Prenatal administration of progestogens for preventing spontaneous preterm birth in women with a singleton pregnancy

Abstract

This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:

To assess the benefits and harms of progesterone administration for the prevention of preterm birth in women with a singleton pregnancy who are considered to be at increased risk of preterm birth.

Background

Description of the condition

A birth is considered preterm when a woman gives birth before 37 completed weeks of pregnancy. Preterm birth is the leading cause of morbidity, affecting approximately 15 million children every year (Blencowe 2012). Furthermore, approximately one million children die each year as a result of prematurity or its complications. While the global rate of preterm birth is around 11%, the rate varies considerably, being as high as 18% in sub‐Saharan Africa, and as low as 5% in many northern European countries (Blencowe 2012).

Infants who are born preterm are recognised to be at increased risk of adverse health outcomes (AIHW 2014), and are more likely to die within the first year of life and beyond (Martin 2003), reflecting an increased susceptibility to infection and other illnesses (Blencowe 2013; Howson 2013). Recognised longer‐term health complications related to prematurity include recurrent hospital admissions (Elder 1999), blindness, hearing impairment, respiratory disease, cerebral palsy, and ongoing disability (Blencowe 2013; Hack 1999; Stanley 1992). The effects of preterm birth, both in the neonatal period and extending into childhood, represent a significant financial and social burden for individuals, families, and the community at large (Kramer 2000).

Preterm birth can be categorized according to the gestational age at birth, with birth before 28 weeks' gestation considered extremely preterm; between 28 and 32 weeks' gestation very preterm; between 32 and 34 weeks' gestation moderately preterm; and between 34 and 37 weeks' gestation late preterm (WHO 2015).

Preterm birth may also be categorised into spontaneous and iatrogenic, broadly reflecting the causation or events leading to the preterm birth. Recognising that spontaneous preterm birth is multifactorial in causation, this does allow the differentiation of spontaneous birth following the onset of labour or prelabour premature rupture of membranes (PPROM), and birth following a medical decision to initiate early birth due to concerns about either the health of the woman or her unborn baby (iatrogenic; Goldenberg 2012). The contribution of spontaneous preterm birth to overall preterm birth rates varies significantly between populations and settings, and changes over time, but in general, spontaneous preterm birth accounts for 50% to 75% of all preterm births (Moutquin 2003).

While spontaneous preterm birth reflects a combination of factors that culminate in the initiation of labour, the underlying process reflects complex interactions between a variety of genetic, environmental, and social characteristics (Menon 2008; Plunkett 2008). In particular, women who have had a previous spontaneous preterm birth are recognised to be at increased risk of spontaneous preterm birth in a subsequent pregnancy (Adams 2000; Bakketieg 1979; Berkowitz 1993; Bloom 2001; Goldenberg 1998). Furthermore, there are many complications that may develop over the course of pregnancy and place a woman at increased risk of early birth. These factors may include identification of a shortened cervix by ultrasound assessment (Iams 1996; Smith 2007), the presence of fetal fibronectin in vaginal secretions (Leitich 1999; Smith 2007), or presentation with signs or symptoms of preterm labour (Garbaciak 1992). For example, women identified by ultrasound examination as having a cervical length less than 2.5 cm are more likely to give birth before 34 weeks' gestation (Smith 2007).

Description of the intervention

Progestogens are a group of hormones that interact with the progesterone receptor, and may be either naturally occurring or synthetically manufactured (Schindler 2008). Natural progesterone and its metabolite 17‐hydroxyprogesterone are produced in high concentrations by the body during pregnancy. In contrast, 17‐hydroxyprogesterone caproate and its metabolites are synthetic progestins, which are lipophilic, protein bound, and metabolized by the liver (Feghali 2014).

Progestogens have many different formulations, can be administered by different routes (for example, oral, vaginal, intramuscular), and therefore, have different bio‐effects (Feghali 2014). For example, vaginally administered progesterone has a half‐life of approximately 18 hours, while orally administered progesterone undergoes a significant first pass effect on the liver, substantially reducing its half‐life (Feghali 2014). In contrast, 17‐hydroxyprogesterone caproate is administered by intramuscular injection, and while the half‐life is approximately 16 days, it can be detected several weeks after administration (Caritis 2012).

