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The Cochrane Database of Systematic Reviews logoLink to The Cochrane Database of Systematic Reviews
. 2023 Sep 8;2023(9):CD015586. doi: 10.1002/14651858.CD015586

Tenofovir for children and adults with chronic hepatitis B

Huijuan Li 1,2, Minyan Yang 2,3,4, Mina Ma 2,3,4, Zijun Li 2,3,4, Meixuan Li 2,3,4, LongDong Zhu 5, Liang Yao 6, Junfeng Li 5, Linda Zhong 1,7, Kehu Yang 2,3,4,
Editor: Cochrane Hepato-Biliary Group
PMCID: PMC10485896

Objectives

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

To evaluate the benefits and harms of tenofovir versus no intervention or placebo for children and adults with chronic hepatitis B.

Background

Description of the condition

Chronic hepatitis B is a serious disease caused by hepatitis B virus (HBV) (Tan 2021; Tang 2018). It is a major global health problem because it can significantly increase the risk of developing cirrhosis and liver cancer. 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 (Easterbrook 2021). There are about 820,000 deaths per year, mostly due to cirrhosis and hepatocellular carcinoma (Easterbrook 2021). The prevalence of chronic hepatitis B varies greatly, from about 0.35% in the US (Lim 2020) to 5.1% in Thailand (Leroi 2016), and 5.2% in China (Wang 2017). Chronic hepatitis B is a highly endemic disease, and potential reasons for the different prevalences could be vaccine rate, awareness of diseases, and healthcare accessibility.

Chronic hepatitis B can be asymptomatic and symptomatic. Many people with chronic hepatitis B might be unaware of their infection due to lack of symptoms or signs. According to the WHO, as of 2019, 10.5% of 30.4 million people with hepatitis B were aware of their infection, and of this group, 22% (about 6.6 million) of people diagnosed with hepatitis B received treatment in 2019 (WHO 2022).

Liver failure and liver cancer are expected to develop in 15% to 40% of untreated people with chronic hepatitis B viral infection (Tang 2018). Chronic hepatitis B can significantly increase the risk 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). The evolution to cirrhosis and hepatocellular carcinoma might be related to the process of inflammation, regeneration, and fibrosis due to the hepatitis B infection (Di Bisceglie 2009).

HBV could be spread through sexual contact, sharing needles, accidental needle sticks, and mother‐to‐child transmission. Perinatal transmission is a major route of infection, which accounts for more than one‐third of hepatitis B infections (Vodkin 2014).

Description of the intervention

Currently, chronic hepatitis B treatments include injections of interferon and antiviral therapy. Interferon treatment has a higher likelihood of hepatitis B surface antigen clearance and less drug resistance compared with antiviral therapy (Perrillo 2009). However, the limitations of interferon treatment for chronic hepatitis B are its adverse effects (Ye 2021), which include swelling, influenza‐like symptoms, fatigue, nausea, and vomiting. Antiviral drugs can inhibit virus replication and slow the progression of cirrhosis and hepatocellular carcinoma (Jiang 2021). The approved antiviral drugs include entecavir, tenofovir, lamivudine, adefovir, and telbivudine (Charlton 2020; Chien 2022; EASL 2017). Monotherapy is recommended for most people with chronic hepatitis B because combination treatments fail to show a superior effect (Martin 2022).

Tenofovir is one of the first‐line agents used in people with chronic HBV infection. There are two different tenofovir formulations, tenofovir disoproxil fumarate and tenofovir alafenamide (Pilkington 2020). As one of the effective antiviral agents, tenofovir disoproxil fumarate, prodrug of tenofovir, has been used in the US for the treatment of HIV infection since 2001 (Charlton 2020; Jenh 2009). In 2008, tenofovir disoproxil fumarate was approved by the US Food and Drug Administration for HBV infection. Tenofovir alafenamide, prodrug of tenofovir, was approved in the USA in November 2016. Tenofovir alafenamide shows greater antiviral activity, and is distributed more quickly to the blood and body's tissues than tenofovir disoproxil fumarate (Eisenberg 2001). Currently, the American Association for the Study of Liver Diseases and the WHO recommend tenofovir because of its good efficacy in blocking, or slowing down the speed, of HBV replication and avoid further liver damage (Terrault 2016). However, how well this treatment works may vary greatly amongst individuals.

