Preterm birth remains the leading cause of early neonatal death and infant mortality, often from respiratory distress syndrome as a consequence of immature lung development (Nassar 2001). Between 5% and 9% of pregnant women will give birth before 37 weeks' gestation, with higher rates in developing countries (Li 2012). Preterm babies who survive the early weeks of life are at risk of long-term neurological disability (Moore 2012; Saigal 2008; Serenius 2013). Parents are understandably worried and distressed when their baby is born preterm. Strategies to reduce the risk of preterm birth and, in particular, neonatal respiratory disease receive considerable attention (Crowther 2011; Roberts 2006; Stevens 2007).
The first report of a trial of prenatal thyrotropin-releasing hormone (TRH) given with antenatal corticosteroids to women threatening to give birth preterm with the aim of enhancing lung development was presented, in abstract form, by Liggins and his co-workers in 1988 (Liggins 1988). The rationale for the use of TRH was based on previous research by Liggins' group (Schellenberg 1988). In an elegant series of experiments in preterm lambs they showed both an increase in lung fluid phospholipids and an increase in lung distensibility when thyroid hormones were used in combination with corticosteroids. TRH and glucocorticoids showed similar synergism (Liggins 1988).
Thyroid hormones (T3 and T4) given antenatally to the mother do not readily reach the fetal circulation due to metabolism by the placenta and membranes. However, TRH given to the mother elevates thyroid stimulating hormone (TSH) and thyroid hormones concentrations in the fetus (Roti 1981). The exact action of TRH on the fetal lung is not known and it is possible that any action may be mediated via non-hormonal pathways.
In adults, intravenous TRH administration is associated with side effects, which are often transient, of nausea, vomiting, light headedness, facial flushing, metallic taste, and a rise in blood pressure (Jackson 1982).
Since the initial abstract reported by Liggins 1988, the use of prenatal TRH as an intervention strategy to reduce the risk of neonatal lung disease and its sequelae has been evaluated in several randomised trials.
This review updates a previously published Cochrane review on TRH added to corticosteroids for women at risk of preterm birth for preventing neonatal respiratory disease (Crowther 2004). The previous version of this review was able to include 13 trials, and concluded that prenatal TRH in addition to corticosteroids does not improve infants outcomes, and can be associated with maternal side effects.
This review assesses the current available evidence regarding the effectiveness and safety of prenatal TRH given in addition to corticosteroids to women at risk of preterm birth.
To assess the effects of TRH administered in addition to corticosteroids to women at risk of preterm birth on fetal and infant mortality and morbidity, and on maternal side effects.
Criteria for considering studies for this review
Types of studies
All published, unpublished and ongoing randomised controlled trials and quasi-randomised controlled trials with reported data that compare outcomes in women and babies exposed to prenatal thyrotropin-releasing hormone (TRH) and corticosteroids with outcomes in controls receiving corticosteroids alone, with or without placebo. We planned to include cluster-randomised trials, and exclude cross-over trials. We planned to include studies published as abstracts only.
Types of participants
Women at sufficiently high risk of preterm birth to warrant administration of prenatal corticosteroids to promote fetal lung maturity. High-risk groups were those women showing signs of threatening to give birth preterm, or needing early delivery because of maternal or fetal complications.
Types of interventions
TRH (any dosage) administered to the women intravenously and corticosteroids, compared with corticosteroids with either placebo or no placebo.
Types of outcome measures
Pre-specified clinical measures of outcome related to fetal and neonatal mortality, neonatal morbidity, childhood development and maternal morbidity.
Primary outcomes were chosen to be most representative of the clinically important measures of effectiveness and safety for the infants.
- Death prior to hospital discharge;
- chronic lung disease (variously defined by authors);
- respiratory distress syndrome (RDS).
Secondary outcomes included other measures of effectiveness, complications and health services use.
For the infant
- Chronic lung disease (variously defined by authors) or death;
- need for oxygen therapy;
- severe RDS (variously defined by authors);
- use of respiratory support (mechanical ventilation or continuous positive airway pressure, or both);
- admission to neonatal intensive care unit;
- intraventricular haemorrhage;
- intraventricular haemorrhage grade three or four;
- periventricular leucomalacia;
- air leak syndrome;
- pulmonary haemorrhage;
- necrotising enterocolitis;
- patent ductus arteriosus;
- low Apgar score at five minutes;
- gestational age at birth;
- use of surfactant;
- neurodevelopmental abnormality at follow-up (variously defined by authors);
- visual impairment at follow-up (variously defined by authors);
- hearing impairment at follow-up (variously defined by authors);
- motor delay at follow-up (variously defined by authors);
- motor impairment at follow-up (variously defined by authors);
- fine motor delay at follow-up (variously defined by authors);
- sensory impairment at follow-up (variously defined by authors);
- language development delay at follow-up (variously defined by authors);
- social delay at follow-up (variously defined by authors);
- Bayley Mental Development Index (variously defined by authors);
- Bayley Psychomotor Developmental Index (variously defined by authors).
For the mother
- light headedness;
- urgency of micturition;
- facial flushing;
- systolic blood pressure rise during treatment (variously defined by authors);
- diastolic blood pressure rise during treatment (variously defined by authors).
Search methods for identification of studies
We searched the Cochrane Pregnancy and Childbirth Group’s Trials Register by contacting the Trials Search Co-ordinator (30 June 2013).
The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co-ordinator and contains trials identified from:
- monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
- weekly searches of MEDLINE;
- weekly searches of Embase;
- handsearches of 30 journals and the proceedings of major conferences;
- weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.
Details of the search strategies for CENTRAL, MEDLINE and Embase, the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service can be found in the ‘Specialized Register’ section within the editorial information about the Cochrane Pregnancy and Childbirth Group.
