Relaxin for preventing preterm birth in threatened preterm labour
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the effects of relaxin for women in threatened preterm labour on preterm birth and associated maternal and neonatal/infant health outcomes.
Background
Description of the condition
Approximately 5% to 9% of births today in high‐income countries occur preterm (before 37 completed weeks), and the rate of preterm birth is increasing in a number of these countries (Goldenberg 2008). Preterm birth is a leading cause of perinatal morbidity, mortality and infant mortality (Goldenberg 2008; Heron 2010). Therefore, much research has focused on identifying and assessing interventions that may reduce the occurrence of preterm birth. Tocolytic agents are those that are intended to prevent uterine contractions during an episode of threatened preterm labour (acute tocolytic agents) or maintain quiescence of the uterus following an acute episode (maintenance tocolytic agents) (Conde‐Agudelo 2011). The efficacy of particular tocolytic agents is difficult to quantify, although there is evidence that some of these agents can help to delay birth (Conde‐Agudelo 2011). In particular, nifedipine (a calcium channel blocker) is increasingly being recommended as a first line tocolytic agent, due to its efficacy and favourable side‐effect profile compared with a number of alternative tocolytics that have been assessed to date, including betamimetics and magnesium sulphate (Conde‐Agudelo 2011; Crowther 2002; King 2003). This review will however, examine the evidence for use of the hormone relaxin as a tocolytic agent for preventing preterm birth for women in threatened preterm labour.
Description of the intervention
The intervention to be assessed is relaxin, administered during threatened preterm birth, compared with other tocolytic agents, placebo and/or no treatment. Relaxin is a two‐chain peptide hormone that was first identified in 1926 (Gunnersen 1996; Hisaw 1926). Relaxin is encoded by two non allelic genes (H1 and H2) in humans and great apes and a single gene in all other species studied (Gunnersen 1996). Relaxin is produced in the corpus luteum, decidua, placental trophoblast and prostate gland (Gunnersen 1996; Hansell 1991). During pregnancy in humans, relaxin concentrations are highest in the first trimester, reaching a peak during the eighth to twelfth weeks (Weiss 2005). Concentrations then decrease and are maintained at constant or slightly decline throughout the rest of the pregnancy (Weiss 2005).
Relaxin was one of the first potential tocolytic agents to be studied, with reports of its use dating back to the 1950s. It is believed to have since fallen out of favour as a tocolytic, due its perceived lack of efficacy (Keirse 2003). No formal systematic review has however, evaluated its effectiveness for delaying birth for women in threatened preterm labour.
In recent years, relaxin has been found to be a pleiotropic hormone with multiple other non‐reproductive functions in various tissues, and it is commercially available for use in research (Bani 2008; Dschietzig 2006; Ferlin 2010). Adverse effects of relaxin are reportedly rare, regardless of dose and delivery route. The most common potential adverse effects are injection site pain or erythema; however, anaphylactic reactions have been reported with repeated systemic administration of crude porcine (pig) relaxin, and relaxin may increase uterine bleeding tendency (Bani 2009).
How the intervention might work
In the 1950s, it was hypothesised that if relaxin has an inhibitory effect on myometrial tissue, it may be useful for delaying parturition. Prior to 1974, when relaxin was isolated in a highly purified form (Sherwood 1974), studies were conducted examining the tocolytic properties of relaxin using relatively impure preparations (MacLennan 1981). Studies on myometrial contractility, using relaxin‐containing extracts from pig ovaries, demonstrated inhibition of uterine contractility in rats (Miller 1957; Sawyer 1953), but not in rabbits or humans (Miller 1957). Whilst several clinical case series suggested that relaxin may have an inhibitory effect on preterm labour in women (Abramson 1955; Eichner 1956; Folsome 1956; Majewski 1955), a quasi‐randomised trial at this time (Kelly 1959) found that a similar number of cessations of preterm labour occurred for women receiving a placebo, as for women receiving relaxin. Kelly 1959 also investigated the effects of relaxin on the non‐pregnant myometrium in vivo, and on the pregnant uterus in vivo and found negligible effects on contractility (Kelly 1959).