Concerns have been raised about the use of progesterone and risk of fetal anomalies. Case control studies evaluating both natural progesterone and 17‐hydroxyprogesterone caproate in pregnancy have not identified an increased risk of congenital anomalies (Michaelis 1983; Raman‐Wilms 1995; Resseguie 1985; Shardein 1980; Varma 1982).

For the woman, the use of progesterone therapy has been associated with the occurrence of headache, breast tenderness, nausea, cough, and if administered intramuscularly, localised irritation (Greene 2003;Iams 2003).

How the intervention might work

Whilst the biological mechanisms behind preterm birth remain largely unknown, various agents have been suggested to be effective in preventing preterm birth and prolonging gestation. The mechanisms by which these agents (including progesterone) act to prevent preterm birth and prolong gestation is unclear. Progesterone is thought to act by suppressing smooth muscle activity in the uterus to maintain uterine quiescence (Astle 2003;Grazzini 1998). It has been suggested that changes in the expression of progesterone receptors within the uterus may simulate a functional withdrawal, and precipitate the onset of labour (Astle 2003;Condon 2003;Haluska 2002;Peiber 2001).

Why it is important to do this review

Preterm birth and its consequences are a significant health issue for women and their babies. While suppressing or preventing preterm labour and preterm birth may be associated with prolonged gestation and therefore, improved outcomes for babies, it is possible that ongoing development and exposure to an unfavourable in‐utero environment may be harmful, and associated with an increased risk of morbidity. The purpose of this review is to assess the benefits and harms of progesterone, administered to prevent preterm birth in women with a singleton pregnancy, for both women and their infants, when considering the risk factors present for preterm birth.

An existing Cochrane review examined the prenatal administration of progesterone for preventing preterm birth in women considered to be at risk of preterm birth (Dodd 2013). The review has now been split into two reviews, with this review focusing on women with a singleton pregnancy at risk of preterm birth, and a second review focusing on women with a multiple pregnancy (Dodd 2016).

Objectives

To assess the benefits and harms of progesterone administration for the prevention of preterm birth in women with a singleton pregnancy who are considered to be at increased risk of preterm birth.

Methods

Criteria for considering studies for this review

Types of studies

All published and unpublished randomised controlled trials, in which progesterone is administered for the prevention of preterm birth in women with singleton pregnancies at increased risk of preterm birth. We will include studies published as abstracts or brief reports, provided there is sufficient information to assess risk of bias.

Trials will be excluded if:

• they used quasi‐randomised methodology or cross‐over design;

• progesterone was administered for the acute treatment of actual or threatened preterm labour (that is, where progesterone was administered as an acute tocolytic medication); or

• progesterone was administered in the first trimester to prevent miscarriage.

Types of participants

Pregnant women considered to be at increased risk of preterm birth with a singleton pregnancy. Risk factors include:

• past history of spontaneous preterm birth (including preterm prelabour rupture of membranes);

• ultrasound identified short cervix length;

• fetal fibronectin testing;

• past history of acute presentation with signs or symptoms of threatened preterm labour (where a tocolytic agent may have been administered);

• other reasons considered to increase the risk of preterm birth.

We will include studies that recruit women with multiple pregnancies, provided that findings for women with singleton pregnancies at increased risk of preterm birth are reported separately, or can be obtained from trial authors.

Types of interventions

Administration of progesterone by any route for the prevention of preterm birth compared with placebo or no treatment. We will examine the effects of progesterone in different increased risk groups in separate comparisons; different routes of administration of progesterone (vaginal and intramuscular (IM)) will also be examined separately.

