Entecavir for children and adults with chronic hepatitis B

Objectives

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

To evaluate the benefits and harms of entecavir versus no treatment or placebo for chronic hepatitis B infection in children and adults with chronic hepatitis B infection, who are either HBeAg‐positive or HBeAg‐negative.

Background

Description of the condition

Hepatitis B virus (HBV) is a virus that affects the liver. Chronic hepatitis B is still a major, worldwide, public health concern, though effective vaccination and antiviral drugs have reduced the infection (McMahon 2005; WHO 2022). According to the World Health Organization (WHO) report, there were 296 million people infected with chronic hepatitis B in 2019, and the estimated number of new infections each year was 1.5 million (WHO 2022). Nearly 90% of people are unaware of their infection and 78% of diagnosed people do not receive treatment (Hutin 2018; WHO 2022). The prevalence of chronic hepatitis B varies widely amongst different regions. The African region had the highest hepatitis B surface antigen (HBsAg) seroprevalence (8.83%, 95% confidence interval (CI) 8.82% to 8.83%), followed by the Western Pacific region (5.26%, 95% CI 5.26% to 5.26%) (Schweitzer 2015). China does not have the highest prevalence (5.49%, 95% CI 5.47% to 5.50%) (Schweitzer 2015), but it has the largest population living with HBV, accounting for one‐third of chronic hepatitis B infections worldwide (Chen 2018; Wang 2017). Chronic hepatitis B can present as hepatitis B virus e antigen (HBeAg) positive or HBeAg negative. Based on one study from 2006, the proportion of HBeAg‐negative chronic hepatitis B was 72%, and it was particularly higher in people born in Europe, Middle East, and Africa (WHO 2015; Zarski 2006).

HBV is commonly spread through horizontal transmission (such as injectable drug abuse, transfusion of infected blood, unhygienic tattooing practices, and encountering blood infected with HBV), unprotected sex, and vertical or perinatal exposure (mother‐to‐child transmission) (Nelson 2011). Chronic hepatitis B caused more than 800,000 deaths in 2019; cirrhosis and hepatocellular carcinoma, related to chronic hepatitis B, were the leading cause of death (Marrero 2018; WHO 2022). HBV was responsible for 33% of liver cancer deaths in 2015 (Akinyemiju 2017; McGlynn 2021). One study from the US showed that adults with chronic hepatitis B had a two‐fold higher risk of death than uninfected adults (Zhou 2020).

Mother‐to‐child transmission is one of the most common routes of HBV transmission due to direct infection or long‐term close contact, which is the main cause of familial HBV infection (Obayashi 1972). Data from the WHO have shown that in the absence of any preventive interventions, the risk of mother‐to‐child transmission is between 70% and 90% for HBeAg‐positive mothers, and that the risk reduces to 10% and 40% for HBeAg‐negative mothers (WHO 2020). In general, approximately 90% of infected neonates and infants will develop chronic hepatitis B infection, which is much higher than 5% for infected adults (Indolfi 2019). The risk of cirrhosis and hepatocellular carcinoma in infected offspring is significantly increased (Sun 2014). 

Description of the intervention

The goal of chronic hepatitis B treatment is to permanently suppress HBV replication, reduce hepatic complications, and improve long‐term survival (Lok 2009). Antiviral therapy is regarded as conventional therapy for chronic hepatitis B, including interferon‐α (IFN‐α) therapy and nucleos(t)ide analogues therapy. Entecavir is one option of a nucleos(t)ide analogue antiviral therapy, which was approved for chronic hepatitis B treatment in 2005 in the US and in 2006 in Europe (Dimou 2007).

Entecavir has a high resistance barrier, and its cumulative genotypic resistance rate reaches only 1.2% after six years for nucleos(t)ide‐naïve people (Lok 2012). However, this number increases to 57% for people who are lamivudine‐refractory (Tenney 2009). Entecavir and tenofovir have equal effectiveness in HBeAg clearance (risk ratio (RR) 1.05, 95% CI 0.68 to 1.62) and HBeAg seroconversion (RR 0.93, 95% CI 0.54 to 1.61) for people with nucleos(t)ide analogue‐naive chronic hepatitis B (Chen 2019; Sriprayoon 2017). The safety of entecavir is comparable with lamivudine and most of its adverse reactions are of mild‐to‐moderate severity. The frequency of serious adverse events in people with chronic hepatitis B, with a mean exposure to entecavir of 75 weeks was 8% (27/354), and the rate of discontinuation due to adverse events was less than 1% (Chang 2006). In addition, entecavir was at a lower cost when compared with other drugs for chronic hepatitis B such as lamivudine and telbivudine (Ruggeri 2017; Wiens 2013), which is critical for equity and long‐term adherence to treatment measures. Entecavir and tenofovir were recommended as first‐line drugs for children with chronic hepatitis B, but only entecavir can be used for children aged two to 11 years (Terrault 2018). One randomised clinical trial demonstrated that the rates of HBeAg seroconversion and HBV DNA less than 50 IU/mL in the entecavir group were significantly higher than placebo after 48 weeks (Jonas 2016). Although lamivudine was approved for children aged two years or older, its risk of resistance is higher than entecavir.

