Tenofovir versus 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 tenofovir versus entecavir in children and adults with chronic hepatitis B.

Background

Description of the condition

Hepatitis B is a liver infection caused by hepatitis B virus (HBV) (WHO 2022). Chronic hepatitis B is a major, worldwide, public health concern because it can significantly increase the risk of developing cirrhosis and liver cancer (McMahon 2005). According to the World Health Organization (WHO), it was estimated that 296 million people were living with chronic hepatitis B in 2019, with 1.5 million new infections each year (Hutin 2018; WHO 2022). One study indicated that adults with chronic hepatitis B had a nearly two‐fold higher risk of death than uninfected adults in the US (Zhou 2020). In 2019, chronic hepatitis B caused more than 800,000 deaths, mostly due to cirrhosis and hepatocellular carcinoma (WHO 2022). The prevalence of chronic hepatitis B varies greatly, from about 0.35% in the US (Lim 2020) to 5.2% in China (Wang 2017).

Most people with chronic hepatitis B are asymptomatic. Nearly 90% of people are unaware of their infection, and 78% of those diagnosed were not receiving treatment (Hutin 2018; WHO 2022). Liver failure and liver cancer are expected to develop in 15% to 40% of untreated people with chronic HBV infection (Tang 2018). Chronic hepatitis B is a common cause of cirrhosis and hepatocellular carcinoma; it was estimated that between 2003 and 2020, 84% of hepatocellular carcinomas in China were due to chronic hepatitis B (Lin 2022).

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). Mother‐to‐child transmission is one of the most common routes of HBV transmission, which can occur antenatally during pregnancy, natally during labour, or postnatally through close contact such as in breastfeeding (WHO 2022). The risk of progression to chronic HBV infection decreases with age, and it is 80% to 90% amongst those with HBV infection during infancy, 30% amongst those with HBV infection before the age of six years, and 1% to 12% amongst those infected with HBV as an older child (i.e. at least 14 years old) or adult (Schillie 2018).

Description of the intervention

People infected with HBV should be evaluated for the risk of disease progression to determine whether to start treatment based on a comprehensive assessment of serum HBV‐DNA levels; alanine aminotransferase (ALT) levels; the severity of liver disease; as well as their age, family history, and concomitant diseases (EASL 2017; Wang 2021). According to a WHO report, about 12% to 25% of people with chronic hepatitis B would have required treatment in 2021, depending on setting and eligibility criteria (WHO 2022). Treatment can achieve sustained suppression of HBV replication without the development of antiviral resistance, slow the progression of cirrhosis, reduce the incidence of liver cancer, and improve long‐term survival (Lok 2009). Currently, there are two major treatment options for chronic hepatitis B: pegylated interferon‐alpha (PegIFNα) and nucleos(t)ide analogues (EASL 2017; Terrault 2018). The use of PegIFNα is constrained by its significant response variability and negative safety profile (EASL 2017). To achieve safe, long‐lasting, and effective antiviral suppression in people with chronic hepatitis B, treatment with nucleos(t)ide analogues may be preferable to PegIFNα (Santantonio 2014; Terrault 2018). Tenofovir and entecavir were categorised as nucleos(t)ide analogues with a strong barrier against HBV resistance while lamivudine, adefovir dipivoxil, and telbivudine constitute a class of nucleos(t)ide analogues with a low barrier against HBV resistance (EASL 2017).

Tenofovir is available in two forms: the older tenofovir disoproxil fumarate (TDF) and the newer tenofovir alafenamide (TAF). TDF was approved in 2008 by the US Food and Drug Administration for treatment of adult HBV infection (Jenh 2009). TAF was approved in 2015 in the US and EU (De Clercq 2016). TAF is a novel prodrug formulated to deliver the active metabolite to target cells more efficiently than TDF at a lower dose, thereby reducing systemic exposure (De Clercq 2016).

Entecavir was approved for treatment‐naïve and lamivudine‐resistant chronic hepatitis B in the US in 2005 and in Europe in 2006 (Dimou 2007). Because of its high genotypic resistance barrier, resistance is uncommon when used in treatment‐naïve chronic hepatitis B. Entecavir demonstrated superior histological, virological, and biochemical benefits in people with nucleoside‐naïve chronic hepatitis B, and it is most promising for long‐term treatment (Dimou 2007).

