Postoperative vaginal swabbing versus no vaginal swabbing following caesarean section for preventing maternal infection
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the effect of postpartum vaginal swabbing on maternal infection following caesarean section.
Background
Description of the condition
Endometritis is the most common cause for puerperal sepsis and remains a leading cause of preventable morbidity and mortality worldwide (Say 2014). Peurperal bacterial infections account for 1/10th of global maternal deaths, with the incidence being highest in low‐income countries (15% of maternal mortality) (Van Dillen 2010).
Postpartum endometritis is defined as infection of the uterus within six weeks of giving birth and results from ascending infection from the vagina. If untreated, the infection can spread to the parametrium and beyond. Outcomes can be as fatal as sepsis, pulmonary emboli and death or as long term and disabling as chronic pelvic pain and infertility (Mackeen 2015).
The symptoms and signs of endometritis may include the following.
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Fever > 38 °C
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Chills/rigours
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Malaise/lethargy
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Lower abdominal pain/tender uterus
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Purulent, foul‐smelling, blood‐stained vaginal discharge (lochia)
Endometritis may also include light vaginal bleeding and shock.
Investigations will often include bacterial cultures (blood, vaginal swabs), inflammatory markers and ultrasound imaging as an adjunct. Other sources of fever (urine, breast, lungs, blood clots) must also be ruled out (Dolea 2003; RCOG 2012).
Description of the intervention
At the conclusion of a caesarean section, most practitioners seek to empty major clots out of the vagina to prevent postpartum haemorrhage in the recovery room and to accurately assess total blood loss (de Costa 2006; Maxwell 2004).
There is no standardised practice as to how to clear vaginal clots and cleanse postoperatively. Some practitioners insert gauze swabs vaginally to remove residual clots, others perform uterine fundal massage without inserting anything into the vagina (de Costa 2006; Maxwell 2004).
How the intervention might work
Examinations and procedures in the lower vagina may enable microbes to ascend the genital tract and cause infection (Alexander 2010; Downe 2013; Newton 1993). Organisms in the vaginal flora differ between the lower and upper vagina, particularly given the perineal and anal flora associated with the lower vagina. This contributes to the polymicrobial nature of endometritis. Infective microbes can be endogenous from the vagina or exogenous from unsterile products and examiners hands.
The hypothesis is that avoidance of inserting a swab into the vagina postoperatively can prevent ascending infection.
Why it is important to do this review
The World Health Organization (WHO) has renewed calls for further research into peripartum infection prevention (Gulmezoglu 2015 (WHO)). In the 19th century, sepsis caused 50% of maternal deaths. The basic intervention of hand hygiene reduced this dramatically. Since that time, despite the advent of antibiotics, puerperal sepsis still causes an estimated 75,000 maternal deaths per year (Van Dillen 2010). The United Nations Millennium Development Goals had aimed for a reduction in maternal mortality of 75% between 1990 and 2015. Whilst there was an increase in skilled birth attendants, the goal was not reached. For example, in sub‐Saharan Africa the risk of peripartum death is 1:38 (compared to 1:3700 in developed nations). Increasing antimicrobial resistance, particularly in sub‐Saharan Africa, has caused significant limitations in treatment options for established infection. Accordingly, renewed attention towards preventative infection control measures and hygiene is warranted (Essack 2017; Halfon 2016; Leopold 2014; Tadesse 2017). As a result, maternal mortality remains on the world agenda as an ongoing concern (Gulmezoglu 2015 (WHO)).
Caesarean section remains the single most important risk factor for postpartum endometritis. Endometritis is up to 10 times more likely after caesarean section compared to vaginal birth, occurring in up to 27% of caesarean births compared to less than 3% of vaginal births (Calhoun 1995; Leth 2009; Mackeen 2015). This disparity remains despite the use of prophylactic antibiotics at caesarean section (Burrows 2004; Fernandez 1993). Compounding this, is increasing caesarean section rates, particularly those due to questionable clinical indication (Gibbons 2010; Van Dillen 2010).
Whilst research has directly addressed infection control antecedent to birth (number of vaginal examinations (Ohlsson 2014; Seaward 1997; Soper 1996), antiseptic cleansing prior to caesarean section (Haas 2018), avoiding pubic shaving (Basevi 2014), use of prophylactic antibiotics (Smaill 2014), and intraoperative techniques (suture selection, closure techniques, mode of placental delivery) (CORONIS 2013), little attention has been drawn to postpartum infection control behaviours. Without considering the vagina’s infective potential after birth, sepsis cannot be addressed in the puerperium in its totality (Gulmezoglu 2015 (WHO); Lumbiganon 2014).
Objectives
To assess the effect of postpartum vaginal swabbing on maternal infection following caesarean section.
Methods
Criteria for considering studies for this review
Types of studies
We will include all published and unpublished randomised, quasi‐randomised and cluster‐randomised controlled trials. We will also include conference abstracts of trials assessing the effects of postpartum vaginal swabbing for the prevention of maternal infection following caesarean section. Cross‐over trials will be excluded.
Types of participants
Pregnant women undergoing caesarean section.
Types of interventions
The intervention will include vaginal swabbing, with or without an antiseptic solution immediately postoperative following a caesarean section. The comparison will be no vaginal swabbing immediately postoperative following a caesarean section.