After purified porcine relaxin became available, Porter 1979 showed it to have an inhibitory effect on spontaneous intrauterine pressure cycles in anaesthetised rats. MacLennan 1986 similarly demonstrated that porcine relaxin had a refractory effect on myometrial activity in vitro in rat and porcine myometrium, but not in human myometrium. Thus, while relaxin was found to have an inhibitory effect on in vitro myometrial contractility in rats (MacLennan 1986; Miller 1957; Sawyer 1953) and pigs (MacLennan 1986), this was not replicated in human myometrial tissue with either crude (Miller 1957) or purified relaxin (MacLennan 1986).
Recent research has further indicated that relaxin may be ineffective as a tocolytic agent in humans. Human recombinant relaxin (hRLX‐1 and hRLX‐2) became available for use in research in the early 1990s, and its tocolytic effect has been tested in vitro (Bullesbach 1991; MacLennan 1994). As in earlier in vitro studies, studies testing synthetic human relaxin showed species‐dependent effects, with an inhibitory effect on contractility found in rats (Petersen 1991), and pigs (MacLennan 1981; MacLennan 1995) but not humans (MacLennan 1981; MacLennan 1995; Petersen 1991). Such studies have indicated that species specificity does not lie with the origin of the relaxin (e.g. porcine, human) but rather with the origin of the target tissues (MacLennan 1991).
In pregnancies following in vitro fertilisation‐embryo transfer (IVF‐ET) or gamete intrafallopian transfer (GIFT), concentrations of serum relaxin are substantially higher than in normal pregnancies (McGovern 2004). The higher concentration of relaxin following IVF‐ET/GIFT is the product of multiple corpora lutea, resulting from the stimulation of multiple ovarian follicles with injectable gonadotropins (McGovern 2004; Sachdev 1993). High concentrations of relaxin have been shown to persist throughout pregnancy (Mushayandebvu 1998) and be associated with premature cervical change and preterm birth (McGovern 2004). A prospective study that compared the risk of preterm birth in women achieving pregnancy with and without ovarian stimulation, found a significant positive association between elevated circulating maternal relaxin and risk of preterm birth (Weiss 1993). Thus, it is possible that administration of relaxin may in fact increase rather than decrease the risk of preterm birth.
Why it is important to do this review
Early animal and clinical studies have provided some, limited support that relaxin may have an inhibitory effect on preterm birth for women in threatened preterm labour. Further recent evidence has been conflicting, suggesting that relaxin may be ineffective for this indication, and may in fact increase the risk of preterm birth. It is therefore important to systematically assess the evidence surrounding the benefits and harms of the use of relaxin for women in threatened preterm labour.
Objectives
To assess the effects of relaxin for women in threatened preterm labour on preterm birth and associated maternal and neonatal/infant health outcomes.
Methods
Criteria for considering studies for this review
Types of studies
Randomised and quasi‐randomised controlled trials will be included. Cross‐over studies and cluster‐randomised trials will be excluded. Studies that are available as abstracts only will be included when other inclusion criteria are met and relevant outcome data are reported.
Types of participants
Pregnant women of any age assessed as being in threatened preterm labour (gestational age less than 37 weeks) and considered suitable candidates for tocolysis, regardless of the reason for threatened preterm birth, the number of babies in utero, and parity.
Types of interventions
Administration of relaxin via any route (oral, intravenous, intramuscular, or other) (with dose as specified by authors) compared with an alternative tocolytic agent, a placebo or with no treatment. Only data from studies where relaxin was administered independent of another (alternative) tocolytic agent will be included in analyses.
