Description of the condition
Preterm birth, defined as birth occurring before 37 completed weeks of gestation, remains the single most important cause of perinatal mortality and morbidity. While preterm birth may occur for a variety of reasons, most preterm births occur as a result of spontaneous preterm labour. In addition to the short-term morbidity in infants born preterm there is a significant risk of long-term neurological sequelae in the survivors (Johnson 1993). The lower the gestational age of the baby at birth, the higher the risk of complications. This risk remains very high for those born extremely preterm (Agustines 2000; Kok 1998). Prematurity and its complications contribute greatly to the emotional trauma caused to the parents of the preterm infant. Therefore, a quest for interventions to prevent or reduce the incidence of preterm birth continues.
Description of the intervention
Tocolytic agents have been used to inhibit preterm labour. However, these agents have so far succeeded only in prolonging preterm labour rather than improving infant outcomes (Gyetvai 1999). Tocolytics conventionally have been used to try to prevent preterm birth, but now are mainly used to buy time for corticosteroids to be administered to mothers, to exert their beneficial effect in reducing the risks of respiratory distress syndrome and the other problems of immaturity in babies. Current evidence supports the use of a course of antenatal corticosteroids to accelerate fetal lung maturation in women at risk of preterm birth, however further evidence surrounding the optimal dose to delivery interval, optimal corticosteroid to use and longer-term effects is required (Roberts 2006).
Preterm labour is diagnosed by the presence of regular painful uterine contractions and/or evidence of cervical dilatation and effacement prior to 37 weeks' gestation. A substantial proportion of women who have an episode of threatened preterm labour and are actively treated with an acute tocolytic therapy stop contracting and have still not given birth after 48 hours. For these women, the use of tocolytic maintenance medication has been advocated to try to reduce the risk of recurrence of preterm labour and to prolong gestation.
Most tocolytics have to be administered intravenously which makes long-term therapy a difficult proposition. Moreover, there is minimal evidence to suggest that delaying birth beyond 48 hours after administration of corticosteroids is associated with clinically significant improvements for the baby, woman or the health system (Gyetvai 1999). Any benefits of prolonging gestation could be offset by potential risks such as intrauterine infections and side effects of the drugs. Infants born preterm are at increased risk of infection, jaundice, respiratory disease, intracranial haemorrhage, chronic lung disease, necrotising enterocolitis and retinopathy of prematurity. These complications translate into delayed physical and cognitive development in the child, emotional trauma for the families, and enormous costs for the healthcare system.
How the intervention might work
Calcium channel blockers have been shown to be effective acute tocolytic drugs with minimal maternal adverse effects for women in preterm labour (King 2003). These agents act to inhibit calcium influx across cell membranes, thereby decreasing tone in the smooth muscle. They act as profound vasodilatory agents and have minimal effects on the cardiac conduction system (Economy 2001). Although concerns about the effects of these agents on utero-placental blood flow have been raised in animal studies (Harake 1987), they have not been substantiated in human studies (Meyer 1990). Oral administration and minimal adverse effects make calcium channel blockers potential suitable maintenance tocolytic agents to be used longer-term to prevent preterm birth after an episode of threatened preterm labour.
Why it is important to do this review
This review updates a previously published Cochrane review on maintenance therapy with calcium channel blockers for preventing preterm birth after threatened preterm labour (Gaunekar 2004). This review included only one randomised trial (Carr 1999) and found no difference in the risk of preterm birth when calcium channel blocker maintenance therapy (nifedipine) was compared with no treatment. Stillbirths, neonatal deaths and neurological follow-up of infants were not reported. The review concluded that high-quality evidence from randomised trials was lacking in this area.
It is currently uncertain whether maintenance therapy with calcium channel blockers is effective in preventing preterm birth and its sequelae and what the personal, emotional and healthcare costs are to society. This review assesses the effectiveness of calcium channel blockers for maintenance therapy after preterm labour has been successfully arrested with an initial dose of acute tocolytic therapy. Other Cochrane reviews address the use of terbutaline pumps (Nanda 2002), magnesium sulphate (Han 2013), oral betamimetics (Dodd 2012) and oxytocin antagonists (Papatsonis 2009) for maintenance therapy.
To assess, using the best available evidence, whether calcium channel blockers as maintenance therapy after an episode of threatened preterm labour are effective and safe in preventing preterm birth and its sequelae.
Criteria for considering studies for this review
Types of studies
All published, unpublished and ongoing randomised controlled trials with reported data that compare outcomes in women and babies given calcium channel blockers after an episode of threatened preterm labour with outcomes in controls given alternative drug therapy, placebo or no treatment. We planned to exclude quasi-randomised trials and cross-over trials, and planned to include cluster-randomised trials. We have included studies published in abstract form only, along with those published as full-text manuscripts.
Types of participants
Pregnant women who have had at least one episode of threatened preterm labour (as defined by the authors) that settled without giving birth.
Types of interventions
Calcium channel blockers administered as maintenance therapy by any route and dose to women prior to birth compared with either a placebo, no treatment or alternative drug therapy. We planned to exclude studies where calcium channel blockers were used in combination with other tocolytic drugs.