The WHO recommends oral TDF, TAF, and entecavir as the most potent drugs to suppress HBV (WHO 2022), and these three drugs were also recommended as the first‐line drugs in some clinical guidelines for chronic hepatitis B (EASL 2017; Marrero 2018; WHO 2015). An increasing number of studies have demonstrated that tenofovir and entecavir have potent antiviral activity and high resistance barriers (Kao 2021). For example, one study found continuous treatment with entecavir over four years in nucleos(t)ide analogue‐naïve chronic hepatitis B individuals resulted in a 96% likelihood of undetectable HBV DNA and only a 0.4% probability of developing entecavir‐resistant mutations (Ono 2012). Several studies showed that long‐term treatment with TDF demonstrated sustained viral suppression without the development of resistance for up to five to seven years, and there were no new safety concerns with TDF identified in Caucasian or Asian people with chronic hepatitis B (Buti 2015; Liang 2019; Marcellin 2008). TAF treatment for 96 weeks remained as effective as TDF, with continued improved kidney and bone safety, and no substitutions associated with resistance to TAF or TDF were detected (Cathcart 2018).

Additionally, tenofovir and entecavir were at a lower cost when compared with other drugs for chronic hepatitis B, such as lamivudine and telbivudine, which is critical for equity and long‐term adherence to treatment measures (Ruggeri 2017; You 2008).

How the intervention might work

Tenofovir is a nucleotide reverse transcriptase inhibitor which is activated by bidirectional phosphorylation and inhibits the HBV polymerase by direct binding competition with the natural deoxyribonucleotide substrate (deoxyadenosine 5’‐triphosphate) and after integration into the DNA chain (Buti 2021; Chien 2022; Marcellin 2013). Once tenofovir is incorporated into the chain, it induces a chain termination which inhibits viral replication (Jenh 2009). Although tenofovir does not cure hepatitis B, it could effectively suppress the replication of hepatitis B and slow the speed of development of severe liver diseases, such as cirrhosis and liver cancer (Marcellin 2013).

Both TDF and TAF are prodrugs of tenofovir. After oral absorption, the majority of TDF is rapidly converted to tenofovir in the plasma, and then intracellularly to the active tenofovir diphosphate (Wassner 2020). In contrast, TAF could remain stable within the plasma and is only converted intracellularly to tenofovir. It is reported that TAF is associated with lower risks of bone and kidney adverse events compared with TDF (Hill 2018; Sax 2015). The usual dosing of TDF for adults is 300 mg once daily and can be taken with or without food, and the recommended dosage of TAF is 25 mg once daily, to be taken orally with food (Charlton 2020).

Entecavir is a cyclopentyl guanosine nucleoside analogue that has selective activity against the HBV polymerase (Seifer 1998). It is effectively phosphorylated by host cellular kinases to become its active triphosphate form. Entecavir inhibits HBV replication at three crucial stages: 1. HBV polymerase priming, 2. reverse transcription of the negative strand from the pregenomic messenger ribonucleic acid, and 3. DNA‐dependent plus‐strand DNA synthesis and polymerisation (Seifer 1998). After three years of entecavir treatment, most people (94%) may have serum HBV DNA levels that are undetectable by sensitive polymerase chain reaction assays (Dimou 2007). 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 (EASL 2017).

Why it is important to do this review

The efficacy and safety of tenofovir versus entecavir in the treatment of chronic hepatitis B have been controversial. Several non‐Cochrane reviews have addressed this topic (Cheung 2020; Choi 2021; Dave 2021; Tseng 2020; Yuan 2021); however, the results of these reviews remain conflicting. For example, one systematic review published in 2021 indicated that the risk of hepatocellular carcinoma amongst people treated with entecavir was 27% higher than with TDF (adjusted hazard ratio (HR) 1.27, 95% confidence interval (CI) 1.01 to 1.61) (Dave 2021), whereas another systematic review published in 2020 found that tenofovir and entecavir had a comparable effect on reducing the risk of hepatocellular carcinoma (adjusted HR 0.88, 95% CI 0.73 to 1.07) (Tseng 2020). Moreover, most of the above systematic reviews were based on retrospective observational studies. Furthermore, the earlier reviews had several other limitations: 1. lacked appropriate subgroup analyses, such as children versus adults (of different ages), and short versus long follow‐up duration; 2. ignored some patient‐important outcomes, such as adverse events (Iida‐Ueno 2019); and 3. failed to assess the certainty of the evidence. This Cochrane Review plans to overcome their limitations.

In the past years, several randomised clinical trials were set up to compare the benefits and harms of tenofovir and entecavir, which make it possible to conduct a new systematic review based on these trials (Luo 2017; Toka 2021; Yim 2018). Therefore, conducting a Cochrane Review, based on randomised trials, is crucial to summarise the benefits and harms of these treatments and keep updating the findings when evidence evolves.