Trials identified through the searching activities described above are each assigned to a review topic (or topics). The Trials Search Co-ordinator searches the register for each review using the topic list rather than keywords.
Searching other resources
We did not apply any language restrictions.
Data collection and analysis
The following methods were used for this update.
Please see Crowther 2004 for methods used in the previous version of this review.
Selection of studies
Two review authors independently assessed for inclusion all the potential studies we identified as a result of the search strategy. We resolved any disagreement through discussion, or if required we consulted a third review author.
Data extraction and management
We designed a form to extract data. At least two review authors extracted the data using the agreed form. We resolved discrepancies through discussion, or if required we consulted a third review author. Data were entered into Review Manager software (RevMan 2012) and checked for accuracy.
When information regarding any of the above was unclear, we attempted to contact authors of the original reports to provide further details.
Assessment of risk of bias in included studies
Two review authors independently assessed risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We resolved any disagreement by discussion or by involving a third assessor.
(1) Sequence generation (checking for possible selection bias)
We described for each included study the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.
We assessed the method as:
- low risk of bias (any truly random process, e.g. random number table; computer random number generator);
- high risk of bias (any non-random process, e.g. odd or even date of birth; hospital or clinic record number);
- unclear risk of bias.
(2) Allocation concealment (checking for possible selection bias)
We described for each included study the method used to conceal the allocation sequence and determine whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.
We assessed the methods as:
- low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
- high risk of bias (open random allocation; unsealed or non-opaque envelopes, alternation; date of birth);
- unclear risk of bias.
(3.1) Blinding of participants and personnel (checking for possible performance bias)
We described for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We considered that studies are at low risk of bias if they were blinded, or if we judged that the lack of blinding would be unlikely to affect results. We assessed blinding separately for different outcomes or classes of outcomes.
We assessed the methods as:
- low, high or unclear risk of bias for participants;
- low, high or unclear risk of bias for personnel.
(3.2) Blinding of outcome assessment (checking for possible detection bias)
We described for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We assessed blinding separately for different outcomes or classes of outcomes.
We assessed methods used to blind outcome assessment as:
- low, high or unclear risk of bias.
(4) Incomplete outcome data (checking for possible attrition bias through withdrawals, dropouts, protocol deviations)
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, the numbers included in the analysis at each stage (compared with the total randomised participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. Where sufficient information was reported, or could be supplied by the trial authors, we re-included missing data in the analyses which we undertook.
We assessed methods as:
- low risk of bias (e.g. no missing outcome data; missing outcome data balanced across groups);
- high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis done with substantial departure of intervention received from that assigned at randomisation);
- unclear risk of bias.
(5) Selective reporting bias
We described for each included study how we investigated the possibility of selective outcome reporting bias and what we found.
We assessed the methods as:
- low risk of bias (where it was clear that all of the study’s pre-specified outcomes and all expected outcomes of interest to the review had been reported);
- high risk of bias (where not all the study’s pre-specified outcomes had been reported; one or more reported primary outcomes were not pre-specified; outcomes of interest were reported incompletely and so could not be used; study fails to include results of a key outcome that would have been expected to have been reported);
- unclear risk of bias.
(6) Other sources of bias
We described for each included study any important concerns we had about other possible sources of bias.
We assessed whether each study was free of other problems that could put it at risk of bias:
- low risk of other bias;
- high risk of other bias;
- unclear whether there is risk of other bias.
(7) Overall risk of bias
We made explicit judgements about whether studies were at high risk of bias, according to the criteria given in the Cochrane Handbook (Higgins 2011). With reference to (1) to (6) above, we assessed the likely magnitude and direction of the bias and whether we considered it was likely to impact on the findings. We planned to explore the impact of the level of bias through undertaking sensitivity analyses - see Sensitivity analysis.
Measures of treatment effect
For dichotomous data, we presented results as summary risk ratio with 95% confidence intervals.
For continuous data, we used the mean difference when outcomes were measured in the same way between trials. If necessary, we would have used the standardised mean difference to combine trials that measured the same outcome, but used different methods.
Unit of analysis issues
We did not identify any cluster-randomised trials for inclusion. In future updates of this review, if we identify cluster-randomised trials, we plan to include them in the analyses along with individually-randomised trials. We will adjust their sample sizes using the methods described in the Cochrane Handbook using an estimate of the intracluster correlation co-efficient (ICC) derived from the trial (if possible), from a similar trial or from a study of a similar population (Higgins 2011). 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 also plan to acknowledge heterogeneity in the randomisation unit and perform a sensitivity analysis to investigate the effects of the randomisation unit.
We considered cross-over trials as inappropriate for inclusion in this review.
Dealing with missing data
For included studies, we noted levels of attrition. We 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 a Tau² was greater than zero, or there was a low P value (less than 0.10) in the Chi² test for heterogeneity.
Assessment of reporting biases
In future updates of this review, if 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.
We carried out statistical analysis using Review Manager software (RevMan 2012). We used fixed-effect meta-analysis for combining data where it was reasonable to assume that studies were estimating the same underlying treatment effect: i.e. where trials were examining the same intervention, and the trials’ populations and methods were judged sufficiently similar. Where there was clinical heterogeneity sufficient to expect that the underlying treatment effects differed between trials, or where substantial statistical heterogeneity was detected, we used random-effects meta-analysis to produce an overall summary if an average treatment effect across trials was considered clinically meaningful. The random-effects summary has been treated as the average range of possible treatment effects and we have discussed the clinical implications of treatment effects differing between trials. If the average treatment effect was not clinically meaningful, we would not have combined trials.
Where we used random-effects analyses, we have presented the results as the average treatment effect with its 95% confidence interval, and the estimates of Tau² and I².