Main comparisons:

1. IM progesterone versus placebo or no treatment for women with previous history of preterm birth

2. Vaginal progesterone versus placebo or no treatment for women with a previous history of preterm birth

3. IM progesterone versus placebo or no treatment for women with short cervix

4. Vaginal progesterone versus placebo or no treatment for women with short cervix

5. IM progesterone versus placebo or no treatment for women with arrested threatened preterm labour

6. Vaginal progesterone versus placebo or no treatment for women with arrested threatened preterm labour

7. IM progesterone versus placebo or no treatment for women with other risk factors*

8. Vaginal progesterone vs placebo or no treatment for women with other risk factors*

* other risk factors = may include in‐vitro fertilisation (IVF), prelabour premature rupture of membranes (PPROM), active military service, advanced maternal age and indications not specified in previous comparisons

If trials report multiple modes of administration (e.g. oral or intravenous (IV)) they will be reported in separate comparisons, by risk factor, as above.

Types of outcome measures

We have selected the following outcomes from the recent core outcome set for preterm birth prevention (Van't Hooft 2016).

Primary outcomes

Maternal

1. Maternal mortality

Infant

1. Perinatal mortality

2. Preterm birth (less than 34 weeks' gestation)

3. Major neurodevelopmental disability at childhood follow‐up

Secondary outcomes

Maternal

1. Threatened preterm labour (as defined by trial authors)

2. Prelabour spontaneous rupture of membranes

3. Adverse drug reaction

4. Pregnancy prolongation (interval between randomisation and birth)

5. Mode of birth

6. Number of antenatal hospital admissions

7. Satisfaction with the therapy

8. Use of tocolysis

9. Antenatal corticosteroids

10. Maternal quality of life

Infant

1. Birth before 37 completed weeks

2. Birth before 28 completed weeks

3. Mean gestational age at birth

4. Birthweight less than the third centile for gestational age

5. Birthweight less than 2500 g

6. Mean birthweight

7. Apgar score of less than seven at five minutes

8. Respiratory distress syndrome

9. Use of mechanical ventilation

10. Duration of mechanical ventilation

11. Intraventricular haemorrhage ‐ grades III or IV

12. Periventricular leucomalacia

13. Retinopathy of prematurity

14. Retinopathy of prematurity ‐ grades III or IV

15. Chronic lung disease

16. Necrotising enterocolitis

17. Neonatal sepsis

18. Fetal death

19. Neonatal death

20. Admission to neonatal intensive care unit

21. Neonatal length of hospital stay

22. Teratogenic effects (including virilisation in female infants)

23. Patent ductus arteriosis (not a prespecified outcome)

Child

1. Major sensorineural disability (defined as any of legal blindness, sensorineural deafness requiring hearing aids, moderate or severe cerebral palsy, or developmental delay or intellectual impairment (defined as developmental quotient or intelligence quotient less than ‐2 standard deviations below mean))

2. Developmental delay (however defined by the authors)

3. Intellectual impairment

4. Motor impairment

5. Visual impairment

6. Blindness

7. Deafness

8. Hearing impairment

9. Cerebral palsy

10. Child behaviour

11. Child temperament

12. Learning difficulties

13. Growth assessments at childhood follow‐up (weight, head circumference, length, skin fold thickness)

Search methods for identification of studies

The following methods section of this protocol is based on a standard template used by Cochrane Pregnancy and Childbirth.

Electronic searches

We will search Cochrane Pregnancy and Childbirth’s Trials Register by contacting their Information Specialist.

The Register is a database containing over 22,000 reports of controlled trials in the field of pregnancy and childbirth. For full search methods used to populate Pregnancy and Childbirth’s Trials Register including the detailed search strategies for CENTRAL, MEDLINE, Embase and CINAHL; the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service, please follow this link to the editorial information about Cochrane Pregnancy and Childbirth in the Cochrane Library and select the Specialized Register section from the options on the left side of the screen.

Briefly, the Cochrane Pregnancy and Childbirth’s Trials Register is maintained by their Information Specialist and contains trials identified from:

1. monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);

2. weekly searches of MEDLINE (Ovid);

3. weekly searches of Embase (Ovid);

4. monthly searches of CINAHL (EBSCO);

5. handsearches of 30 journals and the proceedings of major conferences;

6. weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.