Types of outcome measures
- Preterm birth
- Birth within 48 hours of treatment
- Death prior to discharge among liveborn infants
- Any neurological disability at paediatric follow-up (impairment of vision, hearing, intelligence or cerebral palsy)
These relate to other neonatal morbidity, adverse effects, women's assessment of the therapy and use of health resources.
- Maternal adverse drug reaction (such as hypotension, nausea, palpitations, headache)
- Cessation of treatment for maternal adverse drug reaction
- Maternal sepsis
- Antepartum haemorrhage
- Postpartum haemorrhage
- Maternal death
- Maternal satisfaction with treatment
- Pregnancy prolongation (interval between randomisation and delivery)
- Birth prior to 34 completed weeks
- Birth prior to 28 completed weeks
- Birth within seven days of treatment
- Gestation at birth
- Perinatal mortality
- Small-for-gestational age (as described by the authors)
- Apgar score of less than seven at five minutes
- Neonatal sepsis
- Neonatal jaundice
- Respiratory distress syndrome
- Use of mechanical ventilation
- Periventricular haemorrhage
- Intraventricular haemorrhage (grade three or four)
- Periventricular leukomalacia
- Chronic lung disease
- Air leak syndrome
- Necrotising enterocolitis
- Admission to neonatal intensive care unit
- Retinopathy of prematurity
Use of health resources
- Maternal admission to intensive care unit
- Maternal readmission for threatened preterm labour
- Neonatal length of hospital stay
- Need for maternal readmission
- Costs of therapy
Search methods for identification of studies
We searched the Cochrane Pregnancy and Childbirth Group's Trials Register by contacting the trials search coordinator (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:
- monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
- weekly searches of MEDLINE;
- weekly searches of Embase;
- handsearches of 30 journals and the proceedings of major conferences;
- weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.
Details of the search strategies for CENTRAL, MEDLINE and Embase, the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service can be found in the ‘Specialized Register’ section within the editorial information about the Cochrane Pregnancy and Childbirth Group.
Trials identified through the searching activities described above are each assigned to a review topic (or topics). The Trials Search Co-ordinator searches the register for each review using the topic list rather than keywords.
Searching other resources
We also searched reference lists of relevant articles.
We did not apply any language restrictions.
Data collection and analysis
For this update we used the following methods when assessing the reports identified by the updated search.
Selection of studies
Two review authors independently assessed for inclusion all the potential studies we identified as a result of the search strategy. We resolved any disagreement through discussion or, if required, we consulted a third 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. We entered data into Review Manager software (RevMan 2012) and checked for accuracy.
When information regarding any of the above was unclear, we attempted 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). We resolved any disagreement by discussion or by involving a third assessor.
(1) Random sequence generation (checking for possible selection bias)
We described for each included study the methods used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.
We assessed the method as:
- low risk of bias (any truly random process, e.g. random number table; computer random number generator);
- high risk of bias (any non-random process, e.g. odd or even date of birth; hospital or clinic record number);
- unclear risk of bias.
(2) Allocation concealment (checking for possible selection bias)
We described for each included study the method used to conceal allocation to interventions prior to assignment and assessed whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.
We assessed the methods as:
- low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
- high risk of bias (open random allocation; unsealed or non-opaque envelopes, alternation; date of birth);
- unclear risk of bias.
(3.1) Blinding of participants and personnel (checking for possible performance bias)
We described for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We considered that studies were at low risk of bias if they were blinded, or if we judged that the lack of blinding would be unlikely to affect results. We assessed blinding separately for different outcomes or classes of outcomes.
We assessed the methods as:
- low, high or unclear risk of bias for participants;
- low, high or unclear risk of bias for personnel.
(3.2) Blinding of outcome assessment (checking for possible detection bias)
We described for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We assessed blinding separately for different outcomes or classes of outcomes.
We assessed methods used to blind outcome assessment as:
- 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 have stated whether attrition and exclusions were reported and the numbers included in the analysis at each stage (compared with the total randomised participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. Where sufficient information was reported, or could be supplied by the trial authors, we re-included missing data in the analyses which we undertook.
We assessed methods as:
- low risk of bias (e.g. no missing outcome data; missing outcome data balanced across groups);
- high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis done with substantial departure of intervention received from that assigned at randomisation);
- unclear risk of bias.
(5) Selective reporting (checking for reporting bias)
We described for each included study how we investigated the possibility of selective outcome reporting bias and what we found.
We assessed the methods as:
- low risk of bias (where it is clear that all of the study’s pre-specified outcomes and all expected outcomes of interest to the review have been reported);
- high risk of bias (where not all the study’s pre-specified outcomes have been reported; one or more reported primary outcomes were not pre-specified; outcomes of interest are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported);
- unclear risk of bias.
(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)
We described for each included study any important concerns we had about other possible sources of bias.
We assessed whether each study was free of other problems that could put it at risk of bias:
- low risk of other bias;
- high risk of other bias;
- unclear whether there is risk of other bias.
