Tratamiento de mantenimiento con bomba de infusión de terbutalina después de la amenaza de trabajo de parto prematuro para la reducción de resultados neonatales adversos
Resumen
Antecedentes
Después de la inhibición exitosa del trabajo de parto prematuro las pacientes tienen alto riesgo de trabajo de parto prematuro recurrente. El tratamiento de mantenimiento con bomba de infusión de terbutalina se ha utilizado para reducir los resultados neonatales adversos. Esta revisión sustituye a una revisión anterior Cochrane publicada en 2002 que dejó de ser actualizada por el equipo.
Objetivos
Determinar la efectividad del tratamiento de mantenimiento con bomba de infusión de terbutalina después de la amenaza de trabajo de parto prematuro para reducir los resultados neonatales adversos.
Métodos de búsqueda
Se hicieron búsquedas en el registro de ensayos del Grupo Cochrane de Embarazo y Parto (Cochrane Pregnancy and Childbirth Group) (31 de enero de 2014) y en las listas de referencias de los estudios recuperados.
Criterios de selección
Ensayos controlados aleatorios que compararon tratamiento con bomba de infusión de terbutalina con tratamiento alternativo, placebo o ningún tratamiento después de la detención de la amenaza de trabajo de parto prematuro.
Obtención y análisis de los datos
Dos revisores de forma independiente evaluaron los estudios para inclusión y luego cuando fueron elegibles extrajeron los datos para inclusión en una síntesis cualitativa y cuantitativa (metanálisis).
Resultados principales
Se incluyeron cuatro estudios con 234 pacientes asignadas al azar. La calidad metodológica general de los estudios incluidos fue variada; dos estudios proporcionaron muy poca información sobre los métodos de estudio, hubo un gran desgaste en la muestra en un estudio y en tres estudios el riesgo de sesgo de realización fue alto. No se encontraron pruebas sólidas de que el tratamiento de mantenimiento con terbutalina ofreciera alguna ventaja sobre la solución salina placebo o el tratamiento de mantenimiento con terbutalina oral para reducir los resultados neonatales adversos al prolongar el embarazo entre las pacientes en las que se detuvo el trabajo de parto prematuro. La diferencia de medias (DM) para la edad gestacional al nacer fue ‐0,14 semanas (intervalo de confianza [IC] del 95%: ‐1,66 a 1,38) en el tratamiento con bomba de infusión de terbutalina en comparación con la bomba de infusión de solución salina placebo en dos ensayos combinados. Un ensayo informó un cociente de riesgos (CR) de 1,17 (IC del 95%: 0,79 a 1,73) de parto prematuro (menos de 37 semanas completas) y un CR de 0,97 (IC del 95%: 0,51 a 1,84) de parto muy prematuro (menos de 34 semanas completas) para la bomba de infusión de terbutalina en comparación con la bomba de infusión de solución salina placebo. No se encontraron pruebas de que el tratamiento con bomba de infusión de terbutalina se asocie con reducciones estadísticamente significativas del síndrome de dificultad respiratoria neonatal ni con el ingreso a la unidad de cuidados intensivos neonatales en comparación con placebo. En comparación con la terbutalina oral, no se encontraron pruebas de que el tratamiento con bomba aumente la tasa de continuación del tratamiento o reduzca la tasa de complicaciones infantiles o reingresos hospitalarios maternos. Un estudio indicó que el tratamiento con bomba dio lugar a un aumento significativo del costo/mujer semanal, $580 versus $12,50 (p < 0,01). No se informaron datos sobre resultados infantiles a largo plazo.
Conclusiones de los autores
No se encontraron pruebas de que el tratamiento de mantenimiento con bomba de infusión de terbutalina reduzca los resultados neonatales adversos. Unido a la falta de pruebas de efectos beneficiosos, el gasto significativo y la falta de información sobre la seguridad del tratamiento no apoyan su uso en el tratamiento del trabajo de parto prematuro detenido. En el futuro solamente se debe utilizar en el contexto de ensayos controlados aleatorios bien realizados y con poder estadístico suficiente.
PICO
Resumen en términos sencillos
Tratamiento de mantenimiento con bomba de infusión de terbutalina después de la amenaza de trabajo de parto prematuro para la reducción de resultados neonatales adversos
Los niños que nacen demasiado temprano (parto prematuro) tienen alto riesgo de presentar resultados deficientes, y cuanto más temprano nacen, mayor es su riesgo. Los recién nacidos prematuros tienen mayores probabilidades de morir o presentar discapacidad grave en la infancia, que incluye la parálisis cerebral y otras afecciones similares. Las pacientes que comienzan el trabajo de parto muy temprano (antes de las 34 semanas) y en las que las contracciones se detienen mediante fármacos intravenosos tienen alto riesgo de volver a iniciar el trabajo de parto prematuro. La terbutalina es un fármaco que puede relajar el útero y posiblemente detener las contracciones. Sin embargo, tomada por vía oral no parece prevenir el reinicio de las contracciones. Otra opción es utilizar una bomba portátil pequeña que administra una dosis continua de terbutalina bajo la piel. Lo anterior tiene la ventaja de utilizar una dosis diaria inferior con una aparición más rápida de la acción y buena tolerabilidad debido a menos efectos secundarios que cuando se toma por vía oral. Se encontraron cuatro estudios que incluyeron 234 pacientes que habían presentado trabajo de parto prematuro y en las que se habían detenido las contracciones. No se encontraron pruebas de que el tratamiento de mantenimiento con terbutalina ofrezca cualquier ventaja sobre el tratamiento de mantenimiento con bomba de solución salina placebo o terbutalina oral para reducir los resultados neonatales adversos al prolongar el embarazo entre las pacientes en las que se ha detenido el trabajo de parto prematuro. La revisión encontró que no hay ensayos suficientemente grandes para indicar si el tratamiento de mantenimiento con bomba de infusión de terbutalina es seguro o eficaz.