Objectives

To evaluate the benefits and harms of tenofovir versus entecavir in children and adults with chronic hepatitis B.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised clinical trials, with any trial design, which have evaluated the benefits and harms of tenofovir or any of the two tenofovir formulations, that is TDF and TAF, versus entecavir, in children and adults with chronic hepatitis B. We will include the trials irrespective of publication status, country, year, language of publication, and outcomes assessed. We will also consider for inclusion trials with unpublished data, cluster‐randomised trials, and the first period of cross‐over trials.

We will exclude quasi‐randomised controlled studies as these are pseudo‐randomised (i.e. the method of allocation to the study groups is not truly random), and other observational studies (e.g. case reports, case series, cross‐sectional studies, case‐control studies, and cohort studies).

Types of participants

We will include people diagnosed with chronic hepatitis B. In this review, we will define an adult as 16 years old or above, and a child as two to 16 years old, as tenofovir is approved by European Medicines Agency for children aged two years and above (Stinco 2021).

People with chronic hepatitis B can either be hepatitis B e antigen (HBeAg)‐positive or HBeAg‐negative (EASL 2017).

• HBeAg‐positive people: hepatitis B surface antigen (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 showing 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 people: HBsAg positivity for more than six months, serum HBeAg negative usually with detectable anti‐HBe, 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.

We will include trials with participants irrespective of whether they are treatment‐naïve or have previously been treated for chronic hepatitis B infection with other antiviral drugs. We will also accept any other definitions employed by the authors of the publications making it likely that the participants had chronic hepatitis B.

We will not consider for inclusion pregnant women with chronic hepatitis B or people with acute hepatitis B, or hepatitis A, C, D, or E infection. We will not restrict inclusion of participants to ethnicity, age, or sex. We will exclude trials including participants with other significant underlying diseases, such as chronic kidney failure, heart disease, cirrhosis, cancer, HIV infection, and so forth.

If we identify trials with a subset or subsets of participants diagnosed with diseases other than chronic hepatitis B (e.g. acute hepatitis B or HIV), and their data are not reported separately from the data of people with chronic hepatitis B or the trial authors do not send us the data we need, then we will exclude the trial. We will also exclude trials if the included number of participants with chronic hepatitis B is fewer than 10, as results from small trials may overestimate or underestimate intervention effects (McKenzie 2022a).

Types of interventions

Experimental intervention

• Tenofovir or any of the two formulations (TDF and TAF)

Control intervention

• Entecavir

Both the experimental and control interventions could have been administered orally, at any dose, for any duration, at any frequency, or time of administration.

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

Types of outcome measures

We plan to include all trials that meet the eligibility selection criteria, irrespective of whether the outcomes of our protocol are reported or not.

For our main analysis, we will analyse the outcomes data at the longest follow‐up.

Primary outcomes

• All‐cause mortality and proportion of people with hepatitis B‐related morbidity (number of participants who developed cirrhosis, ascites, variceal bleeding, hepato‐renal syndrome, hepatocellular carcinoma, or hepatic encephalopathy and who have not died). We will test these outcomes as a composite outcome as well as individually (mortality or morbidity).

• Health‐related quality of life (evaluated using any validated participant‐reported scales, such as the EuroQol five dimensions questionnaire (EQ‐5D) or 36‐Item Short Form Health Survey (SF‐36)). If a trial reported multiple health‐related quality of life measures, we will choose one in the following order: SF‐36, EQ‐5D, General Well‐Being Scale, Subjective Quality of Life Scale (SQOL), and 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 inpatient hospitalisation or prolongation of existing hospitalisation, results in persistent or significant disability or incapacity, or is a congenital anomaly/birth defect) (ICH‐GCP 2016).

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 adverse events considered non‐serious (any untoward medical occurrence in a participant or clinical investigation participant that does not meet the above criteria for a serious adverse event, is defined as a non‐serious adverse effect).

• Proportion of people without histological improvement.

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

• Proportion of people with detectable HBsAg 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).

Where a published trial does not report outcomes of interest to our review, we will check the trial protocol to see what outcomes were planned. If we cannot find the protocol, we will attempt to contact the trial authors to find out whether there were outcomes that were measured but not reported. If relevant trials measured the outcomes of interest to our review, but they did not report the data we need, or data were not in a usable format, we will attempt to contact the trial authors to request usable data. If we obtain the requested data, we will include them in the meta‐analyses. If we do not obtain the data, we will only include these trials in the review as part of the narrative.