(7) Overall risk of bias
We made explicit judgements about whether studies were at high risk of bias, according to the criteria given in the Cochrane Handbook (Higgins 2011). With reference to (1) to (6) above, we assessed the likely magnitude and direction of the bias and whether we considered it was likely to impact on the findings. We explored the impact of the level of bias through undertaking sensitivity analyses - see Sensitivity analysis.
Measures of treatment effect
For dichotomous data, we have presented results as summary risk ratio with 95% confidence intervals.
For continuous data, we have used the mean difference when outcomes were measured in the same way between trials. We planned to use the standardised mean difference to combine trials that measured the same outcome, but used different methods.
Unit of analysis issues
We planned to include cluster-randomised trials in the analyses along with individually-randomised trials. In future updates of this review if we include cluster-randomised trials, we plan to adjust their sample sizes using the methods described in the Cochrane 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 plan to 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 was little heterogeneity between the study designs and the interaction between the effect of intervention and the choice of randomisation unit is considered to be unlikely.
We plan to also acknowledge heterogeneity in the randomisation unit and perform a sensitivity analysis to investigate the effects of the randomisation unit.
We considered cross-over trials as inappropriate for inclusion in this review.
Dealing with missing data
For included studies, we noted levels of attrition. We explored 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, and all participants were analysed in the group to which they were allocated, regardless of whether or not they received the allocated intervention. The denominator for each outcome in each trial 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 the I² was greater than 30% and either the T² was greater than zero, or there was a low P value (less than 0.10) in the Chi² test for heterogeneity.
Assessment of reporting biases
If there had been 10 or more studies in a meta-analysis we planned to investigate reporting biases (such as publication bias) using funnel plots. We planned to assess funnel plot asymmetry visually. If asymmetry was suggested by a visual assessment, we planned to perform exploratory analyses to investigate it.
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. Where there was clinical heterogeneity sufficient to expect that the underlying treatment effects differed between trials, or where 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 have 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 have used random-effects analyses, the results have been presented as the average treatment effect with 95% confidence intervals, and the estimates of T² and I².
Subgroup analysis and investigation of heterogeneity
Where we have identified substantial heterogeneity, we have investigated it using subgroup analyses and sensitivity analyses. We planned to consider whether an overall summary was meaningful, and if it was, use random-effects analysis to produce it.
We planned to carry out the following subgroup analyses:
- dosage administered (i.e. high dose versus low dose);
- type of calcium channel blocker (i.e. nifedipine versus nicardipine);
- duration of use of treatment (i.e. short versus long duration of use);
- type of therapy (other tocolytic agent) in control group (i.e. placebo versus oral magnesium sulphate versus terbutaline).
We used only the primary outcomes in subgroup analyses.
We assessed subgroup differences by interaction tests available within RevMan (RevMan 2012). We have reported the results of subgroup analyses quoting the χ2 statistic and P value, and the interaction test I² value.
We were not able to perform a subgroup analysis based on type of calcium channel blocker assessed in the trial, as all trials evaluated nifedipine for maintenance tocolysis.
We carried out sensitivity analysis to explore the effects of trial quality assessed by allocation concealment and sequence generation, by omitting studies rated as 'high risk of bias' or an 'unclear risk of bias' for these components. We restricted this to the primary outcomes.
Description of studies
Results of the search
The updated search of the Pregnancy and Childbirth Group's Trials Register identified seven reports relating to five trials, which have been included in the update of this review (Lyell 2008; Parry 2012; Roos 2013; Sayin 2004; Uma 2012). In the previous version of this review, we included one trial (Carr 1999), and excluded 11 studies (Bracero 1991; El-Sayed 1998; Ferguson 1990; Garcia-Velasco 1998; Glock 1993; Janky 1990; Jannet 1997; Koks 1998; Kupferminc 1993; Larmon 1999; Papatsonis 1997). Therefore, we have included a total of six trials in the review.
The six included trials enrolled 794 women, and were conducted across a range of healthcare settings; two trials were conducted in the United States (Carr 1999; Lyell 2008), and one in Malaysia (Uma 2012), Turkey (Sayin 2004), the Netherlands (Roos 2013) and New Zealand (Parry 2012). Five of the six trials (Carr 1999; Lyell 2008; Parry 2012; Sayin 2004; Uma 2012) recruited less than 100 women; Roos 2013 was the largest trial, recruiting 406 women across 11 perinatal units in the Netherlands.
The gestational ages at which women were eligible for the six included trials varied: three trials recruited women between 24 weeks' and 34 weeks' gestation (Carr 1999; Lyell 2008; Parry 2012), one trial recruited women between 26 weeks and 32 weeks plus two days (Roos 2013), and one trial recruited women between 22 and 34 weeks (Uma 2012). The final trial (Sayin 2004) did not report the gestational ages at which women were eligible, however had a mean gestational age at trial entry for women in the treatment group of 32.3 (standard deviation (SD): 3.5) and 31.0 weeks in the control group (SD: 3.1).
In all six trials nifedipine was the calcium channel blocker assessed for the prevention of preterm birth after threatened preterm labour. Three of the six trials used a placebo (Lyell 2008; Parry 2012; Roos 2013), while three of the trials compared nifedipine with no treatment (Carr 1999; Sayin 2004; Uma 2012).
