High‐dose versus low‐dose oxytocin for augmentation of delayed labour
Abstract
Background
A major cause of failure to achieve spontaneous vaginal birth is delay in labour due to presumed inefficient uterine action. Oxytocin is given to increase contractions and high‐dose regimens may potentially increase the number of spontaneous vaginal births, but as oxytocin can cause hyperstimulation of the uterus, there is a possibility of increased adverse events.
Objectives
To compare starting dose and increment dose of oxytocin for augmentation for women delayed in labour to determine whether augmentation by high‐dose regimens of oxytocin improves labour outcomes and to examine the effect on both maternal/neonatal outcomes and women's birth experiences.
Search methods
We searched the Cochrane Pregnancy and Childbirth Group's Trials Register (31 May 2013) and reference lists of retrieved studies.
Selection criteria
We included all randomised and quasi‐randomised controlled trials for women in delayed labour requiring augmentation by oxytocin comparing high‐dose regimens (defined as starting dose and increment of equal to or more than 4 mU per minute) with low‐dose regimens (defined as starting dose and an increment of less than 4 mU per minute). Increase interval: between 15 and 40 minutes. The separation of low‐ and high‐dose regimens is based on an arbitrary decision.
Data collection and analysis
Four review authors undertook assessment of trial eligibility, risk of bias, and data extraction independently.
Main results
We included four studies involving 644 pregnant women. Three studies were randomised controlled trials and one trial was a quasi‐randomised study. A higher dose of oxytocin was associated with a significant reduction in length of labour reported from one trial (mean difference (MD) ‐3.50 hours; 95% confidence interval (CI) ‐6.38 to ‐0.62; one trial, 40 women). There was a decrease in the rate of caesarean section (risk ratio (RR) 0.62; 95% CI 0.44 to 0.86 four trials, 644 women) and an increase in the rate of spontaneous vaginal birth in the high‐dose group (RR 1.35; 95% CI 1.13 to 1.62, three trials, 444 women), although for both of these outcomes there were inconsistencies between studies in the size of effect. When we carried out sensitivity analysis (temporarily removing a study at high risk of bias) the differences between groups were no longer statistically significant
There were no significant differences between high‐ and low‐dose regimens for instrumental vaginal birth, epidural analgesia, hyperstimulation, postpartum haemorrhage, chorioamnionitis or women's perceptions of experiences. For neonatal outcomes, there was no significant difference between groups for Apgar scores, umbilical cord pH, admission to special care baby unit, or neonatal mortality. The following outcomes were not evaluated in the included studies: perinatal mortality, uterine rupture, abnormal cardiotocography, women's pyrexia, dystocia and neonatal neurological morbidity.
Authors' conclusions
Higher‐dose regimens of oxytocin (4 mU per minute or more) were associated with a reduction in the length of labour and in caesarean section, and an increase in spontaneous vaginal birth. However, there is insufficient evidence to recommend that high‐dose regimens are advised routinely for women with delay in the first stage of labour. Further research should evaluate the effect of high‐dose regimens of oxytocin for women delayed in labour and should include maternal and neonatal outcomes as well as the effects on women.
PICOs
Plain language summary
Oxytocin in high versus low doses for augmentation of delayed labour
Women have different lengths of labour, with first labours lasting on average eight hours (and unlikely to last more than 18 hours) and second and subsequent labours lasting an average of five hours and unlikely to last more than 12 hours. Assessment of progress in labour takes into account not just cervical dilatation, but also descent and rotation of the fetal head and the strength, duration and frequency of contractions. Some evidence suggests that up to one‐third of women in their first labour experience delay. They are often given a synthetic version of the hormone oxytocin to increase uterine contractions and shorten labour. Surprisingly for such a routine treatment, the ideal dose at which it should be given is not known, although some comparisons suggest that higher‐dose regimens of oxytocin could shorten labour and reduce the chance of caesarean section with an increase in the numbers of women having a spontaneous vaginal birth compared with lower‐dose regimens. However, there are potentially harmful side effects as oxytocin may cause the uterus to contract too quickly, and the baby to become distressed. Clinicians attempt to mitigate these side effects by adjusting the dose of oxytocin with the contractions to reduce the chances of the baby being distressed in labour.
