Types of studies

We will include randomised clinical trials (i.e., studies in which participants were allocated to entecavir or placebo arms at random) and non‐randomised controlled trials (i.e., studies that allocated participants to treatment arms by a non‐random methods such as alternation between groups and the use of birth dates or weekdays).

Types of participants

We will include participants (children or adults) with chronic active HBV infection. For the purpose of this review we will define a child as aged 15 years or less, and an adult as aged 16 years or older. Individuals with chronic active HBV infection may be either HBeAg‐positive or HBeAg‐negative, defined as follows (EASL 2009; Lok 2009; APASL 2012).

• HBeAg‐positive chronic hepatitis B infection ‐ HBsAg positivity for more than six months, serum HBV‐DNA positivity more than 20,000 IU/mL (i.e., 10⁵ copies/mL), persistent or intermittent elevation in levels of aspartate aminotransferase (AST) or ALT, and liver biopsy findings showing chronic hepatitis B with 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 chronic hepatitis B infection ‐ HBsAg positivity for more than six months, serum HBV‐DNA positivity with values ranging from 2000 to 20,000 IU/mL (i.e., 10⁴ to 10⁵ copies/mL), persistent or intermittent elevation in levels of AST or ALT, and liver biopsy findings showing chronic hepatitis B with 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.

Participants will be included 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 concomitant human immunodeficiency virus (HIV), hepatitis C virus (HCV), or hepatitis D virus infection, or hepatocellular carcinoma or other liver‐related comorbidities, but we will analyse participants with and without these conditions as separate subgroups. We will also include participants who have undergone prior liver transplantation or those with concomitant renal failure, but again we will analyse them separately.

Types of interventions

The intervention is this review will be entecavir and the comparison (control) will be placebo or no intervention.

We will include studies in which cointerventions to entecavir are administered, provided such cointerventions are administered equally to both the intervention and control groups.

Types of outcome measures

Electronic searches

We will search the Cochrane Hepato‐Biliary Group Controlled Trials Register (Gluud 2014), the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, EMBASE, Science Citation Index EXPANDED, and LILACS (Royle 2003). We will also search the World Health Organization International Clinical Trials Registry Platform (www.who.int/ictrp) for ongoing studies. We provide the preliminary search strategies in Appendix 1, together with the expected time spans of the searches. We will improve the  searches at the review stage, if necessary.

Searching other resources

We will identify further trials by screening the reference lists of eligible studies and relevant review articles. We will write to the principal authors of the identified randomised trials and to researchers active in the field to enquire about additional randomised trials they might know of. In order to obtain details of unpublished trials, we will contact pharmaceutical companies who are involved in the production and assessment of entecavir.

Selection of studies

Two authors (MHI and JDRC) will independently screen the titles and abstracts of papers identified through the search strategy (described above) for potentially eligible studies. We will retrieve full texts of potentially eligible studies for further assessment, and the two authors will independently apply the inclusion criteria to these publications. Disagreements between the two authors with regard to both the screening and full‐text assessment will be resolved through discussion and consensus. CSW and MJK will serve as arbitrators to resolve disagreements that MHI and JDRC are unable to resolve through discussion and consensus. We will present reasons for excluding studies in a 'Characteristics of excluded studies' table.

Data extraction and management

We will record relevant baseline and outcome data in data collection forms designed for this aim. We will extract outcome data at the end of the treatment and at the longest follow‐up reported. MHI and JDRC will independently extract data from the trials, after which they will compare the extracted data. Any differences in opinion will be resolved by discussion and consensus, failing which CSW and MJK will arbitrate. We will contact trial authors in order to clarify or obtain any information that is lacking or not clearly described in the published trials.

We provide the data that we will need to extract in order to perform a review in Table 1. In particular, we will extract the following participant, intervention, and outcome data.

Participants

Sex, ethnic origin, forms of transmission, previous antiviral treatment, presence of cirrhosis at randomisation, criteria used to classify chronic hepatitis, HIV, and HCV coinfections, infection with HBV mutants, number of participants randomised, and reasons for withdrawal from the trial.

Interventions

Intervention in the experimental and control groups, dosage and duration of therapy, method of administration, and any cointerventions.

Outcomes

For both HBeAg‐positive and HBeAg‐negative participants, we will extract the following data from each intervention group:
1. number of deaths;
2. number of participants without clinical events (e.g., compensated cirrhosis, decompensated cirrhosis, hepatocellular carcinoma);
3. number without disappearance of serum HBV‐DNA or a decrease in HBV‐DNA level below 100,000 copies/mL (lack of end of treatment virological response) at the end of treatment;
4. number without return of liver enzyme levels to normal range (lack of end of treatment biochemical response);
5. number without disappearance of HBV‐DNA or a decrease in HBV‐DNA level below 100,000 copies/mL with maintenance of this status for at least six months after discontinuation of drug (lack of sustained virological response);
6. number without liver histological improvement;
7. number with serious adverse events;
8. number with non‐serious adverse events;
9. number with development of viral resistance to the drug.

