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.

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.

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).

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.