From the four randomised controlled trials involving 644 pregnant women that we included in this review, results indicate that a higher dose of oxytocin (4‐7 mU per minute, compared with 1‐2 mU per minute) reduced the length of labour and the rate of caesarean sections with increased spontaneous vaginal births, but the studies did not provide enough evidence on possible differences between the high‐ and low‐dose regimens on adverse events including hyperstimulation of the uterus, and outcomes for the newborn infant. Only one trial reported on the possible effect on women. The overall quality of the included trials was mixed, but this might reflect how clinical trials were reported in the past.
While the current evidence is promising and suggests that the high‐dose regimens reduce the length of labour and the rate of caesarean sections, this evidence is not strong enough to recommend that high‐dose regimens are used routinely for women delayed in labour. We recommend that further research is carried out.
Authors' conclusions
Background
Description of the condition
Length of labour varies between women, with first labours lasting on average eight hours (and unlikely to last more than 18) and second and subsequent labours lasting on average five hours (and unlikely to last more than 12 hours). Progress in labour should take into account not just cervical dilatation, but also descent and rotation of the fetal head and strength, duration and frequency of contractions. The definition of delay varies, but cervical dilatation of 2 cm in four hours is widely accepted as being normal (NICE 2007). The incidence of delay in labour is not accurately known. Some evidence suggests that up to one‐third of women in their first labours experience delay (Williams 1998). Other evidence suggests the incidence of prolonged labour is more than 10% of women (DOH 2004), and about 40% to 60% of these women have their labour augmented with oxytocin due to slow progress or other reasons in first stage of labour (Gottschall 1997; Impey 2000). Many women would have already had their membranes ruptured spontaneously, and amniotomy is not recommended as routine practice (Smyth 2007).
Description of the intervention
Oxytocin has been widely used in obstetric practice and increases both the frequency and strength of uterine contractions in labour. In doses under 4 mU/min, it has been shown to shorten labour but not alter mode of birth (Wei 2007).
How the intervention might work
It is plausible that increasing both the dose and speed of the oxytocin will increase the number of women having a spontaneous vaginal birth. It is currently routine treatment for women delayed in labour, and while it does carry potentially harmful side effects, clinicians routinely effectively titrate the dose against uterine contractions.
Why it is important to do this review
Evidence suggests that high doses of oxytocin may increase spontaneous vaginal birth but not enough is known about neonatal outcomes or how this might affect women's birth experience. One non‐Cochrane systematic review included trials that compared high versus low doses of oxytocin for augmentation of labour (Wei 2010) but some of the trials were undertaken in the context of active management of labour.
This review intends to assess the risks and benefits of high‐ and low‐dose regimens of oxytocin for augmentation of labour due to delayed first stage of labour. We have excluded trials undertaken in the context of active management of labour (one‐to‐one continuous support, strict definition of established labour, early amniotomy, routine two‐hourly vaginal examinations and oxytocin if labour becomes slow), or as part of induction of labour.
Objectives
To compare starting dose as well as increment dose of oxytocin for augmentation in delayed labour to determine whether augmentation by high dose of oxytocin improves labour outcomes and women's satisfaction.
Methods
Criteria for considering studies for this review
Types of studies
All randomised and quasi‐randomised controlled trials. We intended to include both published or unpublished trials.
Types of participants
Women in labour assessed as requiring augmentation by oxytocin for delay or slow progress in labour. We only included women with live fetuses.
Types of interventions
High starting and increment dose (4 micro unit (mU) per minute or more) of oxytocin for augmentation in delayed labour compared with low dose (less than 4 mU per minute). We defined amount of oxytocin as below:
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high‐dose regimens: defined as starting dose and increment of equal to or more than 4 mU per minute;
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low‐dose regimens: defined as starting dose and an increment of less than 4 mU per minute;
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increase interval: between 15 and 40 minutes.
The separation of low and high doses is based on an arbitrary decision.
