Immediate versus deferred delivery of the preterm baby with suspected fetal compromise for improving outcomes
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the effects of immediate versus deferred delivery of preterm babies with suspected fetal compromise due to placental insufficiency on neonatal, maternal and long‐term outcomes.
Background
Description of the condition
Fetal compromise occurs when there is inadequate oxygen or nutrient supply to the developing baby. This can be recognised by progressive alterations in the growth, metabolic, cardiovascular and behavioural parameters of the fetus, which represent increasing hypoxaemia and acidosis. The function of vital organs may be affected, leading to temporary or permanent damage or intrauterine death. Fetal compromise is most commonly a result of placental insufficiency, which occurs in approximately 3% of pregnancies (Alberry 2007). This is thought to originate from defective trophoblast invasion in the first trimester (Miller 2008), leading to increased placental vascular resistance that impairs oxygen and nutrient supply to the fetus. Other causes include congenital abnormality, isoimmunisation, intrauterine infection and twin‐twin transfusion syndrome in monochorionic twins. The degree and progression of fetal compromise is variable, and is probably dependant on gestation, maternal factors and the nature and severity of the underlying cause (Miller 2008).
A number of interventions have been proposed as in utero treatments for fetal compromise, including calcium channel blockers, hormones, steroids, nutritional supplementation, oxygen therapy, plasma volume expansion, abdominal decompression, electrostimulation, betamimetics and bed rest. Many of these have been reviewed in other Cochrane Reviews and none have been found to be effective in improving outcome (Hofmeyr 1996; Say 1996d; Say 1996a; Say 1996b; Say 1996c; Say 2001; Say 2003c; Say 2003a; Say 2003b). An exception is in cases of compromise due to twin‐twin transfusion syndrome. This is a distinct condition where compromise arises due to vascular anastomoses in the placental circulation of monochorionic twins. In this situations there is some evidence that laser coagulation of anastomotic vessels improves perinatal outcome (Roberts 2008), hence we have excluded this group from this review. In all other situations leading to fetal compromise, in the absence of effective interventions, the mainstay of management is based on monitoring progression of fetal compromise and delivering the baby at a time that is thought to minimise risk to the infant.
Deciding the optimal timing for delivery of preterm babies with fetal compromise is often difficult. Immediate delivery removes the baby from the hostile uterine environment, decreasing the risk of damage due to hypoxia. However, these benefits must be offset against the risks of increased morbidity and mortality associated with premature delivery. The earlier the gestation at delivery, the greater the risk to the baby of developing complications (Iacovidou 2010). Immaturity of neonatal homeostatic mechanisms predispose preterm babies to respiratory distress, hypothermia, hypoglycaemia, infection and jaundice. The incidence of serious morbidities increases as gestation decreases, including chronic lung disease, necrotising enterocolitis, retinopathy of prematurity, intraventricular haemorrhage and periventricular leukomalacia, which all can lead to death or long‐term disability. In survivors, there is also an apparent dose response between gestation at delivery and cerebral palsy, intellectual impairment and behavioural problems.
The presentation of fetal compromise is variable. Recognition of the pregnancy at risk of fetal compromise may be based on clinical features, such as obstetric history or the presence of medical conditions associated with placental insufficiency. Abnormal fetal growth or liquor production may be found on abdominal palpation, or on ultrasound examination. A decrease in fetal movements may be perceived by the mother, or fetal heart rate abnormalities may be detected on cardiotocograph (CTG).
Several different methods can be used to assess fetal compromise including the following.
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Serial ultrasound biometry (Bricker 2009), which can detect reduction in fetal growth velocity. This is often performed in conjunction with ultrasound assessment of amniotic fluid, which if reduced may reflect reduction in fetal urine production secondary to reduced renal blood flow which occurs as a physiological response to poor placental blood flow.
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Umbilical artery Doppler ultrasound (Alfirevic 2010), which can detect increased resistance or absent or reversed end‐diastolic flow. This reflects increasing placental vascular resistance and damage.
