Position in the second stage of labour for women with epidural anaesthesia
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the effects of different birthing positions during the second stage of labour, on important maternal and fetal outcomes for women with epidural analgesia.
Background
Epidural analgesia is commonly used as a form of pain relief in labour. Systematic reviews of randomised controlled trials (RCTs) have found that it is more effective than other non‐epidural methods (Anim‐Somuah 2005). However, epidurals result in a longer second stage of labour and more instrumental deliveries (Anim‐Somuah 2005). This matters because prolonged labour may increase the risk of fetal respiratory acidosis and postpartum haemorrhage (Watson 1994). Instrumental deliveries are associated with prolapse, urinary incontinence, and dyspareunia (Liebling 2004; MacLennan 2000). A survey during 2005 and 2006 showed that 22% of all deliveries in NHS hospitals involve an epidural (Richardson 2007); in other countries such as Canada epidural rates may be even higher. This is why strategies to shorten the second stage of labour and reduce instrumental deliveries in this setting are important.
There are several proposed mechanisms for the association between epidurals and increased instrumental deliveries. Epidurals increase the risk of malposition of the fetal head, in particular the fetal occiput‐posterior position, a key factor in instrumental delivery and prolonged labour (Lieberman 2005; Martino 2007). Secondly, epidurals may interfere with the release of oxytocin as the pelvic floor stretches in the late second stage of labour (Goodfellow 1983; Rahm 2002). Finally, epidurals may inhibit the mother's bearing down reflex at the same time.
With the advancement of low‐dose epidural techniques, also known as 'walking' epidurals, women with an epidural are now being provided with the opportunity to remain mobile during their labour, and to adopt upright positions such as standing and ambulation (COMET 2001). The use of ambulation during labour has been associated with more efficient uterine action, labours of a shorter duration, and aiding the descent of the fetal head through encouraging the effects of gravity (COMET 2001; Flynn 1978). The use of low‐dose epidurals is also thought to aid the maternal efforts required to give birth through the preservation of motor function (COMET 2001). The increased number of vaginal deliveries seen with this form of analgesia is thought to be due to the ability of the women to adopt an upright position during labour (COMET 2001).
One suggestion to reduce adverse outcomes in labour with an epidural is the use of alternative maternal delivery positions. Although it has become more common in the west to deliver in the supine position, this position may result in a higher number of instrumental deliveries and episiotomies (De Jonge 2004). In women without an epidural, a number of observational studies have suggested that delivering in an upright position results in shorter labours, lower incidence of instrumental deliveries and episiotomies, and is a more comfortable delivery position (Bodner‐Adler 2003; Mendez‐Bauer 1975). Some small RCTs (Chen 1987) and two systematic reviews (De Jonge 2004; Gupta 2004) have confirmed this. It has been proposed that these benefits are due to a higher resting intrauterine pressure which contributes to the downward delivery force and the bearing‐down forces (Chen 1987), as well as contractions of a greater intensity (Mendez‐Bauer 1975).
Although a Cochrane review (Gupta 2004) has assessed the use of upright positions in the second stage of labour, this systematic review did not include women with epidurals, and therefore the findings can not be generalised. With the benefits associated with upright positions counteracting the key negative aspects associated with epidurals, it highlights the importance of carrying out this systematic review. A recent non‐Cochrane review (Roberts 2005) attempted just this; however, this review was unable to report any data for the fetal outcomes as the trials did not make this information available. Therefore, it is our aim to apply the more stringent Cochrane approach, which would involve contacting authors where data are missing, in evaluating this much disputed aspect of obstetrics.
Objectives
To assess the effects of different birthing positions during the second stage of labour, on important maternal and fetal outcomes for women with epidural analgesia.
Methods
Criteria for considering studies for this review
Types of studies
All randomised or quasi‐randomised trials.
Types of participants
All pregnant women (primigravidae and multigravidae) in the second stage of induced or spontaneous labour receiving epidural analgesia. We will include women with any type of epidural. We will only include singleton pregnancies at term gestation (37 weeks + 0 days).
Types of interventions
We will assume the experimental type of intervention to be the maternal use of any upright position during the second stage of labour, compared with the control intervention of the use of any recumbent position.
The second stage of labour can be divided into two distinct phases: the latent phase (also known as the passive phase), and the active phase. We will define the latent phase as the period of time from full dilatation until the head has descended to the pelvic floor, with the mother experiencing no desire to push. We will define the active phase as the period from the head descending to the pelvic floor until the birth of the baby, with the mother having a strong desire to push (O'Driscoll 2003).
We will classify studies as either a comparison of an upright versus a recumbent position in the latent phase of the second stage of labour, or a comparison of an upright versus a recumbent position in the active phase of the second stage of labour. We will consider studies eligible for inclusion if it was intended that participants spent at least 30% of time in the relevant phase of second stage labour in the allocated position. Finally, studies which compared an upright position in both phases of the second stage with a recumbent position in both phases of the second stage will form a third group. There are three potential time phases in which the effects of different positions can be studied: namely the latent phase; the active; and both.