How the intervention might work

Entecavir is phosphorylated to the active triphosphate form and has an intracellular half‐life of 15 hours. In healthy people, peak plasma concentrations of entecavir were reached within 0.5 to 1.5 hours and steady‐state was reached after 6 to 10 days of once‐daily dosing (Osborn 2011). The recommended dose of entecavir for adults with chronic hepatitis B infection is 0.5 mg daily; however, if that adult has decompensated cirrhosis or is refractory to lamivudine, a larger dose (1.0 mg daily) should be used (Terrault 2018).

Entecavir has potent antiviral activity in multiple long‐term clinical studies (Ridruejo 2011; Seto 2011; Zoutendijk 2011), with HBV‐DNA response rates of approximately 95% (Pol 2012). Entecavir can effectively inhibit HBV reverse transcriptase through three activities: base priming, reverse transcription of the negative strand DNA from the pregenomic messenger ribonucleic acid, and synthesis of the positive strand of HBV DNA (Seifer 1998). When using entecavir in people with nucleoside‐naïve chronic hepatitis B, its high genotypic resistance barrier made the resistance rare. Meanwhile, entecavir showed superior virological and biochemical benefits for the nucleoside‐naïve people. One global multicentre study showed, in the fifth year of entecavir therapy, 94% of HBeAg‐positive chronic hepatitis B people had HBV DNA less than 300 copies/mL and 80% reached normal alanine aminotransferase (ALT) levels (Chang 2010). Another study demonstrated that more than 90% of nucleos(t)ide analogues‐naïve Chinese chronic hepatitis B people achieved undetectable HBV DNA after two years of entecavir treatment (Luo 2013).

Why it is important to do this review

Entecavir is recommended as the first‐line drug for chronic hepatitis B in many clinical guidelines (EASL 2017; Terrault 2018; WHO 2015), but none of them have issued the recommendation based on the direct comparison of entecavir versus placebo/no treatment in a systematic review. The net effect of entecavir versus no treatment or placebo is still uncertain. Several randomised clinical trials on this topic are available (Jonas 2016; Tseng 2014). Therefore, we designed this review to address the benefits and harms of entecavir.

Objectives

To evaluate the benefits and harms of entecavir versus no treatment or placebo for chronic hepatitis B infection in children and adults with chronic hepatitis B infection, who are either HBeAg‐positive or HBeAg‐negative.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised clinical trials, with any trial design, which compare entecavir with no treatment or placebo in people with chronic hepatitis B, without restrictions to publication language, publication status and format, year of publication, and the outcomes reported. 

We will consider for inclusion trials with a subset of participants diagnosed with chronic hepatitis B (see Unit of analysis issues). 

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

Types of participants

We will include children and adults with chronic hepatitis B. In this review, we will define a child as aged less than 16 years, and an adult as aged 16 years or more. People with chronic active HBV infection may either be HBeAg‐positive or HBeAg‐negative, as defined in the European Association for the Study of the Liver (EASL) guideline from 2017 (EASL 2017).

• HBeAg‐positive means chronic hepatitis B‐HBsAg positivity for more than six months, serum HBeAg positivity, serum HBV‐DNA positivity with values ranging from 10⁴ IU/mL to 10⁷ IU/mL, persistent or intermittent elevation in levels of ALT, and liver biopsy shows moderate or severe necroinflammation, or any other definitions employed by the authors of the publications making it likely that the participants had chronic hepatitis B.

• HBeAg‐negative means chronic hepatitis B‐HBsAg positivity for more than six months, serum HBeAg negativity usually with detectable Hepatitis B e antibody, serum HBV‐DNA positivity with values greater than 2000 IU/mL (i.e. 10⁴ copies/mL), persistent or intermittent elevation in levels of ALT, and liver biopsy shows moderate or severe necroinflammation (EASL 2017). 

We will include trials with participants irrespective of whether they are treatment‐naïve or have previously been treated unsuccessfully for chronic HBV infection with another antiviral drug. We will include participants with evidence of other viral co‐infections such as HIV, hepatitis C virus (HCV), or hepatitis D virus (HDV). We will also accept any other definitions employed by the authors of the publications making it likely that the participants had chronic hepatitis B.

For trials that include only a subset of relevant participants, we will attempt to obtain individual data by contacting study authors. See Unit of analysis issues.