Subgroup analysis and investigation of heterogeneity
Where we identified substantial heterogeneity, we investigated it using subgroup analyses and sensitivity analyses. We considered whether an overall summary was meaningful, and if it was, we used random-effects analysis.
We planned subgroup analyses to examine separately the primary outcomes for infants based on:
- the reasons the women were considered at risk of preterm birth;
- the number of infants in utero (singleton, twins or higher order multiple pregnancy);
- the gestational age TRH treatment was given;
- the dose of TRH given;
- the outcome for optimally treated infants, which was variously defined by the authors.
These analyses were only possible for the dose of TRH given, and the outcome for optimally treated infants.
The greatest beneficial effect of antenatal corticosteroids was observed in the group of infants delivered 24 hours or more and 10 days or less after start of therapy (Liggins 1972). An expectation that this may be the case for the combination of prenatal TRH and corticosteroids prompted the secondary timed analysis as follows:
- birth less than 24 hours after first dose;
- birth between 24 hours and 10 days, inclusive, after first dose;
- birth more than 10 days after first dose.
Initial analyses were limited to the pre-specified outcomes and sensitivity and secondary analyses to the pre-specified primary outcomes, and the secondary outcomes:
- chronic lung disease (variously defined by authors) or death;
- need for oxygen therapy;
- severe RDS (variously defined by authors);
- use of respiratory support (mechanical ventilation or continuous positive airway pressure, or both).
We assessed subgroup differences by interaction tests available within RevMan (RevMan 2012). We have reported the results of subgroup analyses quoting the Chi² statistic and P value, and the interaction test I² value.
We carried out a sensitivity analysis to explore the effects of trial quality assessed by sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting, by omitting studies rated as 'unclear risk of bias' or 'high risk of bias' for these components. The sensitivity analysis has been restricted to those pre-specified outcomes listed above.
Description of studies
Results of the search
The updated search of the Pregnancy and Childbirth Group's Specialist Register identified four reports that have been added as additional references under previously included trials (Chile 1998; Kim 2000; Knight 1994). We have included two additional trials in this update that were previously excluded, due to not reporting any relevant outcome data (Crowther 1995; Voto 1998).
Therefore, of the 22 studies that were identified, 15 met our inclusion criteria (Abuhamad 1999; ACTOBAT 1995; Ballard 1992b; Ballard 1998; Campos 1993; Carlan 1991; Ceriani 1992; Chile 1998; Crowther 1995; Europe 1999; Jikihara 1990; Kim 2000; Knight 1994; Morales 1989; Voto 1998).
Over 4600 women were recruited into the 15 trials that met the pre-specified criteria for inclusion in this review (Abuhamad 1999; ACTOBAT 1995; Ballard 1992b; Ballard 1998; Campos 1993; Carlan 1991; Ceriani 1992; Chile 1998; Crowther 1995; Europe 1999; Jikihara 1990; Kim 2000; Knight 1994; Morales 1989; Voto 1998).
Gestational age at trial entry varied between 24 to 33 completed weeks: 24 to 31 completed weeks in ACTOBAT 1995, Ballard 1992b and Campos 1993; 24 to less than 30 weeks in Ballard 1998; 24 to less than 33 weeks in Chile 1998 and Knight 1994; 24 to less than 34 weeks in Carlan 1991 and Crowther 1995; 24 to 34 weeks in Abuhamad 1999; less than 32 weeks in Europe 1999; less than 34 weeks in Morales 1989; 23 to 29 completed weeks in Jikihara 1990; 26 to 31 weeks in Ceriani 1992; and 26 to 34 weeks in Kim 2000.
All trials used the administration of antenatal corticosteroids as an inclusion criterion. The thyrotropin-releasing hormone (TRH) regimens varied as follows.
- Voto 1998 used 400 μg TRH every six hours for four doses.
- Knight 1994 used 400 μg TRH every 12 hours for a maximum of four doses.
- Abuhamad 1999 used 500 μg TRH every eight hours up to a maximum of four doses, repeated weekly for a maximum of four weeks or until delivery.
- In Crowther 1995, two treatment groups received either 200 μg TRH or 400 μg TRH over 30 minutes.
For further details see: Characteristics of included studies.
We excluded six trials (Devlieger 1997; Dola 1997; Roti 1990; Torres 1994; Torres 1995; Yoder 1997) for a variety of reasons. In four trials it was unclear as to whether all women (including those in the control group) received corticosteroids (Devlieger 1997; Dola 1997; Roti 1990; Torres 1995); in one trial a cross-over design was used (Devlieger 1997); for one trial it was unclear as to whether it was randomised (Torres 1994); and one trial stopped without enrolling any women (Yoder 1997).
For further details see: Characteristics of excluded studies.
Risk of bias in included studies
See Characteristics of included studies, Figure 1 and Figure 2 for further information on the risk of bias in the included studies. Overall, the risk of bias in the 15 included trials was judged to be moderate.
|Figure 1. 'Risk of bias' graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.|
|Figure 2. 'Risk of bias' summary: review authors' judgements about each risk of bias item for each included study.|
Six of the 15 included trials used adequate methods for sequence generation. Four trials (ACTOBAT 1995; Chile 1998; Europe 1999; Voto 1998) used central telephone randomisation, and two trials (Ballard 1992b; Knight 1994) used random number tables. Sequence generation was unclear for the remaining trials (Abuhamad 1999; Ballard 1998; Campos 1993; Carlan 1991; Ceriani 1992; Crowther 1995; Jikihara 1990; Kim 2000; Morales 1989).