Types of outcome measures
Primary outcomes
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Perinatal mortality rate (as defined by trial authors)
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Neonatal mortality rate
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Caesarean section rate
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Women's satisfaction (measured quantitatively using validated questionnaires)
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Length of labour
Secondary outcomes
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Spontaneous vaginal birth
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Instrumental vaginal birth
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Incidence of hyperstimulation (contracting greater than five in 10 minutes for at least 20 minutes with fetal heart rate changes)
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Incidence of ruptured uterus
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Diagnosis of chorioamnionitis
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Incidence of postpartum haemorrhage (blood loss more than 500/1000 mL)
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Use of epidural analgesia
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Incidence of abnormal cardiotocography (considered only if blindly assessed)
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Incidence of women's pyrexia
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Incidence of dystocia
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Neonatal outcomes of Apgar scores, umbilical cord pH, neurological morbidity, admission to special care baby units
Search methods for identification of studies
Electronic searches
We contacted the Trials Search Co‐ordinator to search the Cochrane Pregnancy and Childbirth Group's Trials Register (31 May 2013).
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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monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
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weekly searches of MEDLINE;
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weekly searches of Embase;
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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, 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.
Searching other resources
We searched the reference lists of retrieved studies.
We did not apply any language restrictions.
Data collection and analysis
We used the following methods when assessing the reports identified by the search.
Selection of studies
Review authors Rintaro Mori (RM), Hironobu Tokumasu (HT), Therese Dowswell (TD) and Sara Kenyon (SK) independently assessed for inclusion all the potential studies identified as a result of the search strategy. We intended to resolve any disagreement through discussion or, if required, consult Debbie Pledge (DP); there was no disagreement found.
Data extraction and management
We designed a form to extract data prior to the review. For eligible studies, RM, HT and TD extracted the data using the agreed form, which was checked by SK. We resolved discrepancies through discussion or, if required, we planned to consult DP (though we were able to resolve all discrepancies by discussion). We entered data into Review Manager software (RevMan 2012) and checked for accuracy.
Assessment of risk of bias in included studies
RM, HT, TD and SK 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 all disagreement by discussion.
(1) Random sequence generation (checking for possible selection bias)
We 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 assessed 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 describe for each included study the method used to conceal allocation to interventions prior to assignment and assess whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.
We assessed 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) Blinding of participants, personnel and outcome assessment (checking for possible performance bias)
We 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 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:
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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;
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low, high or unclear risk of bias for outcome assessment.
(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)
We 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 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 was supplied by the trial authors, we re‐included missing data in the analyses which we have undertaken.
We assessed 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);
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unclear risk of bias.
(5) Selective reporting (checking for reporting bias)
We describe for each included study how we investigated the possibility of selective outcome reporting bias and what we found.
We assessed 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 describe 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:
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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 made 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 assessed the likely magnitude and direction of the bias and whether we considered it is 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
We carried out statistical analysis using the Review Manager software (RevMan 2012). We used fixed‐effect meta‐analysis for combining data where trials examined the same intervention, and the trials' populations and methods were judged to be sufficiently similar. Where we suspected clinical or statistical heterogeneity between studies, sufficient to suggest that treatment effects might differ between trials, we carried out random‐effects meta‐analysis.
Dichotomous data
For dichotomous data, we presented results as summary risk ratio with 95% confidence intervals.
Continuous data
For continuous data, we used the mean difference if outcomes were measured in the same way between trials. We used the standardised mean difference to combine trials that measure the same outcome, but used different methods.
Unit of analysis issues
Cluster‐randomised trials
We did not identify any cluster‐randomised trials for inclusion in this review. However, if we identify cluster‐randomised trials for inclusion in future updates, we will include them in the analyses along with individually‐randomised trials. We will adjust their sample sizes 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.
Cross‐over trials
We did not include cross‐over trials.
Dealing with missing data
For included studies, we noted levels of attrition. We planned to explore the impact of including studies with high levels of missing data (over 10% for outcomes where data were collected in labour) in the overall assessment of treatment effect by using Sensitivity analysis. In this version of the review we did not carry out planned sensitivity analysis because labour outcomes studies were rated as being at low risk of bias with little loss of follow‐up or missing data reported.
For all outcomes, we carried out analyses, as far as possible, on an intention‐to‐treat basis, i.e. we attempted to include all participants randomised to each group in the analyses, and analysed 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 was the number randomised minus any participants whose outcomes were known to be missing.
