Hepatitis B vaccination during pregnancy for preventing infant infection
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the effectiveness and adverse effects of hepatitis B vaccine administered to pregnant women for preventing HBV infection in infants.
Background
Description of the condition
Hepatitis B virus (HBV) is an enveloped, double‐stranded DNA virus. Hepatitis B is an infection caused by the HBV and occurs worldwide. The highest rates of HBV carriers are found in developing countries with limited medical facilities. In highly endemic areas of Asia, Africa, and the Pacific, approximately 75% of hepatitis B carriers usually acquire the virus perinatally or in childhood (Safary 2000). Whereas in western and northern European countries and North America, HBV infection is relatively rare and acquired primarily in adulthood. HBV infections result in 500,000 to 1.2 million deaths per year caused by chronic hepatitis, cirrhosis, and hepatocellular carcinoma (HCC) (Lavanchy 2004). Globally, HBV causes 60% to 80% of the worlds primary liver cancers (Parkin 2001).
Diagnosis of hepatitis is made by biochemical assessment of liver function and coagulation studies (Hollinger 2001). Diagnosis is confirmed by demonstration of specific antigens and/or antibodies. Three clinically useful antigen antibody systems have been identified for hepatitis B: (1) hepatitis B surface antigen (HBsAg) and antibody to HBsAg (anti‐HBs IgG); (2) antibody (anti‐HBc IgM) and anti‐HBc IgG) to hepatitis B core antigen (HBcAg); and (3) hepatitis B e antigen (HBeAg) and antibody to HBeAg (anti‐HBe) to determine infectivity.
For infants and children, the two primary sources of HBV infection are perinatal transmission from infected mothers and horizontal transmission from infected household contacts. Perinatal transmission is common in hyperendemics areas, especially when HBsAg carrier mothers are also HBeAg positive (Hollinger 2001; Mahoney 1999). For a newborn infant whose mother is positive for both HBsAg and HBeAg, the risk for chronic HBV infection is 70% to 90% by age six months in the absence of postexposure immunoprophylaxis (Wong 1984). By comparison, the infant risk for chronic infection is less than 10% in the mother with HBeAg negative (Stevens 1985). Of persons who are infected with HBV as infants or young children, 25% to 90% become chronic carriers, and approximately 25% of those with chronic infection die prematurely from cirrhosis or liver cancer (hepatocellular carcinoma) (Gitlin 1997; McMahon 1990). Development of chronic HBV infection at an early age increases the risk of HCC more than infection at older age (Hsieh 1992). Nearly 100% of HCC children were hepatitis B surface antigen seropositive (Chang 1998). Breastfeeding by an HBsAg positive mother does not increase the risk for acquisition of HBV infection in the infant (Beasley 1975).
Description of the intervention
Hepatitis B vaccines are composed of the surface antigen of HBV (HBsAg), and are produced by two different methods: plasma derived or recombinant DNA (Assad 1999). Plasma‐derived vaccines, derived from the plasma of HBsAg‐positive donors, consist of highly purified, formalin‐inactivated and/or heat‐inactivated, alum‐adsorbed, hepatitis B subvirion particles (22 nm) of HBsAg that are free of detectable nucleic acid, and, therefore, noninfectious. Recombinant DNA yeast‐derived or mammalian cell‐derived vaccines, the S gene (pre‐S1, pre‐S2, S), is cloned and isolated, inserted into an expression plasmid and introduced into yeast or mammalian cells. The desired protein is expressed and assembled into 22 nm antigenic particles. As on natural HBsAg particles, the epitope that elicits the most important immune response is exposed on the surface of artificial particles. Vaccines used for primary prevention have effectively reduced risk of infection in most populations (Mahoney 1993). Completion of hepatitis B vaccine programmes induces protection in about 95% of recipients (Jackson 2007). Vaccination during pregnancy is safe and provides passive transfer of antibodies to the newborn (Anonymous 1991; Gupta 2003; Levy 1991).There are no known side effects from vaccination, in either pregnant women or their offspring (Grosheide 1993). The most common side effects from hepatitis B vaccination are pain at the injection site and mild to moderate fever (Andre 1989; Greenberg 1993).
Hepatitis B vaccine is given into the deltoid intramuscularly in a series of three doses (de Lalla 1988; Krugman 1981). The first shot is given at the elected date; the second dose a month later; and the third dose six months after the first dose. Vaccine batches should be stored at 2° to 8°C. Freezing destroys the potency of the vaccine. Factors that may reduce the immunogenicity of hepatitis vaccines include age (greater than 40 years), weight, genetics, haemodialysis, HIV infection, immunosuppression, tobacco smoking, subcutaneous injection, injection into the buttocks, and accelerated schedule (Ingardia 1999).
How the intervention might work
The mechanism of hepatitis B vaccination during pregnancy for preventing neonatal infection is the production of maternal antibodies that can be transferred across the placenta and provide the neonate with high antibody titers. This could protect the neonate from horizontal infection until active immunization after birth is protective (Reddy 1994).