Eight of the 15 trials (Abuhamad 1999; ACTOBAT 1995; Ballard 1992b; Ballard 1998; Chile 1998; Europe 1999; Knight 1994; Voto 1998) reported an adequate method for concealing allocation. Four trials (Abuhamad 1999; Ballard 1992b; Ballard 1998; Knight 1994) used a central allocation (pharmacy-controlled), and three trials (ACTOBAT 1995; Chile 1998; Europe 1999) used central telephone randomisation service. Voto 1998 used sequentially numbered drug containers of identical appearance. Allocation concealment was unclear in the remaining seven trials (Campos 1993; Carlan 1991; Ceriani 1992; Crowther 1995; Jikihara 1990; Kim 2000; Morales 1989).
Seven of the 15 included trials (ACTOBAT 1995; Ballard 1992b; Ballard 1998; Chile 1998; Europe 1999; Knight 1994; Voto 1998) were blinded throughout the study. In ACTOBAT 1995, assessment of neonatal outcomes was blinded, and a placebo was used except for with the first 198 women recruited. In the other six studies, all women, investigators, clinicians and pregnancy outcome assessors were blinded, and a placebo was used (Ballard 1992b; Ballard 1998; Chile 1998; Europe 1999; Knight 1994; Voto 1998).
In Abuhamad 1999, while a placebo was used and women and personnel were blinded, the blinding of outcome assessors was not detailed. Similarly, in Ceriani 1992, while a placebo was used, and the trial was described as "double-blind", no detail regarding blinding of outcome assessors was provided. In Morales 1989, neonate outcome recorders and neonatal respiratory distress assessors were blinded, however a placebo was not used (and thus women and other study personnel were not blinded).
Incomplete outcome data
Losses to follow-up in six trials (Abuhamad 1999; ACTOBAT 1995; Ballard 1998; Crowther 1995; Europe 1999; Knight 1994) were less than 3%. In Chile 1998, losses to follow-up were 21/370 (5.7%) for the main trial; however for the follow-up, losses were over 50%. In Voto 1998 data were missing for 4/35 (11.4%) of women; and in Carlan 1991, losses to follow-up were 7/44 (15.9%). No information was available on losses to follow-up in two trials (Jikihara 1990; Kim 2000).
An intention-to-treat analysis (with data analysed from all women randomised) was reported as being used in six trials (Abuhamad 1999; ACTOBAT 1995; Ballard 1998; Chile 1998; Europe 1999; Knight 1994), was probably used in three others (Carlan 1991; Jikihara 1990; Kim 2000) and was not used in Ballard 1992b; Campos 1993 and Morales 1989.
There was no obvious risk of selective reporting in five of the 15 trials (ACTOBAT 1995; Ballard 1998; Chile 1998; Europe 1999; Knight 1994). In six trials there was insufficient information to make a clear judgement (Abuhamad 1999; Carlan 1991; Ceriani 1992; Crowther 1995; Jikihara 1990; Kim 2000; Voto 1998).
Four trials (Ballard 1992b; Campos 1993; Ceriani 1992; Morales 1989) only presented outcomes for a subgroup of participants expected to benefit most from the exposure to prenatal TRH. This led to significant numbers of women who were randomised, being excluded from analysis in Morales 1989 (148/248; 60% excluded); Ballard 1992b (343/446; 77% infants excluded); probably Ceriani 1992 (percentage not reported); and Campos 1993 (percentage not reported). Morales 1989 gave outcome data for infants delivered within one week from the start of therapy. Ballard 1992b reported data for neonates born after full treatment, weighing less than 1500 g at birth and delivering less than 10 days after TRH treatment. Ceriani 1992 reported data for infants born within 10 days of entry who were fully treated (received all doses of TRH or corticosteroids, or both). Campos 1993 reported data on fully treated infants (received all doses of TRH or corticosteroids, or both) who were born within 48 hours of the last hormonal dose.
Neurological outcomes at childhood follow-up were reported for three trials (ACTOBAT 1995; Chile 1998; Europe 1999). ACTOBAT 1995 assessed neurological outcomes with a questionnaire completed by parents when their infants were 12 months of age. Some data were available for 1022 (81%) of the 1262 infants discharged home alive, but not all outcome data were available for all infants. A subset of 39 of 52 (75%) children recruited at a single centre in Europe 1999 (16% of the infants recruited to the trial overall and alive at end of data collection) were assessed at 12 months and 24 months using the Bayley Scales of Infant Development and by a paediatrician. Similarly, at 18 months, 66 (49%) of the 134 infants enrolled during a 12-month period (July 1997 to December 1998) of the Chile 1998 study were assessed using the Bayley Scales of Infant Development (2nd edition) by a neonatologist or neonatal fellow.
Other potential sources of bias
Ten of the 15 trials were judged to be at a low risk of other potential bias, with no other obvious sources of bias identified (ACTOBAT 1995; Ballard 1992b; Ballard 1998; Campos 1993; Chile 1998; Crowther 1995; Europe 1999; Knight 1994; Morales 1989; Voto 1998). For the other five trials, the risk of other potential bias was judged to be unclear, with insufficient information available to make a confident judgement (Abuhamad 1999; Carlan 1991; Ceriani 1992; Jikihara 1990; Kim 2000).
Effects of interventions
Fifteen trials involving over 4600 women were included, although only 13 trials contributed data to the meta-analyses. All trials used a combination of TRH and antenatal corticosteroids in the intervention group and corticosteroids alone (with or without a placebo) in the control group.
Comparison of TRH with corticosteroids versus corticosteroids alone
All eligible trials analysed by intention-to-treat
No beneficial effects of prenatal TRH were seen for the primary outcomes: death prior to hospital discharge (risk ratio (RR) 1.05, 95% confidence interval (CI) 0.86 to 1.27, six trials, 3694 infants) ( Analysis 1.1), chronic lung disease (RR 1.01, 95% CI 0.85 to 1.19, five trials, 2511 infants) ( Analysis 1.2) or respiratory distress syndrome (RDS) (average RR 1.05, 95% CI 0.91 to 1.22, nine trials, 3833 infants) ( Analysis 1.3). Moderate statistical heterogeneity was found for the outcome RDS (Tau² = 0.02; I² = 48%), and thus a random-effects model was used.