The treatment regimens by which nifedipine was administered varied across the six trials.
- Four trials (Carr 1999; Lyell 2008; Roos 2013; Sayin 2004) used very similar dosing regimens, with 20 mg oral nifedipine given every six hours (80 mg daily). In Carr 1999, Lyell 2008 and Sayin 2004 treatment was continued until 37 weeks' gestation, however in Roos 2013 treatment was phased out from day 10 (daily dose of 60 mg) until day 12 (daily dose of 20 mg), and discontinued on day 13. In three of these trials (Carr 1999; Lyell 2008; Roos 2013), it was specified that the dosing interval could be decreased by the treating physician if the symptoms continued.
- In Uma 2012, following three doses every half an hour of 20 mg oral nifedipine, 20 mg of nifedipine was given three times daily up to 36 weeks' gestation (60 mg daily).
- In Parry 2012, nifedipine was given as maintenance treatment to women in the same dose as prescribed in the preceding 24 hours until 37 weeks' gestation (no further details provided).
In three of the six trials (Carr 1999; Lyell 2008; Sayin 2004), it was detailed that if threatened preterm labour reoccurred, women could receive acute intravenous tocolytic treatment (e.g. magnesium sulphate, terbutaline), and again recommence on their maintenance study medication if the recurrent preterm labour was successfully arrested.
The acute tocolytics received by women in the six included trials prior to commencement of study treatment differed, with some trials having more than one acute tocolytic medication used; in Carr 1999 and Lyell 2008 intravenous magnesium sulphate was used; Lyell 2008, Parry 2012, Roos 2013 and Uma 2012 used nifedipine; Roos 2013 used atosiban; and Sayin 2004 used intravenous ritodrine and verapamil.
In five of the six trials (Carr 1999; Lyell 2008; Parry 2012; Roos 2013; Sayin 2004), all women received corticosteroids prior to study treatment; this was unclear in Uma 2012 (as information included in this review has been taken from a published abstract only).
Eleven studies were excluded; 10 because women were randomised for acute tocolytic therapy rather than for maintenance treatment (see Characteristics of excluded studies). These studies are (or will likely be) included in the Cochrane review 'Calcium channel blockers for inhibiting preterm labour' (King 2003). One further study, El-Sayed 1998 was excluded, as it compared two calcium channel blockers.
Risk of bias in included studies
Overall, the six included trials were judged to be at a moderate risk of bias (with the Roos 2013 and Parry 2012 trials being the only trials judged to be at a low risk of bias overall). See Figure 1 and Figure 2, and the Characteristics of included studies tables for further details.
|Figure 1. 'Risk of bias' graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.|
|Figure 2. 'Risk of bias' summary: review authors' judgements about each risk of bias item for each included study.|
Four trials were judged to be at a low risk of selection bias when considering generation of the random number sequence and allocation concealment (Carr 1999; Lyell 2008; Parry 2012; Roos 2013). In Carr 1999 and Lyell 2008 random number tables were used, while in Roos 2013 and Parry 2012 computer-generated random number sequences were used. Allocation was concealed in Carr 1999 with the use of opaque, sequentially numbered, sealed envelopes, while in Lyell 2008 and Parry 2012 pharmacy-controlled randomisation occurred, and in Roos 2013, allocation was through a central Internet-based procedure.
Three trials were judged to be at a low risk of performance bias, with blinding of women and study personnel with the use of a placebo (Lyell 2008; Parry 2012; Roos 2013). A further trial (Uma 2012) was judged to be at an unclear risk of performance bias. The final two trials, Carr 1999 and Sayin 2004 were judged to be at a high risk of performance bias, with no blinding of women or study personnel (and with no placebo used).
Lyell 2008, Parry 2012 and Roos 2013 were judged to be at a low risk of detection bias, with blinding of outcome assessors, through the use of a placebo. For the remaining three trials, the risk of detection bias was judged to be unclear, with no or inadequate descriptions of blinding to make confident judgements (Carr 1999; Sayin 2004; Uma 2012).
Incomplete outcome data
Two trials (Parry 2012 and Roos 2013) were judged to be at a low risk of attrition bias, with data collected for all women and infants (including those who discontinued the intervention), and with intention-to-treat principles applied. For three trials (Lyell 2008; Sayin 2004; Uma 2012), the risk of attrition bias was judged to be unclear. In Sayin 2004 it is unclear as to whether there are any missing data from twin pregnancies for infant level outcomes (and if any twin pregnancies were included); in Lyell 2008 two women were excluded as they were minors, and one further woman was lost to follow-up and not included in the analyses; however, it was not reported from which groups these women were lost/excluded. In Uma 2012 there was insufficient information to determine the risk of attrition bias.
The final trial, Carr 1999, was judged to be at a high risk of attrition bias, as of the 86 women randomised, the trial report detailed that for 12 (14%) women the birth and neonatal data "were not available for analysis", with no further details provided.
