Prophylactic oral betamimetics for reducing preterm birth in women with a twin pregnancy
Abstract
Background
Twin pregnancies are associated with a high risk of neonatal mortality and morbidity due to an increased rate of preterm birth. Betamimetics can decrease contraction frequency or delay preterm birth in singleton pregnancies by 24 to 48 hours. The efficacy of oral betamimetics in women with a twin pregnancy is unproven.
Objectives
To assess the effectiveness of prophylactic oral betamimetics for the prevention of preterm labour and birth for women with twin pregnancies.
Search methods
We searched the Cochrane Pregnancy and Childbirth Group Trials Register (21 September 2015), MEDLINE (January 1966 to 31 July 2015), EMBASE (January 1985 to 31 July 2015) and reference lists of retrieved studies.
Selection criteria
Randomised controlled trials in twin pregnancies comparing oral betamimetics with placebo or any intervention with the specific aim of preventing preterm birth. Quasi‐randomised controlled trials, cluster‐randomised trials and cross‐over trials were not eligible for inclusion.
Data collection and analysis
Two review authors independently assessed trials for inclusion and risk of bias, extracted data and checked them for accuracy. Two authors assessed the quality of the evidence using the GRADE approach.
Main results
Overall, the quality of evidence is low for the primary outcomes. All of the included trials had small numbers of participants and few events. Preterm birth, the most important primary outcome, had wide confidence intervals crossing the line of no effect.
Six trials (374 twin pregnancies) were included, but only five trials (344 twin pregnancies) contributed data. All trials compared oral betamimetics with placebo.
Betamimetics reduced the incidence of preterm labour (two trials, 194 twin pregnancies, risk ratio (RR) 0.37; 95% confidence interval (CI) 0.17 to 0.78; low quality evidence). However, betamimetics did not reduce prelabour rupture of membranes (one trial, 144 twin pregnancies, RR 1.42; 95% CI 0.42 to 4.82; low quality evidence), preterm birth less than 37 weeks' gestation (four trials, 276 twin pregnancies, RR 0.85; 95% CI 0.65 to 1.10; low quality evidence), or less than 34 weeks' gestation (one trial, 144 twin pregnancies, RR 0.47; 95% CI 0.15 to 1.50; low quality evidence). Mean neonatal birthweight in the betamimetic group was significantly higher than in the placebo group (three trials, 478 neonates, mean difference 111.22 g; 95% CI 22.21 to 200.24). Nevertheless, there was no evidence of an effect of betamimetics in reduction of low birthweight (two trials, 366 neonates, average RR 1.19; 95% CI 0.77 to 1.85, random‐effects), or small‐for‐gestational age neonates (two trials, 178 neonates, average RR 0.90; 95% CI 0.41 to 1.99, random‐effects). Two trials showed that betamimetics significantly reduced the incidence of respiratory distress syndrome (388 neonates, RR 0.30; 95% CI 0.12 to 0.77), but the difference was not significant when the analysis was adjusted to account for the non‐independence of twins (194 twins, RR 0.35; 95% CI 0.11 to 1.16). Three trials showed no evidence of an effect of betamimetics in reducing neonatal mortality, either with the unadjusted analysis, assuming twins are completely independent of each other (452 neonates, average RR 0.90; 95% CI 0.15 to 5.37, random‐effects), or in the adjusted analysis, assuming non‐independence of twins (226 twins, average RR 0.74; 95% CI 0.23 to 2.38, random‐effects). A maternal death was reported in one trial without a significant difference between the groups (144 women, RR 2.84; 95% CI 0.12 to 68.57).
Authors' conclusions
There is insufficient evidence to support or refute the use of prophylactic oral betamimetics for preventing preterm birth in women with a twin pregnancy.
PICOs
Plain language summary
Oral betamimetics for the prevention of preterm labour and birth for women with twin pregnancies
There is insufficient evidence from randomised controlled trials to support the routine use of oral betamimetics (drugs that reduce or prevent uterine contraction) to prevent preterm birth of twins.
When babies are born too early they can suffer from ill health, which is sometimes severe and very occasionally babies die. This may be due to their lungs and other organs not being mature enough. The problems related to preterm birth may also result in long‐term disabilities including cerebral palsy. Twins are more likely to be born early, have intrauterine growth restriction, and suffer from these problems. Drugs that reduce labour contractions (betamimetics) have been found to delay preterm birth when the mothers are carrying a single baby. However, this review of six trials (374 twin pregnancies) with only five trials (344 twin pregnancies) contributing data, found insufficient evidence to support the routine use of oral betamimetics. The results of two small studies suggested that betamimetics can reduce the incidence of preterm labour, but the results from four trials did not show a reduction in preterm births at less than 34 or 37 weeks' gestation. There was no evidence of an effect of betamimetics in reducing the number of low‐ or small‐for‐gestational age babies or deaths in newborns. The difference in the incidence of respiratory distress syndrome with betamimetics was not clear. Betamimetic drugs can cause maternal adverse effects such as heart palpitations, although this was not reported in the included trials. The quality of evidence is low because there were small numbers of participants and few outcomes in the included trials.