Two people independently search results and review the full text of all relevant trial reports identified through the searching activities described above. Based on the intervention described, the Information Specialist assigns each trial report a number that corresponds to a specific Pregnancy and Childbirth review topic (or topics), and then adds it to the Register. The Information Specialist searches the Register for each review using this topic number, rather than keywords. This results in a more specific search set that will be fully recorded in the relevant review sections (Included, Excluded, Awaiting Classification, or Ongoing studies).

In addition, we will search ClinicalTrials.gov and the WHO International Clinical Trials Registry Platform (ICTRP) for unpublished, planned, and ongoing trial reports. The search terms we plan to use are in Appendix 1.

Searching other resources

We will search the reference lists of retrieved studies.

We will not apply any language or date restrictions.

Data collection and analysis

The following methods section of this protocol is based on a standard template used by the Cochrane Pregnancy and Childbirth Group.

Selection of studies

Two review authors will independently assess all the potential studies we identify as a result of the search strategy for inclusion. We will resolve any disagreement through discussion, or if required, we will consult a third person.

We will create a study flow diagram to map out the number of records identified, included, and excluded.

Data extraction and management

We will design a form to extract data. For eligible studies, two review authors will independently extract the data, using the agreed form. We will resolve discrepancies through discussion, or if required, we will consult a third person. We will enter data into Review Manager 5 software (RevMan 5) and check for accuracy (RevMan 5 2014). 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 by involving a third assessor.

(1) Random sequence generation (checking for possible selection bias)

For each included study, we will describe 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:

• 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)

For each included study, we will describe the method used to conceal allocation to interventions prior to assignment, and will assess whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.

We will assess 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)

For each included study, we will describe 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:

• 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)

For each included study, we will describe 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:

• 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)

For each included study, and for each outcome or class of outcomes, we will describe the completeness of data, including attrition and exclusions from the analysis. We will state 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 is reported, or can be supplied by the trial authors, we will re‐include missing data in the analyses that we undertake.

We will assess methods as:

• low risk of bias (e.g. no missing outcome data; missing outcome data balanced across groups);

• high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis done with substantial departure of intervention received from that assigned at randomisation);

• unclear risk of bias.

(5) Selective reporting (checking for reporting bias)

For each included study, we will describe how we investigated the possibility of selective outcome reporting bias and what we found.

We will assess the methods as:

• low risk of bias (where it is clear that all of the study’s pre‐specified outcomes and all expected outcomes of interest to the review have been reported);

• high risk of bias (where not all the study’s pre‐specified outcomes have been reported; one or more reported primary outcomes were not pre‐specified; outcomes of interest are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported);

• unclear risk of bias.

(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)

For each included study, we will describe 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:

• low risk of other bias;

• high risk of other bias;

• unclear whether there is risk of other bias.

(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 Cochrane Handbook of Systematic Reviews of Interventions (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.

Assessment of the quality of the evidence using the GRADE approach

The quality of the evidence will be assessed using the GRADE approach as outlined in the GRADE handbook, in order to assess the quality of the body of evidence relating to the following outcomes for the main comparison: administration of a progestogen by any route for the prevention of preterm birth compared with placebo or no treatment.

1. Perinatal mortality

2. Preterm birth (less than 34 weeks' gestation)

3. Major neurodevelopmental disability at childhood follow‐up

4. Prelabour spontaneous rupture of membranes

5. Adverse drug reaction

6. Birth before 37 completed weeks

7. Birth before 28 completed weeks

We will use GRADEpro Guideline Development Tool to import data from RevMan 5 in order to create ’Summary of findings’ tables. We will produce a summary of the intervention effect and a measure of quality for each of the above outcomes, using the GRADE approach. The evidence can be downgraded from high quality by one level for serious (or by two levels for very serious) limitations, taking into consideration the assessments for risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates, or potential publication bias.

Measures of treatment effect

Dichotomous data

For dichotomous data, we will present results as a summary risk ratio (RR) with 95% confidence intervals (CI).