Assessment of heterogeneity
We assessed statistical heterogeneity in each meta‐analysis using the T², I² and Chi² statistics. We regarded heterogeneity as substantial if a T² was greater than zero and either an I² was greater than 30% or there was a low P value (less than 0.10) in the Chi² test for heterogeneity.
Assessment of reporting biases
Where we suspected reporting biases (such as publication bias), we attempted to contact study authors asking them to provide missing outcome data.
In future updates of this review, if more data become available and 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 asymmetry. 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 carried out statistical analysis using the Review Manager software (RevMan 2012). We used 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. If there was clinical heterogeneity sufficient to expect that the underlying treatment effects differ between trials, or if high statistical heterogeneity was identified, we planned to use random‐effects meta‐analysis to produce an overall summary if an average treatment effect across trials was considered clinically meaningful. For random‐effects analysis the effect estimate represents the average treatment effect 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
We intended to conduct planned subgroup analysis using the methods described by Deeks 2001 and set out in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).
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By parity (nulliparous versus multiparous women).
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By previous experience of caesarean section (women who had a caesarean before this delivery versus those who had not).
We planned to use the following outcomes in subgroup analysis.
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Perinatal mortality rate.
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Neonatal mortality rate.
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Women's satisfaction.
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Mode of birth.
We were only able to carry out limited subgroup analysis due to insufficient data. We assessed differences between subgroups using the subgroup interaction tests available in Revman (RevMan 2012).
Sensitivity analysis
The quality of included studies varied in terms of risk of bias; one of the studies used a method at high risk of bias for allocation concealment and, where data were available, we carried out sensitivity analysis by temporarily removing this study from the analyses to examine the impact on results.
Results
Description of studies
Results of the search
The search of the Pregnancy and Childbirth Group's Trials Register found 18 studies. We also identified, and subsequently excluded, two additional reports from the reference lists of retrieved studies (Cummiskey 1989; Satin 1994). In total, we initially considered 20 studies published in 24 articles/reports. From these, we included four studies and excluded 15 studies, and one trial is still ongoing. One trial that was included in the previous version of the review was excluded from this update; careful consideration of the inclusion criteria for this study from a translation of the published report led us to conclude that women recruited to the trial were not necessarily experiencing delay in labour (Supajitkulchi 2003). We did not identify any unpublished trials. For further information on trial characteristics, please refer to the Characteristics of included studies and Characteristics of excluded studies tables.
Included studies
We included four studies, involving 644 women. Please refer to Characteristics of included studies for the further details.
Among the included trials, three trials (Bidgood 1987; Jamal 2004; Kenyon 2013) were randomised controlled trials and one trial (Xenakis 1995) employed a quasi‐randomised design, where allocation of intervention was made on the basis of the day of the week.
With the exception of one, three‐armed trial (Bidgood 1987), all of the included studies were two‐armed trials. Data from one arm of the three‐arm trial were not used as the data did not meet our inclusion criteria.
Two trials included only nulliparous women (Bidgood 1987; Kenyon 2013), while the other two trials included both nulliparous and parous women (Jamal 2004; Xenakis 1995). In the Xenakis 1995 trial, separate data on mode of birth were provided for nulliparous and parous women. Three trials excluded women with previous caesarean section (Jamal 2004; Kenyon 2013; Xenakis 1995).
Possible maximum dose for oxytocin was reported by one trial (Bidgood 1987) as 40 mU/min, and by (Kenyon 2013) as 64 mU/min for the high‐dose group and 32 mU/min for the low‐dose group.
Excluded studies
We excluded 15 studies. Please see Characteristics of excluded studies for the further details.
One report (Alderman 1974) was a letter with no primary data.
Six trials (Arulkumaran 1989; Lazor 1993; Lowensohn 1990; Majoko 2001; Satin 1994; Seitchik 1982) examined different rates of oxytocin administration for augmentation of labour; their stated doses are outside of the preset criteria of low and high doses.
One trial (Cummiskey 1989) compared pulsatile administration of oxytocin for augmentation with continuous administration.
One trial (Parpas 1995) compared high and low doses of oxytocin for augmentation and induction of labour but the two populations were not reported separately.