The gestational age at trial entry ranged from 20 weeks to 34 weeks. The types and doses of betamimetics used in the trials varied and the outcomes reported were incomplete and defined in different ways. None of the included trials described whether or not steroids were used before birth to improve the baby’s lung maturity.
Authors' conclusions
Summary of findings
| Oral betamimetic versus placebo for pregnant women with a twin pregnancy to prevent preterm birth | ||||||
| Patient or population: pregnant women with a twin pregnancy Comparison: placebo | ||||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect | No of participants | Quality of the evidence | Comments | |
| Assumed risk | Corresponding risk | |||||
| Control | Oral betamimetic versus placebo | |||||
| Preterm labour | Study population | RR 0.37 | 194 | ⊕⊕⊝⊝ | ||
| 179 per 1000 | 66 per 1000 | |||||
| Moderate | ||||||
| 314 per 1000 | 116 per 1000 | |||||
| Prelabour rupture of membranes | Study population | RR 1.42 | 144 | ⊕⊕⊝⊝ | ||
| 57 per 1000 | 81 per 1000 | |||||
| Preterm birth (less than 37 weeks' gestation) | Study population | RR 0.85 | 276 | ⊕⊕⊝⊝ | ||
| 478 per 1000 | 406 per 1000 | |||||
| Moderate | ||||||
| 427 per 1000 | 363 per 1000 | |||||
| Very preterm birth (less than 34 weeks' gestation) | Study population | RR 0.47 | 144 | ⊕⊕⊝⊝ | ||
| 114 per 1000 | 54 per 1000 | |||||
| *The basis for the assumed risk (e.g. the median control group risk across studies) is provided in footnotes. The corresponding risk (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). | ||||||
| GRADE Working Group grades of evidence | ||||||
| 1 Unclear risk of selection bias (‐1). | ||||||
Background
Description of the condition
The incidence of twins and higher order multiple pregnancy is increasing because of various factors including the wide availability of assisted reproductive technologies. In the United States, the rate of twin pregnancies rose from 18.9 per 1000 births in 1980 to 33.1 per 1000 births in 2012 (Martin 2013). Twin pregnancies carry a higher risk of neonatal mortality compared to singleton pregnancies. In 2010 in the United States, infant mortality in twin pregnancies was 24.03 per 1000 livebirths while it was 5.45 per 1000 livebirths in singleton pregnancies (Mathews 2013). In addition to increased perinatal mortality, perinatal morbidity is also more likely. The increased risk of neonatal death and long‐term morbidity among twin infants is likely attributable to increased preterm birth and low birthweight (Newman 2012).
Nearly 60% of twins are born preterm (Conde‐Agudelo 2014). Twins are 5.7 times more likely to be born at less than 37 weeks of gestation compared with singletons and 7.1 times more likely to be born at less than 32 weeks of gestation (Conde‐Agudelo 2014). Problems related to preterm birth result in significant anxiety for the parents; in addition, these problems are also public health concerns because the premature babies need care with high cost and may have long‐term disabilities. Preterm birth is associated with respiratory distress syndrome (a respiratory disorder that is characterised by failure of the immature lungs to expand and contract properly during breathing), intracranial haemorrhage (bleeding within the brain), necrotising enterocolitis (a serious gastrointestinal disease in neonates characterised by mucosal or transmucosal necrosis of part of the intestine), bronchopulmonary dysplasia (a chronic lung condition that is caused by tissue damage to the lungs and usually occurs in immature infants who have received mechanical ventilation and supplemental oxygen), and cerebral palsy (a disability resulting from damage to the brain before, during, or shortly after birth and outwardly manifested by muscular incoordination and speech disturbances). A case‐control study based on the Swedish Medical Birth Registry and the Swedish Hospital Discharge Registry showed that when looking at a group of infants with cerebral palsy and a group of non‐cerebral palsy controls, twins were identified significantly more often in the group with cerebral palsy (odds ratio 1.4, 95% confidence interval 1.1 to 1.6) (Thorngren‐Jerneck 2006). From a European multicentre study, the rate of cerebral palsy in children born in 1975 to 1990 increased from 1.8 per 1000 live births of singleton pregnancy to 7.6 per 1000 live births of twin pregnancy (Topp 2004).
