Agentes progestacionales para el tratamiento de la amenaza de trabajo de parto prematuro o del trabajo de parto prematuro establecido
Resumen
Antecedentes
La prematurez no solamente es la causa principal de morbilidad y mortalidad perinatal si no que se asocia con daños a largo plazo. Estudios de diversos agentes tocolíticos han mostrado resultados mixtos con escaso efecto en la mejoría de la duración del embarazo y datos insuficientes para confirmar un efecto beneficioso definitivo sobre la morbilidad o la mortalidad neonatal. Es conocido que la progesterona tiene un efecto inhibitorio sobre la contractilidad uterina y se considera que desempeña una función clave en el mantenimiento del embarazo hasta el término.
Objetivos
Determinar si el uso de agentes progestacionales es efectivo como una forma de tratamiento o tratamiento adyuvante para las mujeres con amenaza de trabajo de parto prematuro o con trabajo de parto prematuro establecido con membranas intactas.
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 agosto de 2013), CENTRAL (The Cochrane Library 2013, número 10), MEDLINE (1966 hasta el 31 de agosto de 2013) y en Embase (1974 hasta el 31 de agosto de 2013). Se verificaron las listas de referencias de todos los estudios incluidos para identificar estudios adicionales y se estableció comunicación con los autores y la industria farmacéutica.
Criterios de selección
Ensayos controlados aleatorios que comparen agentes progestacionales, administrados solos o en combinación con otros tocolíticos, con un grupo control al que se le administró un tocolítico diferente, placebo o ningún tratamiento, para el tratamiento del trabajo de parto prematuro.
Obtención y análisis de los datos
Dos revisores de forma independiente extrajeron los datos y evaluaron la calidad de los ensayos.
Resultados principales
En esta revisión se incluyeron ocho estudios con 563 pacientes, pero solamente siete estudios con 538 pacientes aportaron datos para los análisis. Existen algunos datos que indican que el uso de agentes progestacionales da lugar a una reducción de los partos prematuros con menos de 37 semanas de gestación y a un aumento del peso al nacer. La administración de un agente progestacional también puede reducir la frecuencia de las contracciones uterinas, prolongar el embarazo y atenuar el acortamiento del cuello uterino. Sin embargo, el análisis se vio limitado por el número relativamente pequeño de estudios disponibles. El poder del metanálisis también fue limitado por las variaciones en los tipos, las dosis y las vías de administración de la progesterona.
Conclusiones de los autores
No hay pruebas suficientes para recomendar los agentes progestacionales como tocolíticos para las pacientes con trabajo de parto prematuro.
PICO
Resumen en términos sencillos
Uso de progesterona para el tratamiento del trabajo de parto prematuro
El parto prematuro se asocia con diversos problemas médicos para el recién nacido que incluyen la muerte y problemas de salud a largo plazo. Los padres de los recién nacidos prematuros pueden experimentar conmoción emocional y los costos económicos son elevados para los sistemas de asistencia sanitaria. Se han utilizado diversos fármacos para retrasar el inicio del trabajo de parto y prevenir los partos prematuros, pero han tenido un éxito limitado. Algunos de los fármacos tienen efectos secundarios. Se sabe que la progesterona es una hormona que suprime la actividad uterina y mantiene el útero inactivo hasta el término. Los fármacos con acción similar a la de esta hormona (agentes progestacionales) se probaron por primera vez a fines de los años cincuenta, aunque luego el interés disminuyó. Recientemente se han publicado nuevos ensayos que estudian el uso de agentes progestacionales para la prevención y el tratamiento del trabajo de parto prematuro. Esta revisión de la bibliografía encontró ocho ensayos controlados aleatorios que incluyeron a 563 pacientes, pero solamente siete estudios con 538 pacientes con amenaza de trabajo de parto prematuro o trabajo de parto prematuro establecido con membranas intactas contribuyeron con datos a esta revisión actualizada. Cuatro ensayos compararon el uso de agentes progestacionales versus placebo en pacientes tratadas de forma concurrente con otro fármaco para reducir las contracciones uterinas (agente tocolítico). La progesterona se administró de forma independiente en los otros cuatro ensayos comparada con otros agentes tocolíticos o placebo. Pruebas limitadas indican que la administración de una progesterona como tratamiento adyuvante puede reducir los partos prematuros con menos de 37 semanas de gestación y aumentar el peso al nacer. No hay pruebas suficientes a partir de los siete estudios pequeños que contribuyeron con datos para recomendar los agentes progestacionales como un agente tocolítico en las pacientes que se presentaban con trabajo de parto prematuro.
Authors' conclusions
Background
Preterm labour is one of the commonest complications of pregnancy (Haram 2003), and it results in preterm birth. According to the World Health Organization, delivery before completion of 37 weeks of gestation (WHO 1977) is defined as preterm birth. Prematurity is a leading cause of perinatal morbidity and mortality in many countries, accounting for at least one third of infant deaths (Callaghan 2006). This results in significant emotional distress for parents as well as economic costs (Petrou 2001). Neonates born prematurely, especially those delivered before 32 weeks of gestation, are at risk of developing various complications including respiratory distress syndrome, necrotising enterocolitis and intraventricular haemorrhage. These complications often lead to prolonged stay in the neonatal intensive care unit and the need for different interventions. Recent studies have shown that, in addition to the perinatal morbidity and mortality related to preterm labour, preterm birth can lead to diminished long‐term survival and reproduction in persons born preterm (Swamy 2008). The risks of medical and social disabilities in adulthood also increased with decreasing gestational age at birth (Moster 2008).
