Timing of prophylactic antibiotics for preventing postpartum infectious morbidity in women undergoing cesarean delivery
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the effects of antibiotics given prior to skin incision compared with administration after cord clamping in newborns and women undergoing caesarean section.
Background
Cesarean birth is one of the most common surgical procedures performed worldwide. Internationally, approximately 15% of all births occur by cesarean birth, with Latin America and the Caribbean demonstrating rates as high as 29.2% (Betrán 2007). In the United States, there were an estimated 1.37 million cesarean births in 2007, accounting for 31.8% of all births (Hamilton 2007). Worldwide, infectious morbidity, consisting primarily of endomyometritis and wound infection, occurs in approximately 5% to 10% of cesarean births (Henderson 1995; Olsen 2008; Opoien 2007; Yokoe 2001). As the cesarean birth rate continues to rise in most developed countries, postpartum infectious morbidity will become an even more significant problem. Therefore, measures aimed at decreasing postpartum infectious morbidity are an important area of focus.
Description of the condition
Surgical site infections are the most common nosocomial infections among surgical patients, accounting for 38% of all such infections (Mangram 1999). The United States National Nosocomial Infections Surveillance (NNIS) System reported a surgical site infection rate of 2.71% for cesarean births in the absence of risk factors for infection and 7.53% for high‐risk cesarean births between 1992 and 2004 (NNIS System 2004). Infectious complications after cesarean birth include, but are not limited to, cellulitis, endomyometritis, urinary tract infection, pelvic abscess, septic shock, septic pelvic thrombophlebitis, necrotizing fasciitis and pneumonia.
The risk of postpartum infection after cesarean birth is nearly five‐fold that of vaginal birth (Leth 2009). Many interventions have been studied in an attempt to decrease the incidence of surgical site infections after cesarean birth: prophylactic antibiotics, surgical hand antisepsis, skin preparation methods, surgical techniques, subcutaneous drain placement, and postoperative surveillance (Barwolff 2006; Edi‐Osagie 1998; Hellums 2007; Lorenz 1988; Magann 1993; Starr 2005; Ventolini 2004).
Description of the intervention
In 2008, the World Health Organization established a 'Safe Surgery Saves Lives' campaign. An intra‐operative surgical checklist was developed to reduce post‐surgical infection as well as other associated morbidities. This checklist acknowledged the evidence‐based value of antibiotic prophylaxis administration 60 minutes prior to skin incision (Soar 2009).
The obstetric population poses a unique challenge for antibiotic prophylaxis as there is known transplacental delivery of antibiotics to the fetus. Traditionally, the administration of prophylactic antibiotics has been withheld until after umbilical cord clamping during cesarean birth in order to avoid transfer of antibiotics to the fetus. The theoretical concerns of neonatal antibiotic exposure include the masking of neonatal infection, interference with sepsis workup and the selection of antibiotic‐resistant bacterial strains in both neonatal colonization and infection (Cunningham 1983). Due to these theoretical risks, the Centers for Disease Control and Prevention's 'Guideline for Prevention of Surgical Site Infection, 1999' stated with high level evidence, that for high‐risk cesarean birth, prophylactic antimicrobial agents should be given immediately after umbilical cord clamping, rather than preoperatively (Mangram 1999).
How the intervention might work
The general surgery tenet of antibiotic prophylaxis was born out of animal studies that demonstrated maximum suppression of infection when adequate tissue antibiotic levels were present at the time of microbial contamination (Burke 1961). These findings were confirmed in clinical practice: less surgical‐wound infections were noted when antibiotics were administered within two hours before skin incision as compared to when antibiotics were administered postoperatively (Classen 1992). One of the most commonly used antibiotics for cesarean birth is cefazolin. Pharmacokinetic studies of cefazolin demonstrate that mean inhibiting concentration levels for group B streptococcus are attained in maternal, fetal and amniotic fluid samples within 30 minutes of administration (Fiore 2001). It has also been demonstrated that bactericidal levels against group B streptococcus are achieved in maternal, fetal and amniotic fluid samples within five minutes of ampicillin administration (Bloom 1996). The current CDC recommendation to withhold antibiotic prophylaxis until after cord clamping contradicts the basic principle of surgical prophylaxis, i.e., to attain bactericidal concentration in the tissues prior to skin incision.
Why it is important to do this review
The benefit of using prophylactic antibiotics in order to prevent surgical site infection has been demonstrated in the obstetric literature. A 2010 Cochrane review concluded that antibiotic prophylaxis, as compared to no prophylaxis, was associated with a reduction in the incidence of febrile morbidity, wound infection, endomyometritis and other serious maternal infectious complications (Smaill 2010). This review also found that infectious complications were similar despite whether the antibiotics were administered prior to or after umbilical cord clamping.