For the infant
No effects of prenatal TRH were shown on the composite outcome of death or chronic lung disease (RR 1.06, 95% CI 0.95 to 1.18, six trials, 3694 infants) ( Analysis 1.4), on the need for oxygen therapy (RR 1.05, 95% CI 0.97 to 1.13, four trials, 2387 infants) ( Analysis 1.5), or on the outcome severe RDS (average RR 0.88, 95% CI 0.57 to 1.36, three trials, 2119 infants; Tau² = 0.11; I² = 73%) ( Analysis 1.6). The need for respiratory support was significantly increased in the TRH treated group (RR 1.16, 95% CI 1.03 to 1.29, three trials, 1969 infants) ( Analysis 1.7).
No effects of prenatal TRH on gestational age at birth (mean difference (MD) -0.43 weeks, 95% CI -0.86 to 0.01, two trials, 1563 infants) ( Analysis 1.17) or on need for admission to the neonatal intensive care unit (RR 1.04, 95% CI 0.98 to 1.11, two trials, 1637 infants) ( Analysis 1.8) were discernible. Similarly, no effects were seen on the risk of intraventricular haemorrhage (RR 1.08, 95% CI 0.93 to 1.26, six trials, 3645 infants) ( Analysis 1.9), severe intraventricular haemorrhage (RR 1.13, 95% CI 0.82 to 1.57, five trials, 3313 infants) ( Analysis 1.10), air leak syndrome (average RR 1.14, 95% CI 0.71 to 1.83, four trials, 3103 infants) ( Analysis 1.11), pulmonary haemorrhage (RR 0.83, 95% CI 0.25 to 2.80, three trials 1969 infants) ( Analysis 1.12), necrotising enterocolitis (RR 0.91, 95% CI 0.64 to 1.30, four trials, 3103 infants) ( Analysis 1.13), patent ductus arteriosus (average RR 1.00, 95% CI 0.79 to 1.28, six trials, 3645 infants) ( Analysis 1.14), or use of surfactant (RR 1.10, 95% CI 0.98 to 1.25, four trials, 3103 infants) ( Analysis 1.16). A low Apgar score at five minutes was significantly more common in TRH treated infants (RR 1.48, 95% CI 1.14 to 1.92, three trials, 1969 infants) ( Analysis 1.15). Moderate statistical heterogeneity was seen for the outcomes air leak syndrome (Tau² = 0.12; I² = 55%), pulmonary haemorrhage (Tau² = 0.64; I² = 56%) and patent ductus arterious (Tau² = 0.04; I² = 44%), and thus for each outcome, a random-effects model was used.
For the child
Outcomes for children at 12 months of age or later were available from three trials (ACTOBAT 1995; Chile 1998; Europe 1999). As the three trials followed up infants at different ages (i.e. 18 versus 24 months) and used different methods of assessment, it was difficult to pool these data in meta-analyses.
In the ACTOBAT 1995 trial, an increased risk in the TRH treated group was shown for motor delay (RR 1.31, 95% CI 1.09 to 1.56, 971 infants) ( Analysis 1.18), motor impairment (RR 1.51, 95% CI 1.01 to 2.24, 972 infants) ( Analysis 1.19), sensory impairment (RR 1.97, 95% CI 1.10 to 3.53, 1004 infants) ( Analysis 1.21), and social delay (RR 1.25, 95% CI 1.03 to 1.51, 966 infants) ( Analysis 1.23); but not for fine motor delay (RR 1.10, 95% CI 0.91 to 1.32, 926 infants) ( Analysis 1.20), or language delay (RR 1.20, 95% CI 0.93 to 1.54, 1004 infants) ( Analysis 1.22).
While the Europe 1999 trial did not find any difference in neurological abnormality overall between the two groups (RR 4.75, 95% CI 0.61 to 37.01, 39 infants) ( Analysis 1.24), at 24 months, the mean Bayley Mental Developmental Index (MDI) was significantly lower (worse) in the TRH exposed children (MD -15.70, 95% CI -30.86 to -0.54, 39 infants). However, in the Chile 1998 trial, at 18 months, no significant difference between groups was shown in the Bayley MDI (MD 0.00, 95% CI -8.36 to 8.36, 60 infants); and when the data from the two trials were pooled, no difference was shown overall (MD -6.52, 95% CI -21.69 to 8.64; Tau² = 84.25; I² = 68%) ( Analysis 1.25). The Bayley Psychomotor Developmental Index (PDI) was not shown to be significantly different between groups at follow-up in either the Europe 1999 trial or the Chile 1998 trial (pooled MD -2.73, 95% CI -8.58 to 3.12, 99 infants) ( Analysis 1.26). The Chile 1998 trial (assessing 60 infants) also found no significant differences on follow-up between the TRH and corticosteroids and corticosteroids only group for the mean Bayley Behavioural Rating Scale (BRS) (MD 9.00, 95% CI -4.88 to 22.88) ( Analysis 1.27), the mean Language Developmental Age (LDA) (MD 2.00, 95% CI -0.36 to 4.36) ( Analysis 1.28), or for the mean Cognitive Developmental Age (CDA) (MD 1.70, 95% CI -0.64 to 4.04) ( Analysis 1.29). No ophthalmologic or hearing abnormalities were reported at follow-up for the 60 infants assessed in Chile 1998 ( Analysis 1.31), and only one serious neurological abnormality at follow-up was reported in each group ( Analysis 1.30); an infant from the TRH and corticosteroids group was reported to have congential ventriculomegaly, and one infant in the corticosteroids only group was reported to have hypotonia of congenital origin.