Types of interventions

Experimental intervention

• Entecavir (at any dose, frequency, or duration of administration)

Control intervention

• No treatment or placebo

We will allow co‐interventions in the experimental and control intervention groups provided that the co‐interventions are administered equally to all the intervention groups of a trial.

Types of outcome measures

We will analyse the following primary and secondary outcomes. We will include trials that meet our inclusion criteria, regardless of the outcomes they report. We will evaluate the outcomes at the longest follow‐up.

Primary outcomes

• All‐cause mortality.

• Health‐related quality of life (evaluated using a validated scale such as the 36‐Item Short Form Health Survey (SF‐36) or EuroQol five dimensions questionnaire (EQ‐5D) at maximal follow‐up). If a trial reported multiple health‐related quality of life measures, we plan to choose one in the following order: SF‐36, EQ‐5D, General Well‐Being Scale, Subjective Quality of Life Scale (SQOL), Perceived Quality of Life Scale (PQOL).

• Proportion of people with serious adverse events (a serious adverse event, defined according to the International Conference on Harmonisation (ICH) Guidelines for Good Clinical Practice (ICH‐GCP 2016), is any untoward medical occurrence that results in death, is life‐threatening, requires hospitalisation or prolongation of existing hospitalisation, results in persistent or significant disability or incapacity, or is a congenital anomaly/birth defect).

Secondary outcomes

• Mortality due to hepatitis B‐related liver disease (caused by morbidities or decompensation of the liver, such as liver cirrhosis or hepatocellular carcinoma).

• Proportion of people with non‐serious adverse events (defined as any untoward medical occurrence in a participant or clinical investigation participant that does not meet the above criteria for a serious adverse event).

• Proportion of people without histological improvement.

• Proportion of people with detectable HBsAg in serum or plasma.

• Proportion of people with detectable HBV‐DNA in serum or plasma.

• Proportion of people with detectable HBeAg in serum or plasma (this outcome is only relevant for HBeAg‐positive participants).

• Proportion of people without HBeAg seroconversion in serum or plasma (this outcome is only relevant for HBeAg‐positive participants).

• Proportion of people without normalisation of transaminases (i.e. biochemical response).

Search methods for identification of studies

To minimise bias in our search results, we have followed the guidance in Chapter 4 of the Cochrane Handbook for Systematic Reviews of Interventions (Lefebvre 2022a) and in PRISMA‐S (PRISMA-S Checklist; Rethlefsen 2021) to plan and describe the search process for the review.

Electronic searches

We will search the Cochrane Hepato‐Biliary Group Controlled Trials Register, which the Cochrane Hepato‐Biliary Group Information Specialist searches via the Cochrane Register of Studies Web. We will also search the Cochrane Central Register of Controlled Trials in the Cochrane Library, MEDLINE Ovid, Embase Ovid (Excerpta Medica Database), LILACS (Bireme), Science Citation Index Expanded, and Conference Proceedings Citation Index – Science. We will search the latter two simultaneously through the Web of Science.

Appendix 1 provides the search strategies for the respective databases, with the expected date range of the searches. We will provide the actual date of the electronic searches at the review stage.

Searching other resources

We will search online trial registries including ClinicalTrial.gov (clinicaltrials.gov/), WHO International Clinical Trial Registry Platform (www.who.int/ictrp), EU Clinical Trials Register (www.clinicaltrialsregister.eu/), the ISRCTN registry (www.isrctn.com/), European Medicines Agency (EMA; www.ema.europa.eu/ema/), Food and Drug Administration (FDA; www.fda.gov), and pharmaceutical company sources for ongoing or unpublished trials, and for study information. We will contact relevant individuals and organisations for information about unpublished or ongoing studies.

We will search for relevant grey literature sources such as reports, dissertations, theses, and conference abstracts (e.g. in Google Scholar).

We will use the PubMed/MEDLINE "similar articles search" tool on all included studies. We will manually check citations and reference lists of the included studies, and any relevant systematic reviews identified.

We will search for and examine any relevant retraction statements (through the Retraction Watch Database (retractionwatch.com/retraction-watch-database-user-guide/)) and errata for information as errata can reveal important limitations or even fatal flaws in included studies (Lefebvre 2022b).

We will contact authors of identified trials for additional published or unpublished trials.

We will provide the actual date of searching other sources at the review stage.

Data collection and analysis

Selection of studies

Four review authors (STX, YFM, QLS, and QQG) will independently screen the titles and abstracts of articles identified through the searches (described above) for potentially eligible studies using Covidence (www.covidence.org/). Two review authors (STX and YFM) will independently evaluate the full text of potentially relevant articles applying the specified inclusion criteria, and resolve any disagreements with another review author (JW). We will attempt to contact the study authors to request further details in case information from the trial is unclear or missing.