The Roos 2013 trial was judged to be at a low risk of reporting bias, with data reported for all of the pre-specified outcomes, as detailed in the published trial protocol. The other five trials (Carr 1999; Lyell 2008; Parry 2012; Sayin 2004; Uma 2012) were judged to be at an unclear risk of selective reporting, with insufficient information available for the review authors to confidently assess this. In Lyell 2008, while the outcome data were reported for all outcomes pre-specified in a trial registration, no data were reported for a number of other important clinical outcomes, and for neonatal outcomes, data for a composite morbidity outcome were reported without any data being presented for the individual morbidity components.
Other potential sources of bias
Three trials (Carr 1999; Roos 2013; Sayin 2004) were judged to be at a low risk of other bias, with no obvious sources of other bias identified. The other three trials (Lyell 2008; Parry 2012; Uma 2012) were judged to be at an unclear risk of other bias: in Lyell 2008, while most characteristics were similar between groups, there appeared to be some baseline imbalances, with the placebo group being significantly more likely to have a shorter cervical length, and with more twin pregnancies in the nifedipine group (non-significant). For Parry 2012 and Uma 2012, there was insufficient information available to determine the risk of other bias.
Effects of interventions
Calcium channel blocker versus placebo or no treatment
There was no significant difference in the risk of preterm birth for women who received nifedipine for maintenance tocolysis when compared with women who received a placebo/no treatment (risk ratio (RR) 0.97; 95% confidence interval (CI) 0.87 to 1.09; five trials, 681 women) ( Analysis 1.1). One trial did not report on this outcome (Uma 2012).
Birth within 48 hours of treatment
Only two trials (Lyell 2008; Parry 2012) reported on birth within 48 hours of treatment and found no significant difference between the nifedipine and control groups (RR 0.46; 95% CI 0.07 to 3.00; 128 women) ( Analysis 1.2).
Stillbirth and neonatal death
No stillbirths occurred in the one trial that reported data for this outcome (Parry 2012), and there was no significant difference in the risk of neonatal death in the two trials that reported on this outcome (Parry 2012; Sayin 2004) (average RR 0.75; 95% CI 0.05 to 11.76; 133 infants) ( Analysis 1.3). Moderate statistical heterogeneity was found for this outcome (with the Parry 2012 trial reporting only one neonatal death in the nifedipine group; and conversely the Sayin 2004 trial reporting two neonatal deaths in the control group) (T² = 1.46; I² = 37%), and thus a random-effects model was used.
Any neurological disability at paediatric follow-up
None of the trials to date have reported on neurological disability at follow-up for the infants.
No trials reported on maternal adverse drug reactions, and only the Lyell 2008 trial of 68 women reported on maternal adverse drug reactions leading to treatment cessation, with no events occurring in either group (Lyell 2008) ( Analysis 1.4).
There was no significant difference in the risk of maternal intrauterine infection in the Roos 2013 trial (RR 0.88; 95% CI 0.43 to 1.81; one trial, 406 women) ( Analysis 1.5) or postpartum haemorrhage in the Roos 2013 and Parry 2012 trials (RR 1.54; 95% CI 0.84 to 2.81; two trials, 466 women) ( Analysis 1.7) for women receiving nifedipine as maintenance tocolysis, as compared with women receiving a placebo/no treatment.
There were no cases of antepartum haemorrhage in the one trial that reported this outcome (Parry 2012) ( Analysis 1.6) or maternal death ( Analysis 1.8) in the two trials that reported on this outcome (Parry 2012; Roos 2013). None of the trials reported on maternal satisfaction with treatment.
A statistically significant increase in pregnancy prolongation was shown for women receiving nifedipine maintenance tocolysis, as compared with a placebo/no treatment (mean difference (MD) 5.35 days; 95% CI 0.49 to 10.21; four trials, 275 women) ( Analysis 1.9). Roos 2013, the largest trial included in this review (n = 406), provided data for this outcome, which was not able to be included in the meta-analysis (as data were reported as medians and interquartile ranges); this trial however found no statistically significant difference between the two groups for this outcome (reporting as a hazard ratio (HR) of 1.0) ( Analysis 1.10).
While a significant increase in pregnancy prolongation was shown, no significant differences between the nifedipine and control groups were shown for the outcomes birth prior to 34 completed weeks (RR 1.07; 95% CI 0.88 to 1.30; three trials, 540 women) ( Analysis 1.1); birth prior to 28 completed weeks (RR 3.21; 95% CI 0.35 to 29.11; one trial, 60 women) ( Analysis 1.1); birth within seven days of treatment (RR 1.07; 95% CI 0.40 to 2.87; two trials, 128 women) ( Analysis 1.11); and gestational age at birth (MD 0.32 weeks; 95% CI -0.61 to 1.25; five trials, 681 infants) ( Analysis 1.12). Substantial statistical heterogeneity was observed for the outcome gestational age at birth (T² = 0.62; I² = 58%), greatly influenced by the Sayin 2004 trial, which showed a significant increase in gestational age with nifedipine that was not seen in any of the other trials. The Sayin 2004 trial was judged to be at an unclear to high risk of bias overall, and when this trial was excluded from this meta-analysis for this outcome, no statistical heterogeneity was observed (I² = 0).