Various drugs and strategies have been used for the treatment of preterm labour. The pharmacologic agents currently used include betamimetics, calcium channel blockers, nitric oxide donors, magnesium, cyclo‐oxygenase inhibitors and oxytocin receptor antagonists. Studies of these drugs have shown mixed results with little effect in improving pregnancy duration and insufficient data to confirm a definite beneficial effect on neonatal morbidity or mortality (Berkman 2003). Although betamimetics have been shown to be effective in delaying birth for 48 hours, which allows the administration of corticosteroids and in‐utero transfer to tertiary centres, they are associated with significant side‐effects that may be harmful to mothers (Anotayanonth 2004; Berkman 2003). Calcium channel blockers are therefore suggested to be the preferred agents, should tocolysis be indicated. However, the use of calcium channel agonists for treatment of preterm labour also does not lead to significant improvements in important neonatal outcomes such as admission to neonatal intensive care unit, low Apgar score and perinatal mortality (King 2003). Oxytocin receptor antagonists seem particularly promising as an effective tocolytic agent with minimal adverse effects (Lamont 2003). However, a Cochrane review on the use of this tocolytic agent does not support the superiority of atosiban over betamimetics or placebo in terms of the tocolytic efficacy or neonatal outcome (Papatsonis 2005). In addition, its current cost is prohibitive. Insufficient data are available for the use of cyclo‐oxygenase inhibitors (King 2005) or nitric oxide donors (Duckitt 2002) for women in preterm labour. Magnesium sulphate is not recommended as a tocolytic agent as it is ineffective at delaying preterm birth and is associated with increased mortality for the child (Crowther 2002). Thus, there is a need for further therapeutic options that are effective, affordable and safe.
Progesterone is known to have an inhibitory effect on uterine contractility (Lye 1978) and is thought to play a key role in the maintenance of pregnancy until term (Henderson 2001; Karalis 1996). In animal studies, progesterone decreases the concentration of oxytocin (Fuchs 1983) and alpha‐adrenergic receptors (Roberts 1977; Williams 1977) in the myometrium, as well as local synthesis of prostaglandin F2 (Thoburn 1979). Progesterone is also able to modify the ultrastructural organisation of the myometrium by inhibiting the appearance of gap junctions, and preventing co‐ordinated muscular contraction (Garfield 1982). Different routes of administration of progesterone have been described in the literature. These include weekly intramuscular injections from 16 to 20 weeks through to 36 weeks (Meis 2003) and daily vaginal progesterone suppositories from 24 weeks to 34 weeks of gestation (da Fonseca 2003).The safety of progesterone therapy in pregnancy is also well established (Check 1986). Several small studies (Hartikainen‐Sorri 1980; Hauth 1983; Johnson 1975; LeVine 1964; Papiernik 1970) have been conducted to test the effect of progestational agents for the prevention of preterm labour, but a systematic review at the end of the 1980s concluded that progestational agents were not effective for that purpose (Goldstein 1989). However, another meta‐analysis (Keirse 1990) analysing trials using 17 alpha‐hydroxyprogesterone caproate only found a significant reduction in low birthweight babies in the treated group. Interest in the use of progestational agents for the prevention of preterm birth in high‐risk women has also recently been revived with the publication of two randomised controlled trials (da Fonseca 2003; Meis 2003) showing a reduction in the rate of preterm delivery in treated women. Recent systematic reviews of the literature have shown that progesterone, when used for prevention of preterm labour, is effective to reduce the incidence of preterm birth and low birthweight newborns (Dodd 2008; Farine 2008; Sanchez‐Ramos 2005) and that women at high risk of preterm birth should be recommended progestational agent therapy (Coomarasamy 2006). A recently published Cochrane review further confirmed the beneficial effects of progesterone in infant health following administration in women considered to be at increased risk of preterm birth due either to past history of preterm birth or when a short cervix was identified on ultrasound (Dodd 2013).
Besides focusing on the use of progestational agents to pre‐empt the onset of preterm labour in high‐risk women, some investigators have looked at the use of progestational agents for the treatment of threatened or established preterm labour. The first randomised controlled trial investigating the use of progesterone as a tocolytic agent dates back to 1960 (Fuchs 1960). With the revived interest in progestational agents in relation to preterm birth in recent years, we systematically surveyed the literature for studies on this subject with a view to performing a meta‐analysis in order to assess the efficacy of progestational agents in the treatment of threatened or established preterm labour.
Objectives
To determine if the use of progestational agents is effective as a form of treatment or co‐treatment for women with threatened or established preterm labour with intact membranes.
Methods
Criteria for considering studies for this review
Types of studies
All published, unpublished and ongoing randomised and quasi‐randomised trials. Cluster‐randomised and cross‐over trials are not considered eligible for inclusion.
Types of participants
Pregnant women diagnosed with established or threatened preterm labour before 37 completed weeks of gestation. Established labour is defined as the presence of regular uterine contractions and cervical dilatation of at least 3 cm. For threatened labour, uterine contractions are present but cervical dilatation is either absent or is less than 3 cm.
We excluded women with ruptured membranes and women with the possibility of placental abruptio. Women with ruptured membranes are at risk of chorioamnionitis, which is not a complication in women with preterm labour with intact membranes. The treatment including justification for tocolysis is different and hence the reason why we excluded this group of women. Women with the possibility of placental abruptio would likely require delivery instead of being treated with tocolysis. This group of women were therefore also excluded. Women with cervical incompetence were excluded due to the difference in the mechanism of the preterm labour.
Types of interventions
Progestational agents given either alone or in combination with other tocolytics, for the treatment of preterm labour, administered by any route and in any dose compared to a control group receiving another tocolytic, placebo or no treatment.
Types of outcome measures
Primary outcomes
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Very preterm birth (before completion of 34 weeks of gestation).
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Low birthweight (less than 2500 g and less than 1500 g).