We will illustrate the study selection process in a PRISMA 2020 flow diagram (Page 2021a; Page 2021b), and list all studies excluded after full‐text assessment and their reasons for exclusion in a 'Characteristics of excluded studies' table.

For screening of non‐English language publications, we will use Google Translate to assist with eligibility assessment in the first instance (translate.google.com). If needed, we will seek translators to assist with assessing the eligibility of studies and, if eligible, assist with data extraction by native speakers.

During the selection of trials, we may also identify observational studies on the topic of our review (e.g. quasi‐randomised studies, cohort studies, or case reports). We will check these studies for reporting of adverse effects from the experimental intervention during the study period. If such is reported, then we will present our findings in a narrative format only, at the end of the 'Results' section. We will not meta‐analyse these data. We will not specifically search for observational studies for inclusion in this review, which is a limitation. We are aware that by not looking for all observational studies on adverse events, we allow the risks of putting more weight on potential benefits than on potential harms, and of overlooking uncommon and late adverse events (Storebø 2018).

Data extraction and management

Review authors (STX, YFM, QW, and MXL) will independently and in duplicate extract data from the included trials using a standardised data extraction form that has been piloted on two or more trials. This should ensure that all review authors understand the extraction items. We will extract data from non‐English studies after translation if the studies are included. Data from trials published in duplicate will be retained only once. We will resolve disagreements relating to data extraction through discussion with another review author (JW). We will extract the following data.

• Study details: first author, journal, country, year of publication, type of publication, correspondence information, trial registration, trial protocol.

• Methods: study design, number of potential participants screened, number of participants randomised, exclusions postrandomisation, length of treatment regimen, length of longest follow‐up, number of dropouts/losses to follow‐up/withdrawals/discontinuations from treatment and reasons given, study methods required to assess risk of bias and certainty of evidence

• Participant characteristics: country, setting, age, sex, inclusion and exclusion criteria, number of participants who were HBeAg‐positive and HBeAg‐negative, number of participants who were treatment naïve, number of participants with comorbidities including hepatitis C, and HIV/AIDS or decompensation of the liver (cirrhosis and hepatocellular carcinoma).

• Intervention details: dose, regimen, and duration of entecavir, control, and co‐intervention.

• Outcome data: for continuous data, we will extract the mean values, standard deviation, and number of participants for each treatment group at different time points; for binary data, we will extract information on the number of events and the number of participants assessed at that time point.

• Funding source, differences between planned outcomes (registration/protocol/methods) and measured outcomes, conflict of interest of the study authors.

Assessment of risk of bias in included studies

Review authors (QLS, QQG, QW, and NJY) will independently and in duplicate assess the risk of bias of each included trial using the Cochrane RoB 2 tool for randomised clinical trials (Sterne 2019), as outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022a). We will use the following RoB 2 domains of the tool in Excel (available from riskofbiasinfo.org):

• bias arising from the randomisation process; 

• bias due to deviations from intended interventions (effect of assignment to intervention); 

• bias due to missing outcome data; 

• bias in measurement of the outcome; 

• bias in selection of the reported result.

As we will assess the effect of assignment to the intervention, we will make the assessments using the intention‐to‐treat (ITT) principle. ITT includes all randomised participants, regardless of the interventions they actually received.

We will use the signalling questions in the RoB 2 tool, based on the five domains above, to assess each domain as 'low risk of bias', 'some concerns,' or 'high risk of bias' (Sterne 2019). We will resolve any disagreements in decisions by discussion with a fifth review author (LY). The response options for the signalling questions are:

• yes;

• probably yes;

• probably no;

• no;

• no information.

We will assess the risk of bias in cross‐over trials as in trials with parallel group design because we will use the data from the first period only (i.e. before cross‐over) (Higgins 2022b). 

When using RoB 2 for cluster‐randomised trials, we will assess one additional domain: bias arising from the timing of identification and recruitment of participants. We will follow the guidance at www.riskofbias.info/welcome/rob-2-0-tool/rob-2-for-cluster-randomized-trials. 

We will use the RoB 2 Excel tool (Sterne 2019). An algorithm, in Excel, maps the responses to the signalling questions per outcome, and proposes a risk of bias judgement for each domain.

We will use the overall risk of bias for a study result, rather than specific domains. The overall risk of bias for the result is the least favourable assessment across the domains of bias.

• Low risk of bias means that the study is judged at low risk of bias for all domains for this result.

• Some concerns mean that the study is judged to raise some concerns in at least one domain for this result, but not to be at high risk of bias for any domain.

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

We will use the Microsoft Excel tool available on www.riskofbias.info, and we will make it available online (we will provide details at the review stage).