Search methods for identification of studies

We will perform systematic searches for randomised trials based on the guidance in Chapter 4 of the Cochrane Handbook for Systematic Reviews of Interventions (Lefebvre 2022a) and PRISMA‐S (Rethlefsen 2021). There will be no restrictions on language, publication year, or publication status.

Electronic searches

The Cochrane Hepato‐Biliary Group Information Specialist will search the Cochrane Hepato‐Biliary Group Controlled Trials Register 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 (VHL Regional Portal), Science Citation Index Expanded, and Conference Proceedings Citation Index – Science. The latter two will be searched 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 trial registration resources including ClinicalTrial.gov (clinicaltrials.gov/), WHO International Clinical Trial Registry Platform (www.who.int/ictrp), Food and Drug Administration (FDA; www.fda.gov/), European Medicines Agency (www.ema.europa.eu/ema/), EU Clinical Trials Register (www.clinicaltrialsregister.eu/), International Clinical Trials Registry Platform, and pharmaceutical company sources for ongoing or unpublished trials and for study information.

We will search for grey literature such as meeting abstracts and internal reports in Europe 'OpenGrey' (www.opengrey.eu), as well as Google Scholar (scholar.google.com).

We will check the reference lists of all potentially relevant primary studies and reviews for additional references.

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 studies (Lefebvre 2022b).

If necessary, we will contact the study authors of identified trials for additional published or unpublished trials.

We will provide the actual date of searching other resources at the review stage. We will use the relevant sections of the PRISMA‐S checklist for our review to ensure that we have reported and documented our searches as advised (PRISMA-S Checklist; Rethlefsen 2021).

Data collection and analysis

We will conduct the data collection and analysis according to the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022a).

Selection of studies

We will manage and screen the studies identified by the search strategies using Covidence online software (www.covidence.org). Two pairs of review authors (ML, YQ, YL, and MM) will independently screen all titles and abstracts. We will retrieve the full‐text reports of all potentially eligible trials, and then the same four review authors (ML, YQ, YL, and MM) will independently evaluate each potentially eligible full text for eligibility, recording the reasons for exclusion of ineligible studies. We will resolve any disagreements by consensus, and when necessary, we will consult a fifth review author (LY or KY). If multiple reports are related to a single study, we will group these reports under a single reference ID. If studies were published only as abstracts with insufficient information, or data are not clearly described in the full text to determine whether to include them or not, we will contact study authors to confirm whether the trial is eligible. We will record the selection process in sufficient detail to complete a PRISMA 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 non‐English language publications, we will use Google Translate to aid with eligibility assessment when screening (translate.google.com). If necessary, we will seek translators or native speakers to assist with assessing the eligibility of studies and data extraction.

If during the selection of trials, obtained through our searches for randomised clinical trials, we identify controlled (quasi‐randomised or controlled studies) and observational studies (cohort studies or case reports) on the topic of our review that have reported adverse events during the study period, we will include these studies for a review of the reported adverse events only. We will present these data separately. We will not run a systematic 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

Two pairs of review authors (ML, YQ, KG, and YML) will design and pilot a data extraction form on at least three trials. We will then independently extract data from the included trials and summarise the details in the 'Characteristics of included studies' table. We will follow guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022a). We will resolve disagreements by discussion or by involving a fifth review author (KY or LY).

We will collect the following information from each eligible trial, based on the PICOTs (participants, interventions, comparators, outcomes, follow‐up times, and ranges) as well as study design and other information of relevance.

• Participants: number randomised for each group, number lost to follow‐up/withdrawn, number analysed, mean age, age range, sex, the severity of the condition, number of participants who were HBeAg‐positive and HBeAg‐negative, number of participants who were treatment‐naïve, diagnostic criteria, inclusion criteria, and exclusion criteria.

• Interventions: experimental intervention, control intervention, duration of treatment, dose, regimen, and co‐intervention.

• Outcomes: outcomes specified and collected at the latest time points.

• Follow‐up: time of follow‐up for the outcomes, period, or range of follow‐up.

• Study design: the first author, published journal, country, year of study, study design type, total duration of the study, number of study centres and location, correspondence information, and trial registration.

• Other information: information for risk of bias, information for GRADE assessment (including the baseline imbalance in each group), funding source, conflict of interest of the trial authors, clinical trial registration number, a priori sample size estimation, and ethics committee approval and ethics committee approval (for trials launched after 2005).

Assessment of risk of bias in included studies

Two pairs of review authors (ML, YQ, KG, and YML) will independently assess the risk of bias of the included trials using Cochrane's RoB 2 tool (Sterne 2019), and instructions given in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022b). If there are any disagreements, a fifth review author (KY or LY) will arbitrate. Our assessment will focus on the effect of assignment to the interventions, based on the intention‐to‐treat principle, which includes all randomised participants regardless of the interventions that they received.