Authors' conclusions
Background
Description of the condition
Preterm birth refers to a birth that occurs before 37 completed weeks of gestation. About 40% of preterm births are due to complications mandating early delivery such as placenta previa, pre‐eclampsia, fetal growth restriction and infection. Approximately 30% of preterm births occur following preterm pre‐labour rupture of membranes (PPROM) and the remainder are due to spontaneous preterm labour (Beck 2010). Preterm birth is the single most important cause of infant mortality, and is associated with long‐term serious disability in children, including cerebral palsy and sensory and cognitive impairments (Elliott 2013; Goldenberg 2008; Pennell 2007).
Even though the ability of obstetric care providers to identify women at risk of preterm birth has improved, the potential interventions for prevention of spontaneous preterm birth remain limited, and overall, the incidence of preterm deliveries has not decreased (Callaghan 2006). This is partly explained by the rise over the last decade in near‐term births and those associated with medical complications, while early deliveries from spontaneous preterm labours have decreased (Ananth 2006; Goldenberg 2008). Recent evidence reports that about 30% to 50% of pregnant women with threatened preterm labour who had only bed rest developed recurrent preterm labour, and 30% of these women proceeded to deliver preterm (Chawanpaiboon 2009; Chawanpaiboon 2011; Vatish 2005).
Many interventions have been introduced in an attempt to improve neonatal outcomes after preterm birth, including antepartum corticosteroid administration, exogenous surfactant therapy and new methods of mechanical ventilation. With the introduction of such interventions following very preterm birth or extremely preterm birth, neonates have more chances of survival, but they are at risk of neurological damage, and may face extended hospital stays (incurring high healthcare costs). Therefore, the prevention of preterm labour is very important to minimise or delay preterm birth. However, there is little definite evidence that interventions can prevent preterm labour or minimise preterm birth, and the goal is to identify preterm labour at the earliest possible time so that pregnancy prolongation can be obtained through acute and maintenance tocolysis. Pregnant women with threatened preterm labour at 34 weeks of gestation or less are usually treated with tocolytic therapy to inhibit uterine contractions. Tocolytics are used for at least 48 hours to allow corticosteroid administration to accelerate fetal lung maturity.
Therefore, in this review we were interested in assessing whether terbutaline pump maintenance therapy is effective in preventing preterm labour or minimising preterm birth, and in examining possible benefits or harms associated with this therapy.
Description of the intervention
Terbutaline is a beta‐2 adrenergic receptor agonist, which has been used as a treatment for preterm labour. It is an off‐label drug and is not approved by the Food and Drug Administration (FDA). It is a pregnancy category B medication prescribed to stop uterine contractions. In recent years, terbutaline has only rarely been used as an intravenous tocolytic to treat acute threatened preterm labour because of concerns about its safety (Elliott 2013). However, in some settings, subcutaneous terbutaline (0.25mg subcutaneous terbutaline) has been used as a single dose as a test for whether the woman will stop contractions (false labour); if true preterm labour (contractions less than five minutes with cervical dilatation) occurs, intravenous magnesium or atosiban, or oral nifedipine, or indomethacin (given orally, or as rectal suppositories) have been used as treatment (Valenzuela 2000). The aim of treatment is to inhibit labour for at least 48 hours. This time can then be used to administer steroid injections to the mother, which help fetal lung maturity, or allow transfer to the appropriate level of care in an attempt to reduce complications of prematurity (Hofmeyr 2009).
After successful tocolysis for threatened preterm labour, little evidence exists to show that oral terbutaline is effective for maintenance therapy (Goldenberg 2002), but subcutaneous terbutaline has been used as a maintenance tocolytic following initial treatment (Elliott 2013). A portable terbutaline pump, similar to an insulin pump, is used to infuse terbutaline subcutaneously. The initial minimum rate is started, increasing as needed to stop uterine contraction. When continuous terbutaline is administered via a programmable pump, with assessment of uterine contractions to individualise bolus therapy, significant pregnancy prolongation has been noted. However, both the basal infusion and bolus rates (four to six/24 hours ‐ 0.25 mg) need to be determined in consultation with the pharmacist, taking account of weight, height, volume of distribution and renal clearance (Elliott 2013).
Terbutaline is easily absorbed subcutaneously and is not expensive. Pump therapy has the advantages over oral therapy because of lower total daily dose, fewer side effects and less tachycardia, faster onset of action and good tolerability (Elliott 2004; Perry 1995). Continuous subcutaneous terbutaline infusion has been associated with an extremely low incidence of serious adverse events (Elliott 2004; Perry 1995). On the other hand, high doses of terbutaline by the intravenous route have been associated with serious maternal side effects including pulmonary oedema, myocardial ischaemia, cardiac arrhythmias, hypotension and metabolic alterations, although women experiencing side effects may also had comorbid factors such as multi‐fetal gestations, sepsis, pre‐eclampsia, or cardiac arrhythmias (Iams 2009).
