coffin 2018; NICE 2017; Terrault 2018), with specific indications for different stages of infection (EASL 2017). PEG‐IFN‐α is the first line treatment for people with HBsAg positivity, HBeAg positivity, and compensated liver disease, while nucleos(t)ide analogues are used as a second‐line treatment for people who do not undergo HBeAg seroconversion or who relapse (revert to HBeAg positivity following seroconversion) after first‐line treatment with PEG‐IFN‐α (Coffin 2018; NICE 2017; Terrault 2018).

The clinical course of HBV infection varies from acute, self‐limiting stage into chronic hepatitis B with further complications such as cirrhosis and HCC. If HBV infection is not properly treated, people with acute HBV infection can progress to serious complications such as fulminant hepatitis and acute liver failure, both of which have high mortality (EASL 2017; NHS 2019; Terrault 2018).

Description of the intervention

Thymosin‐α1, a synthetic 28‐amino acid polypeptide with a molecular weight of 3 kiloDaltons (Goldstein 2005), belongs to the class of biological response modifiers (Samara 2016). It is also a powerful mediator of immunity and inflammatory responses (Pica 2016). Studies have reported that thymosin‐α1 may reduce the occurrence of infection in acute pancreatitis (Wang 2011), lower the incidence of infection in people with nephrotic syndrome (Wu 2012), and tends to inhibit the development of HCC in people with hepatitis B (Wu 2018). Due to its immunomodulatory effect, thymosin‐α1 is used for treatment of sepsis and septic shock (Li 2015; Liu 2017). However, these findings could be confounded by host factors (e.g. age and sex of the participants, presence of comorbid diseases, and compliance to the treatment), virus‐related factors (e.g. genotype of HBV or the causal organism), and treatment‐related factors (e.g. different dosage or different regimen). Thymosin‐α1 is used as a 1.6 mg, subcutaneous injection, twice a week (You 2006).

How the intervention might work

Thymosin‐α1 is a potential therapeutic agent for HBV infection due to its antiviral activity. Chronic HBV infection exhibits a dynamic state of interaction between the virus, the affected hepatocytes, and the host immune response (Wu 2015). Immunological studies have shown that impaired HBV‐specific T‐cell reactivity is a major reason for the development of chronic infection (Zhang 2009). Thymosin‐α1 may be considered as treatment of diseases with immune dysfunction such as HBV and hepatitis C virus (HCV) infections, and cancer (Pica 2016). Although the exact mechanism of action of thymosin‐α1 is not fully understood, the proposed mechanisms, responsible for the anti‐inflammatory and immunomodulatory effects, include:

• modulation of the immune system (Zhang 2019);

• acceleration of the replenishment and maturation of thymocytes (Wu 2015);

• increasing T‐cell function and maturation, stimulation of differentiation into active T cells, and antigen recognition (Chan 2001; Liu 2016; Low 1984; Wu 2015);

• enhancing T‐cell‐mediated antibody production (Wu 2015);

• enhancing the function of intrahepatic natural killer T cells (NKT) and cytotoxic T‐lymphocytes (CTLs) (Wu 2015);

• stimulation of interferon (IFN) and cytokine production (Chan 2001; Chien 1998);

• enhancing the activity of natural killer cell‐mediated cytotoxicity (Chan 2001; Low 1984).

Why it is important to do this review

One study from 2015 reported that the number of people infected with HBV was increasing, and likely, the cumulative number of deaths would reach 20 million by 2030 (WHO 2016b). One meta‐analysis with eight randomised clinical trials using data from 583 participants with HBeAg‐positive chronic HBV infection showed that a combination treatment of thymosin‐α1 plus lamivudine was significantly superior versus lamivudine alone in terms of ALT normalisation (P = 0.01), virological response (P = 0.002), and HBeAg seroconversion (P < 0.001) (Zhang 2009). Another meta‐analysis with five randomised clinical trials using data from 353 participants reported that thymosin‐α1 alone was around three‐fold superior compared with placebo (usual care) in terms of virological response at 12 months post‐treatment (odds ratio (OR) 2.67, 95% confidence interval (CI) 1.25 to 5.68), but there was no significant virological response at the end of treatment (OR 0.56, 95% CI 0.20 to 1.52) or six months post‐treatment (OR 1.67, 95% CI 0.83 to 3.37) (Chan 2001). Most of the current guidelines for the treatment of chronic HBV do not include thymosin‐α1 as a part of the treatment (Coffin 2018; NICE 2017; Terrault 2018). One meta‐analysis incorporating seven randomised clinical trials reported that the combination of thymosin‐α1 plus entecavir seemed safer and more effective than entecavir monotherapy for HBV‐infected people with cirrhosis (Peng 2020). Yang and colleagues found that thymosin‐α1 was better tolerated than IFN‐gamma and might gradually induce sustained ALT normalisation and HBV‐DNA/HBeAg loss in the management of chronic hepatitis B (Yang 2008). We are aware of a published Cochrane protocol entitled "Thymosin alpha1 for chronic hepatitis B" (Saconato 2018). This protocol was withdrawn as the systematic review was not conducted. We are not aware of any other published reviews on thymosin‐α1 for chronic hepatitis B. We will perform this Cochrane systematic review to assess the benefits and harms of thymosin‐α1 as a treatment or an adjunct treatment for people with HBV infection.

Objectives

To assess the benefits and harms of thymosin‐α1 in people with chronic hepatitis B, regardless of their age, sex, and ethnicity

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised clinical trials with a parallel‐group design, which assess the benefits and harms of thymosin‐α1 in people with chronic hepatitis B. We will include trials irrespective of publication type and design, publication status, publication year, language, and outcomes reported.

If found, we will include randomised trials with a cluster design. Cluster randomised trials are those in which groups of individuals are randomised (e.g. schools, villages, medical practices, patients of a single doctor, or families).