Only two trials (Parry 2012; Roos 2013) reported on perinatal mortality, and no significant difference in the risk of death was found for infants who had been exposed to nifedipine maintenance tocolysis and those exposed to no treatment/placebo (RR 1.48; 0.45 to 4.86; 466 infants) ( Analysis 1.13).
No other significant differences between groups were shown for the secondary infant outcomes, including for birthweight (MD -17.45 g; 95% CI -189.37 to 154.48; four trials, 298 infants) ( Analysis 1.14; Analysis 1.15), small-for-gestational age (RR 1.50; 95% CI 0.27 to 8.46; one trial, 74 infants) ( Analysis 1.16), low birthweight (RR 0.90; 95% CI 0.62 to 1.30; one trial, 91 infants) ( Analysis 1.17), Apgar score less than seven at five minutes (RR 3.20; 95% CI 0.14 to 75.55; one trial, 60 infants) ( Analysis 1.18), neonatal sepsis (RR 0.96; 95% CI 0.52 to 1.79; two trials, 479 infants) ( Analysis 1.19), neonatal jaundice (RR 1.00; 95% CI 0.64 to 1.56; one trial, 74 infants) ( Analysis 1.20), respiratory distress syndrome (RR 0.84; 95% CI 0.47 to 1.50; three trials, 554 infants) ( Analysis 1.21), mechanical ventilation (RR 1.07; 95% CI 0.70 to 1.64; two trials, 576 infants) ( Analysis 1.22), intraventricular haemorrhage (RR 0.41; 95% CI 0.12 to 1.42; three trials, 553 infants) ( Analysis 1.24), chronic lung disease (RR 0.74; 95% CI 0.25 to 2.20; two trials, 479 infants) ( Analysis 1.25), and necrotising enterocolitis (RR 1.68; 95% CI 0.53 to 5.35; three trials, 553 infants) ( Analysis 1.26).
None of the included trials provided data for the review outcomes periventricular haemorrhage, air leak syndrome and retinopathy of prematurity.
Neonatal outcomes that were not pre-specified
We have also included in this review the data from two trials that reported on a relevant, non-specified outcome 'composite neonatal morbidity'. For the Roos 2013 trial this was defined as any of perinatal death, chronic lung disease, neonatal sepsis, intraventricular haemorrhage greater than grade two, periventricular leukomalacia greater than grade one, or necrotising enterocolitis; and for the Lyell 2008 trial, this was defined as any respiratory distress syndrome, intraventricular haemorrhage, necrotising enterocolitis or death. On meta-analysis, no significant difference was shown between groups for this outcome (RR 1.03; 95% CI 0.69 to 1.54; two trials, 497 infants) ( Analysis 1.27).
Use of health resources
No significant differences between the nifedipine maintenance tocolysis group and the control group were shown for the outcomes neonatal intensive care unit admission (RR 1.06; 95% CI 0.87 to 1.28; four trials, 709 infants) ( Analysis 1.28), maternal admission to the intensive care unit (RR 1.02; 95% CI 0.06 to 16.19; two trials, 466 infants) ( Analysis 1.29), need for maternal readmission for threatened preterm labour (average RR 0.75; 95% CI 0.29 to 1.93; three trials, 543 women: heterogeneity: T² = 0.30; I² = 38%) ( Analysis 1.30) or length of neonatal intensive care unit stay (MD -0.14 days; 95% CI -3.25 to 2.96; three trials, 132 infants) ( Analysis 1.31).
Infants in the nifedipine group of one trial were however found to have a significantly longer length of neonatal hospital stay (MD 14.00 days; 95% CI 4.21 to 23.79; one trial, 60 infants) ( Analysis 1.33). Additional data have been provided from the Roos 2013 trials for the outcomes length of neonatal intensive care unit stay and length of neonatal hospital stay (medians and interquartile ranges were reported); however no significant differences between groups were shown for these outcomes ( Analysis 1.32; Analysis 1.34).
No trials reported on costs of therapy.
Subgroup analysis based on control group
Subgroup analyses were performed based on control group, comparing studies where a placebo was used (Lyell 2008; Parry 2012; Roos 2013), with studies where no treatment was given to the control group (Carr 1999; Sayin 2004; Uma 2012). The subgroup analyses revealed no significant subgroup differences for the primary outcomes of preterm birth (χ² = 0.75, P = 0.38, I² = 0%) ( Analysis 2.1), or neonatal death (χ² = 1.58, P = 0.21, I² = 36.8%) ( Analysis 2.3), indicating no differential effects for these outcomes based on the type of control group. For both of these outcomes, no significant differences between groups were shown for either of the subgroups as in the main analysis. The two trials that reported on birth within 48 hours of treatment (Parry 2012; Sayin 2004) both used a placebo control, as did the one study (Parry 2012) that reported on stillbirth alone; we therefore could not conduct subgroup analyses for these outcomes.