Types of outcome measures
Primary outcomes
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Maternal endometritis (as defined by trialists)
Secondary outcomes
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Postpartum haemorrhage (as defined by trialists)
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Postpartum pyrexia (as defined by trialists)
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Postoperative blood transfusion
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Maternal mortality
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Re‐admission resulting from infection
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Women's satisfaction with care (as defined by trialists)
Search methods for identification of studies
The following methods section of this protocol is based on a standard template used by Cochrane Pregnancy and Childbirth.
Electronic searches
We will search Cochrane Pregnancy and Childbirth’s Trials Register by contacting their Information Specialist.
The Register is a database containing over 25,000 reports of controlled trials in the field of pregnancy and childbirth. It represents over 30 years of searching. For full current search methods used to populate Pregnancy and Childbirth’s Trials Register including the detailed search strategies for CENTRAL, MEDLINE, Embase and CINAHL, the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service, please follow this link.
Briefly, the Cochrane Pregnancy and Childbirth’s Trials Register is maintained by their Information Specialist 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 (Ovid);
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weekly searches of Embase (Ovid);
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monthly searches of CINAHL (EBSCO);
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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.
Search results are screened by two people and the full text of all relevant trial reports identified through the searching activities described above is reviewed. Based on the intervention described, each trial report is assigned a number that corresponds to a specific Pregnancy and Childbirth review topic (or topics), and is then added to the Register. The Information Specialist searches the Register for each review using this topic number rather than keywords. This results in a more specific search set that will be fully accounted for in the relevant review sections (Included, Excluded, Awaiting Classification or Ongoing).
In addition, we will search ClinicalTrials.gov and the WHO International Clinical Trials Registry Platform (ICTRP) for unpublished, planned and ongoing trial reports using the search methods detailed in Appendix 1.
Searching other resources
We will search the reference lists of retrieved studies.
We will not apply any language or date restrictions.
Data collection and analysis
The following methods section of this protocol is based on a standard template used by Cochrane Pregnancy and Childbirth.
Selection of studies
Two 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 or, if required, we will consult a third review author.
We will create a study flow diagram to map out the number of records identified, included and excluded.
Data extraction and management
We will design a form to extract data that will be piloted. 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 seek external advice. We will enter data into Review Manager software (RevMan 2014) 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. Information regarding source of trial funding, trialists declarations of interest and trial dates will be extracted.
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 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), we will consider attrition in excess of 20% to be indicative of a high risk of bias;
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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 which may include the trial stopping before anticipated, imbalance between groups at baseline or claims of fraudulence associated with study.
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.
Assessment of the quality of the evidence using the GRADE approach
The quality of the evidence will be assessed using the GRADE approach as outlined in the GRADE handbook in order to assess the quality of the body of evidence relating to the following outcomes for the main comparisons.
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Maternal endometritis (as defined by trialists)
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Postpartum haemorrhage (as defined by trialists)
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Postpartum pyrexia (as defined by trialists)
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Postoperative blood transfusion
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Maternal mortality
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Re‐admission resulting from infection
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Women's satisfaction with care (as defined by trialists)
We will use the GRADEpro Guideline Development Tool to import data from Review Manager 5.3 (RevMan 2014) in order to create ’Summary of findings’ tables. A summary of the intervention effect and a measure of quality for each of the above outcomes will be produced using the GRADE approach. The GRADE approach uses five considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of the body of evidence for each outcome. The evidence can be downgraded from 'high quality' by one level for serious (or by two levels for very serious) limitations, depending on assessments for risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates or potential publication bias.
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 sample sizes using the methods described in the Handbook [Section 16.3.4 or 16.3.6] 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‐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 sensitivity analysis to investigate the effects of the randomisation unit.
Trials with multiple arms
For included multi‐arm trials, we will use the methods described in the Cochrane Handbook for Systematic Reviews of Interventions to overcome possible unit‐of analysis errors (Higgins 2011), by combining groups to make a single pair‐wise comparison (where appropriate), or by splitting the ’shared’ group into two (or more) groups with smaller sample sizes, and including the two (or more) comparisons.
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.
Assessment of heterogeneity
We will assess statistical heterogeneity in each meta‐analysis using the Tau², I² and Chi² statistics. We will regard heterogeneity as substantial if an I² is greater than 30% and either a Tau² 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 2014). 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 of the 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 Tau² 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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In labour versus not in labour
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Pre‐existing rupture of membranes versus membranes intact
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Preoperative antiseptic vaginal cleansing versus no preoperative antiseptic vaginal cleansing
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Antiseptic swabbing versus non‐antiseptic swabbing
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Postoperative antibiotics versus no postoperative antibiotics
Subgroup analysis will be restricted to the review's primary outcomes: maternal endometritis (as defined by trialists).
We will assess subgroup differences by interaction tests available within RevMan (RevMan 2014). We will report the results of subgroup analyses quoting the Chi2 statistic and P value, and the interaction test I² value.
Sensitivity analysis
If there is evidence of significant heterogeneity, we will explore this by carrying out sensitivity analysis for the review's primary outcome. We will explore the effects of trial quality assessed by sequence generation, concealment of allocation, and inadequate blinding, by omitting trials rated as ’high risk of bias’ or ’unclear risk of bias’ for any one or more of these sources of bias, to assess whether this makes any difference to the overall result. We will perform a sensitivity analysis to investigate the effect of the randomisation unit where we combine data from cluster‐RCTs and individually‐randomised trials.