How the intervention might work
The rationale for maintenance therapy after threatened preterm labour for preventing preterm birth is based on a number of factors including (1) persistence of the underlying condition stimulating uterine contraction, as this may cause a recurrence; (2) an episode of recent uterine contraction may mean that the myometrium has a low threshold for recurrence; and (3) positive feedback from myometrial contractility can result in further contractions (Soloff 2000).
Therefore, maintenance tocolytic therapy with a terbutaline pump has been attempted to prolong pregnancy and decrease preterm birth. Home therapy is possible and stress from prolonged intravenous tocolysis decreased, although uterine contractions should continue to be assessed at home so that the bolus doses can be individualised and so that repeat episodes of preterm labour can be detected as early as possible (Elliott 2013).
Why it is important to do this review
Terbutaline has been used in clinical practice to inhibit uterine contractions, although in the United States, the FDA currently has not approved its use during pregnancy and there have been concerns about its use in pregnancy (FDA 2011). Previous evidence regarding the effectiveness of a terbutaline pump for maintenance therapy after successful tocolysis has been mixed and inconclusive (Hayes 2008). Two randomised controlled trials (Guinn 1998a; Wenstrom 1997a), involving 94 participants, of whom 39 used the terbutaline pump, did not show positive results. These trials were included in an earlier review (Nanda 2002). However, observational studies examining the use of subcutaneous terbutaline infusion have shown improvements in pregnancy prolongation, neonatal outcomes, and cost; Elliott 2013 summarised findings from 26 observational case control/cohort studies and 17 descriptive case series, involving over 24,000 women and reported positive findings relating to prolongation of pregnancy, gestational age at delivery, neonatal morbidity, and/or cost, which favoured women who had used terbutaline pump therapy. Perry 1995 and Elliott 2004 studied almost 18,000 women and found the incidence of adverse maternal effects to be similar in women whether or not they were exposed to subcutaneous terbutaline.
This review replaces the earlier Cochrane review (Nanda 2002), which is no longer being updated by the team.
Objectives
To assess the effects of continuous low‐dose subcutaneous terbutaline infusion maintenance therapy after threatened preterm labour for reducing adverse neonatal outcomes. Safety and adverse maternal and neonatal outcomes were also determined.
Methods
Criteria for considering studies for this review
Types of studies
All published, unpublished and ongoing randomised controlled trials (including cluster‐randomised trials) comparing outcomes between women given terbutaline pump maintenance therapy and controls given alternative therapy, placebo, or no therapy after successful arrest of threatened preterm labour. We did not include studies where allocation to groups was not truly random (e.g. allocation by day of the week).
We planned to include trials reported in abstracts if results were reported by randomisation group and provided sufficient information was reported (or could be obtained from the authors) to allow us to assess risk of bias.
Types of participants
Pregnant women with intact membranes who had had at least one episode of threatened preterm labour that was halted by tocolytic therapy.
Types of interventions
Terbutaline pump maintenance therapy compared with alternative drug therapy, placebo, or no therapy.
Types of outcome measures
Primary outcomes
Reduction in serious neonatal morbidity and mortality.
Secondary outcomes
Neonatal
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Preterm birth less than 37 completed weeks.
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Very preterm birth (less than 34 completed weeks).
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Extremely preterm birth (less than 28 completed weeks).
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Gestational age at birth (not pre‐specified).
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Apgar score (not pre‐specified).
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Perinatal mortality.
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Birthweight.
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Respiratory distress syndrome.
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Periventricular haemorrhage.
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Need for mechanical ventilation.
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Neurological sequelae (general intelligence, hearing, vision, cerebral palsy and disability).
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Admission to neonatal intensive care unit at > 24 hours (not pre‐specified timing).
Maternal
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Cardiovascular complications (death, cardiac arrest, myocardial infarction, arrhythmia, hypotension).
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Other serious complications (pulmonary oedema, hepatitis).
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Side effects (chest pain, palpitations, shortness of breath, hyperglycaemia, hypokalaemia).
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Maternal compliance with therapy (early discontinuation).
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Maternal satisfaction of therapy.
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Breastfeeding at hospital discharge.
Healthcare system
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Rehospitalisation for threatened preterm labour.
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Cost effectiveness of treatment.
Search methods for identification of studies
Electronic searches
We contacted the Trials Search Co‐ordinator to search the Cochrane Pregnancy and Childbirth Group’s Trials Register (31 January 2014).
The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co‐ordinator and contains trials identified from:
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monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
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weekly searches of MEDLINE;
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weekly searches of Embase;
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handsearches of 30 journals and the proceedings of major conferences;
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weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.
Details of the search strategies for CENTRAL, MEDLINE and Embase, the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service can be found in the ‘Specialized Register’ section within the editorial information about the Cochrane Pregnancy and Childbirth Group.
Trials identified through the search 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 reviewed citations of reference lists of included papers identified through the above search strategy and assessed their suitability for inclusion in the review.
We did not apply any language restrictions.
Data collection and analysis
Selection of studies
Two review authors (Saifon Chawanpaiboon (SC) and Usanee Sangkomkamhang (US)) 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 another review author (Pisake Lumbiganon (PL)).