If found, we will include randomised trials with a two‐period cross‐over design. We will include only the data from the first trial period of the cross‐over trial (Higgins 2021a). The participant in a cross‐over trial is used as his or her own control as they are randomised to a sequence of two or more interventions.

We will exclude pseudo‐randomised studies (i.e. quasi‐randomised studies) as the method of allocation to the study groups is not truly random.

Types of participants

We will include trials that randomised people with evidence of chronic HBV infection (i.e. presence of HBsAg in the serum) regardless of participants' age, sex, and ethnicity.

Specifically, we will consider for inclusion trials that have any of the following types of participants, or both.

• Trials in which all participants have chronic HBV infection, with no other comorbidities.

• Trials in which participants have chronic HBV along with other comorbidities (e.g. HIV or HCV, cirrhosis, HCC, and liver‐related or other comorbidities (e.g. diabetes, concomitant kidney failure).

Types of interventions

We will perform the following pairwise comparisons.

• Thymosin‐α1 at any dose and route of administration (experimental) versus placebo or no intervention (control).

• Thymosin‐α1 at any dose and route of administration (experimental) versus immunomodulatory drugs (conventional interferon‐α (IFN‐α) or pegylated interferon‐α (PEG‐IFN‐α) (control).

• Thymosin‐α1 at any dose and route of administration (experimental) versus nucleoside analogues (entecavir, lamivudine, and telbivudine) (control).

• Thymosin‐α1 at any dose and route of administration (experimental) versus nucleotide analogues (adefovir, tenofovir alafenamide, and tenofovir disoproxil) (control).

We will allow co‐interventions if administered equally to the experimental and control groups.

Types of outcome measures

We will use the data at the longest follow‐up time for our primary analysis. We will include trials regardless of the outcomes they report.

Primary outcomes

• Proportion of people with all‐cause mortality.

• Proportion of people with one or more serious adverse events: we will consider an event as serious if the trial authors clearly stated that it was due to the experimental or control intervention and have defined it as 'serious adverse event' or if it fulfilled the definition of the International Conference on Harmonization (ICH) guidelines for serious adverse events (ICH 2003; ICH‐GCP 2016), that is, any event that leads to death; is life‐threatening; requires hospitalisation or prolongation of existing hospitalisation; results in persistent or significant disability; congenital birth or anomaly; and any important medical event which may have jeopardised the patient or requires intervention to prevent it. We will consider all other adverse events as non‐serious (European Medicines Agency 1995).

• Health‐related quality of life: any validated assessment scale, completed by the trial participants.

Secondary outcomes

• Proportion of people with hepatitis B‐related morbidity: we will define hepatitis B‐related morbidity as the number of participants who developed cirrhosis, ascites, variceal bleeding, hepato‐renal syndrome, HCC, or hepatic encephalopathy.

• Proportion of people with hepatitis B‐related mortality.

• Proportion of people with one or more adverse events considered non‐serious. See text under 'Primary outcomes: proportion of people with one or more serious adverse events'.

• Proportion of people without histological improvement (i.e. histological improvement measured by liver biopsy, analysed by histopathologists for liver necroinflammatory activity and fibrosis with scoring system such as Scheuer scoring system; improvement or progression of necroinflammation is defined as at least one grade lower or higher than the baseline in the necroinflammatory activity).

• Proportion of people without serological and biochemical improvement (i.e. detectable HBsAg, detectable HBV DNA in serum or plasma; detectable HBeAg in serum or plasma (this outcome is only relevant for HBeAg‐positive participants); without HBeAg seroconversion in serum or plasma (this outcome is only relevant for HBeAg‐positive participants); without normalisation of transaminases).

• Proportion of people with individual hepatitis B‐related morbidity (i.e. developed cirrhosis, ascites, variceal bleeding, hepato‐renal syndrome, HCC, or hepatic encephalopathy).

Search methods for identification of studies

Electronic searches

We will search The Cochrane Hepato‐Biliary Group Controlled Trials Register (will be searched internally by the Cochrane Hepato‐Biliary Group Information Specialist via the Cochrane Register of Studies Web. We will provide the date of search at the review stage), Cochrane Central Register of Controlled Trials in the Cochrane Library (the latest issue), MEDLINE Ovid (1946 to the date of the search), Embase Ovid (Excerpta Medica Database; 1974 to the date of the search), LILACS (Bireme; 1982 to the date of the search), Science Citation Index Expanded (Web of Science; 1900 to the date of the search), and Conference Proceedings Citation Index – Science (Web of Science; 1990 to the date of the search). Appendix 1 presents all search strategies in the respective databases with the expected time spans of the searches.

Searching other resources

We will search online trial registries such as ClinicalTrial.gov (clinicaltrials.gov/), European Medicines Agency (EMA; www.ema.europa.eu/ema/), WHO International Clinical Trial Registry Platform (www.who.int/ictrp), Food and Drug Administration (FDA; www.fda.gov), EU Clinical Trials Register (www.clinicaltrialsregister.eu/), International Clinical Trials Registry Platform, and pharmaceutical company sources for ongoing or unpublished trials and for study information. We will also search for grey literature in the System for Information on Grey Literature in Europe 'OpenGrey' (www.opengrey.eu/). We will provide the date of search at the review stage.

We will check the reference lists of all primary studies and relevant review articles for additional references. We will contact authors of identified trials for additional published or unpublished trials.

We will also examine any relevant retraction statements and errata for information as errata can reveal important limitations or even fatal flaws in included studies (Lefebvre 2021).

Data collection and analysis

We will conduct the review according to the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021a). We will use Review Manager Web (RevMan Web 2020) to collect data and perform the analyses. We will use Trial Sequential Analysis software to assess imprecision as sensitivity analysis (Thorlund 2017; TSA 2017).