Secondary outcomes
Fetal and neonatal outcomes
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Admission to the neonatal intensive care unit.
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Apgar score less than seven at five minutes.
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Fetal, perinatal death, and neonatal death.
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Respiratory/gastrointestinal/neurological/other complications.
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Birthweight (not prespecified ‐ see Differences between protocol and review).
Measures of effectiveness
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Preterm birth within 24, 48 and 72 hours, and one week of commencing therapy.
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Delivery before 37, 32 and 28 weeks of gestation.
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Additional tocolytic therapy.
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Cervical length shortening (not prespecified ‐ see Differences between protocol and review).
Adverse effects for women
Women's views and measures of satisfaction
Costs
Outcomes were included in the analysis if data were available according to the original allocation and reasonable measures were taken to minimise observer bias. Data that were not prestated were extracted and reported but these were clearly labelled as not prespecified. The possibility has to be borne in mind that such outcomes were only reported because the difference between the groups, as a result of chance, has reached conventional levels of statistical significance.
Search methods for identification of studies
Electronic searches
We searched the Cochrane Pregnancy and Childbirth Group’s Trials Register by contacting the Trials Search Co‐ordinator (31 August 2013).
The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co‐ordinator and contains trials identified from:
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monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
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weekly searches of MEDLINE;
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weekly searches of Embase;
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handsearches of 30 journals and the proceedings of major conferences;
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weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.
Details of the search strategies for CENTRAL, MEDLINE and Embase, the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service can be found in the ‘Specialized Register’ section within the editorial information about the Cochrane Pregnancy and Childbirth Group.
Trials identified through the searching activities described above are each assigned to a review topic (or topics). The Trials Search Co‐ordinator searches the register for each review using the topic list rather than keywords.
In addition, we searched CENTRAL (The Cochrane Library 2013, Issue 10) using the search strategy listed in Appendix 1; MEDLINE (January 1966 to 31 August 2013) using the search strategy listed in Appendix 2; EMBASE (January 1974 to 31 August 2013) using the strategy listed in Appendix 3.
Searching other resources
We attempted to contact relevant organisations, individual researchers working in the field, and companies for unpublished data, confidential reports, and raw data from published trials. We also checked reference lists of all studies included to look for any additional studies.
We did not apply any language restrictions.
Data collection and analysis
Selection of studies
Two review authors (LL Su and M Samuel) independently examined the abstracts of studies identified by the search strategy. We then retrieved the full publications of the qualifying abstracts. We resolved discrepancies by discussion and by seeking the opinion of the third author (YS Chong).
Data extraction and management
We designed a form to extract data. For eligible studies, two review authors (LL Su and M Samuel) independently extracted data using the agreed form. We resolved differences through discussion or by involving the third assessor (YS Chong). When information regarding any of the above was unclear, we attempted to contact the authors of the original reports to provide further details. We entered data into Review Manager software (RevMan 2012) and checked for accuracy.
Assessment of risk of bias in included studies
Two review authors (LL Su and M Samuel) independently assessed risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Any disagreement was resolved by discussion or by involving a third assessor (YS Chong).
(1) Random sequence generation (checking for possible selection bias)
We described for each included study the methods used to generate the allocation sequence.
We assessed the methods as:
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low risk of bias (any truly random method, e.g. random number table; computer random‐number generator);
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high risk of bias (alternation; hospital or clinic record number);
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unclear risk of bias.
(2) Allocation concealment (checking for possible selection bias)
We described for each included study the method used to conceal the allocation sequence and determined whether intervention allocations could have been foreseen in advance of, or during, recruitment, or could be changed after assignment.
We assessed the methods as:
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low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
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high risk of bias (open random allocation; unsealed or non‐opaque envelopes; alternation; date of birth);
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unclear risk of bias.
(3.1) Blinding of participants and personnel (checking for possible performance bias)
We described for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We considered that studies are at low risk of bias if they were blinded, or if we judged that the lack of blinding would be unlikely to affect the results. We assessed blinding separately for different outcomes or classes of outcomes.
We assessed the methods as:
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low, high or unclear risk of bias for participants;
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low, high or unclear risk of bias for personnel.
(3.2) Blinding of outcome assessment (checking for possible detection bias)
We described for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We assessed blinding separately for different outcomes or classes of outcomes.
We assessed the methods used to blind outcome assessment as:
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low, high or unclear risk of bias.
(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)
We described for each included study, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We stated whether attrition and exclusions were reported and the numbers included in the analysis at each stage (compared with the total randomised participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. Where sufficient information was reported, or could be supplied by the trial authors, we have re‐included missing data in the analyses we have undertaken.
We assessed the methods as:
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low risk of bias (e.g. no missing data; missing outcome data balanced across groups);
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high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; 'as treated' analysis done with substantial departure of intervention received from that assigned at randomisation);
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unclear risk of bias.
(5) Selective reporting (checking for reporting bias)
We described for each included study how we investigated the possibility of selective outcome reporting bias and what we found.
We assessed the methods as:
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low risk of bias (where it is clear that all of the study's pre‐specified outcomes and all expected outcomes of interest to the review have been reported)
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high risk of bias (where not all the study's pre‐specified outcomes have been reported; one or more reported primary outcomes were not pre‐specified; outcomes of interest are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported);
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unclear risk of bias.
(6) Other bias (checking for bias due to problems not covered by 1 to 5 above)
We described for each included study any important concerns we have 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 bias
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high risk of 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 Handbook (Higgins 2011). With reference to (1) to (6) above, we planned to assess the likely magnitude and direction of the bias and whether we considered it is likely to impact on the findings. We planned to explore the impact of the level of bias through undertaking sensitivity analyses ‐ see 'Sensitivity analysis'.
