Interventions for treating genital Chlamydia trachomatis infection in pregnancy
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To establish the most efficacious and best‐tolerated therapy for treatment of genital chlamydial infection in preventing maternal infection and adverse neonatal outcomes.
Background
The prevalence of chlamydial infection in pregnancy is between 2% to 30% depending on the patient's age and risk factors (Berggren 2011; Much 1991). It is particularly common in women younger than 25 years of age (Walker 2012). Genital Chlamydia trachomatis (C.trachomatis) infection has been shown to be associated with pregnancy complications such as miscarriage (Nigro 2011), preterm labour (Pararas 2006; Rours 2011), low birthweight (Attenburrow 1985) and increased perinatal mortality (Silva 2012). There may also be an association with preterm rupture of membranes (Blas 2007) and postpartum endometritis (Ismail 1987). If the mother is untreated, 20% to 50% of newborn babies may develop chlamydial conjunctivitis (Kakar 2010), and another 10% to 20% may develop C.trachomatis pneumonia (Rours 2009). Vaginal birth is associated with the highest risk of transmission of chlamydial infection, however, there is a small risk of acquiring the infection even in infants born by caesarean section with premature rupture of membranes and intact membranes (Pammi 2012; Yu 2009).
Genital C.trachomatis infection is detected by nucleic acid amplification test (NAAT) on the specimens of genital secretions or urine. This test has replaced tissue culture of C.trachomatis (Jespersen 2005).
Description of the condition
Genital C.trachomatis infection is a common bacterial sexually transmitted infection. The majority of women infected with this bacteria are asymptomatic and, therefore, may be more likely to transmit the infection because they do not seek treatment for the infection, which may result in a longer duration of the infection. The sequelae of C.trachomatis genital infection range from cervicitis to pelvic inflammatory disease, perihepatitis, ectopic pregnancy and infertility (Zenilman 2012). We have described complications of pregnancy and diseases of newborn related to genital chlamydia infection in the Background section above.
C.trachomatis is a small gram‐negative intracellular bacterium with a two‐phased life‐cycle, which includes the form that infects new cells, (e.g. the small elementary body) and the active form (e.g. the reticulate body). The life‐cycle is about two to three days, and, therefore, sustained high serum minimum inhibitory concentration of antimicrobial agents is needed to achieve eradication of the infection, which can be achieved by long‐acting antimicrobials treatment or prolonged treatment. The incubation period of C.trachomatis infection varies between seven and 14 days (Zenilman 2012).
Description of the intervention
There are various treatment regimens for the management of chlamydial infection during pregnancy, however, there is no consensus on the most effective and safest option.
According to the Centers for Disease Control and Prevention (CDC) guideline followed by many countries around the world, the recommended regimens for treatment of genital chlamydial infection in pregnancy are azithromycin (1 g orally given as a single dose) or amoxicillin (500 mg orally three times daily for seven days) (Workowski 2010). The alternative regimen according to the CDC guideline is erythromycin (500 mg or 250 mg orally four times daily for seven days) or erythromycin ethylsuccinate (800 mg orally four times daily for seven days or 400 mg orally four times daily for 14 days) (Workowski 2010). Erythromycin is associated with a high degree of gastrointestinal side‐effects (primarily nausea) and the compliance may an issue in such cases Workowski 2010.
Women who present in labour but were not treated for a prior positive chlamydial test are advised to be treated immediately with one of the above regimens. However, such late treatment is unlikely to substantially decrease the risk of transmission of chlamydia to the newborn.
Clindamycin is another alternative drug for treatment of genital C.trachomatis infection. Despite it being safe in pregnancy, clindamycin is not used widely due to its cost (Miller 2000).
Other antibiotics (e.g. doxycycline, levofloxacin, ofloxacin, and erythromycin estolate) used for treatment of genital C.trachomatis are contraindicated in pregnancy and lactation (Workowski 2010).
Azithromycin is believed to be the superior agent in comparison to other antibiotics for treatment of chlamydial infection. New research has emerged suggesting that there is a higher failure rate with azithromycin treatment of chlamydial infection than previously believed Schwebke 2011. One of the explanations for this recent finding is a higher sensitivity of NAAT in comparison to that previously used in the tissue culture as a test of cure (Handsfield 2011), although it does not explain the similar cure rates reported after doxycycline treatment with both of these tests. Another explanation for treatment failure is heterotopic resistance with high chlamydia loads which leads to treatment failures (Horner 2006). Re‐infection is also a cause of treatment failure (Horner 2006).
Cure rates of C.trachomatis in women who are pregnant are lower than in non‐pregnant women. The reasons behind this is a generally higher failure rate of treatment with amoxicillin, which has been traditionally used for treatment of C.trachomatis infection during pregnancy. A test of cure has always been recommended for all pregnant women and is performed no earlier than three weeks after treatment is initiated (Workowski 2010).