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 then integrates into the DNA chain (Buti 2021; Chien 2022; Marcellin 2013). Once tenofovir is incorporated into the chain, it induces a chain termination, and viral replication is inhibited (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 tenofovir disoproxil fumarate and tenofovir alafenamide are prodrugs of tenofovir. After oral absorption, the majority of tenofovir disoproxil fumarate is rapidly converted to tenofovir in the plasma, and then intracellularly to the active tenofovir diphosphate (Wassner 2020). In contrast, tenofovir alafenamide remains stable within the plasma and is only converted to tenofovir intracellularly. It is reported that tenofovir alafenamide is associated with lower risks of bone and kidney adverse events compared with tenofovir disoproxil fumarate (Hill 2018; Sax 2015).

Why it is important to do this review

One prior systematic review compared the efficacies amongst tenofovir alafenamide fumarate, tenofovir disoproxil fumarate, and entecavir for people with chronic hepatitis B (Ma 2021). The review included 28 studies (13 randomised clinical trials, 14 cohort studies, and 1 cross‐sectional study) published from 2012 to 2019. Though the review results showed significant heterogeneity, the authors did not use any methodological or statistical tools to explore potential reasons for it.

One earlier network meta‐analysis compared the efficacy of seven monotherapies for chronic hepatitis B, that is adefovir, entecavir, lamivudine, pegylated interferon, tenofovir alafenamide, telbivudine, and tenofovir disoproxil fumarate (Wong 2019). The date of search for eligible studies was the end of 2017. The network meta‐analysis did not include trials comparing tenofovir versus placebo, and hence, the estimates of tenofovir versus placebo were only based on indirect evidence.

According to a current guideline (Martin 2022), antiviral treatment is recommended in people without cirrhosis when alanine aminotransferase (ALT) is elevated (above 35 IU/mL for men and 25 IU/mL for women) and HBV DNA is greater than 20,000 IU/mL. However, if the level of ALT is normal and HBV DNA is less than 20,000 IU/mL, no treatment is suggested (Martin 2022). The level of ALT and HBV DNA should be monitored every three to six months (Martin 2022). Although tenofovir has been highly recommended for suppression of viral replication, the net effect of tenofovir in people with chronic hepatitis B compared with placebo, especially in the long‐term disease progress, is still unclear (EASL 2009; Terrault 2016).

There is no Cochrane Review assessing the treatment effects of tenofovir versus no intervention or placebo in people with chronic hepatitis B. Therefore, we embarked on this review to evaluate the benefits and harms of tenofovir in people with chronic hepatitis B compared with placebo or no treatment. We have also planned to do a systematic review on the benefits and harms of tenofovir versus entecavir for children and adults with chronic hepatitis B (protocol under development).

Objectives

To evaluate the benefits and harms of tenofovir versus no intervention or placebo for 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 assessed tenofovir or any of the two tenofovir formulations (tenofovir disoproxil fumarate and tenofovir alafenamide) in children and adults with chronic hepatitis B. We will include the trials irrespective of publication status, country, year and language of publication, and outcomes reported. We will also consider for inclusion trials with unpublished data.

We will exclude quasi‐randomised studies as the allocation sequence generation can be anticipated by alternation, date of birth, or day of admission, 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 showing 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 (Hertzog 2008; McKenzie 2022).

Types of interventions

Experimental intervention

  • Tenofovir (tenofovir disoproxil fumarate or tenofovir alafenamide) administered orally and regardless of dose, frequency, time of administration, and treatment duration.

Control intervention

  • Placebo or no treatment

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

Types of outcome measures

We will focus on both beneficial and harmful outcomes. We will not regard outcomes in a single trial as an exclusion criterion in this review.

We will assess all outcomes at maximum 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).

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).

Search methods for identification of studies

To minimise bias in our search results, we will follow the guidance in Chapter 4 of the Cochrane Handbook for Systematic Reviews of Interventions (Lefebvre 2022a) and in PRISMA‐S (Rethlefsen 2021) to plan and describe the search process for the review. There will be no restrictions on the language of publication, country of origin, 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 online trial registries such as 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 (www.ema.europa.eu/ema/), Food and Drug Administration (www.fda.gov), as well as pharmaceutical company sources for ongoing or unpublished trials, and for study information. We will also 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; scholar.google.com/).

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 trials, 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).

We will contact the authors of the included primary trials for additional published or unpublished trials.