One trial (Vorherr 1963) compared effectiveness of oxytocin for augmentation with placebo.
One trial (Merrill 1999) included women with planned routine augmentation of labour by oxytocin; hence these women did not necessarily have delayed labour.
One trial (Akoury 1993) was excluded because it was carried out in the context of active management of labour.
Two trials (Hayakungchat 2011; Supajitkulchi 2003) enrolled women with inadequate contractions rather than women with delayed labour.
One trial (Doppa 2011) enrolled women requiring induction of labour rather than augmentation.
Risk of bias in included studies
Allocation
We rated random sequence generation as 'high risk' of bias in one trial where allocation was according to day of the week (Xenakis 1995). The other trials all used a method to generate the randomisation sequence that we assessed as low risk of bias: in Bidgood 1987 envelopes containing allocations were shuffled at the beginning of the study; in Jamal 2004 a table of random numbers was used; and Kenyon 2013 used an external telephone randomisation service.
Allocation to groups at the point of randomisation was concealed in two trials (Bidgood 1987; Kenyon 2013). Bidgood 1987 used sealed envelopes opened by an investigator not involved in carrying out initial assessments on women recruited to the trial, and in the trial by Kenyon 2013, allocation was by a telephone service. In the Jamal 2004 trial, it was not clear how allocation was concealed at the point of randomisation. There was no concealment of allocation in the (Xenakis 1995) trial where women requiring augmentation were allocated to groups according to days of the week. It was not clear whether all other aspects of care were the same on different days of the week.
Blinding
Blinding was not attempted in two trials (Bidgood 1987; Xenakis 1995), but the other two trials were double blinded with both caregivers and pregnant women blinded to allocation (Jamal 2004; Kenyon 2013).
Incomplete outcome data
All of these trials were rated as being at low risk of bias for labour and delivery outcomes with little loss to follow‐up or missing data reported. Only one of the studies reported data relating to women's experiences of childbirth; in this trial the response rate to postal questionnaire was 63% (59/94) (Kenyon 2013).
Selective reporting
We had sufficient information to assess outcome reporting bias for only one study (Kenyon 2013) where a published protocol was available.
Other potential sources of bias
Assessment of risk of bias was hampered by lack of information on methods in three of the included trials (Bidgood 1987; Jamal 2004; Xenakis 1995). Baseline characteristics were reported as being similar in all four of the trials, although in Xenakis 1995, there were fewer nulliparous women in the high‐dose group (47%) compared with the low‐dose group (60%). Other bias was not apparent, although Bidgood 1987 reported that due to lack of time only 30 rather than 50 women were recruited to each arm.
Effects of interventions
Primary outcomes
There was a significant reduction in length of labour with higher dose of oxytocin reported from one trial (mean difference (MD) ‐3.50 hours; 95% confidence interval (CI) ‐6.38 to ‐0.62; one trial, 40 women (Analysis 1.3)).
There was evidence of a reduction in caesarean section in the high‐dose group (risk ratio (RR) 0.62; 95% CI 0.44 to 0.86, four trials, 644 women (Analysis 1.2)). However, for this outcome there was inconsistency in findings from the trials and substantial statistical heterogeneity (I2 = 58%). More than half of the weight in this analysis was from one trial which was at high risk of bias due to lack of allocation concealment. We therefore carried out a sensitivity analysis, temporarily removing this study from the analysis to examine the impact on results. Removing the Xenakis 1995 trial led to a reduction in heterogeneity (I2 = 0%) and the difference between groups for caesarean section was no longer statistically significant (RR 0.89, 95% CI 0.57 to 1.38; data not shown).
There was no estimable data for neonatal mortality (reported in three trials). No significant differences were seen in women's perceptions of the birth experience (namely support received by staff, women's internal control during labour and birth, and women's external control during labour and birth measured by the SCIB (Support and Control in Birth) questionnaire (Ford 2009) (MD 2.20, 95% CI ‐2.19 to 6.59, (Analysis 1.5); MD ‐0.30, 95% CI ‐4.99 to 4.39, (Analysis 1.6); and MD 2.60, 95% CI ‐2.25 to 7.45, (Analysis 1.7), respectively). None of the included trials reported effects on perinatal mortality.