Data extraction and management
We designed a form to extract data. For eligible studies, two review authors (SC and US) extracted the data using the agreed form. We resolved discrepancies through discussion with a third review author (Malinee Laopaiboon (ML)). We entered data into Review Manager software (RevMan 2012) and checked them 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
Three review authors (SC, ML and PL) 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.
(1) Random sequence generation (checking for possible selection bias)
We have 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 have 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 have 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:
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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 have 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 have 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 supplied by the trial authors, we re‐included 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 have 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 was clear that all of the study’s pre‐specified outcomes and all expected outcomes of interest to the review were reported);
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high risk of bias (where not all the study’s pre‐specified outcomes were reported; one or more reported primary outcomes were not pre‐specified; outcomes of interest were reported incompletely and so could not be used; study failed 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 have 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:
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low risk of other bias;
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high risk of other bias;
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unclear whether there is risk of other bias.
(7) Overall risk of bias
We made explicit judgements about whether studies 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 ‐ seeSensitivity analysis.
Measures of treatment effect
Dichotomous data
For dichotomous data, we have presented results as summary risk ratio with 95% confidence intervals.
Continuous data
For continuous data, we used the mean difference as 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 included only parallel individual randomised controlled trials in this review. The unit of analysis in all trials was women.
Cluster‐randomised trials
We had planned to include cluster‐randomised trials in the analyses along with individually‐randomised trials if such trials were otherwise eligible. We did not identify any cluster‐randomised trials. In updates of the review, if such trials are included we will adjust their sample sizes using the methods described in the Cochrane Handbook (Higgins 2011) using an estimate of the intracluster correlation co‐efficient (ICC) derived from the trial (if possible), from a similar trial or from a study of a similar population. If we use ICCs from other sources, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we identify both cluster‐randomised trials and individually‐randomised trials, we plan to synthesise the relevant information. We will consider it reasonable to combine the results from both if there is little heterogeneity between the study designs and the interaction between the effect of intervention and the choice of randomisation unit is considered to be unlikely.
We will also acknowledge heterogeneity in the randomisation unit and perform subgroup analysis to investigate the effects of the randomisation unit.
Cross‐over trials
Cross‐over trials are not a suitable design for this type of intervention and were therefore not eligible for inclusion.
Other unit of analysis issues
For trials with more than two arms (multi‐arm trials), we planned to include data for all arms relevant to the scope of the review. Where appropriate, we would have combined arms (using methods described in the Cochrane Handbook (Higgins 2011)) to create a single pair‐wise comparison. If it was not appropriate to combine arms, we would have presented results separately for each arm, sharing results for the control group between each to avoid double counting (for dichotomous outcomes we planned to divide the number of events and total sample by two, for continuous outcomes we would have assumed the same mean and standard deviation but halved the control sample size for each comparison). Wenstrom 1997b was the only included study with more than two arms.
We planned to include studies recruiting women with multiple pregnancies. We are aware that in multiple pregnancies outcomes for neonates are not independent; where sufficient information was available we planned therefore to adjust data for multiple pregnancies using the methods described in the Cochrane Handbook (Higgins 2011). In this version of the review included studies only recruited women with singleton pregnancies.
Dealing with missing data
For included studies, we noted levels of attrition and planned to 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, 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 Tau², I² and Chi² statistics. We regarded heterogeneity as substantial if an 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. If we had identified substantial heterogeneity, we planned to explore it by pre‐specified subgroup analysis (see below).
Assessment of reporting biases
In this version of the review very few data were pooled in meta‐analyses. In future updates, in the unlikely event that there are 10 or more studies in a 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 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 examined 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, provided that an average treatment effect across trials was considered clinically meaningful.
Where we used random‐effects analyses, the results have been presented as the average treatment effect with 95% confidence intervals, along with estimates of Tau² and I².
Subgroup analysis and investigation of heterogeneity
Had we identified substantial heterogeneity, we planned to investigate it using subgroup analyses. In this version of the review too few data were pooled in meta‐analysis to allow meaningful subgroup analysis.
We planned to carry out the following subgroup analyses.
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Single versus multiple pregnancy
Any subgroup analysis in updates of the review will be restricted to the review's primary outcomes. We will assess subgroup differences by interaction tests available within RevMan (RevMan 2012). We will report the results of subgroup analyses quoting the Chi² statistic and P value, and the interaction test I² value.
Sensitivity analysis
To test the robustness of results, we had planned to use sensitivity analyses to examine the effect of excluding studies at high risk of bias (such as from lack of allocation concealment) on the overall estimates of effect for primary outcomes. In view of the paucity of data in this version of the review we did not carry out these additional analyses.
Results
Description of studies
See Characteristics of included studies; Characteristics of excluded studies.
Results of the search
See: Figure 1.
The search of the Cochrane Pregnancy and Childbirth Group's Trials Register retrieved six reports corresponding to four studies (some studies resulted in more than one publication) and an additional report was identified by one of the referees.
Included studies
Four studies (Guinn 1998b; Lam 1988; Morales 1990; Wenstrom 1997b) involving 234 women were eligible for qualitative and quantitative synthesis (meta‐analysis).