Description of the intervention
Reducing the rate of preterm birth in twins is a major goal of obstetricians worldwide. However, interventions to prevent preterm labour in twin pregnancies have been disappointing. Bed rest is the oldest proposed method for the prevention of preterm birth in twin pregnancies. A meta‐analysis found not enough evidence to support a policy of routine hospitalisation for bed rest in multiple pregnancy (Crowther 2010). Similarly, prophylactic cerclage has not been shown to be effective in preventing preterm birth in twins (Rafael 2014). Home uterine activity monitoring may possibly have a role in predicting preterm birth in very small and specific populations; however, there is insufficient evidence supporting benefit in preventing preterm birth in twin gestations (Reichmann 2009). Prenatal administration of progesterone has demonstrated an effectiveness on the reduction of preterm birth in singleton pregnancies in women who are high risk for preterm birth (women with a past history of spontaneous preterm birth or short cervix) (Dodd 2013). However, progesterone treatment could not prevent preterm birth in women with a multiple pregnancy (Dodd 2013).
Betamimetics or beta‐adrenergic agonists have been used for tocolysis since the 1980s. These drugs include beta‐1 agonist (isoxsuprine) and beta‐2 agonists (ritodrine, salbutamol, terbutaline, hexoprenaline, orciprenaline, fenoterol). They cause myometrial relaxation by activating adenyl cyclase to form cyclic adenosine monophosphate (cAMP) that will decrease myosin light‐chain kinase activity (Simhan 2007). Betamimetics given to women with preterm labour can delay birth by 48 hours to seven days (Neilson 2014). Additional to intervention for reducing preterm birth, corticosteroids administration to mothers prior to preterm birth was shown to be effective in preventing respiratory distress syndrome and neonatal mortality (Roberts 2006).
How the intervention might work
The uterine contraction is recognised antecedent of preterm birth. To prevent contractions using oral betamimetics might be an approach for reducing preterm labour and preterm birth in twin pregnancies.
Why it is important to do this review
The effectiveness of betamimetics in preventing preterm labour and preterm birth in twins is still unproven. Furthermore, betamimetics can cause maternal adverse effects from minor symptoms such as palpitations to life‐threatening conditions such as pulmonary oedema (Sciscione 2003), and have been associated with maternal death. We conducted this review to evaluate the role of prophylactic oral betamimetics administered to women with a twin pregnancy for the prevention of preterm labour and preterm birth. The primary outcomes are the incidence of preterm labour, preterm birth, neonatal mortality, neonatal morbidity, and adverse maternal effects.
Objectives
To assess the effectiveness of prophylactic oral betamimetics for the prevention of preterm labour and birth for women with twin pregnancies.
Methods
Criteria for considering studies for this review
Types of studies
Randomised controlled trials. Quasi‐randomised controlled trials, cluster‐randomised trials and cross‐over trials were not eligible for inclusion.
Types of participants
All pregnant women carrying twins who did not show signs of preterm labour and had a gestational age between 20 weeks and 37 weeks.
Types of interventions
Oral betamimetic drugs (any dosage regimen, any agent) compared with placebo or any other intervention aimed at decreasing preterm labour and preterm birth.
Types of outcome measures
Primary outcomes
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Spontaneous onset preterm labour
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Preterm prelabour rupture of membranes
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Preterm birth
Secondary outcomes
Neonatal and infant outcomes
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Neonatal mortality
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Low birthweight (less than 2500 g), small‐for‐gestational age (birthweight less than 10th centile) and birthweight (not prespecified)
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Admission neonatal intensive care unit
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Use of mechanical ventilation
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Respiratory distress syndrome
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Intracranial haemorrhage (diagnosed by ultrasonography or postmortem)
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NecrotiSing enterocolitis
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Length of hospital stay
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Bronchopulmonary dysplasia
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Abnormal neurodevelopmental status at more than 12 months corrected age (developmental delay and/or cerebral palsy)
Adverse maternal effects
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Pulmonary oedema
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Cardiac arrhythmias
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Glucose intolerance
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Postpartum haemorrhage
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Maternal death.
Search methods for identification of studies
The following methods section of this review is based on a standard template used by the Cochrane Pregnancy and Childbirth Group.
Electronic searches
We searched the Cochrane Pregnancy and Childbirth Group’s Trials Register by contacting the Trials Search Co‐ordinator (21 September 2015).
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 (Ovid);
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weekly searches of Embase (Ovid);
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monthly searches of CINAHL (EBSCO);
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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, Embase and CINAHL, 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 searched MEDLINE (January 1966 to 31 July 2015) and EMBASE (January 1985 to 31 July 2015) using the search strategy detailed in Appendix 1.
Searching other resources
We searched cited references from retrieved articles and reviewed abstracts and letters to the editor to identify randomised controlled trials that have not been published. If a randomised controlled trial was identified, we contacted the primary author directly to obtain further data. We also reviewed editorials, indicating expert opinion, to identify and ensure that no key studies were missed for inclusion in this review.
We did not apply any language or date restrictions
Data collection and analysis
For methods used in the previous version of this review, see Yamasmit 2012.
For this update, the following methods were used for assessing the reports that were identified as a result of the updated search.
The following methods section of this review is based on a standard template used by the Cochrane Pregnancy and Childbirth Group.