Secondary outcomes
There was significant evidence of increases in spontaneous vaginal birth (RR 1.35; 95% CI 1.13 to 1.62, three trials, 444 women (Analysis 1.8)). We carried out sensitivity analysis for this outcome by temporarily removing one study at high risk of bias from the analysis (Xenakis 1995); without data from this study the difference between groups for spontaneous vaginal birth was no longer statistically significant (RR 1.24, 95% CI 0.68 to 2.25; data not shown).
No significant difference was seen in the incidence of instrumental vaginal birth (RR 0.83, 95% CI 0.61 to 1.13 (Analysis 1.11)); hyperstimulation (RR 1.47, 95% CI 0.73 to 2.94 (Analysis 1.10)); chorioamnionitis (RR 0.70, 95% CI 0.44 to 1.12 (Analysis 1.9)); postpartum haemorrhage (RR 0.95, 95% CI 0.61 to 1.48 (Analysis 1.12)); epidural analgesia (RR 0.98, 95% CI 0.86 to 1.12 (Analysis 1.13)); admission to neonatal units (RR 0.50, 95% CI 0.22 to 1.15 (Analysis 1.15)); pathological cardiotocography (CTG) (RR 0.60, 95% CI 0.29 to 1.23 (Analysis 1.14)); Apgar score less than seven at five minutes (RR 0.37, 95% CI 0.02 to 8.50 (Analysis 1.16)); or umbilical cord pH (MD 0.00, 95% CI ‐0.03 to 0.03 (Analysis 1.17)). No trials reported incidences of ruptured uterus, women's pyrexia and dystocia, and infant neurological morbidities.
Subgroup analyses
By parity
One trial set out data for mode of birth separately for nulliparous and parous women (Xenakis 1995) and two trials recruited only nulliparous women. We therefore carried out subgroup analysis by parity for caesarean section. The subgroup interaction test showed no clear differences in intervention effect between nulli‐ and multi‐parous women (Analysis 1.18) although as in the main analysis, there was evidence of variations in the size and direction of treatment effect between trials and substantial statistical heterogeneity.
Previous caesarean section
No trial considered women with previous caesarean section separately, and therefore we did not conduct subgroup analysis by previous caesarean section.
Discussion
Summary of main results
Available evidence showed that a higher‐dose regimen of oxytocin for augmentation of delayed labour reduced the length of labour and may reduce the number of caesarean sections and increase the number of spontaneous vaginal births. One trial reported effects on women's birth experience, though due to unbalance and incompleteness of the follow‐up, it was difficult to reach a conclusion based upon the data. There was no evidence of difference in incidence of adverse events, though this could be due to the small number of included trials and women. Since this review compared only higher‐ versus lower‐ dose regimens with the same intervals, we can draw no conclusion on the optimal intervals or doses outside the ranges that this review assessed. There is little information on the effect in subgroups of women with previous caesarean section and with different parities.
Quality of the evidence
The overall quality of the included trials was mixed although assessing bias was partly hampered by insufficient information on methods in three of the included trials (Bidgood 1987; Jamal 2004; Xenakis 1995); the most recent trial was mainly rated as being at low risk of bias (Kenyon 2013) and this may reflect changes in reporting of trials. One of the trials was at high risk of bias for allocation concealment (Xenakis 1995) and removing data from this trial from the analyses had an impact on results for outcomes relating to mode of birth with other trials showing a less pronounced effect for high‐dose regimens.
Potential biases in the review process
We were aware of the possibility of introducing bias at every stage of the review process. We attempted to reduce bias in a number of ways: two review authors independently assessed eligibility for inclusion, carried out data extraction and assessed risk of bias. Nevertheless, assessment of risk of bias, for example, is not an exact science and involves subjective judgements. Further, the process of reviewing research studies is known to be affected by attitudes and beliefs and it is not easy to control for this type of bias in the reviewing process. One of the review authors (S Kenyon) was an investigator in one of the included trials, and for this trial two other review authors (R Mori and T Dowswell) carried out independent data extraction and assessment of risk of bias.