We will use the following domains of RoB 2 to assess the risk of bias in a trial (available from riskofbiasinfo.org):

• bias arising from the randomisation process;

• bias due to deviations from intended interventions;

• bias due to missing outcome data;

• bias in the measurement of the outcome;

• bias in the selection of the reported result.

For each domain, there will be a series of signalling questions. The response options for the signalling questions are: 'Yes', 'Probably yes', 'Probably no', 'No', and 'No information'.

We will use the overall risk of bias for a trial outcome result, rather than specific domains (Higgins 2022b). The overall risk of bias for the result is the least favourable assessment across the domains of bias.

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

• Some concerns: the trial has some concerns in at least one domain for this result, but not at high risk of bias for any domain.

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

When assessing the risk of bias in cluster‐randomised trials, we will assess one additional domain, that is bias arising from the timing and recruitment of participants. We will follow the guidance in Chapter 23 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022c) and www.riskofbias.info/welcome/rob-2-0-tool/rob-2-for-cluster-randomized-trials. We will assess the risk of bias in cross‐over trials using the same methods as in parallel group trials because we will only use the data from the first period before the cross‐over, and without additional considerations.

We will use the RoB 2 Microsoft Excel tool (www.riskofbias.info). 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 store the data in Excel, and we will make the judgements available online. We will provide details at the review stage.

The risk of bias assessments for each outcome will feed into one domain of the GRADE approach for assessing the certainty of evidence (Schünemann 2022a). We will assess the risk of bias of the following three outcomes: all‐cause mortality and proportion of people with hepatitis B‐related morbidity, health‐related quality of life, and proportion of people with serious adverse events. When assessing the bias risk of the outcomes 'health‐related quality of life' and 'proportion of people with serious adverse events' regarding the domain 'risk of bias in measurement of the outcome', we will consider who the outcome assessor was, and we will judge the implications for risk of bias if the outcome assessor was aware of the intervention assignment. We will present the three outcomes in a summary of findings table as these outcomes are the most clinically relevant for clinicians and people with chronic hepatitis B.

We will assess the risk of bias of the outcome results at the maximum follow‐up time points.

Measures of treatment effect

We will follow the guidance described in Chapters 9 and 10 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2022; McKenzie 2022b). We will use Review Manager Web to analyse data (RevMan Web 2023). For dichotomous outcomes, we will calculate the risk ratio (RR) with 95% confidence intervals (CI) for individual trials. For continuous variables, we will calculate the mean difference (MD) with 95% CI if trials used the same tool. We will use the standardised mean difference (SMD) with 95% CI if trials used different measurement scales. As the SMD method does not correct for differences in the direction of the scale, if necessary, we will multiply the mean values from one set of studies by −1 to ensure that all the scales point in the same direction according to the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022d). We will interpret SMD as follows: SMD less than 0.40 for small intervention effects, SMD between 0.40 and 0.70 for moderate intervention effects, and SMD greater than 0.70 for large intervention effects (Schünemann 2022b). We will describe skewed data reported as medians and interquartile ranges in a narrative format.

When reporting adverse events in the summary of findings table, we will follow the guidance in Sections 19.5.1 and 19.5.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Peryer 2022).

Unit of analysis issues

We will follow the Cochrane Handbook for Systematic Reviews of Interventions to avoid 'unit of analysis' errors (Higgins 2022b).

For parallel‐randomised trials, the unit of analysis will be the individual participant. Where a trial reports multiple trial groups, we will include only the relevant trial groups. If a trial has two or more experimental groups and one control group, and all are relevant to our review, we will compare each experimental group separately with half of the control arm if used within the same comparison.

For cluster‐randomised trials, the unit of analysis is groups of participants as randomised (Higgins 2022c). If we identify cluster‐randomised trials for inclusion in the review, we may combine these with the individually randomised trials in the same meta‐analysis provided that the cluster effect estimate takes account of the potential clustering. If not, then we will analyse the cluster‐randomised trials separately to avoid a 'unit of analysis error', as highlighted in Chapter 23 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022c). We will consider the generic inverse‐variance approach to analyse the effect estimates and their standard errors (SEs) from correct analyses of cluster‐randomised trials as stated in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022c).

For trials with repeated observations of trial participants (e.g. multiple adverse events per participant), we will only use 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). We will present a table with each type of adverse event 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.

Dealing with missing data

We will deal with the missing data following the recommendations in the Cochrane Handbook for Systematic Review of Interventions (Page 2022).