Why it is important to do this review
Complex HBV epidemiology makes it difficult to evaluate and compare the effectiveness of different immunization policies. HBV infection rates vary in different parts of the world according to the pattern of hepatitis B transmission. In high endemic populations, perinatal transmission has been documented to result in a high rate of hepatitis B infection (Beasley 1983). Many countries have implemented universal hepatitis B immunization at birth, which provides long‐term protection against infection in more than 90% of healthy people (Shepard 2006). Despite this, some infants who are born to HBV sero‐positive mothers have become infected by HBV despite having received passive‐active immunoprophylaxis (Ngui 1998). Maternal hepatitis B vaccine immunization may be a way of preventing hepatitis B infection in infants before hepatitis B vaccine can be administered and provide protection. However, the ideal plan for hepatitis B vaccine administration during pregnancy, taking into consideration risk factors (high risk of HBV infection or the general population); endemic populations (high or low); and cost effectiveness, is not known.
Objectives
To assess the effectiveness and adverse effects of hepatitis B vaccine administered to pregnant women for preventing HBV infection in infants.
Methods
Criteria for considering studies for this review
Types of studies
We will include all randomized controlled trials (RCTs) of hepatitis B vaccination during pregnancy for preventing infant infection. The randomized units could be individual or clustered (e.g. hospitals). We will exclude cross‐over trials and quasi‐randomized trials.
Types of participants
All pregnant women unaware of marker results of hepatitis B virus serology.
Types of interventions
Hepatitis B vaccine compared with placebo or no treatment.
Types of outcome measures
Primary outcomes
Incidence of hepatitis B virus infection in infants.
Secondary outcomes
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Hepatitis B antibody for hepatitis B virus (HBs Ab) in newborns up to six months after birth.
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Maternal antibody for hepatitis B virus (HBs Ab).
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Adverse maternal effects such as local reactions at injection site (soreness, swelling, erythema); fatigue; fever; headache.
Search methods for identification of studies
Electronic searches
We will contact the Trials Search Co‐ordinator to search the Cochrane Pregnancy and Childbirth Group’s Trials Register.
The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co‐ordinator and contains trials identified from:
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quarterly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
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weekly searches of MEDLINE;
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handsearches of 30 journals and the proceedings of major conferences;
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weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.
Details of the search strategies for CENTRAL and MEDLINE, the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service can be found in the ‘Specialized Register’ section within the editorial information about the Cochrane Pregnancy and Childbirth Group.
Trials identified through the searching activities described above are each assigned to a review topic (or topics). The Trials Search Co‐ordinator searches the register for each review using the topic list rather than keywords.
We will not apply any language restrictions.
Data collection and analysis
The methodology for data collection and analysis is based on the Cochrane Handbook of Systematic Reviews of Interventions (Higgins 2008).
Selection of studies
Two review authors, Ussanee S Sangkomkamhang (US) and Pisake Lumbiganon (PL) will independently assess for inclusion all the potential studies we identify as a result of the search strategy. We will resolve any disagreement through discussion or, if required, we will consult an additional review author.
Data extraction and management
We will design a form to extract data. For eligible studies, two review authors will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult an additional review author. We will enter data into Review Manager software (RevMan 2008) and check for accuracy.
When information regarding any of the above is unclear, we will attempt to contact authors of the original reports to provide further details.
Assessment of risk of bias in included studies
Two review authors will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008). We will resolve any disagreement by discussion or by involving an additional assessor.
(1) Sequence generation (checking for possible selection bias)
We will describe for each included study the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.
We will assess the method as:
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adequate (any truly random process, e.g. random number table; computer random number generator);
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inadequate (any non random process, e.g. odd or even date of birth; hospital or clinic record number); or
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unclear.
(2) Allocation concealment (checking for possible selection bias)
We will describe for each included study the method used to conceal the allocation sequence in sufficient detail and determine whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.
We will assess the methods as:
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adequate (e.g. telephone or central randomization; consecutively numbered sealed opaque envelopes);
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inadequate (open random allocation; unsealed or non‐opaque envelopes, alternation; date of birth);
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unclear.
(3) Blinding (checking for possible performance bias)
We will describe for each included study all the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We will also provide information on whether the intended blinding was effective.
We will assess the methods as:
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adequate, inadequate, or unclear for participants;
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adequate, inadequate, or unclear for personnel;
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adequate, inadequate, or unclear for outcome assessors;
where ‘adequate’ is when there was blinding or where we assess that the outcome or the outcome measurement is not likely to have been influenced by lack of blinding.
(4) Incomplete outcome data (checking for possible attrition bias through withdrawals, dropouts, protocol deviations)
We will describe for each included trial, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We will state whether attrition and exclusions were reported, the numbers included in the analysis at each stage (compared with the total randomized participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. Where sufficient information is reported, or can be supplied by the trial authors, we will re‐include missing data in the analyses which we undertake. We will assess methods as:
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adequate;
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inadequate:
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unclear.