Selection of studies

Two review authors (NHH and TTW) will independently screen the titles, abstracts, and records identified from searches. The two review authors will code independently potentially eligible studies as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. We will retrieve the full‐text study reports of all potentially eligible trials, and two review authors (NHH and TTW) will independently screen the publications for inclusion, recording the reasons for exclusion of ineligible studies. We will resolve any disagreement through discussion, or, if required, we will consult a third review author (CN). We will identify and exclude duplicates and collate multiple reports of the same trial so that each trial, rather than each report, is the unit of interest. We will record the selection process in sufficient detail to complete a PRISMA‐S flow diagram (Rethlefsen 2021) and the characteristics of excluded studies table. We will include trials regardless of whether they report on our outcomes of interest. If the trials do not assess the outcomes of our review because trial investigators (e.g. they did not aim to assess such outcomes), we will describe these studies narratively. We will include trials regardless of their format of reporting. If we identify trials with unpublished data, then we will consider these for inclusion in our review.

We will contact authors of identified studies to enquire about additional published and unpublished studies. We will check for post‐publication amendments and examine any relevant retraction statements and errata for information, as errata can reveal important limitations or even fatal flaws in included trials (Lefebvre 2021). We will exclude retracted studies (Retraction Watch Database (retractionwatch.com/retraction-watch-database-user-guide/); Moylan 2016; Wager 2011).

If during the selection of trials, we identify observational studies on the topic of our review (e.g. quasi‐randomised studies, cohort studies, or case reports) that have reported adverse events during the study period, we will include these studies for a review of the reported adverse events only. We will present these data separately. We will not specifically search for observational studies for inclusion in this review, which is a limitation. We are aware that by not searching for all observational studies on adverse events, we allow the risk of placing more weight on potential benefits than on potential harms, and of overlooking uncommon and late adverse events (Storebø 2018).

Data extraction and management

Two review authors (NHH and TTW) will pilot a data extraction form on at least three trials. NHH and TTW will independently extract data. The data needed to perform our systematic review include the following.

• Characteristics of the trial: trial design, total duration of the trial, number of trial centres and location, trial setting, type of trial (superiority, equivalence, or non‐inferiority trial), withdrawals/dropouts, and journal where the trial was published.

• Participants: number of participants in each group, mean age, age range, sex, ethnic group, diagnostic criteria, diagnostic methods, severity of condition, baseline liver function, comorbidities, inclusion criteria, and exclusion criteria.

• Interventions: experimental intervention (dosage, regimen, and route of administration), control intervention (dosage, regimen, and route of administration); and concomitant medications. We will group the drugs following their classification (i.e. immunomodulatory agents (IFN and PEG‐IFN) or antiviral agents (nucleoside and nucleotide analogues)).

• Outcomes and time: planned study outcomes and their reporting in the trial publications; primary and secondary outcomes specified and collected, and time points reported (e.g. 12 months and 24 months). If the trial protocol is available, we will use it for later comparison during risk of bias assessment.

• Notes: dates of trial authors contacted and dates of replies received, source of funding, conflicts of interest of trial authors, clinical trial number, a priori sample estimation, ethics committee approval (for trials launched after 2005).

We will note in the characteristics of included studies table if outcome data were not reported in a usable way. We will resolve disagreements by consensus involving all review authors. One review author (NHH) will perform data entry into the characteristics of included studies table​​​ in Review Manager Web (RevMan Web 2020). Another review author (CN) will check trial characteristics for accuracy against the trial reports.

Assessment of risk of bias in included studies

Two review authors (NHH and TTW) will independently assess the risk of bias of the included trials. We will resolve any disagreement by consensus, or if required, by consulting a third review author (CN). We will assess risk of bias using the RoB 2 tool (Higgins 2019; Higgins 2021b; MECIR 2016; Sterne 2019). We will assess the effect of assignment to the intervention (Higgins 2021b). For the effect of interest, we will analyse RoB 2 against the effect of assignment to intervention using an intention‐to‐treat (ITT) analysis that includes all randomised participants, regardless of the interventions they actually received.

We will use the following five domains to assess bias in the individually randomised trials (Higgins 2021b).

• Bias arising from the randomisation process.

• Bias due to deviations from intended interventions.

• Bias due to missing outcome data.

• Bias in measurement of an outcome.

• Bias in selection of the reported result.

We provide the signalling questions for these domains in Appendix 2. The response options for the signalling questions are 'Yes'/'Probably yes'/'No'/'Probably no'/'No information'. Elaborations to these signalling questions can be found in Higgins 2021b. An algorithm, developed in Microsoft Excel, will map our responses to the signalling questions per outcome and will propose a risk of bias judgement for each domain. We will follow the algorithm for the domain of bias arising from the randomisation process (Higgins 2019).

Cluster randomised trials

The RoB 2 assessment of trials that allocated cluster of individuals will include the aforementioned five domains plus one additional domain specific to the trial design (Eldridge 2020; Higgins 2019; Higgins 2021c). This additional domain is 'Bias arising from the timing of identification and recruitment of individual participants within clusters in relation to timing of randomisation'. We will use the signalling questions as described in Appendix 3 (Eldridge 2020). We will follow the suggested algorithm for reaching risk of bias judgements for bias arising from the timing of identification and recruitment of participants in a cluster‐randomised trial (Eldridge 2020).

Cross‐over trials

We will use the RoB 2 tool for the assessment of the risk of bias of cross‐over trials. We will use the signalling questions as stated in Appendix 4 to assess Domain 2. 'Bias due to deviations from intended interventions' (Higgins 2020). We will address carry‐over effects within this same domain. We will follow the signalling questions and suggested algorithm as indicated (Higgins 2020; Higgins 2021c). Regarding the assessment of risk of bias under Domain 3. 'Bias due to missing outcome data in included cross‐over trials', we will use the signalling question as described in Appendix 5 (Higgins 2020). We plan to address period effects through examination of allocation ratio and the approach to analysis. We plan to address any additional possibility of the selective reporting of the first period in Domain 5. 'Bias in selection of the reported result' (Higgins 2021c).