Measures of treatment effect
Dichotomous data
For dichotomous data, we presented the results as summary risk ratio with 95% confidence intervals.
Continuous data
For continuous data, we used the mean difference for outcomes 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
Cluster‐randomised trials
Cluster‐randomised trials are not a valid study design for inclusion in this review.
Crossover Trials
Cross‐over trials are not a valid study design for inclusion in this review.
Dealing with missing data
For included studies, we noted levels of attrition. We planned to explore the impact of including studies with high levels of missing data in the overall assessment of treatment affect 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 (< 0.10) in the Chi² test for heterogeneity.
Assessment of reporting biases
If there had been 10 or more studies in the meta‐analysis, we would have investigated reporting biases (such as publication bias) using funnel plots. We would have assessed funnel plot asymmetry visually. If asymmetry had been suggested by a visual assessment, we would have performed 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.
If 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
If we had identified substantial heterogeneity, we planned to investigate it using subgroup analyses and sensitivity analyses. We would have considered whether an overall summary was meaningful and, if so, used random‐effects analysis to produce it.
The included trials focused mainly on singleton pregnancies. However, in subsequent updates of this review, if trials involving pregnant women with multiple pregnancies are identified, we plan to carry out the following subgroup analysis.
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Single versus multiple pregnancy.
Any subgroup analysis in future 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
We planned to carry out sensitivity analyses to explore the effect of trial quality assessed by concealment of allocation, high attrition rates (greater than 20%), or both, with poor‐quality studies (high risk of bias; unclear risk of bias) being excluded from the analyses in order to assess whether this made any difference to the overall result.
Results
Description of studies
Results of the search
Five additional trials were identified following the updated search for this review (Arikan 2011; Chawanpaiboon 2011; Goel 2011; Tan 2012; Wood 2011). The trial that was previously ongoing has been published (Tan 2012) and was included. One trial is currently ongoing (Wood 2011). One trial (Goel 2011) was included but the data were limited as it was a poster presentation instead of a journal publication. A total of eight trials were included In this review, involving 563 women, but only seven trials, involving 538 women, contributed data for analyses.
The full text of these reports was then examined independently by two review authors. For details of the eight included studies, see the 'Characteristics of included studies' table.
(For details of the results of the search carried out in the previous version of this review (Su 2010), see Appendix 4.)
Included studies
Out of these eight studies, the participants in four of them (Arikan 2011; Facchinetti 2007; Noblot 1991; Tan 2012) received another form of tocolytic agent prior to being randomised to either the treatment (progesterone) or placebo (or observation) group. The participants in Facchinetti 2007 received atosiban, whereas the participants in Tan 2012 received nifedipine. The participants in both Noblot 1991 and Arikan 2011 received betamimetics (ritodrine). In Chawanpaiboon 2011, the participants were randomised to either nifedipine, progesterone or bedrest. In Goel 2011, the participants received either micronised progesterone or isoxupurine. In Erny 1986 and Fuchs 1960, comparison between progesterone and placebo was made, without concomitant tocolytic agents.
Our primary outcome of preterm births at less than 37 weeks of gestation was reported in four studies (Arikan 2011; Facchinetti 2007; Noblot 1991; Tan 2012). Facchinetti 2007 also analysed the percentage of preterm births at less than 35 weeks' gestation. Other important outcome measures studied included the amount and duration of ritodrine, duration of pregnancy prolongation and duration of hospitalisation (Noblot 1991). Facchinetti 2007 also investigated the effect of progesterone on cervical length changes, which is an important outcome measure due to the access to ultrasound measurement of cervical length as technology advances.
In Erny 1986, plasma progesterone levels were evaluated in the 53 participants after 30 minutes' rest and one hour after a single dose of micronised progesterone or placebo. Frequency of uterine contractions one hour after the intervention was another outcome in this study.
Chawanpaiboon 2011 was the only trial that studied the outcome of the time taken to inhibit uterine contractions among participants randomised to nifedipine, progesterone or bedrest.
Important outcomes related to perinatal morbidity were reported in Arikan 2011 and Tan 2012. While Arikan 2011 was the first study that reported on perinatal mortality, another important outcome of delivery within 48 hours was reported by Tan 2012.
Fuchs 1960 published a randomised double‐blind controlled trial back in 1958, comparing the use of progesterone and placebo for women who presented with symptoms of threatened preterm labour. The study included women with rupture of membrane or vaginal bleeding being the initial symptoms, both of which were exclusion criteria in our review. Only data relating to the symptoms of rhythmic or constant pains were analysed. However, the gestational age of this group of participants was not clear, which made analyses difficult.
Identical data from Noblot 1991 were also published in a French journal (Audra 1991). We only extracted the data from one publication (Noblot 1991). The data from Fuchs 1960 were presented at a conference and published as an abstract in another journal (Fuchs 1959). We only extracted the data from the full publication.
Goel 2011 was a poster presentation instead of journal publication, limiting the data that were available.
Excluded studies
There were a total of five excluded studies.
Two studies (Facchinetti 2008; Szekeres‐Bartho 1983) were excluded as progesterone was used only after the initial treatment of the preterm labour with another tocolytic agent; atosiban in Facchinetti 2008 and betamimetics in Szekeres‐Bartho 1983. Progesterone was used for maintaining the uterine quiescence rather than for treatment of the preterm labour in these studies. Szekeres‐Bartho 1983 showed that preterm delivery occurred more frequently among women who did not receive any progesterone compared with those who received weekly progesterone after the initial resolution of preterm labour. Facchinetti 2008 showed that women who did not receive progesterone after the initial resolution of preterm labour had significantly more cervical length shortening compared with women who received progesterone.
