Criteria for considering studies for this review
Types of studies
All published, unpublished, and ongoing randomised controlled trials with reported data, that compared outcomes for mothers and/or babies who were randomised to a planned elective repeat caesarean birth with outcomes for mothers and/or babies who had a planned vaginal birth where a prior birth was by caesarean section.
Types of participants
Women with one or more prior caesarean section (regardless of indication for primary caesarean birth, number of caesarean births, type of uterine scar, or method of closure of uterine incision) who were planning a vaginal birth in a subsequent pregnancy.
Types of interventions
Planned elective repeat caesarean birth versus planned vaginal birth.
Types of outcome measures
Death or serious maternal morbidity (defined by trial authors)
Death or serious infant morbidity (defined by trial authors)
Outcome measures for the woman
Instrumental vaginal birth
Caesarean birth for fetal distress
Uterine rupture (defined as clinically significant rupture involving the full thickness of the uterine wall and requiring surgical repair)
Uterine scar dehiscence (defined as clinically asymptomatic disruption of the uterus that is discovered incidentally at surgery)
Haemorrhage (blood loss greater than 500 mL and/or requiring blood transfusion)
Evacuation of the uterus after childbirth for postpartum haemorrhage or retained placental tissue
Hysterectomy for any complications resulting from birth
Vulval or perineal haematoma requiring evacuation
Deep vein thrombosis or thrombophlebitis requiring anticoagulant therapy
Pulmonary embolus requiring anticoagulant therapy
Pneumonia due to infection, aspiration or other causes
Adult respiratory distress syndrome
Wound infection (requiring prolongation of hospitalisation or readmission)
Damage to the bladder, bowel or ureter requiring surgical repair
Cervical laceration extending to the lower uterine segment or abnormal extension of the uterine incision
Occurrence of a fistula involving the genital tract and urinary or gastrointestinal tracts
Stroke (acute neurological deficit greater than 24 hours)
Any other serious maternal complication related to birth
Level of pain after birth
Outcome measures for the infant
Neonatal or perinatal death
Apgar score less than seven at five minutes
Admission to the neonatal intensive care unit (NICU)
Birth trauma (subdural or intracerebral haemorrhage, spinal cord injury, basal skull fracture, other fracture, peripheral nerve injury)
Seizures at less than 24 hours of age
Laceration to baby at time of birth
Altered level of consciousness
Use of mechanical ventilation
Any respiratory disease
Severe respiratory distress syndrome requiring oxygen (as defined by trialists)
Any oxygen requirement
Transient tachypnoea of the newborn
Use of tube feeding
Proven systemic infection treated with antibiotics within 48 hours of life
Maternal emotional well-being
Postnatal depression (defined as the number of women screening at risk of postnatal depression, in addition to mean depressive score, using the Edinburgh Postnatal Depression Scale (EPDS))
Maternal anxiety (defined the mean anxiety score as measured using the State Trait Anxiety Index (STAI))
Maternal quality of life (as defined by trialists)
Longer-term outcomes for the woman
Return to 'normal' activities
Health and well-being assessment
Symptoms related to pelvic floor damage
Need for operative pelvic floor repair
Relationship with partner and child(ren)
Future fertility (both voluntary and involuntary)
Development of placenta praevia or placenta accreta/percreta in subsequent pregnancies
Mode of birth in subsequent pregnancy
Longer-term outcomes for the child
Death after discharge from hospital
Disability in infancy
Disability in childhood
Measures of satisfaction include
Women's satisfaction with care
Women's preferences for care
Costs associated with planned elective repeat caesarean birth versus planned vaginal birth
Maternal postnatal length of stay
Neonatal length of stay
Costs associated with readmission of mother
Costs associated with readmission of baby
Outcomes would have been included in the analysis if data were available according to original treatment allocation and reasonable measures were taken to minimise observer bias. Only outcomes with available data would have appeared in the analysis tables. Data that were not prestated would have been extracted and reported. These would have been clearly labelled as such (not prespecified). The possibility has to be borne in mind that such outcomes would only have been reported because the difference between the groups, which is a result of chance, have reached conventional levels of statistical significance. In order to minimise the risk of bias, the conclusions would have been based solely only on the prestated outcomes.
Search methods for identification of studies
We searched the Cochrane Pregnancy and Childbirth Group's Trials Register (30 September 2013).
The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co-ordinator and contains trials identified from:
monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
weekly searches of MEDLINE;
weekly searches of Embase;
handsearches of 30 journals and the proceedings of major conferences;
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.
For details of additional author searching carried out in the initial version of the review, please see Appendix 1.
Searching other resources
We searched the reference lists of retrieved studies.
We did not apply any language restrictions.
Data collection and analysis
For the methods used when assessing the trials identified in the previous version of this review, see Dodd 2004.
For this update we used the following methods when assessing the reports identified by the updated search.