Our risk of bias assessment will inform GRADE and a summary of findings table. We will present the outcomes of all‐cause mortality, health‐related quality of life, and proportion of people with serious adverse events in our summary of findings table as these outcomes are the most clinically relevant for clinicians and people with chronic hepatitis B. We will present the results of these outcomes at the maximum follow‐up time points, and we will provide the median follow‐up and the ranges.

Measures of treatment effect

We will refer to the guidance outlined in Chapters 9 and 10 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2022; McKenzie 2022a). We will calculate the risk ratio (RR) and 95% CIs for meta‐analysed estimates of the effect of dichotomous outcomes. We will calculate the mean difference (MD) and 95% CIs for meta‐analysed estimates of the effect of continuous outcomes measures, such as health‐related quality of life, when studies use the same scales. When studies use different scales, we will calculate the standardised mean difference (SMD) and 95% CIs. Calculations will be at the end of follow‐up. We will interpret SMDs 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 2022b). We will describe in a narrative format skewed data reported as medians and interquartile ranges as described in Section 10.5.3 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2022).

We will follow the guidance in Section 19.5.1 and 19.5.2 of the Cochrane Handbook for Systematic Reviews of Interventions, when we report on adverse events in the summary of findings tables (Peryer 2022).

Unit of analysis issues

The unit of analysis will be the participants randomised into the trials. We plan to include parallel randomised clinical trials, cluster randomised trials, and the first period of cross‐over trials in this review. We will follow the guidance of the Cochrane Handbook for Systematic Reviews of Interventions to avoid the 'unit of analysis' errors (Higgins 2022c). If we identify eligible cluster randomised trials (where schools, villages, medical practices, or families are the unit of analysis), we will combine their data with the data from the individually randomised trials in a meta‐analysis provided that the cluster effect estimate takes account of the potential clustering. If not, we will analyse the cluster‐randomised trials separately. We will consider the generic inverse‐variance approach to analyse the effect estimates and their standard errors from correct analyses of cluster‐randomised trials as stated in Chapter 23 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022b). 

Likewise, if we identify trials with two or more experimental groups and a common control group, we will separately compare each of the relevant experimental groups with the control group divided into the same number of groups if used within the same comparison to avoid unit of analysis issues such as double counting. For cross‐over randomised trials, we will include only data from the first period of the trial (i.e. before the cross‐over) to avoid carry‐over effects (Higgins 2022b). For trials with repeated observations of trial participants (e.g. multiple adverse events per participant), we will only use the data from the participant level for our analysis (e.g. the total number of participants with adverse events rather than the total number of adverse events). However, we will present a table with each type of adverse events separately. We will also try to find out the interdependence of the adverse events in a person when we extract the data for analysis of adverse events. We will provide all treatment groups in the 'Characteristics of included studies' table, even if they are not used in the review.

For a trial with mixed populations, we will include the trial if at least 80% of participants are eligible and their data are reported separately from the data of people of no interest to our review, or if we can obtain the separate data from the trial authors. We will explore the effect of this decision in a sensitivity analysis. We will exclude trials in which less than 80% of the population are of interest, and data for the subgroup of interest are not available as results from small trials may overestimate or underestimate intervention effects (McKenzie 2022b). 

Dealing with missing data

We plan to perform all analyses using the ITT method, that is, including all participants irrespective of compliance or follow‐up. We will contact corresponding authors of studies to verify key study characteristics and obtain missing outcome data in a trial. If we receive no reply within one month, and we cannot find the missing data in other publications on the same trial, we will consider the data unobtainable. Then, for analysis, we will use the data as provided in the trial publications.

We will include participants with incomplete or missing data in sensitivity analyses by imputing them according to the following scenarios (Gamble 2005; Hollis 1999).

• Extreme‐case analysis favouring the experimental intervention ('best‐worst' case scenario); none of the dropouts/participants lost from the experimental group, but all the dropouts/ participants lost from the control group 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 group, but none from the control group experienced the outcome, including all randomised participants in the denominator.

If the missing data are thought to introduce serious bias, we will explore the impact of including such trials in the overall assessment of results, by sensitivity analyses.

Assessment of heterogeneity

We will examine the overall characteristics of the trials, including participants, interventions, and design, to describe the clinical diversity and methodological variability in our review. We will assess their similarity and determine whether a meta‐analysis is appropriate. We will use forest plots of trial results to consider the size and direction of intervention effects. We will perform the Chi² test and calculate the I² statistic. We will use a P value of less than 0.10 to indicate significant statistical heterogeneity. We will quantify and measure heterogeneity amongst the trials in each analysis, using the I² statistic when the P value is less than 0.10. We will interpret heterogeneity as indicated in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2022):

• 0% to 40%: might not be important;

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

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

• 75% to 100%: considerable heterogeneity^a.