The previous Cochrane review on interventions for treating genital C.trachomatis infection in pregnancy found that amoxycillin was as effective as erythromycin (odds ratio 0.54, 95% confidence interval 0.28 to 1.02) (Brocklehurst 1998). Amoxycillin was found to be better tolerated than erythromycin (odds ratio 0.16, 95% confidence interval 0.09 to 0.30). Clindamycin and azithromycin were reported to be effective, however, the numbers of women included in trials were small (Brocklehurst 1998). There are new studies published in this area that are awaiting classification, therefore, it is important to update this review, which will be done under new authorship.
How the intervention might work
Irradicating genital chlamydial infection during pregnancy with antibacterial drugs will lead to following:
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treatment of symptoms and sequelae of genital chlamydial infection such as discharge, cervicitis, pelvic inflammatory disease, tubal disease and infertility;
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a decrease in perinatal complications such as preterm labour and early pregnancy loss, preterm rupture of membranes;
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a decrease in transmission of the infection to the fetus or newborn and, therefore, prevention of intrauterine infection, neonatal conjunctivitis and pneumonia during pregnancy;
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prevention of postpartum infection such as endometritis.
Why it is important to do this review
It is important to assess the different interventions for treating genital C.trachomatis in order to establish whether effective treatment of this infection improves perinatal outcomes and decreases maternal complications.
Objectives
To establish the most efficacious and best‐tolerated therapy for treatment of genital chlamydial infection in preventing maternal infection and adverse neonatal outcomes.
Methods
Criteria for considering studies for this review
Types of studies
We will only include randomised controlled trials. Cluster‐randomised trials will also be eligibile for inclusion in this review. Quasi‐randomised trials and trials using cross‐over design will not be included. We will include studies published in abstract form.
Types of participants
Pregnant women with C.trachomatis infection.
Types of interventions
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Any antibiotic versus no treatment or placebo for genital C.trachomatiss infection in pregnancy
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Different antibacterial regimens
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One antibiotic versus another antibiotic
Types of outcome measures
Primary outcomes
1. Microbiological cure ‐ negative chlamydia test at least three weeks after treatment of the mother.
Secondary outcomes
A. Maternal
2. Repeated infection.
3. Preterm labour.
4. Preterm birth.
5. Preterm rupture of membranes.
6. Chorioamnionitis.
7. Postpartum endometritis.
8. Sepsis.
9. Prolonged hospital stay of the mother.
10. Side‐effects of treatment.
11. Maternal satisfaction with treatment.
B. Fetal/neonatal
12. Perinatal mortality.
13. Neonatal conjunctivitis.
14. Neonatal pneumonia.
15. Fetal anomalies.
16. Low birth weight.
17. Apgar score less than seven at five minutes.
C. Cost
18. Cost of treatment.
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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monthly 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;
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International Clinical Trials Registry Platform.
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.
In addition we plan to search ClinicalTrials.gov for planned, ongoing or unpublished trials. The search terms we plan to use are given in Appendix 1.
Searching other resources
We will search the reference lists of retrieved studies.
We will not apply any language restrictions.
Data collection and analysis
Selection of studies
Both review authors will independently assess for inclusion all the potential studies identified as a result of the search strategy. We will resolve any disagreement through discussion or, if required, we will consult a third person.
Studies published only in abstract form will be included if they otherwise satisfy inclusion criteria. The authors of such studies will be contacted if any additional information is required.
Data extraction and management
We will design a form to extract data. For eligible studies, both review authors will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult a third person. We will enter data into Review Manager software (RevMan 2011) 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
Both 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 2011). We will resolve any disagreement by discussion or by involving a third assessor.
(1) Random 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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low risk of bias (any truly random process, e.g. random number table; computer random number generator);
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high risk of bias (any non‐random process, e.g. odd or even date of birth; hospital or clinic record number);
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unclear risk of bias.
(2) Allocation concealment (checking for possible selection bias)
We will describe for each included study the method used to conceal allocation to interventions prior to assignment and will assess 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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low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
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high risk of bias (open random allocation; unsealed or non‐opaque envelopes, alternation; date of birth);
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unclear risk of bias.
(3.1) Blinding of participants and personnel (checking for possible performance bias)
We will describe for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We will consider that studies are at low risk of bias if they were blinded, or if we judge that the lack of blinding would be unlikely to affect results. We will assess blinding separately for different outcomes or classes of outcomes.
We will assess the methods as:
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low, high or unclear risk of bias for participants;
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low, high or unclear risk of bias for personnel.
(3.2) Blinding of outcome assessment (checking for possible detection bias)
We will describe for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We will assess blinding separately for different outcomes or classes of outcomes.
We will assess methods used to blind outcome assessment as:
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low, high or unclear risk of bias.