Selection of studies
Two review authors independently assessed for inclusion all the potential studies identified as a result of the search strategy. We resolved any disagreement through discussion or, if required, we consulted the third review author.
Data extraction and management
We designed a form to extract data. For eligible studies, two review authors extracted the data using the agreed form. We resolved discrepancies through discussion or, if required, we consulted a third review author. Data were entered into Review Manager software (RevMan 2014) and checked for accuracy.
If information regarding any of the above was unclear, we planned to contact authors of the original reports to provide further details.
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). Any disagreement was resolved 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:
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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 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:
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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.
(3.1) 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 that studies were at low risk of bias if they were blinded, or if we judged that the lack of blinding was 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.
(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:
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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 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 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 which we undertook.
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 described 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 described for each included study any important concerns we had about other possible sources 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 Handbook (Higgins 2011). With reference to (1) to (6) above, we planned to assess the likely magnitude and direction of the bias and whether we considered it is likely to impact on the findings. In future updates, we will explore the impact of the level of bias through undertaking sensitivity analyses ‐ seeSensitivity analysis.
Assessment of the quality of the evidence using GRADE
For this update, we assessed the quality of the evidence using the GRADE approach as outlined in the GRADE Handbook in order to assess the quality of the body of evidence relating to the following outcomes for the main comparisons:
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preterm labour;
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preterm prelabour rupture of membranes;
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preterm birth ‐ less than 37 weeks' gestation;
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preterm birth ‐ less than 34 weeks' gestation
We used the GRADEpro Guideline Development Tool to import data from Review Manager 5.3 (RevMan 2014) in order to create a ’Summary of findings’ table. A summary of the intervention effect and a measure of quality for each of the above outcomes was produced using the GRADE approach. The GRADE approach uses five considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of the body of evidence for each outcome. The evidence can be downgraded from 'high quality' by one level for serious (or by two levels for very serious) limitations, depending on assessments for risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates or potential publication bias.
Measures of treatment effect
Dichotomous data
For dichotomous data, we presented results as summary risk ratio with 95% confidence intervals.
Continuous data
We used the mean difference if outcomes were measured in the same way between trials. In future updates, where necessary, we will use the standardised mean difference to combine trials that measure the same outcome, but used different methods.
Unit of analysis issues
Cluster‐randomised trials
Cluster‐randomised trials are not eligible for inclusion in this review.
Cross‐over trials
Cross‐over trials are not eligible for inclusion in this review.
Multiple pregnancies
We used the number of women as the denominator for the incidence of preterm labour and birth and adverse maternal effects. For neonatal and infant outcomes, we used the number of babies as the denominator. To avoid incorrect conclusions due to the non‐independence of babies from twin pregnancies, the sensitivity analysis was performed assuming different degrees of correlation between twins. This was done by dividing both numerator and denominator by either the numbers one or two. Dividing by one gave the unadjusted figures, assuming independence between twins, whereas dividing by two gave the most conservative figures, assuming complete correlation.
Dealing with missing data
For included studies, levels of attrition were noted. In future updates, if more eligible 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.
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. 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 Tau², I² and Chi² statistics. We regarded heterogeneity as substantial if the I² was greater than 30% and either the Tau² was greater than zero, or there was a low P value (less than 0.10) in the Chi² test for heterogeneity. Had we identified substantial heterogeneity (above 30%), we planned to explore it by pre‐specified subgroup analysis.
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.
Data synthesis
We carried out statistical analysis using the Review Manager software (RevMan 2014). 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 differed between trials, or if substantial statistical heterogeneity was detected, we used random‐effects meta‐analysis to produce an overall summary, if an average treatment effect across trials was considered clinically meaningful. The random‐effects summary was treated as the average range of possible treatment effects and we discussed the clinical implications of treatment effects differing between trials. If the average treatment effect was not clinically meaningful, we did not combine trials. Where we used random‐effects analyses, the results were presented as the average treatment effect with 95% confidence intervals, and the estimates of Tau² and I².
Subgroup analysis and investigation of heterogeneity
Had we identified substantial heterogeneity, we planned to investigate it using subgroup analyses and sensitivity analyses. We would have considered whether an overall summary was meaningful, and if it was, we would have used random‐effects analysis to produce it.
In future updates, we plan to carry out the following subgroup analyses:
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type of betamimetic agent;
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setting (income‐rich countries and income‐poor/medium countries).
The following outcomes were planned for use in subgroup analyses:
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preterm labour;
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preterm prelabour rupture of membranes;
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preterm birth.
There were too few trials included in this review to conduct meaningful subgroup analysis.
In future updates, we will assess subgroup differences by interaction tests available within RevMan (RevMan 2014). We will report the results of subgroup analyses quoting the Chi² statistic and P value, and the interaction test I² value.