We will assign one of the three levels of judgement to each domain as indicated below.

• Low risk of bias: the trial is judged at low risk of bias for all domains for this outcome result.

• Some concerns: the trial is judged to raise some concerns in at least one domain for this outcome result, but is not at high risk of bias for any of the remaining domains.

• High risk of bias: the trial is judged at high risk of bias in at least one domain for this outcome result, or the study is judged to have some concerns for multiple domains in a way that substantially lowers confidence in the result.

The overall risk of bias judgement is the same as for the individual domains (i.e. low risk of bias, some concerns, or high risk of bias). Judging a result to be at a particular level of risk of bias for an individual domain implies that the result has an overall risk of bias at least this severe. We will use the RoB 2 Microsoft Excel tool to store the data (which can be received at request) until we find a place to make the judgements publicly available.

The risk of bias assessments will feed into one domain of the GRADE approach for assessing certainty of a body of evidence (Schünemann 2021a).

In summary of findings tables, we will present the outcomes that we consider most relevant for clinical practice. These outcomes are:

• all‐cause mortality;

• one or more serious adverse events;

• health‐related quality of life;

• hepatitis B‐related morbidity;

• hepatitis B‐related mortality;

• one or more non‐serious adverse events; and

• no histological improvement.

We will present the results of our main analyses (i.e. the outcome result at maximum follow‐up), the mean or median, and their ranges.

Measures of treatment effect

We will use Review Manager Web provided by Cochrane (RevMan Web 2020). We will use random‐effects model meta‐analysis as our primary analyses and the fixed‐effect model meta‐analysis as sensitivity analysis. We will measure dichotomous outcomes using risk ratios (RR) with 95% CI. We will measure continuous outcomes, such as health‐related quality of life, using the mean difference (MD) with 95% CI if trials used the same tool. We will use the standardised mean difference (SMD) with 95% CI to analyse health‐related quality of life if trials used different measurement scales. We will interpret SMD as follows: SMD less than 0.40 for small intervention effects; SMD between 0.40 and 0.70 for moderate intervention effects; and SMD greater than 0.70 for large intervention effects (Schünemann 2021b). We will describe skewed data reported as medians and interquartile ranges in a narrative format. We will estimate the 'overall effect' across all outcomes.

Unit of analysis issues

In trials with individually randomised, parallel‐group design, the unit of analysis will be the trial participants as randomised within the trial.

We will record how trials have presented outcome results (i.e. the total number of participants with an event, or total number of events per participant (e.g. if the same participant was admitted to the hospital more than once or had more than one episode of vomiting)). We will also record occasions where multiple events in a participant had been incorrectly treated as independent, without considering the interdependence of the events (Higgins 2021d).

If a trial has used a multiple trial arm design, we will include in our comparisons only the data relevant to our review arms. We will list all treatment arms in the characteristics of included studies table, even if they are not used in the review. If a trial has two or more experimental arms and one control, and all are relevant to our review, we will compare in separate each of the experimental arms with each half of the control arm if used within the same comparison.

In cluster‐randomised trials, the unit of analysis is groups of participants as randomised (Deeks 2021). If we identify cluster‐randomised trials for inclusion in the review, we may combine these with the individually randomised trials in the same meta‐analysis provided that the cluster effect estimate takes account of the potential clustering. If not, then we will analyse the cluster‐randomised trials separately to avoid a 'unit of analysis error', as highlighted in the Cochrane Handbook for Systematic Reviews of Interventions (Section 23.1.1; Higgins 2021c). We will consider the generic inverse‐variance approach to analyse the effect estimates and their standard errors (SEs) from correct analyses of cluster‐randomised trials as stated in the Cochrane Handbook for Systematic Reviews of Interventions (Section 23.1.3; Higgins 2021c).

If we identify trials with a cross‐over design, we will only extract effect estimates from the first phase of the cross‐over trial to avoid period effect or carry‐over effect of these estimates (Higgins 2021c; Higgins 2021d).

Dealing with missing data

We will contact trial investigators or study sponsors, or both, to verify key study characteristics and obtain missing numerical outcome data whenever possible.

We will investigate attrition bias (i.e. dropouts, losses to follow‐up, and withdrawals). We will perform our analyses based on the ITT principle whenever possible (Newell 1992), or we will perform a modified ITT, based on the study authors' data that we use.

Regarding the primary outcomes, we will attempt to perform a full ITT by including participants with incomplete or missing data in sensitivity analyses. We will impute the missing participants' values according to the following two extreme‐case scenarios (Hollis 1999).

• Extreme‐case analysis favouring the experimental intervention ('best‐worst' case scenario): none of the dropouts/participants lost from the experimental arm, but all the dropouts/participants lost from the control arm will be assumed to have experienced the outcome, including all randomised participants in the denominator.

• Extreme‐case analysis favouring the control intervention ('worst‐best' case scenario): all dropouts/participants lost from the experimental arm, but none from the control arm, will be assumed to have experienced the outcome, including all randomised participants in the denominator.

If the data are likely to be normally distributed, we plan to use the median for meta‐analysis when the mean is not available (Higgins 2021d). If there are missing standard deviations (SD) for the continuous outcome – health‐related quality of life – we will contact the corresponding author to request whether data are available. If data are not available, we plan to calculate the SD using case‐analysis such as imputing SDs from SEs, CIs, t values, or P values (as appropriate) that related to the differences between means in two groups, following the guidance described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021d). If it is not possible to calculate the SD from the P value or the CIs, we plan to impute the SD using the largest SD in other trials for that outcome (Deeks 2021), or we will replace missing SDs for 'change from baseline' with those provided in other trials for the same outcome. If this approach is not applicable, assuming that correlation coefficients from the two intervention groups are similar, we will impute the SD of change from baseline for the experimental intervention, following the formula as described in the Cochrane Handbook for Systematic Reviews of Interventions (Section 6.5.2.8; Higgins 2021d).