The published trial by Guinn 1998b and colleagues recruited 52 women with singleton gestations from 22 to less than 34 weeks of gestation with intact membranes who experienced suspected preterm labour that was arrested with intravenous magnesium sulfate therapy for at least 24 hours before study entry. The study was conducted in the USA. The authors calculated sample size a priori, and determined that a total sample size of 48 women in each group was needed to have 80% power to detect a clinically significant difference of a 14‐day delay in the interval from treatment to birth between the two therapies. Guinn 1998b used a strict case definition of preterm labour. Women had to experience more than four uterine contractions per hour and at least one of the following: 80% or greater effacement, one centimetre or greater dilation, or documented cervical change. Terbutaline pump maintenance therapy was compared with saline placebo pump maintenance therapy. Both therapies used portable subcutaneous pumps (model 404‐S; MiniMed Technologies, Sylmar, CA). Terbutaline therapy consisted of the continuous administration of 1 mg terbutaline/mL saline at the rate of 0.05 mL/hour with five daily bolus injections programmed at regular intervals. Women could also self‐administer boluses of 0.25 mL twice daily for increased uterine activity. Saline placebo pump therapy was identical to terbutaline pump therapy except that saline replaced terbutaline. Women were followed up on a weekly basis during maintenance therapy, and nursing support was constantly available. In the event of recurrent preterm labour before 34 weeks of gestation, pump therapy was discontinued, and another course of intravenous magnesium therapy was given unless there was advanced cervical dilation or ruptured membranes. Pump maintenance therapy resumed if labour was arrested. Both pump therapies continued until either delivery or 36 weeks of gestation was reached.
The published trial by Lam 1988 randomised 68 women into one of two groups after women had completed their initial parenteral tocolysis. Thirty‐five women (mean gestation 27.2 + 3.4 weeks) received oral terbutaline 2.5 to 7.5 mg every two to four hours, and 33 women (mean gestation 28.2 + 3.2 weeks) received terbutaline via a portable subcutaneous infusion pump starting at a basal rate of 0.03 to 0.05 mg/hour and intermittent boluses of 0.25 mg each. Using this regimen, the total daily terbutaline infusion was exceptionally low (< 3 mg/24 hours). An ambulatory tocodynamometer recorded uterine activity data which was transmitted from the woman's home to the study centre daily. Oral and subcutaneous dosages were adjusted accord to uterine activity. The primary outcome was birth at > 36 weeks' gestation. The ratio between the actual prolongation of pregnancy in weeks and the desired prolongation was expressed as the Pregnancy Prolongation Index (PPI). The two groups were compared according to the number of weeks gained in utero, the number of recurrent preterm labour episodes per woman, and the PPI.
The published trial by Morales 1990 recruited 72 women with less than 34 weeks' gestation following arrest of preterm labour. The study was conducted in the United States. The definition of preterm labour was progressive cervical change beyond one centimetre associated with regular uterine contractions. The two study groups were similar in terms of a variety of prematurity risk factors; urinary, cervical and intra‐amniotic infections; gestational age on admission and cervical dilatation. Women were randomly assigned by sealed envelopes to either oral or pump therapy groups.
Wenstrom 1997b and colleagues' published trial recruited 42 women with gestations from 20 to less than 35 weeks who had suspected preterm labour that was arrested with intravenous magnesium sulfate therapy for at least 48 hours before study entry. The authors did not describe sample size calculations. The study was conducted in the USA. Preterm labour was defined only as regular, persistent uterine contractions that produced observed cervical change. Three maintenance therapies were compared: terbutaline pump, saline placebo pump and oral terbutaline. Terbutaline pump and saline pump therapies used the same portable pump model as in the Guinn 1998b trial. The terbutaline pump group received 1 mg terbutaline/mL saline initially administered at rate of 0.05 mL/hour with 0.25 mL bolus injections every six hours. While the basal rate was kept constant, the bolus dose was adjusted to the women's unique contraction patterns. The saline placebo pump group received therapy identical to the terbutaline pump group except that saline replaced the terbutaline. The oral terbutaline group received 5 to 10 mg terbutaline orally every two to six hours, titrated to maintain maternal heart rate at 90 beats per minute or higher and to prevent uterine contractions from occurring at a rate of more than four per hour. If recurrent preterm labour occurred despite maximal therapy, the treatment arm assignment was determined and therapy was changed. Women receiving oral terbutaline or saline placebo therapy were switched to terbutaline pump, and women receiving terbutaline pump were switched to oral terbutaline. Women who had recurrent preterm labour that was not resolved after switching therapies were treated with intravenous tocolysis and aggressive management. Women were followed up on a weekly or biweekly basis according to the department's standard protocol for outpatient management of preterm labour. No gestational age was specified for the discontinuation of therapy. The study authors attributed the low participation rate to women's concerns about the pump and its needle or the use of placebo. Physician reluctance to participate in the trial was not addressed. The treatment arm randomisation code was broken for women with recurrent preterm labour that could not be resolved with the assigned therapy. The assignment code was broken for nine of the 15 women in the terbutaline pump arm; one was switched to oral terbutaline, five received intravenous tocolytic therapy, and three delivered. The code was broken for eight of the 12 women in the saline placebo pump arm; three were switched to terbutaline pump, three received intravenous tocolytics, and two delivered. Two of the 15 women in the oral terbutaline group received intravenous tocolytics. All cases were analysed on an intention‐to‐treat basis. The authors did not describe any cases of loss to follow‐up.
Excluded studies
One study was excluded (Morrison 1993).
Risk of bias in included studies
Four studies (Guinn 1998b; Lam 1988; Morales 1990; Wenstrom 1997b) were included; see Figure 2 and Figure 3 for summaries of the 'Risk of bias' assessments.