Types of outcome measures
Primary outcomes
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Birth within 48 hours of treatment
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Birth within seven days of treatment
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Perinatal mortality (fetal death and neonatal death up to 28 days)
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Serious neonatal adverse outcome composite (as defined by study authors, such as the Neonatal Adverse Outcome Indicator (NAOI) described in Lain 2012)
Secondary outcomes
Maternal outcomes
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Pregnancy prolongation
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Antepartum haemorrhage
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Postpartum haemorrhage
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Maternal sepsis
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Mode of birth (caesarean section, operative vaginal, normal vaginal)
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Mild/moderate adverse effects of treatment (for example: injection site pain or erythema)
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Severe maternal adverse effects (for example: maternal death, cardiac arrest, respiratory arrest, anaphylactic reaction, admission to intensive care unit)
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Maternal length of hospital stay
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Maternal satisfaction with treatment
Fetal and neonatal outcomes
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Fetal death
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Neonatal death (during first 28 days of life)
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Preterm birth (at less than 37 weeks; 34 weeks; 32 weeks and 28 weeks)
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Gestational age at birth
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Birthweight
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Small‐for‐gestational age (defined as birthweight less than 10th centile for gestational age)
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Apgar score of less than seven at five minutes
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Neonatal jaundice
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Respiratory distress syndrome
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Bronchopulmonary dysplasia
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Use of mechanical ventilation
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Duration of mechanical ventilation
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Intraventricular haemorrhage – any grade
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Intraventricular haemorrhage (grade three or four)
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Periventricular leukomalacia
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Retinopathy of prematurity
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Chronic lung disease
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Necrotising enterocolitis
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Neonatal sepsis
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Admission to neonatal intensive care unit
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Length of admission to neonatal intensive care unit
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Length of first hospital admission from birth (including neonatal intensive care unit)
Infant/child
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Developmental delay as defined by study authors
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Intellectual impairment as defined by study authors
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Motor impairment as defined by study authors
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Visual impairment as defined by study authors
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Hearing impairment as defined by study authors
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Cerebral palsy
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Abnormal behaviour as defined by study authors
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Abnormal temperament as defined by study authors
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Learning difficulties as defined by study authors
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Growth assessments at childhood follow‐ up (weight, head circumference, length)
Search methods for identification of studies
Electronic searches
We will contact the Trials Search Co‐ordinator to search the Cochrane Pregnancy and Childbirth Group’s Trials Register.
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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quarterly 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 and MEDLINE, 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.
We will not apply any language restrictions.
Data collection and analysis
Selection of studies
Two review authors will independently assess for inclusion all the potential studies we identify as a result of the search strategy. We will resolve any disagreement through discussion or, if required, we will contact a third author.
Data extraction and management
We will design a form to extract data. For eligible studies, two review authors will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult the third review author. We will enter data into Review Manager software (RevMan 2011) and check for accuracy.
When information regarding any of the above is unclear, we will attempt to contact authors of the original reports to provide further details.
Assessment of risk of bias in included studies
Two review authors will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreement by discussion, or if required we will contact the third review author.
(1) Sequence generation (checking for possible selection bias)
We will describe 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 will assess the method as:
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low risk (any truly random process, e.g. random number table; computer random number generator);
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high risk (any non‐random process, e.g. odd or even date of birth; hospital or clinic record number);
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unclear risk.
(2) Allocation concealment (checking for possible selection bias)
We will describe for each included study the method used to conceal the allocation sequence and determine whether the intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.
We will assess the methods as:
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low risk (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
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high risk (open random allocation; unsealed or non‐opaque envelopes, alternation; date of birth);
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unclear risk.
(3.1) Blinding of participants and personnel (checking for possible performance bias)
We will describe for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We will consider that studies are at low risk of bias if they were blinded, or if we judge that the lack of blinding would be unlikely to affect results. We will assess blinding separately for different outcomes or classes of outcomes.
We will assess 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 will describe for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We will assess blinding separately for different outcomes or classes of outcomes.
We will assess 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 through withdrawals, dropouts, protocol deviations)
We will describe for each included study, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We will state 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 is reported, or can be supplied by the trial authors, we will re‐include missing data in the analyses which we undertake. We will assess methods as:
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low risk;
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high risk;
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unclear risk.
(5) Selective reporting bias
We will describe for each included study how we investigated the possibility of selective outcome reporting bias and what we found.
We will assess the methods as:
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low risk (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 (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.
(6) Other sources of bias
We will describe for each included study any important concerns we have about other possible sources of bias.
We will assess whether each study was free of other problems that could put it at risk of bias:
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low risk;
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high risk;
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unclear risk.
