Mechanical dilatation of the cervix at non‐labour caesarean section for reducing postoperative morbidity
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To determine the effects of mechanical dilatation of the cervix during elective/non‐labour cesarean section on postoperative morbidity.
Background
Description of the condition
Elective or non‐labour caesarean section has increased in developed and developing countries due to the indication of repeated caesarean or breech presentation (Chanthasenanont 2007; Lydon‐Rochelle 2006; Swende 2007; van Roosmalen 1995). Rate of vaginal births after caesarean section is still less common practice in developing countries (Chanrachakul 2000; van der Walt 1994).
Febrile morbidity and anaemia and/or haemorrhage of elective caesarean section (caesarean section before labour) was lower than that of emergency caesarean section (after labour) for term breech (1.5% versus 2.3% and 5.7% versus 7.0%, respectively) (Krebs 2003). Likewise, postpartum haemorrhage was reported in 4.84% in elective and 6.75% in non‐elective caesarean sections (Magann 2005). Although the morbidity in non‐labour caesarean section was low, it showed increasing of wound infection and febrile morbidity compared to induction of labour, especially in nulliparous women (Allen 2006). In addition, planned caesarean section increased the overall risk of severe morbidity, major puerperal infection, wound disruption, wound haematoma, haemorrhage requiring hysterectomy, any hysterectomy, or other complications such as anaesthetic complications, cardiac arrest, or thromboembolism (Liu 2007).
Description of the intervention
A woman's cervix is firm and undilated at the beginning of pregnancy, but progressive remodeling occurs during gestation until the cervix is soft at term, especially the nulliparous cervix (Myers 2008). The progressive dilatation of the cervix needs uterine contraction during labour. A mechanical dilatation of the cervix at caesarean section is defined as an artificial dilatation of the cervix performed by finger, sponge forceps or other instruments at non‐labour caesarean section.
How the intervention might work
Some obstetricians believe that the cervix of women at non‐labour caesarean section is undilated and might cause obstruction of blood or lochia drainage, leading to postpartum haemorrhage and endometritis from collection of lochia or debris. The dilatation of cervix helps the drainage of blood during postpartum, reducing intrauterine infection or the risk of postpartum haemorrhage. To avoid this problem, some obstetricians routinely dilate the cervix from above during an elective/non‐labour caesarean section using finger, sponge forceps or other instruments. A comparative study at Mir Hosseini Hospital, Shiraz, Iran showed lower incidence of postoperative endometritis in women who underwent elective caesarean section with cervix dilated by a ring forceps (5.7%) than in those without cervix dilatation (16.8%) (Malkamy 1995). Collection of blood in the intrauterine cavity and distended uterus in women after elective caesarean section due to repeated sections was reported in two cases, and dilatation and evacuation were needed for treatment (Bollapragada 2002). However, this has not been proven in clinical trials. In contrast, mechanical cervical dilatation using sponge forceps or a finger during caesarean section may result in contamination by vaginal microorganisms during dilatation and increase the risk of infection or cervical trauma. A study found that a positive culture at the lower uterine segment predicted postpartum endometritis (Sherman 1999).
Why it is important to do this review
The information currently available about the advantages of cervical dilatation at caesarean section is inconclusive. Therefore, evidence to support the effectiveness or safety of cervical dilatation at caesarean section is needed.
Objectives
To determine the effects of mechanical dilatation of the cervix during elective/non‐labour cesarean section on postoperative morbidity.
Methods
Criteria for considering studies for this review
Types of studies
All randomised controlled trials, including quasi‐randomised trials, comparing cervical dilatation during caesarean section to no intervention.
Types of participants
All women underwent non‐labour/elective caesarean section for any indications, regardless of degree of cervical dilatation.
Types of interventions
Mechanical dilatation of the cervix using a finger, sponge forceps or other instrument during non‐labour caesarean section versus no mechanical dilatation.
Types of outcome measures
Primary outcomes
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Postpartum haemorrhage: estimated blood loss greater than 1000 ml immediately or delayed after caesarean section.
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Need for blood transfusion: blood transfusion given during or within 24 hours after caesarean section.
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Secondary postpartum haemorrhage: late vaginal bleeding within six weeks postpartum.
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Haematocrit or haemoglobin level: levels of haematocrit or haemoglobin at postoperative period, or the change of level compared to preoperative or baseline level.
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Febrile morbidity: temperature of 38 degrees or higher at any two of the first 10 days postpartum, exclusive of the first 24 hours with unknown causes.
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Endometritis: febrile morbidity due to intrauterine infection, clinically diagnosed by fever, uterine tenderness and/or foul‐smelling discharge.
Secondary outcomes
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Cervical trauma: signs of vaginal bleeding due to the tear of cervical tissue from mechanical dilatation.
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Uterine subinvolution: delayed or absent involution of the uterus during the postpartum period.
Search methods for identification of studies
Electronic searches
We will contact the Trials Search Co‐ordinator to search the Cochrane Pregnancy and Childbirth Group’s Trials Register.
The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co‐ordinator and contains trials identified from:
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quarterly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
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weekly searches of MEDLINE;
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handsearches of 30 journals and the proceedings of major conferences;
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weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.
Details of the search strategies for CENTRAL and MEDLINE, the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service can be found in the ‘Specialized Register’ section within the editorial information about the Cochrane Pregnancy and Childbirth Group.