Assessment of heterogeneity

We will use I² statistic to measure heterogeneity among the trials in each analysis, and we will interpret this recommended in Deeks 2021:

• 0% to 40%: might not be important;

• 30% to 60%: may represent moderate heterogeneity;

• 50% to 90%: may represent substantial heterogeneity;

• 75% to 100%: considerable heterogeneity.

If we identify substantial heterogeneity (i.e. I² > 50%), we will report it and explore the possible causes by performing subgroup analyses.

Assessment of reporting biases

If we are able to analyse at least 10 trials in one meta‐analysis, we will create and examine a funnel plot to explore possible small‐study and publication biases (Deeks 2021).

Data synthesis

If a sufficient number of clinically similar trials are available, we will perform meta‐analyses of their results. We will use a random‐effects model. As we expect to gather data from a series of trials performed by different researchers operating independently, it would be unlikely that all the trials were functionally equivalent with a common effect estimate. Therefore, the random‐effects model is more justified than the fixed‐effect model. We will use the fixed‐effect model as a sensitivity analysis. We will present all results with 95% CIs. We will conduct all analyses according to the guidance provided in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2021), and implement them in Review Manager Web (RevMan Web 2020). We will conduct our primary analyses of trial outcomes, irrespective of risk of bias. We will perform sensitivity analysis to show how conclusions might be affected if only trials at low risk of bias were included (Boutron 2021). We may not perform meta‐analysis if there is considerable heterogeneity that we cannot explain, or trials report outcomes differently (e.g. impossible to calculate for the same effect measure from the available statistics) as described in Table 12.1.a of the Cochrane Handbook for Systematic Reviews of Interventions (McKenzie 2021). In such a setting, we will present a narrative synthesis of the main findings and results of the included trials.

Subgroup analysis and investigation of heterogeneity

In the event of substantial clinical, methodological, or statistical heterogeneity, we will attempt to find possible reasons for it by evaluating the individual trials and their subgroup characteristics. We plan to carry out the following subgroup analyses, regardless of the presence of heterogeneity.

• Trials at 'low' risk of bias compared to trials at 'some concern' or at 'high' risk of bias, as different biases can lead to underestimation or overestimation of the true intervention effect (Higgins 2021b).

• Trials at risk of for‐profit support compared to trials without for‐profit support, as trials with for‐profit support may overestimate beneficial intervention effects or underestimate harmful intervention effects (Lundh 2017).

• Trials without co‐interventions compared to trials with co‐interventions (e.g. antiviral treatment for HCV or medications for diabetes mellitus).

• Comorbidity (e.g. infection with HCV, hepatitis D virus, or comorbidities, such as HIV infection, diabetes mellitus, and HCC at entry, compared to those without comorbidities). We will carry out this subgroup analysis provided that disaggregated data can be obtained from the included trials or from trial investigators.

• Different phases of chronic HBV infection (e.g. HBeAg‐positive compared to HBeAg‐negative participants; immune tolerant, immune clearance, inactive carrier state, reactivation HBeAg‐negative chronic hepatitis stage if the trials report it) (Lok 2019).

• Pre‐existing cirrhosis compared to participants without cirrhosis.

We plan to do stratifications of the participants involved if there are enough data. If the trialists report the number of participants in each group, we will take these numbers for data analysis. If the trialists report percentage of the proportion of participants in each group, we will take a threshold as a percentage, and we will compare the trials as below and above this threshold. Our cut‐off will be 60% threshold, for a clearer comparison.

We will perform subgroup analyses for the following outcomes, under each comparison.

• All‐cause mortality.

• One or more serious adverse events.

• Health‐related quality of life.

• Hepatitis B‐related morbidity.

• Hepatitis B‐related mortality.

We will use the formal test for subgroup interactions in Review Manager Web (RevMan Web 2020).

Sensitivity analysis

We will carry out the following sensitivity analyses for the same outcomes as in the subgroup analyses.

• Excluding trials at some concern for risk of bias and trials at high risk of bias.

• Conducting the analyses with a fixed‐effect model.

• Assessment of imprecision with Trial Sequential Analysis (see below).

We will use Trial Sequential Analysis as the sensitivity analysis for our primary outcomes only: all‐cause mortality; one or more serious adverse events; and health‐related quality of life. We will use the data at maximum follow‐up (Castellini 2018; Gartlehner 2019; Jakobsen 2014).

Trial Sequential Analysis

Trial Sequential Analysis will be performed to control the risk of random errors due to sparse data and repetitive testing of accumulating data (Thorlund 2017; Wetterslev 2008).

We will add trials to the analysis according to the year of publication. If more than one trial is published in a year, we will add the trials in alphabetical order, according to the name of the first author. We will calculate the diversity‐adjusted required information size (DARIS) (i.e. the number of participants needed in a meta‐analysis to detect or reject a certain intervention effect) (Brok 2008; Brok 2009; Thorlund 2010; Wetterslev 2008; Wetterslev 2009; Wetterslev 2017). On the basis of the DARIS, we will construct the trial sequential monitoring boundaries for benefit, harm, and futility (Thorlund 2017; Wetterslev 2008; Wetterslev 2009; Wetterslev 2017). These boundaries determine the statistical inference one may draw regarding the cumulative meta‐analysis that has not reached the DARIS; if the trial sequential monitoring boundary for benefit or harm is crossed before the DARIS is reached, firm evidence may be established, and further trials may be superfluous. However, if the boundaries for benefit or harm are not crossed, it is most probably necessary to continue doing trials in order to detect or reject a certain intervention effect. If the cumulative Z‐curve crosses the trial sequential monitoring boundaries for futility, no more trials will be needed.