For HBeAg‐positive participants only, we will extract the following data from each intervention group:
1. number without disappearance of HBeAg in the serum (HBeAg positivity);
2. proportion without seroconversion from HBeAg‐positive status to antiHBeAg‐positive status (lack of seroconversion).

Assessment of risk of bias in included studies

According to empirical evidence (Schultz 1995; Moher 1998; Kjaergard 2001; Wood 2008; Lundh 2012; Savovic 2012a; Savovic 2012b), risk of bias in a trial can be assessed using the following 'Risk of bias' domains.

Generation of the allocation sequence

• Low risk of bias: the sequence generation was achieved using computer random number generation or a random number table. Drawing lots, tossing a coin, shuffling cards, and throwing dice are adequate if performed by an independent adjudicator

• Unclear risk of bias: the trial was described as randomised but the method of sequence generation was not specified

• High risk of bias: the sequence generation method was not, or may not have been, random; for example, treatment allocation using dates of birth, names, or admission numbers in order to allocate participants are inadequate and will be excluded for the assessment of benefits but not for harms

Allocation concealment

• Low risk of bias: allocation was controlled by a central and independent randomisation unit, opaque and sealed envelopes or similar, so that intervention allocations could not have been foreseen in advance of, or during, enrolment

• Unclear risk of bias: the trial was described as randomised but the method used to conceal the allocation was not described, so that intervention allocations may have been foreseen in advance of, or during, enrolment

• High risk of bias: the allocation sequence was known to the investigators who assigned participants or if the study was quasi‐randomised

Blinding of participants and personnel

• Low risk of bias: it was mentioned that both the participants and the personnel providing the interventions were blinded, and the method of blinding was described, so that knowledge of allocation was prevented during the trial

• Unclear risk of bias: it was not mentioned if the trial was blinded, or the trial was described as blinded, but the method or extent of blinding was not described, so that knowledge of allocation was possible during the trial

• High risk of bias: the trial was not blinded, so that the allocation was known during the trial

Blinded outcome assessment

• Low risk of bias: outcome assessment was carried out blinded for all relevant outcomes, and the method of blinding was described, so that knowledge of allocation was prevented

• Unclear risk of bias: blinding of outcome assessment was not described, or the outcome assessment was described as blinded, but the method of blinding was not described, so that knowledge of allocation was possible

• High risk of bias: outcome assessment was not blinded, so that the allocation was known to outcome assessors

Incomplete outcome data

• Low risk of bias: the numbers and reasons for dropouts and withdrawals in all intervention groups were described and judged to be similar, or it was specified that there were no dropouts or withdrawals

• Unclear risk of bias: the report gave the impression that there had been no dropouts or withdrawals, but this was not specifically stated; or it was not possible to determine if the reasons for dropouts or withdrawals were similar

• High risk of bias: the number or reasons for dropouts and withdrawals were not described; or there were important differences in the reasons for dropouts or withdrawals between the comparison groups

We will also record whether the investigators performed sample‐size calculations before the trial and used intention‐to‐treat analysis in the results they reported.

Selective outcome reporting

• Low risk: all pre‐defined, or clinically relevant and reasonably expected, outcomes are reported on. If the original trial protocol is available, the outcomes should be those called for in that protocol. (Note: If the trial protocol is obtained from a trial registry (e.g., www.clinicaltrials.gov), the outcomes to be sought are those enumerated in the original protocol if the trial protocol was registered before or at the time that the trial was begun; if the trial protocol was registered after the trial was begun, those outcomes will not be considered to be reliable in representing the outcomes initially being sought.) If the trial protocol is not available (or if the protocol was registered after the trial was begun), the review authors will decide, when they are writing the protocol for the systematic review, what clinically relevant and reasonably expected outcomes would be and will explicitly state those outcomes in the pertinent methodology part of their protocol for the systematic review.

• Unclear risk: not all pre‐defined, or clinically relevant and reasonably expected, outcomes are reported fully, or it is unclear whether data on these outcomes were recorded or not.

• High risk: one or more predefined or clinically relevant and reasonably expected outcomes were not reported, despite the fact that data on these outcomes should have been likely to have been available and even recorded.