Several recent studies have evaluated timing of the administration of prophylactic antibiotics, specifically administration prior to skin incision versus after umbilical cord clamping. A meta‐analysis comparing the administration of prophylactic antibiotics prior to skin incision versus after clamping of the umbilical cord concluded that pre‐incision antibiotic prophylaxis for cesarean birth not only decreased the incidence of postpartum endomyometritis and total infectious morbidities, but also did not adversely affect neonatal outcomes (Costantine 2008). Several institutions have evaluated the impact of protocol changes in the timing of perioperative antibiotic administration on post‐operative infectious complications, and have found decreased infectious complications with antibiotics given prior to skin incision compared to after cord clamping (Kaimal 2008; Owens 2009).
In response to the recent attention on the timing of prophylactic antibiotics in cesarean birth, the American College of Obstetricians and Gynecologists (ACOG) recommended antimicrobial prophylaxis for all cesarean births, and further stated that prophylaxis should be administered within 60 minutes of the start of the cesarean delivery (ACOG 2010). These recommendations are consistent with recommendations from the National Surgical Infection Prevention Project (Bratzler 2005).
Given the continued rise in cesarean birth rate and the relatively high risk of surgical site infections after cesarean birth as compared to other surgical procedures (NNIS System 2004), measures must be taken to prevent surgical site infections. Prior Cochrane reviews have looked at the maternal morbidity associated in relation to administration of prophylactic antibiotics at time of cesarean section (Smaill 2010) and various antibiotic regimens for cesarean section (Hopkins 1999). This review will focus on studies comparing antibiotic prophylaxis administered prior to skin incision compared to administration after umbilical cord clamping for cesarean birth. We will compare infectious morbidity and address the concern for neonatal harm.
Objectives
To assess the effects of antibiotics given prior to skin incision compared with administration after cord clamping in newborns and women undergoing caesarean section.
Methods
Criteria for considering studies for this review
Types of studies
Randomized controlled trials only. We will exclude quasi‐randomized studies.
Types of participants
Pregnant women who have undergone cesarean delivery and received prophylactic antibiotics.
Types of interventions
Prophylactic antibiotic administration for cesarean birth 0 to 30 and 30 to 60 minutes prior to skin incision versus prophylactic antibiotic administration for cesarean birth after neonatal umbilical cord clamping. If we discover a study that includes women who receive antibiotics after skin incision but before cord clamping, we will exclude it from this analysis.
Types of outcome measures
Primary outcomes
Composite maternal postpartum infectious morbidity, including serious infectious complication including bacteremia, septic shock, endomyometritis, wound infection, necrotizing fasciitis or death attributed to infection.
Secondary outcomes
Maternal
1. Maternal mortality.
2. Maternal postpartum infection:
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endomyometritis;
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wound infection;
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urinary tract infection;
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sepsis;
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pelvic abscess;
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septic pelvic thrombophlebitis;
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upper respiratory infection (pneumonia);
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length of hospital stay;
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Intensive care unit (ICU) admission;
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cost of antibiotics;
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antibiotic related adverse events (e.g. anaphylaxis);
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fever.
3. Placental transfer of antibiotics.
4. Breastfeeding.
Neonatal outcomes
1. Neonatal mortality.
2. Neonatal morbidity:
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sepsis;
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infection with resistant organism;
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fever;
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admission to ICU;
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length of ICU stay;
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neonatal work‐up for infection;
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antibiotic 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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quarterly 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 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. We will include abstracts in the search. We will not include crossover trials and cluster‐randomized trials in the search.
Data collection and analysis
Selection of studies
All review authors 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 of the whole group.
Data extraction and management
We will design a form to extract data. For eligible studies, all authors will review a portion of the studies and will extract the data using the agreed form. We will resolve discrepancies through group discussion. 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
All 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 group discussion.
(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) or
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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 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 prespecified; 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;
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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
We will use trials of standard design. We will not include cross‐over trials and cluster‐randomized trials.
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 analyze all participants 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 assess statistical heterogeneity in each meta‐analysis using the T², I² and Chi² statistics. We will regard heterogeneity as substantial if I² is greater than 30% and either 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, and use formal tests for funnel plot asymmetry. For continuous outcomes we will use the test proposed by Egger 1997, and for dichotomous outcomes we will use the test proposed by Harbord 2006. If asymmetry is detected in any of these tests or 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. We will treat the random‐effects summary 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, we will present the results as the average treatment effect with its 95% confidence interval, 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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all outcomes by type of prophylactic antibiotics administered;
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labouring versus non‐labouring patients;
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diagnosis of chorioamnionitis prior to cesarean on antibiotic treatment versus diagnosis of chorioamnionitis prior to cesarean not on antibiotic treatment;
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women on antibiotic treatment for other indications versus women only receiving antibiotic prophylaxis in relation to cesarean section;
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timing of antibiotics prior to skin incision by type of antibiotic and interval to incision (e.g. less than 30 minutes to skin incision versus greater than 30 minutes to skin incision).
We will use the combined primary outcome of maternal endomyometritis and wound infection in subgroup analysis.
For fixed‐effect inverse variance meta‐analyses we will assess differences between subgroups by interaction tests. For random‐effects and fixed‐effect meta‐analyses using methods other than inverse variance, 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 to identify trials at low risk of bias in regards to the primary outcomes. We will determine exact tests during the study review process.