For the two dichotomous outcomes, we will base the DARIS on the event proportion in the control group of our meta‐analysis; assuming a plausible relative risk reduction for all‐cause mortality of 20%, for serious adverse events of 10%; a risk of type I error of 2.5% due to the three primary outcomes (Jakobsen 2014); a risk of type II error of 10%; and the diversity of the included trials in the meta‐analysis. For the continuous outcome, health‐related quality of life, we will estimate the DARIS using a minimal relevant difference of half the SD of the meta‐analysis; the SD of the meta‐analysis; alpha of 2.5% due to the three primary outcomes (Jakobsen 2014); beta of 10%; and the diversity as estimated from the trials in the meta‐analysis (Wetterslev 2009). Trial Sequential Analysis considers the choice of statistical model (fixed‐effect or random‐effects) and diversity (Thorlund 2017; TSA 2017). We will use the random‐effects model. We will also calculate the Trial Sequential Analysis‐adjusted CIs (Thorlund 2017; Wetterslev 2017). In Trial Sequential Analysis, we will downgrade our assessment of imprecision by two levels if the accrued number of participants is below 50% of the DARIS, and one level if between 50% and 100% of the DARIS. We will not downgrade if futility or DARIS is reached. We will perform this analysis with TSA software, version 0.9.5.10 beta (TSA 2017).

Summary of findings and assessment of the certainty of the evidence

As we have planned four comparisons (Types of interventions), we will create four summary of findings tables presenting results on seven outcomes of our review:

• all‐cause mortality;

• one or more serious adverse events;

• health‐related quality of life;

• hepatitis B‐related morbidity;

• hepatitis B‐related mortality;

• one or more non‐serious adverse events; and

• no histological improvement.

All outcome results will be given at maximum follow‐up, with mean, or median if data for the mean are not available, and range. We will use the five GRADE domains (i.e. study risk of bias (methodological quality; we will use the overall RoB 2 judgement); inconsistency of results (unexplained heterogeneity); indirectness of evidence (population, intervention, comparator, or outcome); imprecision of results (wide CIs); and publication bias. We will use the methods and recommendations described in Chapter 14 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2021a), using GRADEpro GDT software (GRADEpro GDT). We will justify all decisions to downgrade the certainty of the evidence using footnotes, and we will make comments to aid the reader's understanding of the review where necessary. We will resolve any disagreements through discussion, or, if required, we will consult a third review author (CN).

We will define levels of certainty as 'high', 'moderate', 'low', or 'very low' as follows.

• High certainty: we are very confident that the true effect lies close to that of the estimate of the effect.

• Moderate certainty: we are moderately confident in the effect estimate: the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.

• Low certainty: our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect.

• Very low certainty: we have very little confidence in the effect estimate: the true effect is likely to be substantially different from the estimate of effect.

We will conduct the review according to this published protocol and report any deviations from it in the 'Differences between protocol and review' section of the systematic review.

Appendices

Appendix 1. Search strategies

Database	Time span	Search strategy
Cochrane Hepato‐Biliary Controlled Trials Register (via the Cochrane Register of Studies Web)	Date of the search will be given at the review stage	(thymosin* or Ta1 or T‐a‐1 or T‐a1 or t‐al*a‐1 or t‐al*a1) and (hepatitis B or hep B or HBV)
Cochrane Central Register of Controlled Trials in the Cochrane Library	Latest issue	#1 MeSH descriptor: [Thymosin] explode all trees #2 thymosin* or Ta1 or T‐a‐1 or T‐a1 or t‐al*a‐1 or t‐al*a1 #3 #1 or #2 #4 MeSH descriptor: [Hepatitis B, Chronic] explode all trees #5 hepatitis B or hep B or HBV #6 #4 or #5 #7 #3 and #6
MEDLINE Ovid	1946 to the date of the search	1. exp Thymosin/ 2. (thymosin* or Ta1 or T‐a‐1 or T‐a1 or t‐al*a‐1 or t‐al*a1).mp. [mp=title, abstract, original title, name of substance word, subject heading word, floating sub‐heading word, keyword heading word, organism supplementary concept word, protocol supplementary concept word, rare disease supplementary concept word, unique identifier, synonyms] 3. 1 or 2 4. exp Hepatitis B, Chronic/ 5. (hepatitis B or hep B or HBV).mp. [mp=title, abstract, original title, name of substance word, subject heading word, floating sub‐heading word, keyword heading word, organism supplementary concept word, protocol supplementary concept word, rare disease supplementary concept word, unique identifier, synonyms] 6. 4 or 5 7. 3 and 6
Embase Ovid	1974 to the date of the search	1. exp thymosin/ 2. exp thymosin alpha1/ 3. (thymosin* or Ta1 or T‐a‐1 or T‐a1 or t‐al*a‐1 or t‐al*a1).mp. [mp=title, abstract, heading word, drug trade name, original title, device manufacturer, drug manufacturer, device trade name, keyword, floating subheading word, candidate term word] 4. 1 or 2 or 3 5. exp chronic hepatitis B/ 6. (hepatitis B or hep B or HBV).mp. [mp=title, abstract, heading word, drug trade name, original title, device manufacturer, drug manufacturer, device trade name, keyword, floating subheading word, candidate term word] 7. 5 or 6 8. 4 and 7
LILACS (Bireme)	1982 to the date of the search	((thymosin$ or Ta1 or T‐a‐1 or T‐a1 or t‐al$a‐1 or t‐al$a1)) [Words] and (hepatitis B or hep B or HBV) [Words]
Science Citation Index Expanded (Web of Science)	1900 to the date of the search	#3 #2 AND #1 #2 TS=(hepatitis B or hep B or HBV) #1 TS=((thymosin* or Ta1 or T‐a‐1 or T‐a1 or t‐al*a‐1 or t‐al*a1))
Conference Proceedings Citation Index – Science (Web of Science)	1990 to the date of the search	#3 #2 AND #1 #2 TS=(hepatitis B or hep B or HBV) #1 TS=((thymosin* or Ta1 or T‐a‐1 or T‐a1 or t‐al*a‐1 or t‐al*a1))