For the mother
Maternal side effects were more frequent in the TRH treated women; nausea (RR 3.92, 95% CI 3.13 to 4.92, three trials, 2370 women) ( Analysis 1.32), vomiting (RR 2.35, 95% CI 1.35 to 4.09, one trial, 1011 women) ( Analysis 1.33), light headedness (RR 1.73, 95% CI 1.36 to 2.22, one trial, 1011 women) ( Analysis 1.34), urgency of micturition (RR 2.39, 95% CI 1.75 to 3.27, one trial, 1011 women) ( Analysis 1.35), and facial flushing (RR 2.67, 95% CI 2.26 to 3.16, three trials, 2523 women) ( Analysis 1.36). In the Crowther 1995 trial, side effects of nausea, urgency of micturition, or facial flushing occurred in four (of eight) women receiving 200 μg TRH and six (of nine) receiving 400 μg; it was not detailed if any of the nine control women experienced side effects. There was a significant rise in maternal systolic blood pressure (greater than 25 mmHg) (RR 1.80, 95% CI 1.05 to 3.06, one trial, 1011 women) ( Analysis 1.37) and maternal diastolic blood pressure (greater than 15 mmHg) (RR 1.62, 95% CI 1.24 to 2.12, 1011 women) ( Analysis 1.38) in women given prenatal TRH in the ACTOBAT 1995 trial.
Subgroup analysis based on dose of TRH
Subgroup analyses were performed based on the dose regimen of TRH used (considering dose subgroups 200 μg (x four every 12 hours) versus 400 μg (x four every eight to 12 hours) versus 400 μg (x six every eight hours) versus 500 μg (x four every eight hours)).
The subgroup analyses revealed no subgroup differences for the outcomes death prior to hospital discharge for the infant (Chi² = 1.19, P = 0.28, I² = 15.8%) ( Analysis 2.1); chronic lung disease (variously defined) (Chi² = 0.31, P = 0.58, I² = 0%) ( Analysis 2.2); RDS (Chi² = 3.46, P = 0.33, I² = 13.2%) ( Analysis 2.3); chronic lung disease or death (Chi² = 0.11, P = 0.74, I² = 0%) ( Analysis 2.4); the need for oxygen therapy (Chi² = 0.00, P = 0.95, I² = 0%) ( Analysis 2.5); severe RDS (Chi² = 0.01, P = 0.93, I² = 0%) ( Analysis 2.6); or the use of respiratory support (Chi² = 0.05, P = 0.83, I² = 0%) ( Analysis 2.7) indicating no differential effects for these primary and other pre-specified infant outcomes according to the dose regimen administered.
Subgroup analysis based on timing of birth
We also performed subgroup analyses based on the timing of birth, with six trials contributing data (ACTOBAT 1995; Ballard 1992b; Ballard 1998; Chile 1998; Europe 1999; Knight 1994). Babies born less than 24 hours after trial entry made up 13% of the total population, and babies born between 24 hours and 10 days from trial entry accounted for 38% of the total population; while babies born more than 10 days after trial entry accounted for the majority of the population (49%).
Considering the timing of birth, the subgroup analyses did not reveal any significant subgroup differences for the outcomes death prior to hospital discharge for the infant (Chi² = 0.45, P = 0.80, I² = 0%) ( Analysis 3.1); chronic lung disease (variously defined) (Chi² = 2.76, P = 0.25, I² = 27.6%) ( Analysis 3.2); chronic lung disease or death (Chi² = 3.70, P = 0.16, I² = 45.9%) ( Analysis 3.4); the need for oxygen therapy (Chi² = 1.37, P = 0.50, I² = 0%) ( Analysis 3.5); severe RDS (Chi² = 3.13, P = 0.21, I² = 36.1%) ( Analysis 3.6); or the use of respiratory support (Chi² = 2.40, P = 0.30, I² = 16.6%) ( Analysis 3.7) indicating no differential effects for these infant outcomes according to timing of birth after trial entry.
Considering the outcome RDS, the subgroup interaction test indicated a significant difference (Chi² = 6.39, P = 0.04, I² = 68.7%) ( Analysis 3.3), suggesting a possible differential treatment effect based on timing of delivery in favour of corticosteroids alone (as compared with TRH and corticosteroids) for babies born more than 10 days after trial entry (RR 1.33, 95% CI 1.05 to 1.68). This difference was not seen in either of the other two timing of birth subgroups, or in the main analysis.
Analysis restricted to mothers and babies receiving 'optimal treatment'
A secondary analysis was performed in order to allow the additional inclusion of data from three trials (Campos 1993; Ceriani 1992; Morales 1989) in which results were reported only for a subgroup of participants regarded as optimally treated by the respective trialists. Overall, 10 trials contributed data (ACTOBAT 1995; Ballard 1992b; Ballard 1998; Campos 1993; Ceriani 1992; Chile 1998; Europe 1999; Jikihara 1990; Knight 1994; Morales 1989) to the 'optimal treatment' subgroup. Optimal treatment was described variously by different authors. Morales 1989 presented outcome data for infants delivered within one week of the start of therapy, which represented only 40% of the total number of babies in the study. Ceriani 1992 reported data for infants fully treated (received all doses of TRH or corticosteroids, or both) and born within 10 days of entry. Campos 1993 reported the data on fully treated infants (received all doses of TRH or corticosteroids, or both) who were born within 48 hours of the last hormonal dose. The included data from ACTOBAT 1995; Ballard 1992b; Ballard 1998; Chile 1998; Europe 1999; Jikihara 1990 and Knight 1994 relate to infants born between 24 hours to 10 days after entry into the trial.
