Prophylactic manual rotation for fetal malposition to reduce operative delivery
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the effect of prophylactic manual rotation for women with malposition in labour on mode of delivery and maternal and neonatal outcomes.
Background
Description of the condition
Fetal malposition in labour refers to any position other than occiput anterior (OA) in a fetus with a vertex presentation. Persistent occiput posterior (OP) position is the commonest fetal malposition, with reported prevalence of 15% to 32% at the onset of labour (Cheng 2006a; Sherer 2002) and 5% to 8% at delivery (Lieberman 2005; Ponkey 2003). Occiput transverse (OT) position has a reported prevalence of 19% to 37% at the onset of labour and 3% to 16% at delivery (Akmal 2004; Souka 2003).
Obstetric associations with persistent OP position include more frequent induction and augmentation of labour, prolonged first and second stage and pathological cardiotocograph (Cheng 2006a; Senecal 2005). There are increased rates of chorioamnionitis, postpartum haemorrhage, third‐ and fourth‐degree perineal tears, wound infection and endometritis (Benavides 2005; Souka 2003; Wu 2005). Less information is available regarding the potential complications of occiput transverse position (To 2000). However there is evidence that this position is associated with increased use of oxytocin during labour and increased rates of third‐ and fourth‐degree perineal tears (Senecal 2005).
Adverse neonatal outcomes associated with the OP position include lower five‐minute Apgar scores, meconium‐stained liquor, cord blood gas acidaemia, birth trauma and admission to the neonatal intensive care unit (Cheng 2006b; Ponkey 2003). There is some evidence that the OT position is associated with lower five‐minute Apgar scores, birth trauma and admission to the neonatal intensive care unit (Senecal 2005).
OP position during labour is associated with higher rates of operative vaginal birth, failed attempts of vacuum‐assisted and forceps delivery, and caesarean delivery (De la Torre 2006; Ponkey 2003). Whilst 5% of babies born vaginally are reported OP, this position has been reported present in 19% born by emergency caesarean (Akmal 2004). Persistent OP position is more common in nulliparous women (Fitzpatrick 2001; Ponkey 2003) and only one‐third of nulliparous women with OP position achieve vaginal delivery (Akmal 2004). Failure of rotation of the fetal occiput from the OT position or 'deep transverse arrest' is also associated with operative birth (Pearl 1993).
Operative delivery is associated with significant maternal morbidity. Over the last decades caesarean delivery rates have been rising in many countries; there has been a 50% increase in the caesarean rate in Australia in the last 10 years (Laws 2010) and in France, the rate increased from 11% in 1981 to 20% in 2003 (Deneux‐Tharaux 2006). Caesarean is a major contributing factor to maternal mortality and morbidity following childbirth in high‐income countries (Hall 1999; Minkoff 2003; Schuitemaker 1997) and low‐income countries (Lumbiganon 2010). Although overall risks are small, mortality associated with elective caesarean is higher than for vaginal birth (Cooper 2002; Hall 1999). The presence of a uterine scar puts future pregnancies at increased risk of complications, including ectopic pregnancy in the caesarean scar, placenta praevia and a morbidly adherent placenta leading to caesarean‐hysterectomy. There is an increased risk of uterine rupture in subsequent labour which can lead to fetal or maternal death, or both (Dasche 2002; Gilliam 2002; Lyndon‐Rochelle 2001; Minkoff 2003). The complications of ventouse delivery include life‐threatening neonatal subgaleal haemorrhage, scalp lacerations, cephalohaematomas, retinal haemorrhages and neonatal jaundice (ACOG 2001).
Description of the intervention
Current management of OP and OT position in labour may be expectant, or involve manual rotation, instrumental delivery (with or without manual rotation), or caesarean section. Prophylactic manual rotation is defined as rotation performed without immediate assisted delivery. It is commonly performed in late first or early second stage of labour (Le Ray 2007; Shaffer 2011). Manual rotation may reduce the rate of operative delivery and complications are uncommon (Haddad 1995; Shaffer 2011). In settings where operative delivery is not readily available, this intervention may reduce maternal and neonatal morbidity and mortality.
Manual rotation entails the use of the accoucheur's hand or fingers to rotate the fetal head from the malpresenting (OP or OT) position to the usual OA position. It is most commonly performed at full dilatation after the malposition is diagnosed and is performed with an empty bladder and ruptured membranes. Two primary techniques have been described.
(1) Constant pressure being exerted with the tips of the fingers against the lambdoid suture to rotate fetal head into the OA position.
(2) The whole hand is introduced into the birth canal. The head is then rotated after positioning the fingers and thumb under the lateral posterior parietal bone and the anterior parietal bone.
Manual rotation may take two to three contractions to be performed and the position is commonly held for two contractions whilst the woman bears down to reduce the risk of the fetus reverting to the OP position (Cunningham 1997; Tarnier 1982).
How the intervention might work
The procedure of manual rotation in the management of OP position in labour could effectively reduce the rate of operative delivery by correcting the fetal malpresentation and allowing for normal descent and delivery of the fetus. In settings where operative delivery is not readily available, the intervention has the potential to reduce maternal and neonatal morbidity and mortality.
Why it is important to do this review
Manual rotation is commonly performed to increase the chances of normal vaginal delivery and is perceived to be safe. Manual rotation has the potential to prevent operative delivery and caesarean section, and reduce obstetric and neonatal complications.
Objectives
To assess the effect of prophylactic manual rotation for women with malposition in labour on mode of delivery and maternal and neonatal outcomes.
Methods
Criteria for considering studies for this review
Types of studies
Randomised control trials (RCT), quasi‐RCTs and cluster RCTs. We will include studies with abstracts only.