We will base the analysis on intention‐to‐treat data from individual clinical trials whenever possible. Otherwise, we will perform available case analyses, which assume that data are missing at random. We will assess missing data for each included trial.

We will contact the trial authors or trial sponsors to request missing data or required information by email or telephone. Where possible, we will use Review Manager Web calculator to calculate missing data, for example, we will calculate missing standard deviations using other data from the trial, such as P value and CIs, based on the methods outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Page 2022). Where this is not possible, and 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 a sensitivity analysis in which we will exclude trials with more than 20% missing data.

For the primary dichotomous outcomes, we will also conduct sensitivity analyses by including trial participants with incomplete or missing data. We will impute missing data based on the assumption of the 'best‐case' and 'worst‐case' scenario analyses. The 'best‐case' scenario is that all participants with missing outcomes in the experimental group had good outcomes, and all those with missing outcomes in the control group had poor outcomes; the 'worst‐case' scenario is the opposite (Deeks 2022). See Sensitivity analysis.

Assessment of heterogeneity

We will explore and describe clinical and methodological heterogeneity, considering the characteristics and the design features of the trial, participants, interventions, comparators, outcomes, treatment duration, and follow‐up. We will present a summary of the trial design, participants, interventions, comparisons, outcomes, time, funding, and the risk of bias assessments in the beginning of the 'Results' section.

We will also visually assess statistical heterogeneity by visual inspection of forest plots, considering the direction and magnitude of effects, and the degree of overlap between CIs. We will evaluate statistical heterogeneity with the Chi² and I² statistics, using P < 0.10 as a cut‐off point for statistical heterogeneity (Deeks 2022).

We will use the I² statistic to quantify inconsistency amongst the trials in each analysis. We will also consider the P value from the Chi² test. According to the Cochrane Handbook for Systematic Reviews of Interventions, the threshold value of the I² statistic will be set as the following (Deeks 2022):

• 0% to 40%: might not be important;

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

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

• 75% to 100%: considerable heterogeneity.

If there is substantial heterogeneity (i.e. the I² statistic value is greater than 50%), we will report it and explore possible causes by subgroup analysis and sensitivity analysis.

Assessment of reporting biases

If more than 10 trials are pooled in a meta‐analysis, we will create a funnel plot to assess the potential publication bias and possible small‐study biases. If the funnel plot is asymmetrical, we will examine possible reasons as outlined in Chapter 13 of the Cochrane Handbook for Systematic Reviews of Interventions (Page 2022), and we will relate this to the results of the review. To determine whether there is selective reporting of results, we will also compare trial protocols and registration data against published reports. We will also contact trial authors to request any missing outcome information.

Data synthesis

We will use Review Manager Web to synthesise the data with a meta‐analysis (RevMan Web 2023), following the guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022a) if we find data from more than one trial per outcome. One review author will enter the data into the Review Manager Web and a second review author will check the data for accuracy. We will not limit our primary and subgroup analyses to trials at overall low risk of bias, but we will use sensitivity analysis to present data only from trials at low risk of bias.

If a meta‐analysis is feasible, we will use the random‐effects model for pooling the data as we anticipate that true effects will be related but will not be the same for included trials. We will use the fixed‐effect model as a sensitivity analysis. For dichotomous outcomes, we will base the estimation of the between‐study variance using the Mantel‐Haenszel method. We will use the inverse variance method for continuous outcomes. As mentioned earlier, if we find significant heterogeneity with I² > 50%, we will explore heterogeneity with subgroup and sensitivity analyses. If intention‐to‐treat analyses are not possible, then we will use per‐protocol analyses, and we will record this in the review. If neither intention‐to‐treat analyses nor per‐protocol analyses can be used, we will use the available data in the original trials. If data are not reported in a trial in a format that we can use, we will attempt to convert the data to the required format, following the guidance in Chapter 6 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022d). If the clinical characteristics of individual trials are clinically too heterogeneous, we will not perform a meta‐analysis. We will present the characteristics and findings of the included trials in the text and tables, and we will provide a systematic narrative synthesis to summarise and explain this information in accordance with the Synthesis Without Meta‐analysis (SWiM) guideline (Campbell 2020).

Subgroup analysis and investigation of heterogeneity

In order to investigate heterogeneity, we plan to conduct subgroup analyses with only the primary outcomes if each subgroup includes at least five trials. We will analyse the subgroup differences using the random‐effects model.

• Two formulations of tenofovir: TDF compared with TAF as TAF is a novel prodrug formulated to deliver the active metabolite to target cells more efficiently than TDF at a lower dose (De Clercq 2016), and the treatment may have different effects.