Continuous data

For continuous data, we will use the mean difference (MD) if outcomes are measured in the same way between trials. We will use the standardised mean difference (SMD) to combine trials that measure the same outcome, but use different methods.

Unit of analysis issues

Cluster‐randomised trials

We will include cluster‐randomised trials in the analyses along with individually randomised trials. We will adjust their sample sizes using the methods described in the Cochrane Handbook of Systematic Reviews of Interventions (Section 16.3.4 or 16.3.6), 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 we consider it unlikely that there will be an interaction between the effect of intervention and the choice of randomisation unit,

We will also acknowledge heterogeneity in the randomisation unit and perform a sensitivity analysis to investigate the effects of the randomisation unit.

Cross‐over trials

Cross‐over trials are not a suitable design for this type of intervention, and we will not include them.

Studies with more than two intervention groups

To overcome unit‐of‐analysis errors when a study includes multiple groups, we will apply the methods as detailed in the Cochrane Handbook of Systematic Reviews of Interventions (section 16.5.4), and combine relevant groups to create a single pair‐wise comparison (Higgins 2011).

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.

Whenever possible, for all outcomes, we will carry out analyses 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 Tau², I², and Chi² statistics. We will regard heterogeneity as substantial if I² is greater than 30%, and either Tau² is greater than zero, or P is 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. First, we will assess funnel plot asymmetry visually. If asymmetry is suggested by a visual assessment, we will perform exploratory analyses to investigate it.

Data synthesis

We will carry out statistical analysis using RevMan 5. We will use a fixed‐effect model to combine the data when 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 a random‐effects model to produce an overall summary if an average treatment effect across trials is considered clinically meaningful. We will treat the random‐effects' summary as the average of the 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 the random‐effects model, the results will be presented as the average treatment effect with 95% confidence intervals, and the estimates of Tau² and I².

Subgroup analysis and investigation of heterogeneity

If we identify substantial heterogeneity, we will investigate it using subgroup and sensitivity analyses. We will consider whether an overall summary is meaningful, and if it is, use the random‐effects method to produce it.

We plan to carry out the following subgroup analyses.

1. Time of treatment commencing (before 20 weeks' gestation versus after 20 weeks' gestation)

2. Different dosage regimes (divided arbitrarily into a cumulative dose of less than 250 mg per week versus a dose of 250 mg or more per week)

We will explore the following outcomes in subgroup analyses.

1. Perinatal mortality

2. Preterm birth (less than 34 weeks' gestation)

3. Major neurodevelopmental disability at childhood follow‐up

We will assess subgroup differences by interaction tests available in RevMan 5. We will report the results of subgroup analyses quoting the Chi² statistic and P value, and the interaction statistic I².

Sensitivity analysis

We will carry out sensitivity analyses using different ICCs for outcomes for babies. We will also carry out sensitivity analyses examining the impact of risk of bias on results; studies that are at high risk of bias due to high sample attrition (more than 20% at childhood follow‐up) will be temporarily excluded from the analysis.

Appendices

Appendix 1. Search terms for ClinicalTrials.gov and ICTRP

We will run each line separately and manually deduplicate

progesterone AND pregnancy

progestogen(s) AND pregnancy

progesterone AND preterm

progestogen(s) AND preterm

Contributions of authors

Jodie Dodd (Contact Person for the review) acts as the guarantor of the review. Jodie Dodd conceived and designed the review/protocol, and drafted the protocol. Andrea Deussen coordinated the protocol writing and design process, and reviewed the protocol and structure at all stages. Rosalie Grivell and Cecelia O'Brien assisted with writing the protocol and also with editing after editorial review.

Sources of support

Internal sources

• Discipline of Obstetrics and Gynaecology, The University of Adelaide, Australia.

External sources

• No sources of support supplied

Declarations of interest

Jodie M Dodd: is an investigator on the PROGRESS randomised trial, which may contribute data to this review.

Rosalie M Grivell: none known.

Cecelia M OBrien: none known.

Andrea R Deussen: none known.

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