Sensitivity analysis
We planned to carry out sensitivity analyses to explore the effect of trial quality assessed by concealment of allocation, high attrition rates, or both, with poor quality studies being excluded from the analyses in order to assess whether this makes any difference to the overall result.
There were too few trials included in this review to conduct meaningful sensitivity analysis.
Results
Description of studies
Results of the search
There were no new studies identified in the Pregnancy and Childbirth Group's Trials Register for this update. Our additional MEDLINE and Embase search retrieved 29 hits but none were potentially eligible for inclusion.
Eleven studies were identified as potentially eligible for inclusion in this review. Six trials (involving 374 twin pregnancies) were included, but only five trials (344 twin pregnancies) contributed data towards our analyses (Cetrulo 1976 did not report on the outcomes of interest).
Included studies
A total of 374 twin pregnant women participated in the six included studies comparing oral betamimetic agents with placebo (Ashworth 1990; Cetrulo 1976; Marivate 1977; Mathews 1967; O'Connor 1979; Skjaerris 1982). No outcome data were shown in one preliminary report (Cetrulo 1976), so only five studies with 344 twin pregnant women (Ashworth 1990; Marivate 1977; Mathews 1967; O'Connor 1979; Skjaerris 1982) contributed data. In one study (Mathews 1967), only the subset of trial participants who had a twin pregnancy (39 of 103 participants) was included.
Participants
Two trials (Ashworth 1990; Marivate 1977) were conducted in African countries, one trial was conducted in the United States (Cetrulo 1976), while the remaining three trials were conducted in Europe (Mathews 1967; O'Connor 1979; Skjaerris 1982). The mean age of participants, when described, was between 25.3 and 27.3 years. The gestational age at trial entry ranged from 20 weeks to 34 weeks. The mean gestational age at entry, when reported, was between 27.6 and 31.8 weeks. All trials except two (Cetrulo 1976; Mathews 1967) described that women with medical or obstetrical complications were excluded.
Interventions
All trials compared oral betamimetic agents with placebo, however, the types of betamimetic agents used in the trials were different (seeCharacteristics of included studies). The betamimetic agents in the trials included salbutamol (Ashworth 1990), fenoterol (Marivate 1977), isoxuprine (Mathews 1967), ritodrine (Cetrulo 1976; O'Connor 1979), and terbutaline (Skjaerris 1982). All trials stopped the medication at 36 to 38 weeks of gestation, or when labour started. The mean length of treatment, when reported, was between 32.6 and 63.4 days. None of the included trials described whether or not steroids were used for fetal lung maturity enhancement.
Outcomes
Two studies (Ashworth 1990; Skjaerris 1982) reported the incidence of preterm labour. The incidence of prelabour rupture of membranes was reported in only one trial (Ashworth 1990). All trials except one (Cetrulo 1976) showed the incidence of preterm birth, but they used a different cut‐off for gestational age. Three trials (Ashworth 1990; O'Connor 1979; Skjaerris 1982) used 37 weeks' gestation as a cut‐off, Mathews 1967 used 36 weeks', and Marivate 1977 used 38 weeks'. In addition, the trials used different methods for determining gestational age. Three studies used Dubowitz score (Cetrulo 1976; Marivate 1977; O'Connor 1979), one trial used certain last menstrual date or ultrasound (Ashworth 1990), and the remaining studies did not describe a specific method. There was also some inconsistency across trials with respect to the reporting methods of neonatal and maternal outcomes (seeCharacteristics of included studies).
Excluded studies
Five trials were excluded. Two studies were trials of maintenance tocolytic therapy (Gummerus 1985; Keirse 1990). Two trials were designed to determine the additional effect of betamimetics with other interventions (Endl 1982; Melrose 1988). The other trial was excluded due to participants including triplet pregnancies (Gummerus 1987). SeeCharacteristics of excluded studies table.
Risk of bias in included studies
The risk of bias in the included trials is summarised in the 'Risk of bias' summary figures (Figure 1; Figure 2).
'Risk of bias' summary: review authors' judgements about each risk of bias item for each included study.
'Risk of bias' graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
Allocation
Only one trial (Ashworth 1990) described the method of random sequence generation. Allocation concealment was reported in three trials (Ashworth 1990; Mathews 1967; O'Connor 1979). The remaining trials did not describe the precise method of random allocation.
Blinding
All of the trials were double‐blind studies. The primary and secondary outcomes were all objective outcomes; however, there was some inconsistency across trials with respect to the reporting methods of neonatal and maternal outcomes.
Incomplete outcome data
No outcome data were shown in one trial (Cetrulo 1976). Three of the trials had complete follow‐up (Marivate 1977; Mathews 1967; Skjaerris 1982). One study had a 10% loss to follow‐up rate (Ashworth 1990) that occurred more frequently in the betamimetic (10/80) than in the placebo group (6/80). Another study (O'Connor 1979) had no loss of follow‐up, but in 12.2% of all participants the neonates were not assessed for Dubowitz score (4/25 in the betamimetic group and 2/24 in the placebo group).
