Antibiotic regimens for management of intra‐amniotic infection
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the effects of administering antibiotics regimens for intra‐amniotic infection on maternal and perinatal morbidity and mortality and infection‐related complications.
Background
Description of the condition
Chorioamnionitis is an infection of the fetal membranes, amniotic fluid, and placenta and/or decidua during pregnancy and poses a significant risk to infant and maternal morbidity and mortality. It can also be referred to as intra‐amniotic infection (IAI), amnionitis, and amniotic fluid infection (Incerpi 2010; Tita 2010).
Chorioamnionitis can be defined clinically or histologically. Clinical chorioamnionitis is estimated to occur in 1% to 2% of term and 5% to 10% of preterm births and histological chorioamnionitis is found in nearly 20% of term and 50% of preterm births (Incerpi 2010). The clinical definition of chorioamnionitis can vary but is best characterized as maternal fever (100.4 degrees Fahrenheit) that is not attributable to another cause and exhibits at least one of the following symptoms: maternal tachycardia, fetal tachycardia, uterine tenderness, maternal leukocytosis (white blood cell count greater than 15,000 mL) and amniotic fluid with a foul odor (Fishman 2012).
There are few diagnostic tests that are specific and sensitive, as well as safe for mother and infant, therefore, chorioamnionitis is primarily diagnosed through clinical signs and symptoms. A culture of the amniotic fluid obtained from an amniocentesis is the reference standard for diagnosis but it requires 48 hours for test results and there is insufficient evidence that it reduces maternal or neonatal morbidity. Blood cultures and vaginal swabs are other diagnostic tests for chorioamnionitis but the supportive evidence for both is limited and some recommendations suggest that vaginal swabs should not be used in cases of preterm prelabor rupture of membranes (Czikk 2011).
Like clinical chorioamnionitis, the case definition of histological chorioamnionitis varies between studies (Holzman 2007), but generally can be defined as acute inflammatory changes on the placenta's membrane roll and chorionic plate (Yoon 2001). Diagnosis is made based on microscopic examination of placental and chorioamnionic specimens (Tita 2010).
Chorioamnionitis is most frequently caused by bacteria ascending from the lower genital tract and is predominantly seen in instances of rupture of the membrane, but can occur in intact membranes (Fahey 2008). The infection can also be caused by blood‐borne or transplacental infection, and transuterine infection from invasive procedures such as amniocentesis or chorionic villus sampling, but these routes tend to be less common (Edwards 2005; Fahey 2008).
Chorioamnionitis is generally a polymicrobial infection with most cases having two detectable pathogens but it can be caused by viral and in rare instances, fungal agents (Czikk 2011). The common organisms found in amniotic fluid are Mycoplasma hominis, Ureaplasma urealyticum (Tita 2010) but other pathogens include Chlamydia trachomatis, Neisseria gonorrhoeae, Tichomonas vaginalis, anaerobic Gram‐negative bacilli like Bacteroides and Gardnerella vaginalis, Escherichia coli, anaerobic streptococci and streptococci group B (Czikk 2011; Edwards 2005).
The differential diagnosis of chorioamnionitis includes epidural‐associated fever and other extrauterine and non‐infectious conditions. An epidural‐associated fever may be considered for intrapartum patients with epidurals and a low grade fever but without maternal or fetal tachycardia or other clinical symptoms. Fever and abdominal pain are symptoms of extrauterine infectious including urinary tract infection, influenza, appendicitis and pneumonia. Abdominal pain without a fever may indicate a non‐infectious condition including thrombophlebitis, round ligament pain, colitis, connective tissue disorder and placental abruption (Tita 2010).
Risk factors for developing chorioamnionitis include being in active labor for a long period of time, duration of rupture of membrane and internal monitoring (Newton 1989), meconium staining of amniotic fluid, a high number of digital vaginal examinations (Seaward 2005), nulliparity, African American ethnicity, smoking and alcohol or drug abuse, epidural anesthesia, bacterial vaginosis and colonization with group B streptococcus or Ureaplasma bacterium (Tita 2010).