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

Data collection and analysis

Selection of studies

Two review authors (MY and MM) will independently select studies for inclusion using the Covidence online software (www.covidence.org). We will identify and exclude duplicates not retrieved with the initial deduplication of the search results handled by the Cochrane Hepato‐Biliary Group Information Specialist using the Cochrane Register of Studies Web. We will then screen titles and abstracts of all unique records obtained by electronic and other resource searches for inclusion of potentially relevant studies, and code them as 'eligible' or 'potentially eligible/unclear'. We will retrieve the full text of all relevant and potentially relevant records, and two review authors (MY and MM) will independently screen these to identify studies for inclusion. We will identify and record the reasons for the exclusion of ineligible studies. We will contact primary trial investigators by e‐mail if any information must be clarified or obtained. We will resolve any disagreement through discussion or, if required, we will consult a third person (HL). We will identify and collate multiple reports of the same study so that each study, rather than each record, is the unit of interest in the review. We will record the selection process in sufficient detail to complete a PRISMA flow diagram (for new systematic reviews which includes searches of databases, registers, and other sources) (Page 2021a; Page 2021b). For screening of non‐English language publications, we will, in the first instance, use Google Translate to assist the eligibility assessment (translate.google.com). If needed, we will seek translators through the Cochrane Hepato‐Biliary Group to assist with assessing the eligibility of studies and, if eligible, assist with data extraction by native speakers.

If during the selection of trials, we identify observational studies on the topic of our review (e.g. quasi‐randomised studies, cohort studies, or case reports) that have reported adverse effects from the experimental intervention during the study period, we will include these studies for a review of the reported adverse events only. We will not meta‐analyse the data, but we will use them for a narrative synthesis at the end of the results section. 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

Two review authors (ML and JL) will independently extract data using a piloted data extraction form in an Excel spreadsheet, and any disagreements will be resolved through discussion or, if required, we will consult a third person (HL).

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 study authors, clinical trial registration number, a priori sample size estimation, and ethics committee approval and ethics committee approval (for trials launched after 2005).

We will present a summary of the information extracted from each trial in the 'Characteristics of included studies' table. We will contact trial authors to obtain any missing information or data.

Assessment of risk of bias in included studies

Two review authors (HL and LY) will independently assess the risk of bias of the included randomised trials using Cochrane's RoB 2 tool (Higgins 2022a; Sterne 2019). We will resolve any disagreement through discussion with a third review author (ML). 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 actually received.

We will assess risk of bias using the following five RoB 2 domains, consisting of a series of signalling questions (Higgins 2022a; Sterne 2019):

  • 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.

The answer to the signalling questions can be one of the following: 'Yes', 'Probably yes', 'Probably no', 'No', or 'No information'.

The overall risk of bias for each outcome will be rated at 'low risk of bias' if all domains are at low risk of bias; it will be rated as at 'some concerns' if at least one domain has some concerns, but not to be at high risk of bias for any domain, or it will be rated as at 'high risk of bias' if at least one domain is at high risk of bias, or some domains have some concerns in a way that substantially lowers confidence in the result (Higgins 2022a; Sterne 2019).

Two review authors (HL and LY) will use the Excel tool, downloaded from the website (www.riskofbias.info/), to record the assessment results by answering the signalling questions and presenting risk of bias judgements (Sterne 2019).

In case of cluster randomised trials, we will assess the risk of bias following guidance on RoB 2 for cluster‐randomised trials (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 method as in parallel group trials because we will only use the data from the first period before the cross‐over (Higgins 2022b).

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 a body of evidence (Schünemann 2013). 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 because 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 use Review Manager Web to analyse data (RevMan Web 2023). For binary data, we will calculate risk ratios (RR) and associated 95% confidence intervals (CIs). For continuous data, we will calculate mean differences (MD) and associated 95% CIs if all included trials used the same scale to measure a particular outcome. Otherwise, we will use the standardised mean difference (SMD) and associated 95% CIs where different instruments or scales have been used to report outcomes. 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 2022c). 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 2022a). 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

For trials with a parallel group design, the unit of analysis will be the participants as randomised to the intervention groups of a trial.

In cluster randomised trials, we will treat the cluster (i.e. families, schools, hospitals, etc.) as the unit of analysis (Higgins 2022b). If the baseline characteristics are imbalanced, we will make it clear in the discussion of our review, and we will refer to it when assessing the certainty of evidence with GRADE. We will consider combining data from cluster‐randomised trials with data from the individually randomised trials in a 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 2022b). 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 2022b).