Another study compared the use of orciprenaline with a range of other tocolytic agents for the treatment of threatened premature labour (Bedoya 1972). Progesterone was included in this range of tocolytic agents but there was no specific comparison between the use of orciprenaline with progesterone. This study was therefore excluded.
Benifla 1997 was a double‐blind study comparing the use of progesterone and placebo in women presenting with symptoms of preterm labour. However, the outcome of the study was the effects of progesterone on liver enzymes, which was not one of the outcome measures in our review. The study by Breart 1979 was excluded as this study compared the use of two types of progesterone rather than compared the use of progesterone with another form of tocolytic agent.
Risk of bias in included studies
Please see Figure 1 and Figure 2 for a summary of all 'Risk of bias' assessments.
'Risk of bias' summary: review authors' judgements about each risk of bias item for each included study.
'Risk of bias' graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
Allocation
The randomisation process, in general, and the concealment of allocation, in particular, are considered the most important and sensitive indicators that bias has been minimised in a clinical trial (Schulz 1995). The studies by Arikan 2011, Facchinetti 2007, Noblot 1991 and Tan 2012 were randomised. For Facchinetti 2007, the urn method of randomisation (Wei 1988) with stratification according to clinical centre, was used to create the computer‐generated randomisation sequence. A 2:1 ratio was used for the assignment of women to 17 progesterone or to placebo. In Noblot 1991, randomisation was carried out by a balanced series of six participants according to randomisation tables. In Arikan 2011, participants were randomised according to a computer‐generated number list. In Tan 2012, the randomisation sequence was generated using an electronic generator provided by random.org and a variable block size of eight or 12 was used.
The study by Fuchs 1960 was a quasi‐randomised trial. In this study, participants with uneven admission numbers were treated with one preparation and those with even numbers received another preparation. It was therefore a quasi‐randomised trial. Erny 1986; Goel 2011 and Chawanpaiboon 2011 were randomised trials but the methods of randomisation and allocation concealment were not mentioned. We wrote to the authors in an attempt to obtain more details about the randomisation method but we have not received replies.
Allocation concealment was inadequate in Facchinetti 2007 and Noblot 1991. For Facchinetti 2007, the allocation list was managed by a senior midwife, whereas the interventions in Noblot 1991 were distributed in a random order. For Fuchs 1960, allocation concealment was inadequate as allocation of treatment was based on odd or even numbers indicating that assignment of treatment could be predicted in advance. In Arikan 2011, treatment was allocated based on a computer‐generated numbered list. In Tan 2012, treatment was also allocated based on the computer‐generated randomisation sequence.
Blinding
Noblot 1991 and Fuchs 1960 were appropriately blinded. Both trials mentioned that the preparations containing progesterone and placebo were identical and that the identities were unknown to the physicians. As the preparations were identical, the participants and the staff administering the medications were also blinded to the intervention. Erny 1986 was also a double‐blind study, with the type of intervention being unknown to the woman and physician. For Facchinetti 2007, the authors specifically mentioned that the study was not double blinded as it was not sponsored and the preparation of true placebo (same vial, same oil without active compound) was not possible.
For Arikan 2011, blinding was not used as the authors specifically mentioned that the preparation of a true placebo was not possible in the trial. Tan 2012 was appropriately blinded. The trial agents were packaged in identical containers. Participants and their providers were blinded as to the treatment group assignment. Blinding was not mentioned in Chawanpaiboon 2011 and Goel 2011.
Incomplete outcome data
In Facchinetti 2007, none of the 60 women who received either progesterone or in the observation group was lost to follow‐up. For Noblot 1991 and Erny 1986, no participant was lost to follow‐up. Analyses were performed on all the 44 and 53 participants recruited for the study, respectively. For Fuchs 1960, there was no mention about the number of participants lost to follow‐up. However, the total number of participants reported in the analyses of outcomes was less than the initial 150 participants recruited in the study, ranging from a total of 58 women for the outcome of 'delivery during treatment', 68 for the outcome of 'delivery after treatment' and 126 for the outcome of 'weight distribution of the infants'.
In Arikan 2011, none of the 83 women who were randomly assigned to progesterone or placebo following ritodrine infusion was lost to follow‐up. In Chawanpaiboon 2011, there was no loss of follow‐up to the 150 women recruited in the study.
In Tan 2012, 21 out of the 112 participants (13 randomised to 17 alpha‐hydroxyprogesterone caproate and eight to placebo) delivered in a different hospital of whom six were completely lost to follow‐up. Outcome data for women who delivered elsewhere were limited. In addition, outcomes relating to infant morbidity (intraventricular haemorrhage, necrotising enterocolitis, sepsis, use of mechanical ventilation and oxygen at seven and 28 days) were reported only for those 25 infants admitted to the neonatal intensive care unit (NICU); we assumed that all infants with these serious conditions would be likely to have been admitted to the NICU, but it is possible that infants lost to follow‐up may also have had serious morbidity. For these outcomes we have used the number of infants in each group born in the study hospital as denominators.
Intention‐to‐treat analysis was therefore adhered to for Arikan 2011, Chawanpaiboon 2011, Erny 1986, Facchinetti 2007 and Noblot 1991, with the analyses being performed on all the women recruited for the studies. For Fuchs 1960 and Tan 2012, the analyses were not performed on all the 150 women who received the medications. There was therefore no intention‐to‐treat analysis. As Goel 2011 was presented as a poster and not published in a journal, data were limited and it was not clear whether there was any attrition bias.
Selective reporting
There were no apparent selective reporting bias and other sources of bias in all the trials in this review. All the prespecified outcomes were addressed in the trials.