Subgroup analyses based on dose and duration of tocolysis
Subgroup analyses were performed based on the dose regimen of nifedipine administered to the intervention group - comparing trials where 20 mg of nifedipine was given six hourly (80 mg daily), with the Parry 2012 trial where the regimen administered was based on the dose that had been prescribed in the preceding 24 hours. The Uma 2012 trial, which administered 20 mg of nifedipine three times daily (60 mg daily), did not report on the primary outcomes, and therefore could not be included in the subgroup analyses. The subgroup analyses revealed no differential effects between dosage subgroups for the primary outcomes preterm birth (χ² = 0.10, P = 0.76, I² = 0%) ( Analysis 3.1); birth within 48 hours of treatment (χ² = 0.61, P = 0.43, I² = 0%) ( Analysis 3.2); and neonatal death (χ² = 1.58, P = 0.21, I² = 36.8%) ( Analysis 3.3).
We also performed subgroup analyses for the primary review outcomes based on the duration of tocolysis, comparing those trials that continued treatment until 36 or 37 weeks' gestation, with the Roos 2013 trial, that discontinued treatment on day 13. For the outcome preterm birth, this subgroup analysis did not indicate a differential effect between the two different durations of treatment (χ² = 1.06, P = 0.30, I² = 5.9%) ( Analysis 4.1). For the outcomes birth within 48 hours of treatment and neonatal death, only the trials continuing treatment until 36 to 37 weeks provided data ( Analysis 4.2); and thus no tests for subgroup differences could be conducted.
Sensitivity analysis - including only the higher quality trials
A sensitivity analysis was performed for the primary review outcomes, excluding those trials rated at a high risk of bias or an unclear risk of bias when considering sequence generation and allocation concealment (Sayin 2004; Uma 2012). As in the main analysis, no significant differences between the nifedipine maintenance tocolysis and control groups were shown for any of primary outcomes: preterm birth (RR 1.01; 95% CI 0.90 to 1.14; four trials, 608 women) ( Analysis 5.1), birth within 48 hours of treatment (RR 0.46; 95% CI 0.07 to 3.00; two trials, 128 women) ( Analysis 5.2), stillbirth (no stillbirths reported in the Parry 2012 trial) ( Analysis 5.3), and neonatal death (RR 3.20; 95% CI 0.14 to 75.55; one trial, 60 women) ( Analysis 5.4).
Summary of main results
Calcium channel blockers have been shown to be more effective than betamimetics for initial tocolysis (reducing births within seven days of initiation of treatment, and before 34 weeks' gestation), with improvements in some clinically important neonatal outcomes and a marked reduction in some adverse maternal side effects (King 2003). Maintenance therapy (including therapy with calcium channel blockers) has been evaluated far less. The evidence for maintenance magnesium therapy is insufficient to exclude either important benefits or harms (Han 2013), and other systematic reviews (Berkman 2003; Meirowitz 1999; Sanchez-Ramos 1999) have to date concluded that there is insufficient evidence for any form of maintenance therapy in tocolysis.
This review included six trials, which all assessed nifedipine, and found no convincing evidence to support calcium channel blockers when used as maintenance therapy for preventing preterm birth after threatened preterm labour. No significant differences between the nifedipine and control groups were shown for the review's primary outcomes, of preterm birth, birth within 48 hours of treatment, stillbirth or neonatal death; and none of the trials reported on longer-term follow-up of infants.
Few other statistically significant differences were shown between nifedipine maintenance therapy and a placebo or no treatment, apart from a significant prolongation of pregnancy for women receiving nifedipine. Women who received maintenance therapy with nifedipine were found to be more likely to have their pregnancy prolonged by 5.35 days on average (95% confidence interval 0.49 to 10.21 days), compared with women who received no treatment or a placebo. The meta-analysis, however, was not able to include data from the largest trial included in this review (Roos 2013), which showed no significant difference between groups in pregnancy prolongation (median days were reported). No differences were shown in this review for gestational age at birth, or early and very early preterm birth. Importanly, no significant differences were shown for any of the neonatal morbidities measured, and in fact a significant increase in neonatal length of hospital stay was shown for infants whose mothers had received nifedipine, as compared to infants whose mothers had received a placebo in one trial (Parry 2012).
Quality of the evidence
In this review we included six trials which together recruited in total only 794 women and their babies (Carr 1999; Lyell 2008; Parry 2012; Roos 2013; Sayin 2004; Uma 2012). All trials apart from the Roos 2013 trial, which recruited 406 women, had small sample sizes. The overall risk of bias for the trials was judged to be moderate, with only one trial judged at a low risk of bias across all domains (Roos 2013). For two trials, the risk of bias was predominately unclear (Sayin 2004; Uma 2012), with very little detail available regarding trial methods; and three of the six trials did not use a placebo control (Carr 1999; Sayin 2004; Uma 2012).
Potential biases in the review process
The evidence for this review has been derived from trials identified through a detailed search process. It is possible (but unlikely) that additional trials assessing maintenance therapy with calcium channel blockers for preventing preterm birth after threatened preterm labour have been published but not identified. It is also possible that other studies have been conducted but not published. Should such studies be identified, we will include them in future updates of this review. We attempted to reduce bias wherever possible by having two review authors independently working on study selection and data extraction.
Implications for practice
The role of maintenance therapy with calcium channel blockers for preventing preterm birth is unproven.