If we identify trials with two or more intervention groups, and if some groups are not relevant for our review or cannot be combined, then we will select for analysis only the relevant pair of groups. In case of a relevant common control group and relevant two experimental groups, then we will halve the control group if used within the same comparison. We will use methods recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022b). If the primary or secondary outcomes are measured at different time points, we will only consider the data at the longest follow‐up.

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). 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 follow the recommendations in the Cochrane Handbook for Systematic Review of Interventions to deal with missing data (Page 2022). We will base the meta‐analyses 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 and required information by e‐mail or telephone. Where possible, we will use the Review Manager Web calculator to calculate missing data; for example, we will calculate missing standard deviations using other data from the trial, such as a 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 excluding 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

We will conduct a systematic search, including grey literature, to minimise the reporting bias regardless of the status of the publication. We will also contact trial authors to request unpublished trials or other information of relevance to this review. If an analysis includes 10 or more eligible trials, we will use a funnel plot to investigate publication bias for primary outcomes (Egger 1997).

Data synthesis

We will conduct a meta‐analysis if the trials are sufficiently similar. We will judge and assess the similarity between trials based on the participants (P), interventions (I), comparators (C), outcomes (O) (i.e. PICOs, determined by consensus). We will perform a meta‐analysis of data on a particular outcome if more than one eligible trial provides outcome data. When meta‐analysis is not possible, we will refer to the Synthesis Without Meta‐analysis (SWiM) guideline to summarise and compare characteristics and main findings of the included trials (Campbell 2020).

We will not limit our primary and subgroup analysis to trials at overall low risk of bias, but we will use sensitivity analyses to present data only from trials at low risk of bias. For dichotomous outcomes, we will use the Mantel‐Haenszel method. For continuous outcomes, we will use the inverse variance method. We will use Review Manager Web to perform our meta‐analyses (RevMan Web 2023). We will analyse data with the random‐effects model as our main analysis. We will use the fixed‐effect model as a sensitivity analysis. As mentioned earlier, we aim to perform intention‐to‐treat analyses. If this is not always 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 2022c).

Subgroup analysis and investigation of heterogeneity

In order to investigate heterogeneity, we plan to conduct subgroup analyses of the primary outcomes only if each subgroup includes at least five trials. We will analyse the subgroup differences using the random‐effects model. We will conduct between‐groups testing (reporting Chi2 test and corresponding P value) in Review Manager Web (RevMan Web 2023).

  • Two formulations of tenofovir: tenofovir disoproxil fumarate compared with tenofovir alafenamide as tenofovir alafenamide is a novel prodrug formulated to deliver the active metabolite to target cells more efficiently than tenofovir disoproxil fumarate 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) because the clinical characteristics and disease courses are different between the two age groups (EASL 2017), and the treatment may have different effects.

  • Countries' economic status: that is grouping the trials conducted in low‐income, middle‐income, and high‐income countries according to the World Bank classifications to investigate possible impact of country setting (World Bank 2021).

  • Follow‐up duration: within one year compared to more than one year 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 treatment (EASL 2017).

  • Treatment‐naïve participants compared to those who were previously treated with other antiviral drugs because the resistance barrier of the treatment is different between the two groups of participants and may have different effects (Wong 2019).

Sensitivity analysis

We plan to conduct sensitivity analyses in order to evaluate the robustness of results of the primary outcomes according to the following potential factors.

  • Excluding trials at an overall high risk of bias (see Assessment of risk of bias in included studies)

  • Excluding cluster‐randomised trials (see Unit of analysis issues)

  • 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)

  • Performing 'best‐case' scenario analyses; 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)

  • Performing 'worst‐best' case scenario analyses; 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)

  • Trial Sequential Analysis as a sensitivity analysis to imprecision assessed by GRADE

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 risk ratio 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 required information size based on the standard deviation observed in the control group of the meta‐analysis and a minimal relevant difference of 50% of this standard deviation, and the observed diversity in the trials in the meta‐analysis. We will use the random‐effects model. We plan 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.

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 2022b). 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 no intervention or placebo 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 no intervention or placebo. We will present the certainty of evidence of 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 at the longest follow‐up. After each outcome, 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 limitations (the certainty will not be downgraded)'; 'Some concerns' will indicate either 'no limitations' or 'serious limitations (the certainty will be downgraded one level)'; and 'High' risk of bias will indicate either 'serious limitations' or 'very serious limitations (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, 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 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 (HL and ML) will independently make all the judgements, and any disagreement will be solved through discussion. If required, we will consult a third review author (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 chronic hepatitis B" and "Tenofovir versus entecavir for chronic hepatitis B" review protocols, and therefore parts of Background and Methods text may be the same.