Appendix 2. Risk of Bias 2 (RoB 2)

Bias domain	Issues addressed
Risk of bias arising from the randomisation process	Whether, the allocation sequence random; the allocation sequence was concealed until participants were enrolled and assigned to interventions; baseline differences between intervention groups suggested a problem with the randomisation process.
Risk of bias due to deviation from the intended intervention (effect of assignment to intervention)	Whether, participants were aware of their assigned intervention during the trial; carers and people delivering the interventions were aware of participants and assigned intervention during the trial. When interest is in the effect of assignment to intervention: (if applicable) deviations from the intended intervention arose because of the experimental context and, if so, whether they were unbalanced between groups and likely to have affected the outcome; an appropriate analysis was used to estimate the effect of assignment to intervention. When interest in the effect of adhering to intervention: (if applicable) important non‐protocol interventions were balanced across intervention groups; (if applicable) failure in implementing the intervention could have affected the outcome; (if applicable) study participants adhered to the assigned intervention regimen; (if applicable) an appropriate analysis was used to estimate the effect of adhering to the intervention.
Bias due to missing outcome data	Whether, data for this outcome were available for all, or nearly all, participants randomised; (if applicable) there was evidence that the result was not biased by missing outcome data: (if applicable) missingness in the outcome was likely to depend on its true value (e.g. proportion of missing outcome data, or reasons for missing outcome data, differ between intervention groups).
Bias in measurement of the outcome	Whether, the method of measuring the outcome was inappropriate; measurement or ascertainment of the outcome could have differed between intervention groups; outcome assessors were aware of the intervention received by study participants; assessment of the outcome was likely to have been influenced by knowledge of intervention received.
Bias in selection of the reported results	Whether, trial was analysed in accordance with a prespecified plan that was finalised before unblinded outcome data were available for analysis; the numerical result being assessed is likely to have been selected, on the basis of the results, from multiple outcome measurements (e.g. scales, definitions, time points) within the outcome domain; the numerical result being assessed is likely to have been selected, on the basis of the results, from multiple analyses of the data.

Appendix 3. Risk of bias arising from the timing of identification and recruitment of participants in a cluster randomised trial

Signalling questions	Elaboration
1b.1 Were all the individual participants identified before randomisation of clusters (and if the trial specifically recruited patients were they all recruited before randomisation of clusters)?	Answer "Yes" if participants were identified and recruited prior to the clusters being randomised or if individual participants were not recruited but were identified prior to randomisation. In these cases, identification/recruitment bias is not possible. Answer "No" if either identification or recruitment of participants (or both) takes place after randomisation. Also answer "No" if some participants are identified or recruited (or both) before and some after randomisation as the potential for bias still exists in these trials.
1b.2 If No/Probably no/No information to 1b.1: is it likely that selection of individual participants was affected by knowledge of the intervention?	Answer "Yes" if those recruiting individuals are aware of cluster allocation prior to recruitment and are likely to consciously or subconsciously have differentially recruited in the trial arms; if some of those being recruited are aware of cluster allocation prior to their own recruitment and this is likely to have differentially affected recruitment in the trial arms; if those identifying potential participants (when recruitment is to take place subsequently) or those identifying actual participants (when there is no subsequent recruitment) are aware of cluster allocation and are likely to have consciously or subconsciously differentially included potential individual participants in different trial arms. Answer "No" if all of the following (as relevant depending on the trial) are unaware of cluster allocation at recruitment: those identifying actual participants, those identifying potential participants, those recruiting, and potential participants themselves.
1b.3 Were there baseline imbalances that suggest differential identification or recruitment of individual participants between arms?	As for signalling question 1a.3, imbalances that are compatible with chance should not be highlighted here. Imbalances due to differential identification or recruitment of participants are more common in cluster randomised trials than imbalances due to problems with randomisation. Such imbalances are usually in the numbers of participants recruited into each arm or, less commonly, in the characteristics of such individuals. If there is a noticeable imbalance and imbalance due to the randomisation process and due to identification/recruitment of individuals are both possible, a judgement will need to be made about which is the most likely cause of any imbalance or whether they are both likely.

Appendix 4. Risk of bias due to deviations from intended intervention in a cross‐over trial