Other potential sources of bias
We assessed one study as being at high risk of bias (Noblot 1991). In Noblot 1991, one participant in the placebo arm and three participants in the progesterone arm were pregnant women with multiple pregnancies. The difference in the number of multiple pregnancies in the two arms could pose bias to some of the outcomes such as period of pregnancy prolongation. In one study it was not clear whether there were other sources of bias present (Goel 2011). No other apparent sources of bias were identified for the remaining studies (Arikan 2011; Chawanpaiboon 2011; Erny 1986; Facchinetti 2007; Fuchs 1960; Tan 2012).
Effects of interventions
Primary outcome measures
The two primary outcomes of the review are very preterm births of less than 34 completed weeks of gestation and birthweight of less than 2.5 kg. One study (Tan 2012) studied the outcome of very preterm births of less than 34 completed weeks of gestation and reported no statistically significant difference between the group where progesterone was used as an adjunct treatment to nifedipine and the group where placebo was used with nifedipine (risk ratio (RR) 0.62, 95% confidence interval (CI) 0.30 to 1.27; Analysis 1.1). Tan 2012 was also the first study that looked at the outcome of birthweight of less than 2.5 kg and showed no difference between the progesterone and placebo groups (RR 1.01, 95% CI 0.61 to 1.65, Analysis 1.4).
Secondary outcome measures
Fetal and neonatal outcomes
The recent published trials (Arikan 2011; Tan 2012) addressed our prespecified secondary outcomes related to perinatal morbidity. No statistically significant difference was demonstrated for the outcome of respiratory distress syndrome between the group where progesterone was used as an adjunct treatment to ritodrine and the group where placebo was used with ritodrine (Analysis 1.12). The outcomes of neonatal intensive care admission (Analysis 1.3), need for mechanical ventilation (Analysis 1.9), intraventricular haemorrhage (Analysis 1.5), necrotising enterocolitis (Analysis 1.6), oxygen requirement on day seven and day 28 of life were also studied (Analysis 1.7 and Analysis 1.8). No statistically significant differences were demonstrated for these outcomes from analyses of these data. Peinatal mortality was studied in one study (Arikan 2011), which did not show any statistically significant difference (Analysis 1.11).
Both Facchinetti 2007 and Arikan 2011 showed a statistically significant increase in birthweight in the group co‐treated with progesterone (mean difference (MD) 294 g, 95% CI 91.73 to 496.27; and MD 397.5 g, 95% CI 86.00 to 709.00) (Analysis 1.2). This outcome measure was also studied by Noblot 1991 and showed no difference between the placebo and intervention groups. However, as no standard deviations for birthweight were available in the publication by Noblot 1991, the outcome of birthweight could not be analysed using the forest plot and the data are presented in Table 1. Tan 2012 also studied this outcome; it showed no statistically significant difference between the progesterone and placebo groups. Even though it was mentioned that the total number of participants for this outcome was 105, the number of participants in each group was not reported. The data therefore could not be analysed using the forest plot and data were also presented in Table 1.
| Study ID | Progesterone group | Placebo group |
| 3077 (no SD/SE reported) (n = 22) | 2832 (no SD/SE reported) (n = 22) | |
| 3103 ± 468 (SD) | 2809 ± 317 (SD) | |
| 2.62 ± 0.75 (SD) | 2.53 ± 0.77 (SD) |
SD: standard deviation
SSE: standard error
Measures of effectiveness
The primary outcome of Tan 2012 was the number of deliveries within 48 hours of intervention, which is a prespecified secondary outcome in this review. The results did not show any statistically significant difference between the group where progesterone was used and the group where progesterone was not used (Analysis 1.10).
The use of progestational agents resulted in a statistically significant reduction in preterm deliveries at less than 37 weeks of gestation (average RR 0.62, 95% CI 0.39 to 0.98, I² = 57%, Tau² = 0.11; Analysis 1.1). This is a pre‐specified secondary outcome in our review. This outcome was reported by four studies (Arikan 2011; Facchinetti 2007; Noblot 1991; Tan 2012). In Noblot 1991, the number of participants with deliveries before 37 weeks of gestation was seven in the ritodrine and placebo group and three in the ritodrine and progesterone group, after excluding the participants with multiple pregnancies in each group. The study did not specifically compare the outcomes of the women with multiple pregnancies. All four women with multiple pregnancies (one in the ritodrine and placebo group and three in the ritodrine and progesterone group) had delivery before 37 weeks of gestation. Due to the lack of data and the small number of participants with multiple pregnancies, subgroup analyses were not performed.
Other outcome measures
Facchinetti 2007 also investigated the outcome of delivery before 35 weeks of gestation. Even though there is a trend showing that the addition of progesterone resulted in less deliveries before 35 weeks of gestation, the reduction was not statistically significant (average RR 0.43, 95% CI 0.12 to 1.50; Analysis 1.1).
One of the primary outcomes in Arikan 2011 was the time of intervention until delivery (latency period) and reported that micronised natural progesterone treatment resulted in a prolonged latency period of 32.1 ± 17.8 days versus 21.2 ± 16.3 days in the control group. Chawanpaiboon 2011 analysed the success rate of inhibition of uterine contractions. Nifedipine, 17‐alpha‐hydroxyprogesterone caproate (proluton depot) and bed rest were used to inhibit contractions with a success rate of 80%, 66% and 64% respectively, without statistical significance. However, when a time‐to‐event test was used, nifedipine took the shortest time for contraction inhibition in threatened preterm labour with statistical significance. Nifedipine took the shortest median time to inhibit contraction (3.00 ± 0.48 hours with 95% CI of 4.18 to 5.83) while proluton took 5.00 ± 0.42 hours with 95% CI of 2.07 to 3.93).