No beneficial effects of prenatal TRH were seen between groups for death prior to hospital discharge (RR 0.88, 95% CI 0.67 to 1.14, nine trials, 1465 infants) ( Analysis 4.1), chronic lung disease (RR 0.87, 95% CI 0.72 to 1.04, eight trials, 1318 infants) ( Analysis 4.2), RDS (average RR 0.89, 95% CI 0.77 to 1.03, 10 trials, 1786 infants; Tau² = 0.02; I² = 40%) ( Analysis 4.3), chronic lung disease or death (RR 0.96, 95% CI 0.84 to 1.09; five trials, 1317 infants) ( Analysis 4.4), the need for oxygen therapy (RR 0.99, 95% CI 0.91 to 1.09; one trial, 506 infants) ( Analysis 4.5), or for the use of respiratory support (RR 1.07, 95% CI 0.94 to 1.22; one trial, 506 infants) ( Analysis 4.7) for the optimally treated subgroup of infants. A statistically significant reduction in severe RDS was however observed for the infants exposed to TRH as compared corticosteroids alone when considering only optimally treated infants (RR 0.65, 95% CI 0.49 to 0.86; two trials, 694 infants) ( Analysis 4.6).
When we performed subgroup interaction tests comparing all treated infants versus only those considered 'optimally treated', no significant subgroup differences were observed between the two groups for the outcomes: death (Chi² = 1.12, P = 0.29, I² = 11.0%) ( Analysis 4.1), chronic lung disease (Chi² = 1.40, P = 0.24, I² = 28.6%) ( Analysis 4.2), RDS (Chi² = 2.47, P = 0.12, I² = 59.5%) ( Analysis 4.3), chronic lung disease or death (Chi² = 1.45, P = 0.23, I² = 31.0%) ( Analysis 4.4), the need for oxygen therapy (Chi² = 0.79, P = 0.37, I² = 0%) ( Analysis 4.5), severe RDS (Chi² = 2.26, P = 0.13, I² = 55.7%) ( Analysis 4.6), or for the use of respiratory support (Chi² = 0.74, P = 0.39, I² = 0%) ( Analysis 4.7) indicating no clear differential effects based on optimal treatment for these primary and pre-specified infant outcomes.
Sensitivity analysis by quality rating
Five trials (ACTOBAT 1995; Ballard 1998; Chile 1998; Europe 1999; Knight 1994), considered at a low risk of bias in the domains of sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting, were included in a sensitivity analysis.
No beneficial effects of prenatal TRH were seen for any of the primary infant outcomes of death (RR 1.03, 95% CI 0.84 to 1.25, five trials, 3570 infants) ( Analysis 5.1), chronic lung disease (RR 1.00, 95% CI 0.84 to 1.18, four trials, 2387 infants) ( Analysis 5.2), and RDS (RR 1.06, 95% CI 0.91 to 1.24, five trials, 3521 infants) ( Analysis 5.3), nor for any of the other pre-specified infant outcomes, including chronic lung disease or death (RR 1.05, 95% CI 0.94 to 1.17, five trials, 3570 infants) ( Analysis 5.4), the need for oxygen therapy (RR 1.05, 95% CI 0.97 to 1.13, four trials, 2387 infants) ( Analysis 5.5), and severe RDS (average RR 0.88, 95% CI 0.57 to 1.36, three trials, 2119 infants; Tau² = 0.11; I² = 73%) ( Analysis 5.6), as in the main analysis.
The significant increase in the use of respiratory support for infants exposed to TRH as compared with corticosteroids alone persisted in the sensitivity analysis (with data from the same three trials included: ACTOBAT 1995; Chile 1998; Europe 1999) (RR 1.16, 95% CI 1.03 to 1.29, three trials, 1969 infants) ( Analysis 5.7).
This review does not show that prenatal administration of thyrotropin-releasing hormone (TRH), in addition to corticosteroids, prior to preterm birth reduces the risk of respiratory disease in infants born preterm, or reduces other infant morbidity or mortality. Indeed the data show that this treatment may have adverse effects for women and their infants. All maternal side effects reported in the included trials (nausea, vomiting, light headedness, urgency of micturition, facial flushing) were more likely to occur in women receiving TRH, although their clinical significance and women's perceptions of their importance have not been assessed. For the infants, prenatal TRH increased the risk of infants needing respiratory support, and of having a low Apgar score at five minutes.
In one of the three trials with follow-up data, prenatal TRH was associated with adverse neurodevelopmental outcomes in childhood (such as motor and social delay, and motor and sensory impairment) (ACTOBAT 1995). However, the other two trials that assessed neurodevelopmental outcomes at follow-up using an established developmental instrument (Bayley Infant Scales) (Chile 1998; Europe 1999), did not show any significant differences between groups on follow-up, apart from a significantly lower (worse) Mental Developmental Index for infants exposed to prenatal TRH at 24-month follow-up in one trial (Europe 1999), which was not confirmed in the second trial (Chile 1998).
The first two full trial reports published showed promising therapeutic effects of prenatal TRH, but reported neonatal outcome data only in minority subgroups of babies entered into the trials (Ballard 1992b; Morales 1989). However, a significant proportion of babies in all of the studies (49%) were born more than 10 days after trial entry. The data in this review show that these babies (born more than 10 days after trial entry), if exposed to prenatal TRH in addition to corticosteroids, were more likely to develop respiratory distress syndrome (RDS) compared with babies in the control group, who received only corticosteroids. This highlights the importance of 'intention-to-treat' analyses, and subgroup analyses in this review, since many of the studies excluded categories of babies. Even where data were available for all women who were randomised, results from subgroup analyses (e.g. by timing of treatment) are less reliable than overall analyses. However, it is important to show the data by subgroups since timing of treatment appears to be an important consideration.