Selective reporting
No outcome and follow‐up data were shown in the preliminary report of (Cetrulo 1976). Three trials (Ashworth 1990; Marivate 1977; O'Connor 1979) had no apparent reporting bias. The other trials (Mathews 1967; Skjaerris 1982) had unclear risk for reporting bias.
Other potential sources of bias
One trial (Skjaerris 1982) that showed positive results did not declare sponsorship. The other trials showed no other potential sources of bias.
Effects of interventions
This review included six trials (involving 374 twin pregnancies), but only five trials (344 twin pregnancies) contributed data towards our analyses. Cetrulo 1976 did not report on the outcomes of interest.
From a total of 344 twin pregnancies. A total of 174 women were randomised to prescription of oral betamimetic agents and 170 women were randomised to placebo.
Comparison: Prophylactic oral betamimetics versus placebo
Primary outcomes
Spontaneous onset of preterm labour
Two trials reported this outcome (Ashworth 1990; Skjaerris 1982). The use of oral betamimetic agents resulted in a statistically significant decrease in the incidence of preterm labour (194 twin pregnancies, risk ratio (RR) 0.37; 95% confidence interval (CI) 0.17 to 0.78) (Analysis 1.1).
Prelabour rupture of membranes
Only one trial reported this outcome (Ashworth 1990). The results showed no evidence of an effect of oral betamimetic agents in reduction of prelabour rupture of membranes (144 twin pregnancies, RR 1.42; 95% CI 0.42 to 4.82) (Analysis 1.2).
Preterm birth
Four trials reported the incidence of birth less than 37 weeks' gestation (Ashworth 1990; Mathews 1967; O'Connor 1979; Skjaerris 1982), and one trial reported the incidence of birth at less than 34 weeks' gestation (Ashworth 1990). The results showed no evidence of an effect of oral betamimetic agents in reduction of preterm birth less than 37 weeks' gestation (276 twin pregnancies, RR 0.85; 95% CI 0.65 to 1.10) (Analysis 1.3), or 34 weeks' gestation (144 twin pregnancies, RR 0.47; 95% CI 0.15 to 1.50) (Analysis 1.4). No significant heterogeneity was noted.
Secondary outcomes
Neonatal and infant outcomes
Neonatal mortality
This outcome was not mentioned in two trials (Marivate 1977; Skjaerris 1982). Three trials with a total of 452 neonates (Ashworth 1990; Mathews 1967; O'Connor 1979) showed no evidence of an effect of oral betamimetic agents in reduction of neonatal mortality (average RR 0.90; 95% CI 0.15 to 5.37, I² = 47%, random‐effects) (Analysis 1.5). There was also no evidence of an effect when the analysis was adjusted for correlation of babies from twins (226 twins, average RR 0.74; 95% CI 0.23 to 2.38, I² = 0%, random‐effects).
Low birthweight, small‐for‐gestational age and birthweight
Two trials (Ashworth 1990; Mathews 1967) reported the rate of low birthweight in neonates. No evidence of an effect of oral betamimetic agents in reduction of low birthweight was noted (366 neonates, average RR 1.19; 95% CI 0.77 to 1.85, I² = 54%, random‐effects). If the twins were completely correlated (183 twins), average RR would be 1.09; 95% CI 0.81 to 1.47, I² = 3%, random‐effects (Analysis 1.6). Proportions of neonates with small‐for‐gestational age were reported in two trials (Marivate 1977; O'Connor 1979). There was also no evidence of an effect of oral betamimetic agents in reduction of small‐for‐gestational age either twins were independent (178 neonates, average RR 0.90; 95% CI 0.41 to 1.99, I² = 40%, random‐effects), or correlated (89 twins, average RR 0.95; 95% CI 0.42 to 2.13, I² = 0%, random‐effects) (Analysis 1.7). However, the results from three trials (Ashworth 1990; Marivate 1977; O'Connor 1979) showed that mean birthweight in neonates whose mothers received oral betamimetics was significantly higher than in neonates whose mothers received placebo (478 neonates, mean difference (MD) 111.22 g; 95% CI 22.21 to 200.24) (Analysis 1.8).
Respiratory distress syndrome
Two trials reported the incidence of respiratory distress syndrome in neonates (Ashworth 1990; Skjaerris 1982). In one trial, this outcome was defined as clinically significant if the baby required oxygen therapy from a headbox or ventilator, but the other trial did not show how this outcome was diagnosed. From these trials, neonates in the betamimetics group had a lower incidence of respiratory distress syndrome, compared to those in the placebo group (388 neonates, RR 0.30; 95% CI 0.12 to 0.77) (Analysis 1.9). However, in the adjusted analysis accounting for the correlation of babies from the twin pregnancies, the difference between the groups was not significant (194 twins, RR 0.35; 95% CI 0.11 to 1.16) (Analysis 1.9).