'Risk of bias' graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
'Risk of bias' summary: review authors' judgements about each risk of bias item for each included study.
Allocation
The Guinn 1998b; Morales 1990 and Wenstrom 1997b studies were assessed as at low risk of bias and Lam 1988 was assessed as unclear.
Treatment allocation in the Guinn 1998b trial was based on computer‐generated randomisation with stratification by cervical dilation (< 3 cm versus ≥ 3 cm) and previous indomethacin use.
No information was available in Lam 1988.
In the Morales 1990 trial, treatment allocation was randomly assigned by sealed envelopes to either oral or pump therapy groups.
The pharmacist in the Wenstrom 1997b trial randomised women using a table of random numbers and prepared all solutions.
Blinding
Guinn 1998b was assessed as at low risk of bias and the Lam 1988; Morales 1990 and Wenstrom 1997b studies were assessed as high.
In the Guinn 1998b trial, only the research pharmacist had knowledge of treatment assignment; the pharmacist prepared the pump solutions, which were clear, odourless, and indistinguishable.
The interventions were not blinded to investigators and women in the Lam 1988 trial.
Blinding was not mentioned in the Morales 1990 study.
In the Wenstrom 1997b trial, the pump solutions were identical in appearance and only the pharmacist knew the pump assignments; however, the oral therapy was not blinded.
Incomplete outcome data
The Lam 1988 and Wenstrom 1997b studies were assessed as at low risk of bias and the Guinn 1998b and Morales 1990 studies were assessed as high risk of bias.
In the Guinn 1998b trial, there was a high dropout rate (38%) although an intention‐to‐treat analysis was carried out.
In the Lam 1988 trial, all women appeared to be accounted for in the analyses.
About 15% (11 from 72 women) in the Morales 1990 trial were lost to follow‐up .
Over 90% of eligible women in the Wenstrom 1997b trial declined participation. There were no losses to follow‐up.
Selective reporting
All studies (Guinn 1998b; Lam 1988; Morales 1990 and Wenstrom 1997b) were assessed as at unclear risk of bias.
Assessing outcome reporting bias was difficult as we did not have access to study protocols. In two of the trials assessment was made from brief conference abstracts (Lam 1988; Morales 1990).
Other potential sources of bias
The authors of the previous version of this review (Nanda 2002) wrote to the authors of two studies (Guinn 1998b; Wenstrom 1997b) to request additional information on unreported outcomes. They also queried whether the numbers following the estimates in the tables, which were unlabeled, represented standard deviations. Since they did not receive a response from the authors, they assumed that the authors reported standard deviations.
In the Wenstrom 1997b trial several women crossed over into the other treatment arm (one woman from the terbutaline pump group to oral terbutaline group; and three from the saline pump group to the terbutaline pump).
Effects of interventions
Terbutaline pump versus saline placebo pump (two studies with 79 women)
Overall, there was insufficient evidence to determine whether or not terbutaline pump maintenance therapy was associated with a reduction in preterm birth or its complications compared with placebo. The small sample sizes of the two trials contributing data and the wide 95% confidence intervals for the outcomes reported meant that it was not possible to rule out either clinically important benefit or harm.
Primary outcome: Reduction in serious neonatal morbidity and mortality
No perinatal deaths were reported in either study included in this comparison (Guinn 1998b; Wenstrom 1997b).
The Guinn 1998b study reported that no cases of intraventricular haemorrhage occurred. There was no clear evidence that respiratory distress syndrome (RDS) differed by treatment received (Analysis 1.1). Pooled data from the Guinn 1998b and Wenstrom 1997b trials showed a risk ratio (RR) of 0.82 (95% confidence interval (CI) 0.23 to 2.93, data for 79 infants) of RDS for terbutaline pump versus saline placebo pump.
Secondary outcomes
The Guinn 1998b trial found a RR of 1.17 (95% CI 0.79 to 1.73) of preterm birth (Analysis 1.4) and a RR of 0.97 (95% CI 0.51 to 1.84) of very preterm birth (Analysis 1.3) for terbutaline pump compared with saline placebo pump therapy. Preterm and very preterm birth were not reported in the other trial.
Both trials reported mean gestational age at birth; the difference between groups in gestational age at birth was small, although the 95% CI was wide and did not exclude clinically important effects (mean difference (MD) ‐0.14 weeks, 95% CI ‐1.66 to 1.38) (Analysis 1.2).
There was insufficient evidence and inconclusive results for mean infant birthweight; the mean birthweight was not significantly different for terbutaline pump versus saline placebo pump groups when data from the Guinn 1998b and Wenstrom 1997b trials were combined but there was a wide 95% CI for this outcome (MD 107.72 g, 95% CI ‐216.65 to 432.09) (Analysis 1.5).
The Guinn 1998b study reported a RR of 0.94 (95% CI 0.51 to 1.73, 51 infants) for neonatal intensive care unit (NICU) stay greater than 24 hours (Analysis 1.6).
In the Wenstrom 1997b study, the authors reported no statistically significant differences in length of neonatal hospital stay between the terbutaline pump and saline placebo pump groups, and no differences between these groups for Apgar scores at one and five minutes (data not shown in data and analyses tables).
No data were available on need for mechanical ventilation or long‐term neurological sequelae.