Noblot 1991 showed that the group of participants who received progesterone had a reduction in both the dosage and the duration of the concomitant betamimetics administration. The length of hospitalisation was also significantly shorter in the group who received progesterone compared to the placebo group (13.6 days versus 17.8 days) (Table 2). The results showed no statistically significant differences for outcomes including duration of pregnancy prolongation (Table 3) and frequency of uterine contraction (Table 4). However, the results presented in the publication were not complete, with many outcomes being reported without standard deviations or standard errors. These included important outcome measures such as duration of pregnancy prolongation, birthweight and Apgar scores. Statistical analysis including the forest plots, therefore, could not be generated for these outcomes.
| Study ID | Progesterone group | Placebo group |
| 13.6 (n = 21) | 17.8 (n = 18) |
| Study ID | Progesterone group | Placebo group |
| 6.0 (n = 22) | 6.4 (n = 22) |
| Study ID | Definition of uterine contraction | Progesterone group | Placebo group |
| Frequency of uterine contractions/10 minutes D0 H1 (1 hour after admission) | 0.7 ± 1.26 (not clear SD or SE) (n = 22) | 0.22 ± ‐0.77 (not clear SD or SE) (n = 22) |
SD: standard deviation
SSE: standard error
For the 53 participants with intact membranes in Erny 1986, 42.8% of the participants who received placebo showed decreasing frequency of uterine contractions in the placebo group and 88% of the participants who received utrogestan showed decreasing uterine contractions.
Fuchs 1960 reported that there were no differences between the progesterone group and placebo group with regards to the number of women for whom delivery was successfully postponed. The authors reported that a subanalysis of the women who presented with the initial symptoms of pains did not change the results. In this subgroup, three women in the placebo group delivered within 48 hours of treatment and two women in the intervention group delivered within 48 hours of treatment. The numbers were too small for statistical analysis.
The trials did not address the other secondary outcomes related to adverse effects for women and costs.
Discussion
The first randomised controlled trial investigating progesterone as a tocolytic agent dates back to 1960. However, as other tocolytic agents evolved, the interests in pursuing progesterone for tocolysis waned. Recently, there has been a renewed interest in the use of progestational agents, both as a prophylactic measure for preterm births as well as a treatment option for women in preterm labour.
For trials studying the efficacy of tocolytic agents, the most important clinical outcomes are the rates of preterm deliveries and the rates of low birthweight. Since the previous version of our review, data regarding the primary outcomes of very preterm birth of less than 34 weeks of gestation and birthweight of less than 2.5 kg have emerged. Tan 2012 was the first study to look at both these outcomes and it showed no difference between the progesterone and placebo groups. These should be universal outcome measures, which will allow meta‐analyses to be performed, resulting in more meaningful conclusion.
There is now encouraging data to show that progesterone, when used with another tocolytic agent, results in a reduction of preterm births at less than 37 weeks of gestation. This outcome is studied by four trials thus far. Two studies showed an increase in birthweight in the group treated with progesterone. Rigorous and larger studies will be important to investigate these potential beneficial effects of progesterone for preterm labour.
The effects of the intervention on neonatal mortality and various aspects of neonatal morbidity are also crucial. These outcomes were not addressed in the previous version of our review but were addressed in two studies in this review (Arikan 2011; Tan 2012). No statistically significant difference has been shown for the group randomised to progesterone compared with placebo. However, larger studies or combined data from various studies with similar outcome measures will be needed to achieve clinically meaningful and significant implications. Inclusion of these outcomes should be considered for any future trials investigating the effect of progesterone as a treatment option for threatened or established preterm labour.
Facchinetti 2007 showed a statistically significant reduction in cervical length measurements in the group receiving progesterone compared with the group that did not receive progesterone at both seven (MD ‐1.54 mm; 95% CI ‐2.49 to ‐0.50) and 21 days (MD ‐2.20 mm; 95% CI ‐3.52 to ‐0.88) after randomisation. The difference between the two groups was even higher when the analysis was restricted only to women with a short cervix (less than or equal to 25 mm) at enrolment. This outcome has been reported in the two studies by the Facchinetti group so far (Facchinetti 2007; Facchinetti 2008). With the advances of ultrasound technology, outcome measures such as cervical length measurements will play an increasingly important role. This would pose an interesting research area.
Two of the studies in our review (Erny 1986; Fuchs 1960) included women with rupture of membranes on admission while another study included women with multiple pregnancies (Noblot 1991). Rupture of membranes should be an exclusion criteria in studies investigating the effects of tocolytic agents for preterm labour. Management of women with preterm rupture of labour with added risks of chorioamnionitis is different from the treatment of women admitted for preterm labour with intact membranes. For Noblot 1991, one participant in the placebo arm and three participants in the progesterone arm were pregnant women with multiple pregnancies. However, separate data were not available for these participants. Subgroup analyses were not performed due to the lack of data and the small number of participants. Women with multiple pregnancies are at risk of preterm labour and may benefit from tocolysis. Trials looking at the use of progesterone on this high‐risk group of pregnant women are strongly encouraged. Should future trials on the use of progesterone in women with multiple pregnancies be undertaken, we will include them in our subgroup analysis.
The available studies that investigated the use of progesterone thus far did not look at the same form of progesterone. Utrogestan was the progesterone studied by Noblot 1991 and Erny 1986. Micronised natural progesterone was used in Arikan 2011. Seventeen‐alpha‐hydroxyprogesterone caproate in the form of Lentogest was used in the study by Facchinetti 2007 and in the form of Proluton depot in Chawanpaiboon 2011. Seventeen‐alpha‐hydroxyprogesterone caproate was also used in Tan 2012. The name of the progesterone studied was not mentioned in Fuchs 1960. The dosage and the route of administration also varied in the available studies. Progesterone was administered intramuscularly in Chawanpaiboon 2011, Facchinetti 2007, Fuchs 1960 and Tan 2012. The progesterone in the study by Noblot 1991 and Erny 1986 was given orally while the progesterone in Arikan 2011 was administered via the vaginal route. This led to the more fundamental question of which would be the most effective route of administration of progesterone for tocolysis. The only study comparing different types of progesterone was conducted by Breart el al (an excluded study), who compared the efficiency of hydroxyprogesterone caproate and chlormadinone acetate for the prevention of preterm labour (Breart 1979). The authors found no significant differences between the two groups in either the length of gestation, delay between the beginning of treatment and delivery or other parameters related to prematurity. Studies comparing the routes of administration and the appropriate dosage of progesterone for tocolysis should be encouraged.