Selection of studies
Two review authors independently assessed for inclusion all the potential studies we identified as a result of the search strategy. We resolved any disagreement through discussion or, if required, we consulted a third person.
Data extraction and management
We designed a form to extract data. For eligible studies, at least two review authors extracted the data using the agreed form. We resolved discrepancies through discussion or, if required, we consulted a third person. We entered data into Review Manager software (RevMan 2012) and checked for accuracy.
When information regarding any of the above was unclear, we planned to contact authors of the original reports to provide further details.
Jodie Dodd and Caroline Crowther are the authors of one of the reports included in this review (Crowther 2012b). This study report was assessed by the other review authors.
Assessment of risk of bias in included studies
Two review authors independently assessed risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions ( Higgins 2011 ). We resolved any disagreement by discussion or by involving a third assessor.
(1) Random sequence generation (checking for possible selection bias)
We described 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 assessed the method as:
low risk of bias (any truly random process, e.g. random number table; computer random number generator);
high risk of bias (any non-random process, e.g. odd or even date of birth; hospital or clinic record number);
unclear risk of bias.
(2) Allocation concealment (checking for possible selection bias)
We described for each included study the method used to conceal allocation to interventions prior to assignment and assessed whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.
We assessed the methods as:
low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
high risk of bias (open random allocation; unsealed or non-opaque envelopes, alternation; date of birth);
unclear risk of bias.
(3.1) Blinding of participants and personnel (checking for possible performance bias)
We described for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We considered studies to be at low risk of bias if they were blinded, or if we judged that the lack of blinding would be unlikely to affect results. We assessed blinding separately for different outcomes or classes of outcomes.
We assessed the methods as:
low, high or unclear risk of bias for participants;
low, high or unclear risk of bias for personnel.
(3.2) Blinding of outcome assessment (checking for possible detection bias)
We described for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We assessed blinding separately for different outcomes or classes of outcomes.
We assessed methods used to blind outcome assessment as:
(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)
We described for each included study, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We have stated 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 was reported, or could be supplied by the trial authors, we planned to re-include missing data in the analyses undertaken.
We assessed methods as:
low risk of bias (e.g. no missing outcome data; missing outcome data balanced across groups);
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);
unclear risk of bias.
(5) Selective reporting (checking for reporting bias)
We described for each included study how we investigated the possibility of selective outcome reporting bias and what we found.
We assessed the methods as:
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);
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);
unclear risk of bias.
(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)
We described for each included study any important concerns we had about other possible sources of bias.
We assessed whether each study was free of other problems that could put it at risk of bias:
(7) Overall risk of bias
We made explicit judgements about whether studies were at high risk of bias, according to the criteria given in the Cochrane Handbook (Higgins 2011). With reference to (1) to (6) above, we assessed the likely magnitude and direction of the bias and whether we consider it likely to impact on the findings. We planned to explore the impact of the level of bias through undertaking sensitivity analyses - see Sensitivity analysis.
Measures of treatment effect
For dichotomous data, we presented results as summary risk ratio with 95% confidence intervals.
For continuous data, we used the mean difference if outcomes were measured in the same way between trials. In future updates, if appropriate, we will use the standardised mean difference to combine trials that measure the same outcome, but use different methods.
Unit of analysis issues
No cluster-randomised trials were included in this update.
In future updates, if identified, 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 Cochrane Handbook [Section 16.3.4] 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.
Dealing with missing data
For included studies, we noted levels of attrition. In future updates, if more studies are included, 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.
In future updates of this review, 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
In future updates, if more studies are included and data are available for meta-analysis, we will assess statistical heterogeneity in each meta-analysis using the Tau², I² and Chi² statistics. We will regard heterogeneity as substantial if the I² is greater than 30% and either the 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
In future updates, 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.
We carried out statistical analysis using the Review Manager software (RevMan 2012). However, we were unable to combine data as maternal and infant clinical outcomes were available from only one trial (Crowther 2012b). We planned to use fixed-effect meta-analysis for combining data where it was reasonable to assume that studies were estimating the same underlying treatment effect: i.e. where trials were examining the same intervention, and the trials’ populations and methods were judged sufficiently similar.
In future updates, if more data become available for meta-analysis and 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 Tau² and I².
Subgroup analysis and investigation of heterogeneity
It was not possible to perform the proposed subgroup analyses.
In future updates, 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.
Previous vaginal birth versus no previous vaginal birth.
Single prior caesarean birth versus two or more prior caesarean births.
The following outcomes will be used in subgroup analysis.
Death or serious maternal morbidity (defined by trial authors).
Death or serious infant morbidity (defined by trial authors).
We will assess subgroup differences by interaction tests available within RevMan (RevMan 2012). We will report the results of subgroup analyses quoting the Chi2 statistic and P value, and the interaction test I² value.
It was not possible to perform the proposed sensitivity analyses. In future updates, sensitivity analyses will be performed on the basis of trial quality to explore the effects of any heterogeneity identified.