For‐profit bias

• Low risk of bias: the trial appears to be free of industry sponsorship or other type of for‐profit support that may manipulate the trial design, conduct, or results

• Unclear risk of bias: the trial may or may not be free of for‐profit bias as no information on clinical trial support or sponsorship was provided

• High risk of bias: the trial was sponsored by industry or has received other type of for‐profit support

Other biases

• Low risk of bias: the trial appears to be free of other components that could put it at risk of bias

• Unclear risk of bias: the trial may or may not be free of other components that could put it at risk of bias

• High risk of bias: there are other factors in the trial that could put it at risk of bias

We will consider trials assessed as having a low risk of bias in all of the above‐specified individual domains as trials having a low risk of bias. We will consider trials assessed as having an unclear risk of bias or a high risk of bias in one or more of the above‐specified individual domains as trials having a high risk of bias.

If disagreements occur between the two authors (MHI and JDRC) in their evaluation of risk of bias, we will resolve them by discussion and consensus, failing which CSW and MJK will arbitrate.

Measures of treatment effect

We will use the software package Review Manager 5 provided by The Cochrane Collaboration (RevMan 2012).

Dichotomous data
The effect measures of choice are the risk ratio or risk difference or both, and the number needed to treat (NNT) for an additional beneficial outcome, with 95% confidence intervals (CIs), using both fixed‐effect and random‐effects meta‐analysis models. Calculations of the risk ratio will not include trials in which no events are reported, whereas calculations of the risk difference will. Hence, if the conclusions reached at differ due to the inclusion of trials reporting zero events, we plan to report the results of both effect measures. P values for all trials will be calculated based on the Mantel‐Haenszel method. Review Manager 5 software automatically adds 0.5 to each cell of the 2 x 2 table for any study with zero events (i.e., no events in any one study group) (RevMan 2012), so problems with the computation of estimates and standard errors will be eliminated. Mantel‐Haenszel methods have better statistical properties when there are few events.

Continuous data
We will present the results as mean differences (MDs), with 95% CIs, using both fixed‐effect and random‐effects models, using generic inverse variance. When pooling data across trials, we will estimate the MDs if outcomes are measured in the same way between trials. We will use the standardised mean difference (SMD) to combine trials that measure the same outcome but use different methods. If there is only one trial that provides data on an outcome specified in the protocol, meta‐analyses will not be possible, and we will report and discuss this in the review.

Time‐to‐event data
We will analyse time‐to‐event data as dichotomous data using a fixed time point, so that the proportion of participants who have incurred the event before the time point will be known for both groups. We will then construct a 2 x 2 table, and we will express treatment effects as risk ratios and risk differences. When the overall results are statistically significant by both fixed‐ and random‐effects models, we will calculate the relative risk reduction (RRR) and NNT, or the number needed to treat for an additional harmful outcome (NNH).

Unit of analysis issues

The unit of analysis will be the participants recruited into the trials. We will include in meta‐analyses, simple parallel randomised clinical trials as well as cluster‐randomised trials and cross‐over trials. We will identify any cluster‐randomised trials included in the review, but we will not combine these with individually randomised trials in the same meta‐analysis (i.e., they will be analysed separately). We will meta‐analyse effect estimates and their standard errors from correct analyses of cluster‐randomised trials using the generic inverse‐variance method in Review Manager 5 (RevMan 2012). We will take care to avoid 'unit of analysis' errors when analysing these types of trials (Higgins 2011).

The cross‐over trial is not a suitable method for investigating the condition and intervention of interest in this review because the intervention (i.e., entecavir) could have a lasting effect that compromises entry to subsequent periods of the trial. In the presence of carry‐over, we will include only data from the first period of a cross‐over trial in the meta‐analysis. The first period of a cross‐over trial is in fact a parallel‐group comparison. So, for cross‐over studies, we will follow the guidelines in the Cochrane Handbook for Systematic Reviews of Interventions on how to deal with data from cross‐over studies (Higgins 2011).

We will also perform a sensitivity analysis including only simple parallel randomised clinical trials in the meta‐analysis.

Dealing with missing data

We will contact study authors for relevant missing data. We will perform all analyses according to the intention‐to‐treat method, including all participants irrespective of compliance or follow‐up. Regarding the four primary outcomes, we will include participants with incomplete or missing data in the sensitivity analyses by imputing them according to the following two extreme scenarios (Hollis 1999; Gluud 2014).

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

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

Assessment of heterogeneity

We will formally test for statistical heterogeneity using the Chi² test for statistical homogeneity, with a P value < 0.1 set as the cut‐off. The impact of any statistical heterogeneity will be quantified using the I² statistic (Higgins 2011).

We will interpret the I² value as:

• 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.