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

• Follow‐up duration: less than one year compared with 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).

• Presence compared with absence of previous treatment with other antivirals as the resistance barrier of the treatment is different between the two groups of participants and may have different effects (Tenney 2009).

We will use the formal test (Chi² test and a P value of 0.05) to assess the subgroup differences in RevMan Web 2023 (Deeks 2022).

Sensitivity analysis

We plan to conduct the following sensitivity analyses to evaluate the robustness of results of our primary outcomes and explore their impact on effect size.

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

• Excluding cluster‐randomised trials

• Excluding trials published in an abstract form and unpublished trials

• Excluding trials funded for profit

• Restricting the analysis to treatment‐naïve participants

• Conducting the analyses with a fixed‐effect model (see Data synthesis)

• Excluding trials with missing data greater than 20% (see Dealing with missing data)

• Extreme‐case analysis favouring the experimental intervention ('best‐worse' 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 (see Dealing with missing data)

• 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 (see Dealing with missing data)

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

Trial Sequential Analysis

We will perform Trial Sequential Analysis as a sensitivity analysis to imprecision because Trial Sequential Analysis can control random errors in meta‐analysis (Brok 2008; Brok 2009; Thorlund 2009; Thorlund 2010; Thorlund 2017; TSA 2021; Wetterslev 2008; Wetterslev 2009; Wetterslev 2017). We will calculate the diversity‐adjusted required information size (DARIS) (i.e. the number of participants needed in a meta‐analysis to detect or reject a certain intervention effect) which should also consider the diversity observed in the meta‐analysis (Brok 2008; Brok 2009; Thorlund 2010; Wetterslev 2008; Wetterslev 2009; Wetterslev 2017).

For dichotomous outcomes, we will calculate the DARIS based on the event proportion in the control group; assumption of a relative risk reduction of 10%; a risk of type I error of 2.5% for our three primary outcomes (Jakobsen 2014); a risk of type II error of 10%; and the assumed diversity of the meta‐analysis (Jakobsen 2014). For the continuous outcome, we will estimate the DARIS 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 to conduct a Trial Sequential Analysis with trials at any risk of bias.

We will add the trials according to year of publication. If more than one trial is published during the same year, we will add trials alphabetically according to the last name of the first author. We will construct trial sequential monitoring boundaries on the basis of the required information size (Jakobsen 2014; Thorlund 2017). 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 (Thorlund 2017). We will use the Trial Sequential Analysis software (Version 0.9.5.10) provided by the Copenhagen Trial Unit to conduct the Trial Sequential Analysis (Thorlund 2017; TSA 2021).

We will report the results with Trial Sequential Analysis as sensitivity analysis to imprecision assessed by GRADE. We will downgrade imprecision in Trial Sequential Analysis by two levels if the accrued number of participants is below 50% of the DARIS, and one level if it is between 50% and 100% of DARIS. Furthermore, we will not downgrade if the cumulative Z‐curve crosses the monitoring boundaries for benefit, harm, or futility, or if DARIS is reached.

We will conduct Trial Sequential Analysis for our primary outcomes, irrespective of bias risk.

Stakeholder consultation and involvement

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

Summary of findings and assessment of the certainty of the evidence

We will create a summary of findings table using GRADEpro GDT software (GRADEpro GDT), as described in the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2022a). A GRADE table provides information including anticipated absolute effects, relative effect, trials sample size, number of trials, and rating of overall confidence in effect estimates for each outcome.

We plan to prepare a summary of findings table on tenofovir versus entecavir in children and adults with chronic hepatitis B. The experimental intervention presented in the summary of findings table will be tenofovir. The control intervention (comparator) will be entecavir. We will present the outcome results of all‐cause mortality and proportion of people with hepatitis B‐related morbidity, health‐related quality of life, and proportion of people with serious adverse events. We will also provide the longest follow‐up, median or mean, and the range of follow‐up.

We will use the GRADE approach to assess the certainty of the evidence for each of the above outcomes. We will use the GRADE assessment to draw conclusions about the certainty of evidence within the text of the review. The GRADE approach uses five factors: risk of bias, consistency of effect (heterogeneity), imprecision, indirectness, and publication bias (Schünemann 2013). We will use the overall RoB 2 judgement for each outcome as part of the GRADE assessment.

For 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 one level for serious, and 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 reader's understanding of the review where necessary.

We plan to define the levels of evidence as 'high', 'moderate', 'low', or 'very low' certainty as follows.