^aThe importance of the observed value of the I² statistic depends on the magnitude and direction of effects, and the strength of evidence for heterogeneity (e.g. P value from the Chi² test, or a CI for the I² statistic): uncertainty in the value of the I² statistic is substantial when the number of studies is small.

So, if there are few trials, uncertainty around I² statistic and Tau measurements is expected, and therefore, we will not use the simple thresholds to interpret statistical heterogeneity (Deeks 2022).

Assessment of reporting biases

If there are 10 or more trials in a meta‐analysis, we will undertake formal statistical tests to investigate funnel plot asymmetry following the recommendations in Chapter 13 of the Cochrane Handbook for Systematic Reviews of Interventions (Egger 1997; Page 2022). To evaluate potential publication bias and possible small‐study biases, we will create and visually examine the funnel plot of each primary outcome for evidence of asymmetry. Regarding reporting bias, we will also check trial protocols and information on trial registration against published reports to evaluate whether selective reporting of outcomes is present. We will contact trial authors to request missing outcome data. We plan to assess reporting bias due to missing outcome results on the following outcomes: all‐cause mortality, health‐related quality of life, and serious adverse events.

Data synthesis

We will use the Review Manager Web for analyses (RevMan Web 2022). Two review authors (XNH and XYD) will perform analyses according to the recommendations in Chapter 10 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2022).

We will not limit our primary analysis to trials at overall low risk of bias, but we will perform subgroup analyses comparing trials at low risk of bias to trials at some concern and to trials at high risk of bias to illustrate the effect of risk of bias on the compared interventions. We will also use sensitivity analyses presenting data only from trials at low risk of bias.

When the clinical characteristics of individual studies are sufficiently homogeneous, we will meta‐analyse the data, using the random‐effects model for our primary analysis, with 95% CI. For dichotomous outcomes, we will calculate the RR and the corresponding 95% CI; for continuous outcomes, we will calculate the MD/SMD and corresponding 95% CI. We will use the fixed‐effect model for sensitivity analyses (Deeks 2022). We plan to explore heterogeneity with subgroup analyses.

When the characteristics of the individual trials are too clinically heterogeneous to be combined, we will not perform the meta‐analysis. In such circumstances, we will present a narrative analysis of the eligible trials as outlined in Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (McKenzie 2022c), with a descriptive presentation of the results, grouped by intervention or outcome type, and reported by tables.

Subgroup analysis and investigation of heterogeneity

If the required number of studies for our review data are available, we will perform the following subgroup analyses for the primary outcomes.

• Trials at low risk of bias compared to trials at some concern and compared to trials at high risk of bias as trials at some concern and high risk of bias may overestimate or underestimate the intervention effects (Higgins 2022a) (see Data synthesis).

• Age of participants: children (less than 16 years) compared to adults (16 years or greater) as the clinical characteristics and disease course are different between the two groups of participants (EASL 2017), and the treatment may have different effects.

• Treatment‐naïve participants compared to those who had previous treatment with other antivirals as the resistance barrier of the treatment is different between the two groups of participants (Tenney 2009), and may have different effects.

• Follow‐up duration: less than one year compared to one year and longer as in people with chronic hepatitis B who discontinue nucleos(t)ide analogues, sustained off‐therapy virological response is defined as serum HBV DNA levels less than 2000 IU/mL for at least 12 months after the end of therapy (EASL 2017).

We will test the subgroup differences in Review Manager Web and will consider P less than 0.05 as a subgroup modification. When we observe a subgroup modification, we will assess the credibility of the subgroup effect by referring to the Instrument to assess the Credibility of Effect Modification Analyses (ICEMAN) (Schandelmaier 2020).

Sensitivity analysis

To assess the robustness of our conclusions and explore their impact on effect size, we will carry out the following sensitivity analyses for the primary outcomes.

• Restricting the analysis to trials at low risk of bias (see Data synthesis).

• Restricting the analysis to treatment‐naive participants.

• Restricting the analysis to no industry‐funded trials.

• Restricting the analysis to trial with no missing data (if the missing data are thought to introduce serious bias).

• Restricting the analysis to trials with no mixed populations (if we include trials with mixed populations in which at least 80% of participants are eligible).

• Conducting the analyses with fixed‐effect model.

• Conducting the analyses according to the 'best‐case' scenario (see Dealing with missing data).

• Conducting the analyses according to the 'worst‐case' scenario (see Dealing with missing data).

• Assessing imprecision with Trial Sequential Analysis (TSA) (see below).

Trial Sequential Analysis

We will apply TSA to control random errors in our meta‐analysis (Brok 2008; Brok 2009; Thorlund 2009; Thorlund 2010; Thorlund 2017; TSA 2017; Wetterslev 2008; Wetterslev 2009; Wetterslev 2017). We will calculate the required information size (i.e. the number of participants needed in a meta‐analysis to detect or reject a certain intervention effect) which should also consider the diversity observed in the meta‐analysis (Wetterslev 2008; Wetterslev 2009; Wetterslev 2017).