Agreements and disagreements with other studies or reviews
While other reviews have not focused on women delayed in labour, but have also included women having 'active management of labour', which is a package of care, this review also highlights the uncertainty in the evidence regarding the use of high‐dose oxytocin regimens to reduce caesarean section and increase spontaneous vaginal birth for women with delayed labour and emphasises the need for further research to be undertaken.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 1 Neonatal mortality.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 2 Caesarean section.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 3 Length of labour (hour; oxytocin to delivery).
Comparison 1 High versus low dose of oxytocin (all women), Outcome 4 Length of labour (minute; onset of first stage to delivery).
Comparison 1 High versus low dose of oxytocin (all women), Outcome 5 Support received by staff.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 6 Women's internal control during labour and birth.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 7 Women's external control during labour and birth.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 8 Spontaneous vaginal birth.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 9 Diagnosis of chorioamnionitis.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 10 Incidence of hyperstimulation.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 11 Instrumental vaginal birth.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 12 Incidence of postpartum haemorrhage.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 13 Epidural analgesia.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 14 Pathological cardiotocography (CTG) leading to immediate birth without fetal blood sampling.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 15 Neonatal admission to special care baby units.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 16 Apgar score less than 7 at 5 minutes.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 17 Umbilical cord (artery) pH.
Comparison 1 High versus low dose of oxytocin (all women), Outcome 18 Subgroup analysis: Caesarean section by parity.
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Neonatal mortality Show forest plot | 3 | 604 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.0 [0.0, 0.0] |
| 2 Caesarean section Show forest plot | 4 | 644 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.62 [0.44, 0.86] |
| 3 Length of labour (hour; oxytocin to delivery) Show forest plot | 1 | 40 | Mean Difference (IV, Fixed, 95% CI) | ‐3.50 [‐6.38, ‐0.62] |
| 4 Length of labour (minute; onset of first stage to delivery) Show forest plot | 1 | 92 | Std. Mean Difference (IV, Fixed, 95% CI) | ‐0.10 [‐0.51, 0.31] |
| 5 Support received by staff Show forest plot | 1 | 59 | Mean Difference (IV, Fixed, 95% CI) | 2.20 [‐2.19, 6.59] |
| 6 Women's internal control during labour and birth Show forest plot | 1 | 59 | Mean Difference (IV, Fixed, 95% CI) | ‐0.30 [‐4.99, 4.39] |
| 7 Women's external control during labour and birth Show forest plot | 1 | 59 | Mean Difference (IV, Fixed, 95% CI) | 2.60 [‐2.25, 7.45] |
| 8 Spontaneous vaginal birth Show forest plot | 3 | 444 | Risk Ratio (M‐H, Fixed, 95% CI) | 1.35 [1.13, 1.62] |
| 9 Diagnosis of chorioamnionitis Show forest plot | 2 | 404 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.70 [0.44, 1.12] |
| 10 Incidence of hyperstimulation Show forest plot | 4 | 644 | Risk Ratio (M‐H, Random, 95% CI) | 1.47 [0.73, 2.94] |
| 11 Instrumental vaginal birth Show forest plot | 3 | 444 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.83 [0.61, 1.13] |
| 12 Incidence of postpartum haemorrhage Show forest plot | 1 | 94 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.95 [0.61, 1.48] |
| 13 Epidural analgesia Show forest plot | 2 | 404 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.98 [0.86, 1.12] |
| 14 Pathological cardiotocography (CTG) leading to immediate birth without fetal blood sampling Show forest plot | 1 | 94 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.6 [0.29, 1.23] |
| 15 Neonatal admission to special care baby units Show forest plot | 2 | 404 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.50 [0.22, 1.15] |
| 16 Apgar score less than 7 at 5 minutes Show forest plot | 3 | 444 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.37 [0.02, 8.50] |
| 17 Umbilical cord (artery) pH Show forest plot | 2 | 134 | Mean Difference (IV, Fixed, 95% CI) | 0.0 [‐0.03, 0.03] |
| 18 Subgroup analysis: Caesarean section by parity Show forest plot | 3 | 444 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.64 [0.44, 0.91] |
| 18.1 Nulliparous women | 3 | 300 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.71 [0.47, 1.06] |
| 18.2 Multiparous women | 1 | 144 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.43 [0.19, 0.97] |