Implications for research
Researchers who consider that calcium channel blockers might be an effective maintenance therapy should consider conducting further well-designed randomised controlled trials, of sufficient sample sizes. Any future trials should measure clinically relevant and meaningful outcomes (such as incidence of preterm birth; stillbirth and neonatal death). The trials conducted to date, and any future trials, should follow up infants past the neonatal period to assess long-term safety and neurological outcomes at follow-up.
For this update, we thank Emma Parry and Carolien Roos for their correspondence, and for providing additional information to enable outcome data to be included in the review for the Parry 2012 study.
The National Institute for Health Research (NIHR) is the largest single funder of the Cochrane Pregnancy and Childbirth Group. The views and opinions expressed therein are those of the authors and do not necessarily reflect those of the NIHR, NHS or the Department of Health.
Special thanks to Jacqueline Parsons and Philippa Middleton who helped with the development of the original protocol for this review, supported by a grant from the Commonwealth Department of Health and Ageing, Australia.
Data and analyses
- Top of page
- Authors' conclusions
- Data and analyses
- What's new
- Contributions of authors
- Declarations of interest
- Sources of support
- Differences between protocol and review
- Index terms
Appendix 1. Previous searches
In the 2004 version of the review (Gaunekar 2004), we also searched MEDLINE (1966 to March 2004) and DARE (June 2003) using the terms: preterm labo(u)r, premature labo(u)r, calcium channel blockers, nifedipine, nicardipine.
Appendix 2. Methods used to assess trials included in previous versions of this review
We processed included trial data (Carr 1999) as described in the Cochrane Reviewers' Handbook (Clarke 2003). We evaluated trials under consideration for inclusion and methodological quality, without consideration of their results. Two authors separately assessed the trials and any differences of opinion were resolved by discussion. There was no blinding of authorship.
Quality scores for concealment of allocation were assigned to each trial, using the criteria described in Section VI of the Cochrane Reviewers' Handbook (Clarke 2003a).
A = adequate, B = unclear, C = inadequate, D = not used.
Studies rated as a C or D were excluded.
In addition, quality scores were assigned to each trial for use of a placebo, completeness of follow-up and blinding of outcome assessment as follows.
Use of placebo
(A) Placebo used;
(B) attempt at a placebo;
(C) no placebo;
Completeness of follow-up
(A) Less than 3% of participants excluded;
(B) 3% to 9.9% of participants excluded;
(C) 10% to 19.9% of participants excluded;
(D) 20% or more excluded;
Blinding of assessment of outcome
(A) Double blind, neither investigator nor participant knew or were likely to guess the allocated treatment.
(B) Single blind, either the investigator or the participant knew the allocation. Or, the trial is described as double blind, but side effects of one or other treatment mean that it is likely that for a significant proportion of participants (at least 20%) the allocation could be correctly identified.
(C) No blinding, both investigator and participant knew (or were likely to guess) the allocated treatment.
Two reviewers independently extracted and double entered the data. We resolved discrepancies by discussion and there was no blinding of authorship. We would have assessed statistical heterogeneity between trials. Results are presented using relative risks for dichotomous data and weighted mean differences for continuous data, both with 95% confidence intervals (RevMan 2003).
We decided a priori that all eligible trials would be included in the initial analysis and sensitivity analyses carried out to evaluate the effect of trial quality. This was to be done by excluding trials given a B rating for quality for allocation concealment, then B, C or D for use of a placebo, then D or E for completeness of follow up and then C or D for blinding.
We planned the following subgroup analyses, but these were not carried out due to lack of data:
- dosage of calcium channel blockers;
- type of calcium channel blockers;
- duration of use of calcium channel blockers.
Last assessed as up-to-date: 14 July 2013.
Protocol first published: Issue 1, 2003
Review first published: Issue 3, 2004
Contributions of authors
For the previous versions of this review, Naguesh N Gaunekar conceptualised the review and drafted the protocol and the review; Caroline A Crowther contributed to all drafts of the protocol and the review.
For this update of the review, Puvaneswary Raman, Emily Bain and Naguesh N Gaunekar assessed the new studies for eligibility, extracted data and assessed the risk of bias across the included trials. All review authors commented on and contributed to the draft of the updated review, and approved the final version.
Declarations of interest
Sources of support
- ARCH, Robinson Institute, Discipline of Obstetrics and Gynaecology, The University of Adelaide, Australia.
- National Health and Medical Research Council, Australia.
- Department of Health and Ageing, Australia.
Differences between protocol and review
For this update we have updated the review methods. We have specified that we will exclude quasi-randomised and cross-over trials and that we will include cluster-randomised trials. We have also specified that we will include studies published in abstract form only along with those published as full-text manuscripts. We have reported data for a non pre-specified outcome 'composite neonatal morbidity' as we believed this to be an important, clinically relevant outcome.
Medical Subject Headings (MeSH)
*Obstetric Labor, Premature; Calcium Channel Blockers [*therapeutic use]; Incidence; Infant Mortality; Infant, Newborn; Labor, Obstetric; Nifedipine [*therapeutic use]; Premature Birth [epidemiology; *prevention & control]; Tocolysis [methods]
MeSH check words
Female; Humans; Pregnancy
* Indicates the major publication for the study