Preventing chorioamnionitis is better than treatment and some interventions have been shown to reduce the incidence of chorioamnionitis (Gibbs 2004). A 53% reduction in maternal morbidity due to chorioamnionitis and endometritis was seen in term pregnancies receiving an active management of labor program compared with traditional management (López‐Zeno 1992). For at‐term pregnancies complicated by prelabor rupture of the membranes (PROM), management by immediate oxytocin induction compared with conservative management showed fewer cases of chorioamnionitis (Mozurkewich 1997) and for preterm pregnancies with PROM, the use of broad‐spectrum antibiotics showed a decrease in chorioamnionitis (Kenyon 2010).
Description of the intervention
Some aspects of the timing of antibiotic therapy (intrapartum, postpartum, or combined intra‐ and postpartum), the antibiotic regimen, and the duration of antibiotic therapy have been evaluated in individual situations but not comprehensively (Fishman 2012). A previous Cochrane review (Hopkins 2002) identified two randomized controlled trials assessing the use of ampicillin and gentamicin for the treatment of intra‐amniotic infection versus postpartum treatment and ampicillin/gentamicin/clindamycin versus ampicillin/gentamicin; none of the outcomes showed a statistically significant difference between the different interventions.
How the intervention might work
Treatment for chorioamnionitis is usually with antibiotics that can be administered intrapartum or immediately postpartum. Since the infection could be caused by a wide variety of organisms treatment with broad spectrum of antibiotics is needed. The typically standard of care is clindamycin for anaerobic and gram‐positive bacteria and gentamicin for aerobic and gram‐negative bacteria (Mtira 1997).
Why it is important to do this review
Chorioamnionitis is a common infection that affects both mother and infant. Infant complications associated with chorioamnionitis include early neonatal sepsis, pneumonia, meningitis (Incerpi 2010), asthma (Getahun 2010), cerebral palsy (Wu 2000), intraventricular hemorrhage (Edwards 2005), and periventricular leukomalacia (Edwards 2005; Rocha 2007). Although fetal complications are more common, chorioamnionitis can also result in maternal morbidity such as pelvic infection and septic shock (Incerpi 2010). The risk for cesarean delivery is two to three times higher in women who have chorioamnionitis as well as three to four times greater for endomyometritis, wound infection, pelvic abscess, bacteremia and postpartum hemorrhage (Tita 2010).
A Cochrane review was conducted 10 years ago to study the effects of maternal antibiotic regimens for intra‐amniotic infection on maternal and perinatal morbidity and mortality (Hopkins 2002). The review identified two eligible studies and the conclusions were limited due to the small number of studies. A statistically significant difference was not seen in any of the outcomes and therefore the review was not able to make recommendations on timing of administration of the antibiotic treatment (intrapartum versus postpartum). Additionally, no Cochrane systematic review has evaluated studies in which antibiotic treatment for chorioamnionitis was given during the postpartum period. Currently, there is insufficient information to determine the most appropriate antimicrobial regimen for the treatment of intra‐amniotic infection; whether antibiotics should be continued during the postpartum period, which antibiotic regimen, or what treatment duration should be used. This review will update the review with new references and expand the scope of the review to include antibiotic regimens during the postpartum period.
Objectives
To assess the effects of administering antibiotics regimens for intra‐amniotic infection on maternal and perinatal morbidity and mortality and infection‐related complications.
Methods
Criteria for considering studies for this review
Types of studies
We will include all individually‐ or cluster‐randomized controlled trials comparing antibiotic treatment versus placebo or no treatment. We will also include trials that compare different antibiotics or regimens. Trials of intrapartum antibiotics for intra‐amniotic infection as well as trials comparing intrapartum with postpartum regimens will be included. We will exclude studies that used inappropriate methods of randomization as well as cross‐over trials and quasi‐randomized trials.
Types of participants
Women who experience intra‐amniotic infection. The diagnosis will be based on standard criteria (clinical/test). No limit will be placed on the gestational age.