We will initially categorise the birthing positions as upright (the main axis of the body is more than 45° from the horizontal) or recumbent (the main axis of the body is less than 45° from the horizontal).
Upright positions will include:
-
sitting (on a bed);
-
sitting (on a tilting bed more than 45° from the horizontal);
-
squatting (unaided or using squatting bars);
-
squatting (aided with birth cushion);
-
semi‐recumbent (we will class this as an upright position if the main axis of the body (chest and abdomen) is 45° or more from the horizontal);
-
kneeling (upright, leaning on the head of the bed, or supported by a partner);
-
walking (only for comparison of positions in the latent phase).
Recumbent positions will include:
-
lithotomy position;
-
lateral position (left or right);
-
Trendelenburg's position (head lower than pelvis);
-
knee‐elbow (all fours) position;
-
semi‐recumbent (we will class this as a recumbent position if the main axis of the body (chest and abdomen) is less than 45° from the horizontal).
A number of other names have been used for birthing positions, including:
-
Fowler;
-
tug‐of‐war;
-
throne.
We have decided to delay classifying these three positions until after we have identified the trials. We will arrange to classify these positions from the methods section without knowledge of the trial results. Again, we will use the dividing line of the body at 45° from the horizontal.
Some trials may compare positions with varying degrees of uprightness, which fall the same side of the 45° dividing line. For example, a study might compare the horizontal position (0°) with semi‐recumbent (40°). So long as the two groups clearly differ in degree of verticality, we will be classify them as "more vertical" and "less vertical". We will exclude such studies from the primary analysis, but include them in a secondary sensitivity analysis.
Types of outcome measures
Primary outcomes
Maternal outcomes
-
Operative delivery
-
Duration of second stage labour (from time of randomisation to delivery)
Secondary outcomes
Maternal outcomes
-
Instrumental delivery
-
Caesarean section
-
Trauma to birth canal, requiring suturing
-
Blood loss (greater than 500 ml) (or as defined by trial authors)
-
Prolonged second stage, defined as pushing for more than 60 minutes (or as defined by trial authors)
-
Maternal experience and satisfaction of labour
Baby outcomes
-
Abnormal fetal heart rate patterns, needing intervention
-
Apgar score of less than seven at five minutes (or as defined by trial authors)
-
Low cord pH less than 7.1 (or as defined by trial authors)
-
Admission to neonatal intensive care unit
-
Need for ventilation
-
Perinatal death
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;
-
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.
We will not apply any language restrictions.
Data collection and analysis
Selection of studies
Two review authors will assess for inclusion all potential studies we identify as a result of the search strategy. We will resolve any disagreement through discussion or, if required, consult an outside person.
Data extraction and management
We will design a form to extract data. 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 consult a third person. 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
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 2008). 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:
-
adequate (any truly random process, e.g. random number table; computer random number generator);
-
inadequate (any non‐random process, e.g. odd or even date of birth; hospital or clinic record number); or
-
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:
-
adequate (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
-
inadequate (open random allocation; unsealed or non‐opaque envelopes, alternation; date of birth);
-
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:
-
adequate, inadequate or unclear for participants;
-
adequate, inadequate or unclear for personnel;
-
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:
-
adequate: defined as less than five percent missing data for the particular outcome;
-
inadequate; or
-
unclear.
(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:
-
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);
-
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); or
-
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:
-
yes;
-
no;
-
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.
Unit of analysis issues
We will not include cluster randomised trials. Crossover trials are not apprpriate for adressing this review topic.
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. 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. If we identify substantial heterogeneity we will explore it by pre‐specified 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.
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 we identify substantial heterogeneity 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
Subgroup analyses
We plan to carry out the following subgroup analyses.
-
Time of epidural: sited in the first stage of labour or sited in the second stage of labour.
-
Type of epidural: traditional versus 'walking'. We will classify low‐dose combined spinal epidurals and low‐dose infusion epidurals as "walking".
-
Nulliparous versus multiparous women.
-
Oxytocin used/not used in the second stage.
We will use the following outcomes in subgroup analysis.
-
Operative delivery.
-
Duration of second stage labour (from time of randomisation to delivery).
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
The primary analysis will include all randomised trials comparing upright with recumbent postions as defined. We will carry out sensitivity analysis to explore the effect of trial quality. This will involve an analysis limited to high‐quality trials. This will be defined as follows.
Restricting analysis to: concealment 'A' and attrition 'A'. For the outcomes perinatal death, mode of delivery and duration of second stage (randomisation to delivery), we will include studies where the outcome assessor was not blinded. For all other outcomes, we will exclude studies where the outcome assessor was not blinded from this high‐quality analysis.
We will also perform a second sensitivity analysis including trials comparing "more vertical" with "less vertical" as defined.