We will perform TSA only of our primary outcomes. We will calculate the required information size for dichotomous outcomes based on the event proportion in the control group of the included trials; assumption of an a priori RR of 10%; a risk of type I error of 2.5% (because of three primary outcomes), a risk of type II error of 10% (power 90%); and the observed diversity of the meta‐analysis (Wetterslev 2017). For the continuous outcome, health‐related quality of life, we will estimate the required information size based on the standard deviation observed in the control group of the meta‐analysis and a minimal relevant difference of 50% of this standard deviation, and the observed diversity in the trials in the meta‐analysis. We will use the random‐effects model.

We plan also to conduct a TSA using the RR in trials at low risk of bias, but if we find no such trials, this analysis will have to wait until such trials are identified. 

We will add the trials according to the year of publication. Based on the required information size, we will construct trial sequential monitoring boundaries (Thorlund 2017; Wetterslev 2008). These boundaries determine the statistical inference that one may draw regarding the cumulative meta‐analysis that has not reached the required information size. If the trial sequential monitoring boundary is crossed before the required information size is reached, firm evidence may be established, and further trials may be superfluous. In contrast, if the boundary is not surpassed, it is most likely necessary to continue conducting trials to detect or reject a certain intervention effect. This can be determined by assessing whether the cumulative Z‐curve crosses the trial sequential monitoring boundary for futility (Wetterslev 2008). We will conduct TSA using software from the Copenhagen Trial Unit (Thorlund 2017; TSA 2017).

We will report and compare the results with TSA as sensitivity analysis to imprecision assessed by GRADE. In TSA, we downgrade imprecision by two levels if the accrued number of participants is below 50% of the diversity‐adjusted required information size (DARIS), and one level if it is between 50% and 100% of DARIS. Furthermore, we do not downgrade if the cumulative Z‐curve crosses the monitoring boundaries for benefit, harm, or futility, or if DARIS is reached.

We will conduct TSA for our primary outcomes.

Stakeholder consultation and involvement

We will not involve people with chronic hepatitis B and other stakeholders in the design of this review. However, we will share the review findings with people with chronic hepatitis B.

Summary of findings and assessment of the certainty of the evidence

We will use the GRADE approach and the GRADEpro GDT software to assess the overall certainty of the evidence (GRADEpro GDT). We will use the methods and recommendations described in Section 8.5 and 8.7, and Chapters 13, 14, and 15 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022a; Page 2022; Schünemann 2022a; Schünemann 2022b). We will create a summary of findings table for the comparison of entecavir versus no intervention or placebo, and we will present the meta‐analysed outcome results at the longest follow‐up: all‐cause mortality, health‐related quality of life, and proportion of people with serious adverse events. After each outcome, we will provide the longest follow‐up, median or mean, and the range of follow‐up.

GRADE uses five factors for assessing the certainty of evidence, that is, risk of bias (i.e. overall RoB 2 judgement), heterogeneity, imprecision (we will calculate the optimal information size), indirectness, and publication bias. 

Regarding 'risk of bias', we will use the overall judgement for an outcome result. 'Low' risk of bias will indicate 'no limitation (the certainty will not be downgraded)'; 'some concerns' will indicate either 'no limitation' or 'serious limitation' (the certainty will be downgraded one level); and 'high' risk of bias will indicate either 'serious limitation' or 'very serious limitation' (the certainty will be downgraded two levels). 

Based on defined criteria for risk of bias, inconsistency, indirectness of evidence, imprecision, and publication bias, we will downgrade the evidence by one level for serious, or two levels for very serious limitations.

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 incorporate the GRADE judgements about the certainty of the evidence in our reporting of the results.

The levels of evidence are defined as 'high', 'moderate', 'low,' or 'very low.' 

• 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.

Two review authors (MXL and LY), working independently, will assess the certainty of the evidence. These same review authors will resolve disagreements by discussion, or if needed, they will involve a third review author (JW).