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

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

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

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

Two review authors (ML and YQ) will independently grade the certainty of the evidence for the outcomes. We will resolve differences in assessment by discussion or by consultation with a third review author (KY or LY).

We will conduct our review according to this published protocol, and we will document any deviations from the protocol in the 'Differences between protocol and review' section of the final review.

Notes

The protocol shares common authors with "Entecavir for children and adults with chronic hepatitis B" and "Tenofovir for children and adults with chronic hepatitis B" review protocols, and therefore parts of the Background and Methods text may be the same.

Appendices

Appendix 1. Search strategies

Database	Date range	Search strategy
Cochrane Hepato‐Biliary Group Controlled Trials Register (via the Cochrane Register of Studies Web)	Date of search will be given at review stage	(tenofovir or viread or vemlidy or Tavin or tenof or hepdoze or tentide or PMPA) and (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 MeSH descriptor: [Tenofovir] explode all trees #2 (tenofovir or viread or vemlidy or Tavin or tenof or hepdoze or tentide or PMPA) #3 #1 or #2 #4 MeSH descriptor: [Hepatitis B, Chronic] explode all trees #5 (chronic and (hepatitis b or hep b or hbv)) #6 #4 or #5 #7 #3 and #6
MEDLINE Ovid	1946 to the date of the search	1. exp Tenofovir/ 2. (tenofovir or viread or vemlidy or Tavin or tenof or hepdoze or tentide or PMPA).mp. 3. 1 or 2 4. exp Hepatitis B, Chronic/ 5. (chronic and (hepatitis b or hep b or hbv)).mp. 6. 4 or 5 7. 3 and 6 8. (randomized controlled trial or controlled clinical trial or retracted publication or retraction of publication).pt. 9. clinical trials as topic.sh. 10. (random* or placebo*).ab. or trial.ti. 11. 8 or 9 or 10 12. exp animals/ not humans.sh. 13. 11 not 12 14. 7 and 13
Embase Ovid	1974 to the date of the search	1. exp tenofovir/ 2. (tenofovir or viread or vemlidy or Tavin or tenof or hepdoze or tentide or PMPA).mp. 3. 1 or 2 4. exp chronic hepatitis B/ 5. (chronic and (hepatitis b or hep b or hbv)).mp. 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$1 or assigned or allocated or volunteer or volunteers).ti,ab. 10. (compare or compared or comparison or trial).ti. 11. ((evaluated or evaluate or evaluating or assessed or assess) and (compare or compared or comparing or comparison)).ab. 12. (open adj label).ti,ab. 13. ((double or single or doubly or singly) adj (blind or blinded or blindly)).ti,ab. 14. ((assign$ 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 (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 (VHL Regional Portal)	1982 to the date of the search	(tenofovir or viread or vemlidy or Tavin or tenof or hepdoze or tentide or PMPA) and (entecavir or baraclude) [Words] and (chronic and (hepatitis b or hep b or hbv))
Science Citation Index Expanded (Web of Science)	1900 to the date of the search	#6 #4 AND #5 #5 TI=(random* or blind* or placebo* or meta‐analys* or trial*) OR TS=(random* or blind* or placebo* or meta‐analys*) #4 #3 AND #2 AND #1 #3 TS=(chronic and (hepatitis b or hep b or hbv)) #2 TS=(entecavir or baraclude) #1 TS=(tenofovir or viread or vemlidy or Tavin or tenof or hepdoze or tentide or PMPA)
Conference Proceedings Citation Index – Science (Web of Science)	1990 to the date of the search	#6 #4 AND #5 #5 TI=(random* or blind* or placebo* or meta‐analys* or trial*) OR TS=(random* or blind* or placebo* or meta‐analys*) #4 #3 AND #2 AND #1 #3 TS=(chronic and (hepatitis b or hep b or hbv)) #2 TS=(entecavir or baraclude) #1 TS=(tenofovir or viread or vemlidy or Tavin or tenof or hepdoze or tentide or PMPA)

Contributions of authors

ML, LY, and YQ: drafted the protocol

YL, MM, MY, and KG: revised the protocol

QW, MYL, LZ, XL, and ZZ commented on the protocol

KY: initiated the review, and commented on the protocol

All authors agreed to this final version of the protocol.

Sources of support

Internal sources

• No sources of support provided, Other

External sources

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

  Provided help with the protocol preparation and run the peer review process

Declarations of interest

ML: none.

LY: none.

YQ: none.

YL: none.

MYL: none.

MM: none.

MY: none.

KG: none.

QW: none.

ZZ: none.

LZ: none.

XL: none.

KY: none.

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