(7) Overall risk of bias
We will make explicit judgements about whether studies are at high risk of bias, according to the criteria given in the Handbook (Higgins 2011). With reference to (1) to (6) above, we will assess the likely magnitude and direction of the bias and whether we consider it is likely to impact on the findings. We will explore the impact of the level of bias through undertaking sensitivity analyses ‐ seeSensitivity analysis.
Measures of treatment effect
Dichotomous data
For dichotomous data, we will present results as summary risk ratio with 95% confidence intervals.
Continuous data
For continuous data, we will use the mean difference if outcomes are measured in the same way between trials. We will use the standardised mean difference to combine trials that measure the same outcome, but use different methods.
Unit of analysis issues
We consider cluster‐randomised trials inappropriate for inclusion in this review.
Where multi‐armed studies meet the inclusion criteria, groups will be combined in order to create a single pair‐wise comparison (e.g. relaxin versus alternative tocolytics).
Dealing with missing data
For included studies, we will note levels of attrition. We will explore the impact of including studies with high levels of missing data in the overall assessment of treatment effect by using sensitivity analysis.
For all outcomes, we will carry out analyses, as far as possible, on an intention‐to‐treat basis, i.e. we will attempt to include all participants randomised to each group in the analyses, and all participants will be 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 will be the number randomised minus any participants whose outcomes are known to be missing.
Assessment of heterogeneity
We will assess statistical heterogeneity in each meta‐analysis using the T², I² and Chi² statistics. We will regard heterogeneity as substantial if the I² is greater than 30% and either the T² is greater than zero, or there is a low P value (less than 0.10) in the Chi² test for heterogeneity.
Assessment of reporting biases
If there are 10 or more studies in the meta‐analysis, we will investigate reporting biases (such as publication bias) using funnel plots. We will assess funnel plot asymmetry visually, and use formal tests for funnel plot asymmetry. For continuous outcomes we will use the test proposed by Egger 1997, and for dichotomous outcomes we will use the test proposed by Harbord 2006. If asymmetry is detected in any of these tests or is suggested by a visual assessment, we will perform exploratory analyses to investigate it.
Data synthesis
We will carry out statistical analysis using the Review Manager software (RevMan 2011). We will use fixed‐effect meta‐analysis for combining data where it is reasonable to assume that studies are estimating the same underlying treatment effect: i.e. where trials are examining the same intervention, and the trials’ populations and methods are judged sufficiently similar. If there is clinical heterogeneity sufficient to expect that the underlying treatment effects differ between trials, or if substantial statistical heterogeneity is detected, we will use random‐effects meta‐analysis to produce an overall summary if an average treatment effect across trials is considered clinically meaningful. The random‐effects summary will be treated as the average range of possible treatment effects and we will discuss the clinical implications of treatment effects differing between trials. If the average treatment effect is not clinically meaningful, we will not combine trials.
If we use random‐effects analyses, the results will be presented as the average treatment effect with its 95% confidence interval, and the estimates of T² and I².
Subgroup analysis and investigation of heterogeneity
We will perform separate comparisons for relaxin versus placebo or no treatment, and relaxin versus alternative tocolytic agents.
If we identify substantial heterogeneity, we will investigate it using sensitivity analyses. We will consider whether an overall summary is meaningful, and if it is, use random‐effects analysis to produce it.
We plan to carry out the following subgroup analysis.
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Gestational age at treatment (less than 28 weeks of gestation versus 28 weeks and above).
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Reason for threatened preterm labour (such as preterm premature rupture of membranes, antepartum haemorrhage and cervical incompetence).
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Single verus multiple gestation.
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Dose of relaxin used.
Primary outcomes will be used for the subgroup analyses.
We will assess differences between subgroups using interaction tests available within RevMan 5.1 (RevMan 2011).
Sensitivity analysis
We plan to carry out sensitivity analysis on primary outcomes to explore the effect of trial quality where there is an overall high risk of bias associated with included trials or where quasi‐randomised are included in the review. We will carry out sensitivity analyses to explore the effect of trial quality on primary outcomes. We plan to exclude studies of poor quality in the analysis (those rating as high risk in overall) in order to assess for any substantive difference in the result.