No trials reported on admission neonatal intensive care unit, use of mechanical ventilation, intracranial haemorrhage, necrotising enterocolitis, length of hospital stay, bronchopulmonary dysplasia and abnormal neurodevelopmental status.
Adverse maternal effects
Pulmonary oedema, cardiac arrhythmias, glucose intolerance and postpartum haemorrhage were not reported in the trials. The only maternal death was reported in one trial (Ashworth 1990), and no difference between the groups was noted (144 women, RR 2.84; 95% CI 0.12 to 68.57) (Analysis 1.10).
Discussion
Summary of main results
Results of two studies (Ashworth 1990; Skjaerris 1982) suggested that betamimetics can reduce the rate of preterm labour, but there was not enough evidence to suggest that this intervention could reduce the incidence of prelabour rupture of membranes or preterm birth. The difference in incidence of respiratory distress syndrome in neonates between the groups was not clear because the sensitivity analyses for different degrees of correlation between twins showed contrary results. The criteria used for diagnosis and assessment of severity of respiratory distress syndrome in various studies remains to be verified and the information as to whether there were any undisclosed co‐interventions, such as steroid administration, needs to be ascertained. The neonates in the betamimetic group had a higher mean birthweight than in the placebo group, with a mean difference of 111.22 g. The clinical relevance on childhood and later outcomes is uncertain. This finding was statistically significant, but has limited clinical importance as the mean birthweight of neonates in the placebo group was between 2360 and 2670 g. More importantly, there were no demonstrable differences between neonates in the betamimetic and placebo groups in the incidence of low birthweight, small‐for‐gestational age or neonatal mortality.
Most of the secondary outcomes were not reported in the included trials. These outcomes included admission neonatal intensive care unit, use of mechanical ventilation, intracranial haemorrhage, necrotising enterocolitis, length of hospital stay, bronchopulmonary dysplasia, abnormal neurodevelopmental status, and all maternal morbidities (pulmonary oedema, cardiac arrhythmias, glucose intolerance and postpartum haemorrhage).
One maternal death was reported in one trial (Ashworth 1990). The woman had been taking salbutamol for 12 days before having a precipitous labour at home. Postpartum haemorrhage was reported as the cause of death. The death may be related to the intervention if the haemorrhage was due to uterine atony, but no detail regarding the cause of haemorrhage was described.
Overall completeness and applicability of evidence
There were some limitations that should be considered in interpretation of the results.
Firstly, the allocation concealment was not clearly defined in three of the six trials. Of the other three trials with adequate allocation concealment, two trials had some participants, mostly in the betamimetic group, with incomplete outcome measurements.
Secondly, types and doses of betamimetics used in the trials varied. However, the dosage of each betamimetic used in these trials is comparable to dosage used in a singleton pregnancy (Neilson 2014).
Thirdly, the outcomes reported in the trials were incomplete and variously defined. No trial reported on childhood outcomes.
Quality of the evidence
Overall, the quality of evidence is low for the primary outcomes: preterm labour; prelabour rupture of membranes; preterm birth less than 37 weeks' gestation; very preterm birth less than 34 weeks' gestation, see summary of findings Table for the main comparison. All of the included trials had small numbers of participants and few events, which led to downgrading evidence for imprecision of findings. Preterm birth, the most important primary outcome, had wide confidence intervals crossing the line of no effect.
Potential biases in the review process
We were aware of the possibility of introducing bias at every stage of the reviewing process. In this updated review, we tried to minimise bias in a number of ways. The eligibility for inclusion of the trials was assessed in duplicate, and two review authors carried out data extraction and assessed risk of bias; each worked independently. Nevertheless, the process of assessing risk of bias, for example, is not an exact science and includes many personal judgements. Further, the process of reviewing research studies is known to be affected by prior beliefs and attitudes. It is difficult to control for this type of bias in the reviewing process.
Agreements and disagreements with other studies or reviews
There is limited evidence regarding the use of oral betamimetics for reducing preterm birth. In a Cochrane review (Whitworth 2008), insufficient evidence was also found to support or refute the use of prophylactic oral betamimetics for preventing preterm birth in women at high risk of preterm labour with a singleton pregnancy.
'Risk of bias' summary: review authors' judgements about each risk of bias item for each included study.
'Risk of bias' graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
Comparison 1 Oral betamimetic versus placebo, Outcome 1 Preterm labour.
Comparison 1 Oral betamimetic versus placebo, Outcome 2 Prelabour rupture of membranes.
Comparison 1 Oral betamimetic versus placebo, Outcome 3 Preterm birth (less than 37 weeks' gestation).
Comparison 1 Oral betamimetic versus placebo, Outcome 4 Preterm birth (less than 34 weeks' gestation).
Comparison 1 Oral betamimetic versus placebo, Outcome 5 Neonatal mortality.