Types of interventions
Trials will be included if they compare antibiotic treatment with placebo or no treatment (if applicable), treatment with different antibiotic regimens, or timing of the antibiotic therapy (intrapartum and/or postpartum). Therefore, the review will include trials evaluating intrapartum antibiotics, intra and postpartum antibiotic regimens and postpartum antibiotics.
Types of outcome measures
Primary outcomes
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Maternal and neonatal mortality
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Maternal and neonatal severe infection
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Duration of maternal and neonatal hospital stay
Secondary outcomes
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Need for additional antibiotic therapy
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Endometritis
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Febrile days
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Postpartum readmission for endometritis
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Failure of treatment
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Blood cultures and other diagnostic tests
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Number of doses of antibiotic(s)
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Infection related complications
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Adverse events (e.g. allergic reactions, antibiotic‐associated diarrhea, development of bacterial resistance)
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Suspension or cessation of breastfeeding
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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weekly searches of Embase;
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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, MEDLINE and Embase, 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 will search:
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CENTRAL (see: Appendix 1);
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MEDLINE (accessed via PubMed) (see: Appendix 2);
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Embase (accessed via Ovid) (see: Appendix 3);
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LILACS (from 1982 onwards) (see:Appendix 4) (Manríquez 2008);
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WHO International Clinical Trials Registry Platform (ICTRP) (see: Appendix 5).
Searching other resources
We also will check the reference lists of all the trials identified by the above methods and contact leading researchers to obtain additional published and unpublished trials.
We will not apply any language restrictions.
Data collection and analysis
Selection of studies
Two review authors will independently assess for inclusion the potential studies identified as a result of the search strategy. Disagreements will be resolved through discussion or, if required, the third review author will be consulted.
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 the third review author. We will enter data into Review Manager software (RevMan 2012) 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 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 randomization; 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 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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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 randomization);
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unclear risk of bias.
(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 Handbook(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 standardized 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 standard errors using the methods described in the Handbook using an estimate of the intracluster 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‐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 sensitivity analysis to investigate the effects of the randomization unit.
Other unit of analysis issues
Studies with multiple intervention groups will be dealt with as recommended in the Cochrane Handbook for Systematic Intervention Reviews (Higgins 2011). Each intervention arm will be separately compared with another.
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 randomized to each group in the analyses, and all participants will be analyzed 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 randomized minus any participants whose outcomes are known to be missing.
Assessment of heterogeneity
We will test for heterogeneity between trials using the T2, I² and Chi² statistics. We will regard heterogeneity as substantial if an I2 is greater than 50% and either a T2 is greater than zero, or there is a low P value (less than 0.10) in the Chi² test for heterogeneity. We will explore the heterogeneity by subgroup analysis. We will use the random‐effects meta‐analysis as an overall summary if substantial heterogeneity is found (Higgins 2011).
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 2012). 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 (Higgins 2011).
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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Gestational age (preterm versus term).
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Women who were or were not in labor.
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Women having vaginal versus instrumental or cesarean delivery.
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Women in whom membranes were or were not intact.
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By study design (cluster‐randomized trials versus individually‐randomized controlled trials).
Subgroup analyses will be restricted to the following primary outcomes.
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Maternal and/or neonatal mortality.
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Maternal and/or neonatal severe infection.
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Duration of maternal and/or neonatal hospital stay.
We will assess subgroup differences by interaction tests available within RevMan (RevMan 2012). We will report the results of subgroup analyses quoting the χ2 statistic and P value, and the interaction test I² value.
Sensitivity analysis
Explicit judgments will be made as to whether the studies are at high risk of bias (low versus unclear or high for sequence generation, allocation concealment and blinding domains) according to the criteria in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). The likely magnitude and direction of the bias and the likely impact on the findings will be assessed. Sensitivity analysis will be undertaken using the following outcomes.
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Maternal and/or neonatal mortality.
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Maternal and/or neonatal severe infection.
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Duration of maternal and/or neonatal hospital stay.