Signalling questions	Elaboration
For effect of assignment to intervention
2.1. Were participants aware of their assigned intervention during each period of the trial?	If participants are aware of their intervention assignment, it is more likely that additional health‐related behaviours will differ between the assigned interventions, so risk of bias will be higher. Masking participants, which is most commonly achieved through use of a placebo or sham intervention, may prevent such differences.
2.2. Were carers and trial personnel aware of participants' assigned intervention during each period of the trial?	If those involved in caring for participants or making decisions about their health care are aware of the assigned intervention, then implementation of the intended intervention, or administration of additional co‐interventions, may differ between the assigned interventions. Masking carers and trial personnel, which is most commonly achieved through use of a placebo, may prevent such differences.
2.3. If Yes/Probably yes/No information to 2.1 or 2.2: were there deviations from the intended interventions beyond what would be expected in usual practice?	When interest focusses on the effect of assignment to intervention, it is important to distinguish between: deviations that happen in usual practice following the intervention and so are part of the intended intervention (e.g. cessation of a drug intervention because of acute toxicity); and deviations from intended intervention that arise due to expectations of a difference between intervention and comparator (e.g. because participants prefer 1 intervention over the other). We use the term "usual practice" to refer to the usual course of events in a non‐trial context. Because deviations that arise due to expectations of a difference between experimental intervention and control intervention are not part of usual practice, they may lead to biased effect estimates that do not reflect what would happen to participants assigned to the interventions in practice. Trialists do not always report (and do not necessarily know) whether deviations that are not part of usual practice actually occurred. Therefore, the answer "No information" may be appropriate. However, if such deviations probably occurred you should answer "Probably yes".
2.4. If Yes/Probably yes to 2.3: were these deviations from intended interventions unbalanced between the 2 interventions and likely to have affected the outcome?	Deviations from intended interventions that do not reflect usual practice will be important if they affect the outcome, but not otherwise. Furthermore, bias will arise only if there is imbalance in the deviations across the 2 interventions.
2.5 Was there sufficient time for any carry‐over effects to have disappeared before outcome assessment in the second period?	Carry‐over is a key concern in cross‐over trials. It reflects a deviation from the intended intervention because it acts like a co‐intervention during the second period. An understanding of the likelihood of carry‐over requires content knowledge, and information to inform this judgement may not be available from the report of the cross‐over trial. Carry‐over effects can sometimes be detected by comparing imbalance in participant variables at the start of the second period with imbalance in variables at the start of the first period. If there is an exaggerated imbalance at the start of the second period, it may be due to carry over of effects. It is important that carry‐over effects do not affect outcomes measured in the second period. A long period of wash‐out between periods can be used to ensure participants start the second period in a state that is unaffected by what they received in the first period. However, a wash‐out period is not essential. The important consideration is whether sufficient time passes before outcome measurement in the second period, such that any carry‐over effects have disappeared. (This might sometimes be viewed as the participants having reached "steady state".) If a wash‐out period is absent or is too short for carry‐over effects to have disappeared, then measurements taken early in the second period may be affected by carry‐over.
For effect of starting and adhering to intervention
2.1. Were participants aware of their assigned intervention during each period of the trial?	If participants are aware of their intervention assignment, it is more likely that additional health‐related behaviours will differ between the intervention groups, so risk of bias will be higher. Masking participants, which is most commonly achieved through use of a placebo, may prevent such differences.
2.2. Were carers and trial personnel aware of participants' assigned intervention during each period of the trial?	If those involved in caring for participants and those otherwise involved in the trial are aware of group assignment, then it is more likely that implementation of the intended intervention, or the administration of additional co‐interventions, will differ between the interventions. Masking carers and trial personnel, which is most commonly achieved using a placebo, may prevent such differences.
2.3. If Yes/Probably yes/No information to 2.1 or 2.2: were important co‐interventions balanced across the 2 interventions?	Risk of bias will be higher if unplanned co‐interventions were implemented in a way that would bias the estimated effect of intervention. Co‐interventions will be important if they affect the outcome, but not otherwise. Bias will arise only if there is imbalance in such co‐interventions between the interventions. Consider the co‐interventions, including any prespecified co‐interventions, that are likely to affect the outcome and to have been administered in this study. Consider whether these co‐interventions are balanced between the 2 interventions.
2.4. Was the intervention implemented successfully?	As for parallel‐group trials.
2.5. Did study participants adhere to the assigned intervention regimen?	Largely as for parallel group trials. 1 possibility is that the level of adherence will differ by period. For example, participants may adhere less well during the second period.
2.6. If No/Probably no/No information to 2.3, 2.4, or 2.5: was an appropriate analysis used to estimate the effect of starting and adhering to the intervention?	Largely as for parallel group trials. Note that analyses of the full data from a cross‐over trial cannot generally correct for carry‐over effects when they are present.
2.7 Was there sufficient time for any carry‐over effects to have disappeared before outcome assessment in the second period?	See 2.5 under "For effect of assignment to intervention".

Appendix 5. Risk of bias arising due to missing data in a cross‐over trial

Signalling questions	Elaboration
3.1 Were outcome data available for all, or nearly all, participants randomised?	As for parallel group trials.
3.2 If No/Probably No/No information to 3.1: are the proportions of missing outcome data and reasons for missing outcome data similar across interventions?	"Similar" (with regard to proportion and reasons for missing outcome data) includes some minor degree of discrepancy across intervention groups as expected by chance. Assessment of comparability of reasons for missingness requires the reasons to be reported. Bias would be introduced if, for example, the participants omitted from the analysis were those for whom 1 treatment is superior, leaving in the analysis only those in whom the treatments have the same effect. This is an instance of participants with missing data differing importantly between groups. It would be difficult to address this in an analysis – it would require strong assumptions about informative missingness.
3.3. If No/Probably no/No information to 3.1: is there evidence that results were robust to the presence of missing outcome data?	Evidence for robustness may come from how missing data were handled in the analysis and whether sensitivity analyses were performed by the trial investigators, or from additional analyses performed by the systematic reviewers. Use of last observation carried forward imputation may be particularly problematic if the observations being carried forward were made before carry‐over effects had disappeared. A common debate in analysis of a cross‐over trial is between having the patient effect as fixed or random. The former will automatically exclude (for an AB/BA design) all patients with missing data in either period. The latter will permit the recovery of inter‐patient information and can thus in theory lead to more precise inferences (although in practice the effect is small). Validity of either approach rests on an assumption of data being missing at random.

Contributions of authors

NHH: developed the protocol with suggestions from team members.

CN: commented on the protocol. CN will provide methodological oversight to standardise the review.

SV: commented on the protocol.

TTW: commented on the protocol. TTW will provide methodological oversight to standardise the review.

YP: proposed the idea for the review and commented on the protocol.

All authors agreed on the final version of the protocol.

Sources of support

Internal sources

• None, Other

External sources

• The Cochrane Hepato‐Biliary Group, Denmark

  Copenhagen Trial Unit, Centre for Clinical Intervention Research, Rigshospitalet, Copenhagen University Hospital.

Declarations of interest

NHH: none.

CN: none.

SV: none.

TTW: none.

YP: none.

New