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	Date range	Search strategy
The Cochrane Hepato‐Biliary Group Controlled Trials Register (via the Cochrane Register of Studies Web)	Date of search will be given at review stage	(entecavir or baraclude) and (chronic and (hepatitis b or hep b or hbv))
Cochrane Central Register of Controlled Trials in the Cochrane Library	Latest issue	#1 (entecavir or baraclude) #2 MeSH descriptor: [Hepatitis B, Chronic] explode all trees #3 (chronic and (hepatitis b or hep b or hbv)) #4 #2 or #3 #5 #1 and #4
MEDLINE (Ovid)	1946 to date of search	1. (entecavir or baraclude).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] 2. exp Hepatitis B, Chronic/ 3. (chronic and (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] 4. 2 or 3 5. 1 and 4 6. (randomized controlled trial or controlled clinical trial or retracted publication or retraction of publication).pt. 7. clinical trials as topic.sh. 8. (random* or placebo*).ab. or trial.ti. 9. 6 or 7 or 8 10. exp animals/ not humans.sh. 11. 9 not 10 12. 5 and 11
Embase (Ovid)	1974 to date of search	1. exp entecavir/ 2. (entecavir or baraclude).mp. [mp=title, abstract, heading word, drug trade name, original title, device manufacturer, drug manufacturer, device trade name, keyword heading word, floating subheading word, candidate term word] 3. 1 or 2 4. exp chronic hepatitis B/ 5. (chronic and (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 heading word, floating subheading word, candidate term word] 6. 4 or 5 7. 3 and 6 8. Randomized controlled trial/ or Controlled clinical study/ or randomization/ or intermethod comparison/ or double blind procedure/ or human experiment/ or retracted article/ 9. (random$ or placebo or parallel group$1 or crossover or cross over or assigned or allocated or volunteer or volunteers).ti,ab. 10. (compare or compared or comparison or trial).ti. 11. ((evaluated or evaluate or evaluating or assessed or assess) and (compare or compared or comparing or comparison)).ab. 12. (open adj label).ti,ab. 13. ((double or single or doubly or singly) adj (blind or blinded or blindly)).ti,ab. 14. ((assign$ or match or matched or allocation) adj5 (alternate or group$1 or intervention$1 or patient$1 or subject$1 or participant$1)).ti,ab. 15. (controlled adj7 (study or design or trial)).ti,ab. 16. (erratum or tombstone).pt. or yes.ne. 17. or/8‐16 18. (random$ adj sampl$ adj7 ('cross section$' or questionnaire$ or survey$ or database$1)).ti,ab. not (comparative study/ or controlled study/ or randomi?ed controlled.ti,ab. or randomly assigned.ti,ab.) 19. Cross‐sectional study/ not (randomized controlled trial/ or controlled clinical study/ or controlled study/ or randomi?ed controlled.ti,ab. or control group$1.ti,ab.) 20. (((case adj control$) and random$) not randomi?ed controlled).ti,ab. 21. (Systematic review not (trial or study)).ti. 22. (nonrandom$ not random$).ti,ab. 23. 'Random field$'.ti,ab. 24. (random cluster adj3 sampl$).ti,ab. 25. (review.ab. and review.pt.) not trial.ti. 26. 'we searched'.ab. and (review.ti. or review.pt.) 27. 'update review'.ab. 28. (databases adj4 searched).ab. 29. (rat or rats or mouse or mice or swine or porcine or murine or sheep or lambs or pigs or piglets or rabbit or rabbits or cat or cats or dog or dogs or cattle or bovine or monkey or monkeys or trout or marmoset$1).ti. and animal experiment/ 30. Animal experiment/ not (human experiment/ or human/) 31. or/18‐30 32. 17 not 31 33. 7 and 32
LILACS (Bireme)	1982 to date of search	entecavir or baraclude [Words] and chronic and (hepatitis b or hep b or hbv) [Words]
Science Citation Index Expanded (Web of Science)	1900 to date of search	#5 #3 AND #4 #4 TI=(random* or blind* or placebo* or meta‐analys* or trial*) OR TS=(random* or blind* or placebo* or meta‐analys*) #3 #2 AND #1 #2 TS=(chronic and (hepatitis b or hep b or hbv)) #1 TS=(entecavir or baraclude)
Conference Proceedings Citation Index – Science (Web of Science)	1990 to date of search	#5 #3 AND #4 #4 TI=(random* or blind* or placebo* or meta‐analys* or trial*) OR TS=(random* or blind* or placebo* or meta‐analys*) #3 #2 AND #1 #2 TS=(chronic and (hepatitis b or hep b or hbv)) #1 TS=(entecavir or baraclude)

 

Contributions of authors

JW, STX, and YFM: drafted the protocol.

QW, MXL, and LY: revised the protocol.

QLS and QQG: developed and run the search strategy.

XNH, XYD, and NJY: commented on the protocol.

JW: initiated the review.

All authors agreed to this final version of the protocol.

Sources of support

Internal sources

• No sources of support provided

External sources

• Cochrane Hepato‐Biliary Group, Copenhagen Trial Unit, Centre for Clinical Intervention Research, Capital Region, Rigshospitalet, Copenhagen University Hospital, Copenhagen, Denmark

  Help with protocol preparation

Declarations of interest

JW: none.

STX: none.

YFM: none.

XNH: none.

XYD: none.

QLS: none.

QQG: none.

QW: none.

MXL: none.

NJY: none.

LY: none.

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