(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)
We will describe for each included study, 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 and the numbers included in the analysis at each stage (compared with the total randomised 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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low risk of bias (e.g. no missing outcome data; missing outcome data balanced across groups);
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high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis done with substantial departure of intervention received from that assigned at randomisation);
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unclear risk of bias.
A cut‐off point of 20% will be used to assess the level of missing data as adequate for different outcomes.
(5) Selective reporting (checking for reporting bias)
We will describe for each included study how we investigated the possibility of selective outcome reporting bias and what we found.
We will assess the methods as:
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low risk of bias (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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high risk of bias (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 risk of bias.
(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)
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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low risk of other bias;
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high risk of other bias;
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unclear whether there is risk of other bias.
(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 2011). 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 ‐ seeSensitivity analysis.
Measures of treatment effect
Dichotomous data
For dichotomous data, we will present results as summary risk ratio with 95% confidence intervals.
Continuous data
For continuous data, 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‐randomised trials in the analyses along with individually‐randomised trials. We will adjust their standard errors using the methods described in the Cochrane Handbook for Systematic Reviews of Interventions using an estimate of the intra‐cluster correlation co‐efficient (ICC) derived from the trial (if possible), from a similar trial or from a study of a similar population. If we use ICCs from other sources, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we identify both cluster‐randomised trials and individually‐randomised trials, we plan to synthesise 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 randomisation unit is considered to be unlikely.
We will also acknowledge heterogeneity in the randomisation unit and perform a subgroup analysis to investigate the effects of the randomisation unit.
Cross‐over trials
We will not include cross‐over trials.
Other unit of analysis issues
If we identify the trials with more than three treatment groups, we will include each pair‐wise comparison separately, but with shared intervention groups divided out approximately evenly among the comparisons. For dichotomous outcomes, both the number of events and the total number of patients will be divided up. For continuous outcomes, only the total number of participants will be divided up and the means and standard deviations left unchanged (Cochrane Handbook for Systematic Reviews of Interventions 16.5.4).
Dealing with missing data
For included studies, we will note levels of attrition. We will explore the impact of including studies 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 randomised to each group in the analyses, and all participants will be analysed in the group to which they were allocated, regardless of whether or not they received the allocated intervention. The denominator for each outcome in each trial will be the number randomised minus any participants whose outcomes are known to be missing.
We will exclude studies with more than 20% missing data.
Assessment of heterogeneity
We will assess statistical heterogeneity in each meta‐analysis using the T², I² and Chi² statistics. We will regard heterogeneity as substantial if the I² is greater than 30% and either the T² is greater than zero, or there is a low P value (less than 0.10) in the Chi² test for heterogeneity.
Assessment of reporting biases
If there are 10 or more studies in the meta‐analysis we will investigate reporting biases (such as publication bias) using funnel plots. We will assess funnel plot asymmetry visually. If asymmetry is suggested by a visual assessment, we will perform exploratory analyses to investigate it.
Data synthesis
We will carry out statistical analysis using the Review Manager software (RevMan 2011). We will use fixed‐effect meta‐analysis for combining data where it is reasonable to assume that studies are estimating the same underlying treatment effect: i.e. where trials are examining the same intervention, and the trials’ populations and methods are judged sufficiently similar. If there is clinical heterogeneity sufficient to expect that the underlying treatment effects differ between trials, or if substantial statistical heterogeneity is detected, we will use random‐effects meta‐analysis to produce an overall summary if an average treatment effect across trials is considered clinically meaningful. The random‐effects summary will be treated as the average range of possible treatment effects and we will discuss the clinical implications of treatment effects differing between trials. If the average treatment effect is not clinically meaningful, we will not combine trials.
If we use random‐effects analyses, the results will be presented as the average treatment effect with 95% confidence intervals, and the estimates of T² and I².
Subgroup analysis and investigation of heterogeneity
If we identify substantial heterogeneity, we will investigate it using subgroup analyses and sensitivity analyses. We will consider whether an overall summary is meaningful, and if it is, use random‐effects analysis to produce it.
We plan to carry out the following subgroup analyses.
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Women with a first episode versus women with recurrent (previously treated in pregnancy) genital C.trachomatis infection
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Women in the first half (before 20 weeks) versus women in the second half (including 20 weeks and after 20 weeks) of pregnancy
The following outcomes will be used in subgroup analysis.
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Microbiological cure negative chlamydia test after treatment for the mother
We will assess subgroup differences by interaction tests available within RevMan (RevMan 2011). We will report the results of subgroup analyses quoting the χ2 statistic and P value, and the interaction test I² value.
Sensitivity analysis
Sensitivity analyses will be performed for aspects of the review that might affect the results, for example, where there is risk of bias associated with the quality of some of the included trials. We will undertake analysis of the primary outcome separately for trials with low risk of bias and high and unknown risk of bias (allocation concealment). Sensitivity analysis will be carried out to explore the effects of random‐effects analyses for outcomes with statistical heterogeneity.