Neither of the trials reported serious complications of therapy.There was no clear evidence that terbutaline pump therapy resulted in a higher rate of therapy continuation (Analysis 1.7). For two trials, the RR of early discontinuation from assigned therapy was 1.15 (95% CI 0.68 to 1.95) for terbutaline pump compared with the saline placebo pump. The only cases of early discontinuation reported in the Wenstrom 1997b trial were those resulting from recurrent preterm labour that required the treatment assignment to be broken and therapy switched. Guinn 1998b described both discontinuations resulting from physician decisions (n = 9) as well as those resulting from women's choices (n = 11). No data were presented regarding costs.
Terbutaline pump versus oral terbutaline (three studies with 170 women)
The Lam 1988; Morales 1990 and Wenstrom 1997b trials included a comparison of terbutaline pump with oral terbutaline. For most outcomes there was insufficient evidence to draw conclusions about benefit or harm.
Primary outcome: Reduction in serious neonatal morbidity and mortality
No perinatal deaths were reported in any of the studies included in this comparison. We identified no clear difference in RDS (RR 1.00, 95% CI 0.16 to 6.20, one study, 30 infants) for the terbutaline pump compared with oral terbutaline (Analysis 2.1).
Secondary outcomes
The MD for gestational age at birth in one study was 1.40 weeks (95% CI ‐1.13 to 3.93) for terbutaline pump compared with oral terbutaline therapy (Wenstrom 1997b) (Analysis 2.2). Mean infant birthweight was reported in one study and there was no evidence of a significant difference between groups: MD for birthweight was 484.00 g, 95% CI ‐25.00 to 993.00 for terbutaline pump versus oral terbutaline therapy (Analysis 2.3).
No statistically significant differences between the terbutaline pump and oral terbutaline pump arms in terms of Apgar scores at one and five minutes or length of neonatal hospital stay were identified in one study (non‐prespecified outcomes, data not shown) (Wenstrom 1997b). No data were available on need for mechanical ventilation or long‐term neurological sequelae. No difference was identified in early discontinuation with the terbutaline pump compared with oral terbutaline (RR 3.00, 95% CI 0.72 to 12.55) (Wenstrom 1997b) (Analysis 2.4).
The frequency of recurrent preterm labour was reported to be statistically significantly higher in the group of women receiving oral terbutaline therapy compared with the group receiving terbutaline infusion pump therapy (P < 0.005) (data not shown in the data and analysis) (Lam 1988).
In the study by Morales 1990, no statistically significant differences between therapy groups were reported in terms of number of re‐admissions for intravenous tocolysis (mean 1.8 versus 1.2) (no standard deviations reported and data not shown in the data and analysis). There were no serious medical complications requiring discontinuation of either therapy in this study. Morales 1990 also reported that pump therapy resulted in significantly increased weekly costs/woman, mean $580 versus $12.50 (P < 0.01) (data not shown in data and analysis tables).
Discussion
Summary of main results
There are insufficient data to be able to draw any firm conclusions about terbutaline pump maintenance therapy after threatened preterm labour for reducing adverse neonatal outcomes. The quality of the evidence is not high. The studies had small sample sizes and did not identify significant differences between groups receiving terbutaline pump maintenance therapy versus either placebo or oral therapy for any of our primary or secondary outcomes.Terbutaline pump maintenance therapy does not appear to offer any advantages over saline placebo pump, or oral terbutaline maintenance therapy in reducing adverse neonatal outcomes among women with arrested preterm labour. No trial found terbutaline pump therapy to be efficacious in reducing adverse neonatal outcomes, increasing gestational age at birth or in reducing preterm birth and its complications. Preliminary evidence indicated that pump therapy resulted in significantly increased weekly costs/woman.
Overall completeness and applicability of evidence
There are only four included studies which recruited 234 women; all four studies were conducted in United States. The available evidence was not sufficient to address all of the objectives of the review, and limits the external validity of results especially to low‐resource settings.
All trials (Guinn 1998b; Lam 1988; Morales 1990; Wenstrom 1997b) had small sample sizes. The Guinn 1998b study only enrolled 52 women; however, the sample size was calculated to have sufficient power to detect a clinically significant difference (two weeks) between the two therapies in the interval from initiation of therapy to birth. The Wenstrom 1997b trial enrolled only 42 women despite a recruitment period of four years and four months. Over 90% of eligible women declined participation in the study. Although the authors state that no apparent differences existed between those who agreed to participate and those who declined, the possibility of differences cannot be eliminated. The Lam 1988 and Morales 1990 trials enrolled 68 and 72 women respectively, without explanation of the method of sample size calculation. All trials restricted enrolment to women with arrested preterm labour and, thus, at high risk for preterm birth. The ability to detect an association between terbutaline pump therapy and preterm birth, most likely, was strengthened by the exclusion of women with lower risk of preterm birth.
Elliott 2013 discussed the efficacy of continuous subcutaneous terbutaline infusion related to Wenstrom 1997b and Guinn 1998b and suggested that these studies had major flaws including low recruitment and small sample sizes. Elliott 2013 evinced that the bolus drug dosage administered in these two trials (Guinn 1998b; Wenstrom 1997b) was not altered based on end‐organ response (uterine contraction) data, and this adjustment would be required if any benefit is to be achieved, but in these studies the research protocol did not include uterine contraction monitoring. Another problem in the design of these two studies is that the investigators did not use pharmacologic consultation regarding volume of distribution, body mass, renal clearance, and so forth to determine the appropriate basal dose of terbutaline for infusion, but rather all women (body mass index (BMI) 25 versus 45) received the same fixed dosage of the drug regardless BMI. Both trials were also underpowered (94 enrolled, 320 required by their power calculation) to show a difference from placebo.