Another challenge in this review was the varying concomitant tocolytic agents used with the progesterone. Out of the eight studies, progesterone was used as an independent intervention in Chawanpaiboon 2011, Erny 1986, Fuchs 1960 and Goel 2011, It was used as an adjunct treatment to ritodrine infusion in Arikan 2011 and Noblot 1991. Progesterone was used as an adjunctive treatment to nifedipine in Tan 2012 and atosiban in Facchinetti 2007. Subgroup analyses may be possible with the publication of more studies in each group.
'Risk of bias' summary: review authors' judgements about each risk of bias item for each included study.
'Risk of bias' graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
Comparison 1 Progestational agents versus placebo, Outcome 1 Preterm delivery.
Comparison 1 Progestational agents versus placebo, Outcome 2 Birthweight (g).
Comparison 1 Progestational agents versus placebo, Outcome 3 Admission to neonatal intensive care unit.
Comparison 1 Progestational agents versus placebo, Outcome 4 Low birthweight (< 2.5 kg).
Comparison 1 Progestational agents versus placebo, Outcome 5 Intraventricular haemorrhage.
Comparison 1 Progestational agents versus placebo, Outcome 6 Necrotising enterocolitis.
Comparison 1 Progestational agents versus placebo, Outcome 7 Oxygen requirement on day 7 of life.
Comparison 1 Progestational agents versus placebo, Outcome 8 Oxygen requirement on day 28 of life.
Comparison 1 Progestational agents versus placebo, Outcome 9 Mechanical ventilation.
Comparison 1 Progestational agents versus placebo, Outcome 10 Delivery within 48 hours of intervention.
Comparison 1 Progestational agents versus placebo, Outcome 11 Perinatal mortality.
Comparison 1 Progestational agents versus placebo, Outcome 12 Respiratory distress syndrome.
| Study ID | Progesterone group | Placebo group |
| 3077 (no SD/SE reported) (n = 22) | 2832 (no SD/SE reported) (n = 22) | |
| 3103 ± 468 (SD) | 2809 ± 317 (SD) | |
| 2.62 ± 0.75 (SD) | 2.53 ± 0.77 (SD) | |
| SD: standard deviation | ||
| Study ID | Progesterone group | Placebo group |
| 13.6 (n = 21) | 17.8 (n = 18) |
| Study ID | Progesterone group | Placebo group |
| 6.0 (n = 22) | 6.4 (n = 22) |
| Study ID | Definition of uterine contraction | Progesterone group | Placebo group |
| Frequency of uterine contractions/10 minutes D0 H1 (1 hour after admission) | 0.7 ± 1.26 (not clear SD or SE) (n = 22) | 0.22 ± ‐0.77 (not clear SD or SE) (n = 22) | |
| SD: standard deviation | |||
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
| 1 Preterm delivery Show forest plot | 4 | Risk Ratio (M‐H, Random, 95% CI) | Subtotals only | |
| 1.1 Delivery before 37 weeks | 4 | 293 | Risk Ratio (M‐H, Random, 95% CI) | 0.62 [0.39, 0.98] |
| 1.2 Delivery before 35 weeks | 1 | 60 | Risk Ratio (M‐H, Random, 95% CI) | 0.43 [0.12, 1.50] |
| 1.3 Delivery before 34 weeks | 1 | 62 | Risk Ratio (M‐H, Random, 95% CI) | 0.62 [0.30, 1.27] |
| 2 Birthweight (g) Show forest plot | 2 | Mean Difference (IV, Random, 95% CI) | Subtotals only | |
| 3 Admission to neonatal intensive care unit Show forest plot | 2 | 187 | Risk Ratio (M‐H, Fixed, 95% CI) | 1.08 [0.59, 1.97] |
| 4 Low birthweight (< 2.5 kg) Show forest plot | 1 | 105 | Risk Ratio (M‐H, Fixed, 95% CI) | 1.01 [0.61, 1.65] |
| 5 Intraventricular haemorrhage Show forest plot | 1 | 104 | Risk Ratio (M‐H, Fixed, 95% CI) | 3.12 [0.13, 74.76] |
| 6 Necrotising enterocolitis Show forest plot | 1 | 104 | Risk Ratio (M‐H, Fixed, 95% CI) | 1.04 [0.07, 16.18] |
| 7 Oxygen requirement on day 7 of life Show forest plot | 1 | 104 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.69 [0.21, 2.31] |
| 8 Oxygen requirement on day 28 of life Show forest plot | 1 | 104 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.42 [0.08, 2.05] |
| 9 Mechanical ventilation Show forest plot | 2 | 187 | Risk Ratio (M‐H, Fixed, 95% CI) | 1.18 [0.41, 3.37] |
| 10 Delivery within 48 hours of intervention Show forest plot | 1 | 110 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.76 [0.38, 1.50] |
| 11 Perinatal mortality Show forest plot | 1 | 83 | Risk Ratio (M‐H, Fixed, 95% CI) | 0.31 [0.01, 7.41] |
| 12 Respiratory distress syndrome Show forest plot | 1 | 83 | Risk Ratio (M‐H, Random, 95% CI) | 0.93 [0.06, 14.38] |