We will discuss whether missing data greater than 20% might (a) be reasonably expected (acknowledging that with long‐term follow up, complete data are difficult to attain); and (b) impact on outcomes.
(5) Selective reporting bias
We will describe for each included trial how we investigated the possibility of selective outcome reporting bias and what we found.
We will assess the methods as:
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adequate (where it is clear that all of the study’s pre‐specified outcomes and all expected outcomes of interest to the review have been reported);
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inadequate (where not all the study’s pre‐specified outcomes have been reported; one or more reported primary outcomes were not pre‐specified; outcomes of interest are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported);
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unclear.
(6) Other sources of bias
We will describe for each included study any important concerns we have about other possible sources of bias.
We will assess whether each study was free of other problems that could put it at risk of bias:
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yes;
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no;
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unclear.
(7) Overall risk of bias
We will make explicit judgements about whether studies are at high risk of bias, according to the criteria given in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008). With reference to (1) to (6) above, we will assess the likely magnitude and direction of the bias and whether we consider it is likely to impact on the findings. We will explore the impact of the level of bias through undertaking sensitivity analyses ‐ see 'Sensitivity analysis'.
When information regarding any of the above (1) to (6) is unclear, we will attempt to contact authors of the original reports to provide further details.
Measures of treatment effect
Dichotomous data
For dichotomous data, such as the incidence of hepatitis B virus infection in infants, we will present results as summary risk ratio with 95% confidence interval.
Continuous data
For continuous data, such as maternal antibody levels, we will use the mean difference if outcomes are measured in the same way between trials. We will use the standardised mean difference to combine trials that measure the same outcome, but use different methods.
Unit of analysis issues
Cluster‐randomised trials
We will include cluster‐randomized trials in the analyses, along with individually randomized trials. We will adjust their sample sizes using the methods described in the Handbook, using an estimate of the intracluster correlation co‐efficient (ICC) derived from the trial (if possible), or from another source. If ICCs from other sources are used, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we identify both cluster‐randomized trials and individually‐randomized trials, we plan to synthesize the relevant information. We will consider it reasonable to combine the results from both, if there is little heterogeneity between the study designs and the interaction between the effect of intervention and the choice of randomization unit is considered to be unlikely.
We will also acknowledge heterogeneity in the randomization unit and perform a separate meta‐analysis.
Dealing with missing data
For included trials, we will note levels of attrition. We will explore the impact of including trials with high levels of missing data in the overall assessment of treatment effect by using sensitivity analysis.
For all outcomes we will carry out analyses, as far as possible, on an intention‐to‐treat basis: i.e. we will attempt to include all participants randomized to each group in the analyses. The denominator for each outcome in each trial will be the number randomized minus any participants whose outcomes are known to be missing.
Assessment of heterogeneity
We will use the I2 statistic to measure heterogeneity among the trials in each analysis. If we identify substantial heterogeneity (I2 greater than 50%), we will explore it by prespecified subgroup analysis.
Assessment of reporting biases
Where we suspect reporting bias (see selective reporting bias above), we will attempt to contact study authors, asking them to provide missing outcome data. 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.
Data synthesis
We will carry out statistical analysis using the Review Manager software (RevMan 2008). We will use fixed‐effect inverse variance meta‐analysis for combining data where trials are examining the same intervention, and the trials’ populations and methods are judged sufficiently similar. Where we cannot explain heterogeneity between trials' treatment effects, we will use random‐effects meta‐analysis.
Subgroup analysis and investigation of heterogeneity
If we can include a number of trials, we plan to carry out subgroup analyses for the primary outcome of incidence of hepatitis B virus infection in infant as following:
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low risk of hepatitis B virus (HBV) infection versus high risk (as defined by authors e.g. injection drug users, healthcare workers ) of HBV infection;
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low endemic setting versus high endemic setting of HBV infection;
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vaccination schedule (e.g. three doses versus two doses regimen);
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maternal negative versus positive for marker of hepatitis B virus serology.
For fixed‐effect meta‐analyses we will conduct planned subgroup analyses classifying whole trials by interaction tests as described by (Deeks 2001). For random‐effects meta‐analyses we will assess differences between subgroups by inspection of the subgroups’ confidence intervals; non‐overlapping confidence intervals indicate a statistically significant difference in treatment effect between the subgroups.
Sensitivity analysis
We will perform sensitivity analysis based on trial quality, separating high‐quality trials from trials of lower quality. For the purposes of this sensitivity analysis, we will define 'high quality' as a trial having adequate allocation concealment, and classify an 'unreasonably expected loss to follow up' as less than 20%, given the stated importance of attrition as a quality measure (Tierney 2005).
If we include any cluster‐randomized trials, other sensitivity analysis may also be desirable. If cluster trials have been incorporated with an estimate of the ICC borrowed from a different trial, we will perform a sensitivity analysis to see what the effect of different values of the ICC on the results of the analysis would be.