Assessment of reporting biases

We will assess publication bias by looking for funnel plot asymmetry if we include at least 10 trials in a meta‐analysis (Egger 1997).

Data synthesis

Meta‐analysis

We will perform meta‐analyses according to the recommendations of The Cochrane Collaboration (Higgins 2011). We will perform the analyses using Review Manager software (RevMan 2012). We will attempt to analyse the data using the intention‐to‐treat principle where possible, assigning participants with missing data as treatment failures. In the case of histological responses, each trial will be analysed separately as a few participants may have undergone post‐treatment liver biopsies in trials of antiviral therapy. Binary outcomes will be expressed as risk ratios and 95% CIs. We will meta‐analyse the data using both fixed‐ and random‐effects models to ensure the robustness of the results. The NNT or NNH will be calculated if the results from both fixed‐ and random‐effects models are statistically significant (DerSimonian 1986; DeMets 1987). In case of discrepancy between the results of the two models, we will present the results using both methods. If there is no statistically significant difference between the results, then we will present the results for the fixed‐effect model. If the data are not available for meta‐analyses or if meta‐analyses are considered an inappropriate tool for the included trials, we will attempt to present the data of such outcomes in a descriptive way. For the purposes of the analyses and the forest plots (Lewis 2001), the experimental group will be that which received entecavir (or entecavir at a higher dose or for a longer duration) and the control group will be that which received placebo or no intervention (or entecavir at a lower dose or for a shorter duration).

Trial sequential analysis
Trial sequential analysis (TSA) (CTU 2011; Thorlund 2011a) is a tool for quantifying the statistical reliability of data in cumulative meta‐analysis, adjusting P values for sparse and repetitive testing on accumulating data (Brok 2008; Wetterslev 2008; Brok 2009; Thorlund 2009; Wetterslev 2009; Thorlund 2010;Thorlund 2011a; Thorlund 2011b). TSA is a methodology that combines an information size calculation (cumulated sample sizes of included trials) with the threshold of statistic significance.

We will perform TSA on the data from all trials. We plan to analyse all outcomes using TSA, irrespective of whether they yield a statistically significant result in the meta‐analysis. The meta‐analytic estimate of the control event proportions of the trials with a low risk of bias will be used as the control event proportion in the TSA. We will use the intervention effect estimated in the meta‐analysis using all trials and using an a priori intervention effect of a 20% risk ratio reduction.

For each TSA performed, we will calculate the heterogeneity‐adjusted required information size based on the intervention effect suggested by the trials (LBHIS) and an a priori intervention effect of a 20% risk ratio reduction, a risk of type I error of 5%, and a risk of type II error of 20%. The heterogeneity adjustment will be performed using the observed heterogeneity adjustment factor (1/(1 ‐ I²) using the heterogeneity estimated (I² statistic) among all trials and with an a priori assumed final heterogeneity of 50% (Wetterslev 2009). For the primary outcomes only we will perform separate TSA analyses using a risk of type I error of 5%, with a risk of type II error of 20%, as well as analyses using a risk of type I error of 1% and with a risk of type II error of 10%.

If the number of trials permit, we will perform TSA on trials with a low risk of bias only.

Subgroup analysis and investigation of heterogeneity

If the necessary data are available, we will perform the following subgroup analyses:

• trials with low risk of bias compared to trials with high risk of bias;

• age of participants: children (≤ 15 years) compared to adults (≥ 16 years);

• HBeAg‐positive compared to HBeAg‐negative participants;

• participants with cirrhosis compared to those without cirrhosis;

• treatment‐naïve participants compared to those who relapsed after previous treatment or were non‐responders to other antiviral drugs;

• total dose of entecavir: low dose compared with high dose;

• genotypes of HBV;

• participants coinfected with HIV, HCV, or hepatitis D virus, or with concomitant hepatocellular carcinoma or other liver‐related comorbidities at entry compared with those without coinfection or comorbidities;

• trials without losses to follow‐up compared with trials with losses to follow‐up;

• follow‐up at the end of treatment compared with follow‐up at six months or more than six months after the end of treatment;

• trials published as full paper articles compared with trials published as abstracts only.

We will use the test for interaction (Altman 2003) to assess whether the intervention effects in subgroup analyses are statistically significantly different from each other. We will consider P values ≤ 0.05 to indicate a statistically significant interaction, or difference, of the intervention effects between subgroups.

Sensitivity analysis

We will assess the effect of risk of bias (excluding from the meta‐analyses the trials with a high risk of bias) and losses to follow up ('best‐worst' and 'worst‐best' case scenario analyses, as already described in 'Dealing with missing data') on the robustness of the results.