Elliott 2013 also pointed out that the Guinn 1998b trial was also compromised by the high dropout rate: 41% in both arms of the study, (11 out of 24 women randomised to the terbutaline arm and nine of 28 women in the placebo arm. Wenstrom 1997b also concluded that a much larger study would be more likely to reveal some differences in outcome. In previous work, large observational studies, not randomised controlled trials, have suggested positive results of continuous subcutaneous terbutaline infusion therapy in pregnancy prolongation, neonatal outcome, and cost (Elliott 2004; Elliott 2013; Lam 1998; Perry 1995).
Considering the safety of terbutaline usage, the FDA changed the risk category of terbutaline from category B (no human or animal reproduction studies have demonstrated a fetal risk) to category C (animal reproduction studies have shown an adverse effect on the fetus). Elliott 2013 stated that the FDA used animal data from only one laboratory (Slotkin 2003) that was not replicated in other research studies to change the classification from B to C for terbutaline. More studies on the safety of terbutaline in humans are needed.
Quality of the evidence
All four included studies are under powered (Wenstrom 1997b) to show a difference between groups and there were high dropout rates of participants in Guinn 1998b. Two of the studies reported little information on study methods (Lam 1988; Morales 1990). Several women were crossed over into the other treatment arm in the Wenstrom 1997b trial.
The quality of the evidences is not strong enough to indicate whether or not terbutaline pump maintenance therapy after threatened preterm labour reduces adverse neonatal outcomes.
Potential biases in the review process
We strictly followed the review process recommended by the Cochrane Pregnancy and Childbirth Review Group to try to minimise bias in the review process. Two review authors independently assessed for inclusion all the potential studies we identified as a result of the search strategy. Two review authors independently extracted the data of the included studies using the agreed form. Three review authors independently assessed risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions.
Agreements and disagreements with other studies or reviews
We did not find any other trials (other than the four included studies) addressing this clinical problem. However, observational studies, not randomised controlled trials, suggest positive results for continuous subcutaneous terbutaline infusion therapy in pregnancy prolongation, neonatal outcome, and costs (Elliott 2004; Elliott 2013; Lam 1998; Perry 1995).
'Risk of bias' graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
'Risk of bias' summary: review authors' judgements about each risk of bias item for each included study.
Comparison 1 Terbutaline pump versus saline pump, Outcome 1 Respiratory distress syndrome.
Comparison 1 Terbutaline pump versus saline pump, Outcome 2 Gestational age at birth (in weeks).
Comparison 1 Terbutaline pump versus saline pump, Outcome 3 Very preterm birth (< 34 weeks).
Comparison 1 Terbutaline pump versus saline pump, Outcome 4 Preterm birth (< 37 weeks).
Comparison 1 Terbutaline pump versus saline pump, Outcome 5 Birthweight.
Comparison 1 Terbutaline pump versus saline pump, Outcome 6 Neonatal intensive care unit admissions at > 24 hours.
Comparison 1 Terbutaline pump versus saline pump, Outcome 7 Early discontinuation.
Comparison 2 Terbutaline pump versus oral terbutaline, Outcome 1 Respiratory distress syndrome.
Comparison 2 Terbutaline pump versus oral terbutaline, Outcome 2 Gestational age at birth (in weeks).
Comparison 2 Terbutaline pump versus oral terbutaline, Outcome 3 Birthweight.
Comparison 2 Terbutaline pump versus oral terbutaline, Outcome 4 Early discontinuation.
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Respiratory distress syndrome Show forest plot | 2 | 79 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.82 [0.23, 2.93] |
| 2 Gestational age at birth (in weeks) Show forest plot | 2 | 79 | Mean Difference (IV, Random, 95% CI) | ‐0.14 [‐1.66, 1.38] |
| 3 Very preterm birth (< 34 weeks) Show forest plot | 1 | 52 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.97 [0.51, 1.84] |
| 4 Preterm birth (< 37 weeks) Show forest plot | 1 | 52 | Risk Ratio (M‐H, Fixed, 95% CI) | 1.17 [0.79, 1.73] |
| 5 Birthweight Show forest plot | 2 | 79 | Mean Difference (IV, Fixed, 95% CI) | 107.72 [‐216.65, 432.09] |
| 6 Neonatal intensive care unit admissions at > 24 hours Show forest plot | 1 | 51 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.94 [0.51, 1.73] |
| 7 Early discontinuation Show forest plot | 2 | 79 | Risk Ratio (M‐H, Fixed, 95% CI) | 1.15 [0.68, 1.95] |
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Respiratory distress syndrome Show forest plot | 1 | 30 | Risk Ratio (M‐H, Fixed, 95% CI) | 1.0 [0.16, 6.20] |
| 2 Gestational age at birth (in weeks) Show forest plot | 1 | 30 | Mean Difference (IV, Fixed, 95% CI) | 1.40 [‐1.13, 3.93] |
| 3 Birthweight Show forest plot | 1 | 30 | Mean Difference (IV, Fixed, 95% CI) | 484.0 [‐25.00, 993.00] |
| 4 Early discontinuation Show forest plot | 1 | 30 | Risk Ratio (M‐H, Fixed, 95% CI) | 3.0 [0.72, 12.55] |