Trials identified through the searching activities described above are each assigned to a review topic (or topics). The Trials Search Co‐ordinator searches the register for each review using the topic list rather than keywords.
We will not apply any language restrictions. We will include trials reported as abstracts. If the data in abstracts are not sufficient, we will contact the authors for more information and data.
Data collection and analysis
We will use the methods as described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008).
Selection of studies
Tippawan Liabsuetrakul (TL) and Krantarat Peeyananjarassri (KP) 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.
Data extraction and management
We will design a form to extract data. For eligible studies,TL and KP will independently extract data using the agreed form. We will resolve discrepancies through discussion. We will enter data into Review Manager software (RevMan 2008) and check for accuracy.
When information regarding any of the above is unclear, we will attempt to contact authors of the original reports to provide further details.
Assessment of risk of bias in included studies
TL and KP will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008). We will resolve any disagreement by discussion.
(1) Sequence generation (checking for possible selection bias)
We will describe for each included study the methods used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.
We will assess the methods as:
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adequate (any truly random process, e.g. random number table; computer random number generator);
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inadequate (any non‐random process, e.g. odd or even date of birth; hospital or clinic record number);
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unclear.
(2) Allocation concealment (checking for possible selection bias)
We will describe for each included study the method used to conceal the allocation sequence in sufficient detail and determine whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.
We will assess the methods as:
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adequate (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
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inadequate (open random allocation; unsealed or non‐opaque envelopes; alternation; date of birth);
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unclear.
(3) Blinding (checking for possible performance bias)
We will describe for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We will judge studies at low risk of bias if they were blinded, or if we judge that the lack of blinding could not have affected the results. We will assess blinding separately for different outcomes or classes of outcomes.
We will assess the methods as:
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adequate, inadequate or unclear for participants;
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adequate, inadequate or unclear for personnel;
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adequate, inadequate or unclear for outcome assessors.
(4) Incomplete outcome data (checking for possible attrition bias through withdrawals, dropouts, protocol deviations)
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, 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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adequate (less than 20% of incomplete outcome data);
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inadequate (20% or more of incomplete outcome data);
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unclear (unidentified missing outcome data).
(5) Selective 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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adequate (where it is clear that all of the study’s pre‐specified outcomes and all expected outcomes of interest to the review have been reported);
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inadequate (where not all the study’s pre‐specified outcomes have been reported; one or more reported primary outcomes were not pre‐specified; outcomes of interest are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported);
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unclear.
(6) Other sources of bias
We will describe for each included study any important concerns we have about other possible sources of bias.
We will assess whether each study was free of other problems that could put it at risk of bias:
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yes;
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no;
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unclear.
(7) Overall risk of bias
We will make explicit judgements about whether studies are at high risk of bias, according to the criteria given in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008). With reference to (1) to (6) above, we will assess the likely magnitude and direction of the bias and whether we consider it is likely to impact on the findings. We will explore the impact of the level of bias through undertaking sensitivity analyses ‐ see 'Sensitivity analysis'.
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.
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. 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 use the I² statistic to measure heterogeneity among the trials in each analysis with a cut‐off point of 50%. If we identify substantial heterogeneity we will explore it by prespecified subgroup analysis.
Assessment of reporting biases
Where we suspect reporting bias (see 'Selective reporting bias' above), we will attempt to contact study authors asking them to provide missing outcome data. Where this is not possible, and the missing data are thought to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results by a sensitivity analysis. We will also explore possible publication bias.
Data synthesis
We will carry out statistical analysis using the Review Manager software (RevMan 2008). We will use fixed‐effect inverse variance meta‐analysis for combining data where trials are examining the same intervention, and the trials’ populations and methods are judged sufficiently similar. Where we suspect clinical or methodological heterogeneity between studies sufficient to suggest that treatment effects may differ between trials, we will use random‐effects meta‐analysis.
If substantial heterogeneity is identified in a fixed‐effect meta‐analysis, we will note this and repeat the analysis using a random‐effects method.
Subgroup analysis and investigation of heterogeneity
We plan to carry out the following subgroup analyses:
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nulliparous woman versus multiparous woman;
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no prior caesarean section versus repeat caesarean section;
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no premature rupture of membrane versus premature rupture of membrane.
We will use the following outcomes in subgroup analysis:
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postpartum haemorrhage;
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need of blood transfusion;
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secondary postpartum haemorrhage;
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haematocrit or haemoglobin level;
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febrile morbidity;
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endometritis.
For fixed‐effect meta‐analyses we will conduct planned subgroup analyses classifying whole trials by interaction tests as described by Deeks 2001. For random‐effects meta‐analyses we will assess differences between subgroups by inspection of the subgroups’ confidence intervals; non‐overlapping confidence intervals indicate a statistically significant difference in treatment effect between the subgroups.
Sensitivity analysis
We plan to perform sensitivity analysis if we detect heterogeneity. Sensitivity analyses include:
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omission of studies at high risk of bias, such as quasi‐randomised studies;
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repeating analyses using fixed‐ or random‐effects;
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omission of studies published as abstracts or non‐peer reviewed publications.
We will use the following outcomes in sensitivity analysis:
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postpartum haemorrhage;
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need of blood transfusion;
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secondary postpartum haemorrhage;
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haematocrit or haemoglobin level;
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febrile morbidity;
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endometritis.