The expectation was that the greatest beneficial effect of prenatal TRH would be seen in infants born between 24 hours and 10 days of trial entry as shown with antenatal corticosteroids alone (Liggins 1972). Infants exposed to TRH in this timed subgroup, and a similar 'optimal' timing subgroup, did show a reduced risk of severe RDS; however, subgroup interaction tests were not significant, and therefore no firm conclusion could be made regarding this particular group of infants. Intention-to-treat data for severe RDS were only available from three earlier trials for this timed subgroup (birth more than 24 hours and less than 10 days after first dose) (ACTOBAT 1995; Ballard 1992b; Knight 1994) and thus it would be important to include any further data on severe RDS from the more recent trials if they became available.
Implications for practice
Based on the current available evidence, TRH should not be given to pregnant women at risk of preterm birth in an attempt to prevent neonatal respiratory disease.
This review found that prenatal TRH in addition to corticosteroids given to women at risk of preterm birth does not reduce the risk or severity of neonatal lung disease, may increase the chances of the infant needing respiratory support, and is associated with adverse side effects for the mother.
Implications for research
In the light of the evidence reviewed, no further randomised controlled trials are warranted.
Given the trend to adverse neonatal findings in babies who were born 10 days or more after trial entry, trials should aim to provide outcome and follow-up data on all babies recruited. Those trials that reported data on only minority subgroups of babies should consider retrieving outcome data on the other babies, in particular on mortality and longer-term morbidity.
Adverse maternal side effects of therapy were significant for women receiving prenatal TRH. The duration of the adverse effects, their clinical significance and the consumers' feelings about these have not been assessed.
Five of the trials included in this review have only been reported in abstract form (Abuhamad 1999; Carlan 1991; Ceriani 1992; Jikihara 1990; Kim 2000). One trial using 400 μg TRH treatment dosage was planned in the USA in 1997 and stopped without enrolling (Yoder 1997). Another trial of TRH administration after prelabour rupture of membranes preterm was reported as planned in 1997 (Pearlman 1997).
Professor Adrian Grant compiled the first version of this review published in 1989. We are very grateful to the people who responded to our requests for further information including Professor Yoder and Professor Abuhamad and to the investigators of all the trials who provided additional unpublished information, particularly Professor RA Ballard, Professor M Bracken, Professor JE Hiller, Dr H Jikihara, Dr DB Knight and Professor FR Moya.
We thank Emily Bain and Philippa Middleton from the Australian Research Centre for Health of Women and Babies at The University of Adelaide for assisting with this update of the review.
As part of the pre-publication editorial process, this review has been commented on by three peers (an editor and two referees who are external to the editorial team) and the Group's Statistical Adviser.
The National Institute for Health Research (NIHR) is the largest single funder of the Cochrane Pregnancy and Childbirth Group. The views and opinions expressed therein are those of the authors and do not necessarily reflect those of the NIHR, NHS or the Department of Health.
Data and analyses
- Top of page
- Authors' conclusions
- Data and analyses
- What's new
- Contributions of authors
- Declarations of interest
- Sources of support
- Differences between protocol and review
- Index terms
Appendix 1. Search strategy for additional author searching
For the previous version of the review (Crowther 2004), we searched the Cochrane Central Register of Controlled Trials (The Cochrane Library, 2009, Issue 2), MEDLINE (1965 to 13 July 2009) and EMBASE (1988 to 13 July 2009) using the terms 'thyrotropin-releasing hormone' or 'TRH'.
Last assessed as up-to-date: 17 July 2013.
Protocol first published: Issue 2, 1995
Review first published: Issue 2, 1995
Contributions of authors
For this update, CA Crowther assessed identified studies for eligibility and prepared the new format text of the review, with assistance from SS Han. All review authors contributed to the final version of this updated review.
Declarations of interest
CA Crowther and RR Haslam were two of the chief investigators for the Australian Collaborative Trial of thyrotropin-releasing hormone (ACTOBAT 1995) and the Crowther 1995 trial; and Z Alfirevic was one of the principal investigators for the European TRH trial (Europe 1999). Therefore, all tasks relating to these studies (assessment of eligibility for inclusion, assessment of risk of bias, and data extraction) were carried out by other members of the review team who were not directly involved in the trials.
Sources of support
- ARCH, Robinson Institute, Discipline of Obstetrics and Gynaecology, The University of Adelaide, Australia.
- Division of Perinatal and Reproductive Medicine, The University of Liverpool, UK.
- Department of Perinatal Medicine, Women's and Children's Hospital, Adelaide, Australia.
- National Health and Medical Research Council, Australia.
- Department of Health and Ageing, Australia.
Differences between protocol and review
In this update, we have reduced the number of primary infants outcomes to three (death prior to hospital discharge, chronic lung disease (variously defined by authors), and respiratory distress syndrome), and the other outcomes have been moved to 'secondary outcomes'.
We have clarified that in relation to follow-up outcomes, the definitions are 'variously defined by authors'. We have changed the wording for the outcome 'need for oxygen therapy at 28 days' to 'chronic lung disease (variously defined by authors)' to be more inclusive.
We have updated the review methods.
Medical Subject Headings (MeSH)
*Obstetric Labor, Premature; Drug Therapy, Combination [methods]; Glucocorticoids [*therapeutic use]; Infant, Newborn; Infant, Premature; Randomized Controlled Trials as Topic; Respiratory Distress Syndrome, Newborn [*prevention & control]; Thyrotropin-Releasing Hormone [adverse effects; *therapeutic use]
MeSH check words
Female; Humans; Pregnancy
* Indicates the major publication for the study