Acknowledgements

We would like to thank Dimitrinka Nikolova, the Cochrane Hepato‐Biliary Managing Editor, for her advice and support, and also thank Sarah Louise Klingenberg, the Information Specialist, for building the search strategies.

Cochrane Review Group funding acknowledgement: the Danish State is the largest single funder of the Cochrane Hepato‐Biliary Group through its investment in the Copenhagen Trial Unit, Centre for Clinical Intervention Research, the Capital Region, Rigshospitalet, Copenhagen, Denmark.

Disclaimer: the views and opinions expressed in this protocol are those of the authors and do not necessarily reflect those of the Danish State or the Copenhagen Trial Unit.

The following people from the Cochrane Hepato‐Biliary Editorial Team conducted the editorial process for this protocol.

  • Sign‐off Editor (final editorial decision): Christian Gluud, Denmark

  • Contact Editors (provided editorial decision): Jian Ping Liu, China

  • Statistical Editor (checked statistical methods): Giovanni Casazza, Italy

  • Managing Editor (selected peer reviewers and editors, provided editorial guidance to authors, edited the protocol): Dimitrinka Nikolova, Denmark

  • Information Specialists (search strategy design): Sarah Louise Klingenberg, Denmark

  • Peer‐reviewers (provided clinical and content review comments): Israel Junior Borges do Nascimento, Brazil; Mirella Fraquelli, Italy

  • Peer‐reviewer (Trial Sequential Analysis): Mark Aninakwah Asante, Denmark

  • Peer‐reviewer (design of search strategies): Joanne Abbott, UK

  • Associate Editor (protocol screening): Leslie Choi, Evidence Production and Methods Department, Cochrane, UK

  • Copy Editor (copy editing and production): Anne Lawson, Cochrane Central Production Service, UK

Appendices

Appendix 1. Preliminary search strategies

Database Date range Search strategy
The Cochrane Hepato‐Biliary Group Controlled Trials Register (via the Cochrane Register of Studies Web) Date of search will be given at review stage (tenofovir or viread or vemlidy or Tavin or tenof or hepdoze or tentide or PMPA) 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 date of 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 date of 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 date of search ((mh:(d02.705.429.906 OR d03.633.100.759.138.881)) OR (mh:(tenofovir)) OR (tenofovir OR viread OR vemlidy OR tavin OR tenof OR hepdoze OR tentide OR pmpa)) AND ((mh:(c01.221.250.500.100 OR c01.925.256.430.400.100 OR c01.925.440.435.100 OR c06.552.380.350.100 OR c06.552.380.705.437.100 OR c23.550.291.500.477.500)) OR (mh:(chronic hepatitis b)) OR ((chronic AND (hepatitis b OR hep b OR hbv)))) AND ( db:("LILACS"))
Science Citation Index Expanded (Web of Science) 1900 to date of search #5 #3 AND #4
#4 TI=(random* or blind* or placebo* or meta‐analys* or trial*) OR TS=(random* or blind* or placebo* or meta‐analys*)
#3 #2 AND #1
#2 TS=(chronic and (hepatitis b or hep b or hbv))
#1 TS=(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 date of search #1 TS=(tenofovir or viread or vemlidy or Tavin or tenof or hepdoze or tentide or PMPA)
#2 TS=(chronic and (hepatitis b or hep b or hbv))
#3 #2 AND #1
#4 TI=(random* or blind* or placebo* or meta‐analys* or trial*) OR TS=(random* or blind* or placebo* or meta‐analys*)
#5 #3 AND #4

Contributions of authors

HL: wrote the protocol.

MY: provided general advice on the protocol.

MM: provided general advice on the protocol.

ZL: provided general advice on the protocol.

ML: conceptualised the protocol.

LZ: provided general advice on the protocol.

LY: reviewed the final version of the protocol.

JL: provided general advice on the protocol.

LLZ: reviewed the final version of the protocol.

KY: wrote the protocol.

All authors approved the publication of the protocol.

Sources of support

Internal sources

  • No sources of support provided, Other

    none

External sources

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

    Help and guidance with the protocol development; conducted the editorial process

Declarations of interest

HL: none.

MY: none.

MM: none.

ZL: none.

ML: none.

LZ: none.

LY: none.

JL: none.

LLZ: none.

KY: none.

New

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