Comparison 1 Oral betamimetic versus placebo, Outcome 6 Low birthweight (less than 2500 g).
Comparison 1 Oral betamimetic versus placebo, Outcome 7 Small‐for‐gestational age (birthweight less than 10th centile).
Comparison 1 Oral betamimetic versus placebo, Outcome 8 Birthweight (not prespecified).
Comparison 1 Oral betamimetic versus placebo, Outcome 9 Respiratory distress syndrome.
Comparison 1 Oral betamimetic versus placebo, Outcome 10 Maternal death.
| Oral betamimetic versus placebo for pregnant women with a twin pregnancy to prevent preterm birth | ||||||
| Patient or population: pregnant women with a twin pregnancy Comparison: placebo | ||||||
| Outcomes | Illustrative comparative risks* (95% CI) | Relative effect | No of participants | Quality of the evidence | Comments | |
| Assumed risk | Corresponding risk | |||||
| Control | Oral betamimetic versus placebo | |||||
| Preterm labour | Study population | RR 0.37 | 194 | ⊕⊕⊝⊝ | ||
| 179 per 1000 | 66 per 1000 | |||||
| Moderate | ||||||
| 314 per 1000 | 116 per 1000 | |||||
| Prelabour rupture of membranes | Study population | RR 1.42 | 144 | ⊕⊕⊝⊝ | ||
| 57 per 1000 | 81 per 1000 | |||||
| Preterm birth (less than 37 weeks' gestation) | Study population | RR 0.85 | 276 | ⊕⊕⊝⊝ | ||
| 478 per 1000 | 406 per 1000 | |||||
| Moderate | ||||||
| 427 per 1000 | 363 per 1000 | |||||
| Very preterm birth (less than 34 weeks' gestation) | Study population | RR 0.47 | 144 | ⊕⊕⊝⊝ | ||
| 114 per 1000 | 54 per 1000 | |||||
| *The basis for the assumed risk (e.g. the median control group risk across studies) is provided in footnotes. The corresponding risk (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). | ||||||
| GRADE Working Group grades of evidence | ||||||
| 1 Unclear risk of selection bias (‐1). | ||||||
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Preterm labour Show forest plot | 2 | 194 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.37 [0.17, 0.78] |
| 2 Prelabour rupture of membranes Show forest plot | 1 | 144 | Risk Ratio (M‐H, Fixed, 95% CI) | 1.42 [0.42, 4.82] |
| 3 Preterm birth (less than 37 weeks' gestation) Show forest plot | 4 | 276 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.85 [0.65, 1.10] |
| 4 Preterm birth (less than 34 weeks' gestation) Show forest plot | 1 | 144 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.47 [0.15, 1.50] |
| 5 Neonatal mortality Show forest plot | 3 | Risk Ratio (M‐H, Random, 95% CI) | Subtotals only | |
| 5.1 Assuming independence between twins | 3 | 452 | Risk Ratio (M‐H, Random, 95% CI) | 0.90 [0.15, 5.37] |
| 5.2 Assuming complete correlation between twins | 3 | 226 | Risk Ratio (M‐H, Random, 95% CI) | 0.74 [0.23, 2.38] |
| 6 Low birthweight (less than 2500 g) Show forest plot | 2 | Risk Ratio (M‐H, Random, 95% CI) | Subtotals only | |
| 6.1 Assuming independence between twins | 2 | 366 | Risk Ratio (M‐H, Random, 95% CI) | 1.19 [0.77, 1.85] |
| 6.2 Assuming complete correlation between twins | 2 | 183 | Risk Ratio (M‐H, Random, 95% CI) | 1.09 [0.81, 1.47] |
| 7 Small‐for‐gestational age (birthweight less than 10th centile) Show forest plot | 2 | Risk Ratio (M‐H, Random, 95% CI) | Subtotals only | |
| 7.1 Assuming independence between twins | 2 | 178 | Risk Ratio (M‐H, Random, 95% CI) | 0.90 [0.41, 1.99] |
| 7.2 Assuming complete correlation between twins | 2 | 89 | Risk Ratio (M‐H, Random, 95% CI) | 0.95 [0.42, 2.13] |
| 8 Birthweight (not prespecified) Show forest plot | 3 | 478 | Mean Difference (IV, Fixed, 95% CI) | 111.22 [22.21, 200.24] |
| 9 Respiratory distress syndrome Show forest plot | 2 | Risk Ratio (M‐H, Fixed, 95% CI) | Subtotals only | |
| 9.1 Assuming independence between twins | 2 | 388 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.30 [0.12, 0.77] |
| 9.2 Assuming complete correlation between twins | 2 | 194 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.35 [0.11, 1.16] |
| 10 Maternal death Show forest plot | 1 | 144 | Risk Ratio (M‐H, Fixed, 95% CI) | 2.84 [0.12, 68.57] |