Types of participants
Women at term planning a vaginal birth with a cephalic singleton fetal malposition in labour. Malpositions are cephalic presentations other than direct OA.
Types of interventions
Prophylactic manual rotation in labour for fetal malposition versus expectant management, augmentation of labour or operative delivery. Prophylactic manual rotation is defined as rotation performed without immediate assisted delivery.
Types of outcome measures
We will assess all outcomes after treatment allocation.
Primary outcomes
-
Maternal mortality.
-
Perinatal mortality (stillbirth and neonatal death).
-
Operative delivery (forceps or vacuum delivery or caesarean section).
Secondary outcomes
Maternal
-
Caesarean section
-
Forceps delivery
-
Vacuum assisted delivery
-
Third‐ or fourth‐degree perineal trauma
-
Analgesia (nitrous, opiate, regional)
-
Duration of first and second stage of labour
-
Blood loss (ml) measured or estimated at time of birth
-
Primary postpartum haemorrhage equal to or greater than 500 ml (clinically estimated or measured at the time of birth and up to 24 hours)
-
Secondary postpartum haemorrhage equal to or greater than 500 ml (clinically estimated or measured after 24 hours and before six weeks)
-
Maternal blood transfusion
-
Postnatal infection
-
Duration of hospital stay
-
Postpartum re‐hospitalisation
Longer‐term maternal outcomes
-
Negative experience of childbirth (as defined by trial author)
-
Postnatal depression (positive depression screen ‐ e.g. EDPS >12; or clinical diagnosis or treatment)
-
Breastfeeding failure (not exclusively breast fed; or not breast feeding on discharge from hospital)
-
Relationship with baby (as defined by trial authors)
-
Perineal pain/dyspareunia
-
Abdominal pain
-
Backache reported six weeks postnatal
-
Prolapse or urinary incontinence/faecal incontinence/fistulae
-
Subsequent pregnancy complications
Neonatal and infant outcomes
-
Non‐reassuring or pathological cardiotocograph in first or second stage of labour
-
Cord blood gas acidosis (e.g. pH less than 7.1 or BE >‐12 or lactate greater than 8 mmol/L)
-
Admission to NICU
-
Neonatal resuscitation (positive‐pressure ventilation, cardiac compression or drug therapy)
-
Mechanical ventilation (IPPV/continuous positive airways pressure after resuscitation)
-
Neonatal jaundice treated with phototherapy
-
Exchange transfusion
-
Polycythaemia treated with partial volume exchange transfusion
-
Neonatal stroke
-
Intracranial bleed
-
Fracture
-
Scalp hematoma (e.g. cephalohematoma or subgaleal)
-
Encephalopathy
-
Neuropraxia
-
Duration stay at neonatal intensive care unit
-
Duration hospital stay
-
Severe neurodevelopmental disability in infants (assessed aged at least 12 months of age) defined as any one or combination of the following: non‐ambulant cerebral palsy, severe developmental delay assessed using validated tools, auditory and visual impairment augmentation of labour
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:
-
quarterly 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 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.
In addition, we will search the Australian New Zealand Clinical Trials Registry (ANZCTR), ClinicalTrials.gov, Current Controlled Trials and the WHO International Clinical Trials Registry Platform (ICTRP).
Searching other resources
We will search previous reviews, references of retrieved studies and relevant conference abstracts.
We will not apply any language restrictions.
Data collection and analysis
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 person.
Data extraction and management
We will extract data onto a standardised form. For eligible studies, at least two review authors will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult a third person. We will enter data into Review Manager (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
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) 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:
-
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 will describe for each included study the method used to conceal the allocation sequence 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:
-
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 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:
-
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 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:
-
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:
-
low risk of bias (e.g. less than 20% missing outcome data; missing outcome data balanced across groups);
-
high risk of bias (e.g. 20% or more missing outcome data; numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis done with substantial departure of intervention received from that assigned at randomization);
-
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:
-
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 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:
-
low risk of other bias;
-
high risk of other bias;
-
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 standardised mean difference to combine trials that measure the same outcome, but use different methods.
Unit of analysis issues
The unit of analysis is intended to be the individual woman and infant.
Crossover trials are not appropriate for addressing this review topic.
Cluster‐randomised trials
We will include cluster‐randomised trials in the analyses, along with individually randomised trials. We will adjust their sample sizes or 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‐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 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 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.
We will carry out analyses for all outcomes, 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 analyse 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 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 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 symmetry. 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 we detect asymmetry in any of these tests or 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' population and methods are judged sufficiently similar. If there is clinical heterogeneity sufficient to expect that the underlying treatment effect differs between trials, or if we detect substantial statistical heterogeneity, 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 perform the following subgroup analyses where data permit.
-
Occiput posterior versus occiput transverse position.
-
Nulliparous versus multiparous.
-
Epidural versus no epidural in labour.
-
Digital (fingers) versus whole hand rotation.
-
Term versus preterm.
-
Full dilatation versus less than full dilatation.
We will assess the following outcomes in subgroup analysis.
-
Maternal mortality.
-
Perinatal mortality (stillbirth and neonatal deaths).
-
Severe neurodevelopmental disability in infants (assessed aged at least 12 months of age) defined as any one or combination of the following: non‐ambulant cerebral palsy, severe developmental delay assessed using validated tools, auditory and visual impairment.
-
Operative delivery (forceps or vacuum or caesarean delivery).
-
Caesarean section.
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
If sufficient data are available, we plan to explore methodological heterogeneity through the use of sensitivity analyses. We plan to perform sensitivity analyses through excluding trials of lower quality, based on a lack of any of the following: allocation concealment, adequate randomisation, blinding of treatment, less than 10% loss to follow‐up. We plan to include outcomes in this sensitivity analysis.