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Fetal arterial Doppler ultrasound (e.g. middle cerebral artery or aortic isthmus) (Alfirevic 2010), which can detect decreased resistance, indicative of brain sparing.
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Fetal venous Doppler ultrasound (e.g. ductus venosus or inferior vena cava) (Alfirevic 2010). Abnormalities reflect pre‐terminal impairment of cardiac function.
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Cardiotocograph (CTG) (Grivell 2010), which can detect changes in fetal heart reactivity.
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Computerised CTG (Guzman 1996), which can detect changes suggestive of fetal hypoxaemia and acidaemia.
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Biophysical profile (Lalor 2008), which consists of CTG in combination with ultrasound to detect changes in fetal behaviour and reduction in amniotic fluid volume that can occur secondary to decreased renal blood flow and fetal urine production. The combination of CTG and amniotic fluid volume assessment alone is called the modified biophysical profile.
The diagnosis of fetal compromise, and the uncertainties in its management can be very distressing for women and their families. Suspected or proven fetal compromise is likely to increase anxiety about pregnancy outcome, and the need for intensive monitoring or admission can be disruptive and result in separation from the family.
Description of the intervention
Once fetal compromise is recognised, the options are immediate delivery (with or without awaiting 24 to 48 hours for administration of antenatal steroids to promote fetal lung maturity) or expectant management. Expectant management involves monitoring progression of fetal compromise and, if monitoring is sufficiently reassuring, either allowing pregnancy to continue to a certain gestational age or the onset of spontaneous labour, or delivering the fetus when it is thought that the degree of in utero compromise imminently jeopardises fetal well‐being. Fetal monitoring can involve any of the methods described above, and a combination of methods are often used. Other Cochrane Reviews (Alfirevic 2010; Grivell 2009; Lalor 2008; Nabhan 2008) focus on methods and frequency of assessing fetal compromise. Delivery is most often achieved by caesarean section, although occasionally induction of labour may be attempted.
Why it is important to do this review
Despite advances in technology for recognition of fetal compromise, considerable controversy surrounds whether a policy of immediate or deferred delivery provides the best outcome for these infants. Evidence regarding the risks and benefits of each approach is needed to direct management decisions for women with suspected fetal compromise.
Objectives
To assess the effects of immediate versus deferred delivery of preterm babies with suspected fetal compromise due to placental insufficiency on neonatal, maternal and long‐term outcomes.
Methods
Criteria for considering studies for this review
Types of studies
All randomised trials and quasi‐randomised trials, including cluster randomised trials, comparing a policy of immediate delivery with deferred delivery or expectant management in fetuses with suspected in utero compromise.
Types of participants
Pregnant women at less than 36 weeks' gestation in whom there is clinical suspicion of fetal compromise as defined by trialists.
Outcomes of pregnancies with fetal compromise diagnosed after 36 weeks' gestation are the focus of another Cochrane Review (Planned early delivery versus expectant management of the term suspected compromised baby for improving outcomes ‐ protocol in progress)
We will include multiple pregnancies, separating monochorionic and dichorionic twins where possible. However, if the information is available we will exclude women with twin‐twin transfusion syndrome. This is because interventions are available that are thought to improve outcome in twin‐twin transfusion, so expectant management is less relevant.
Types of interventions
Immediate delivery or deferred delivery. Immediate delivery may be by induction of labour or caesarean section. It may or may not include time for a course of effective antenatal steroids (48 hours). Deferred delivery may be for a set period of time, until test results worsen, or expectant management (waiting for spontaneous labour).
Types of outcome measures
Primary outcomes
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Perinatal mortality (intrauterine death or death in the first week of life).
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Serious neonatal morbidity (composite outcome including bronchopulmonary dysplasia (BPD), necrotising enterocolitis (NEC), intraventricular haemorrhage (IVH), retinopathy of prematurity (ROP), hypoxic Ischaemic encephalopathy (HIE).
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Death or disability at or after two years of age.
Secondary outcomes
Perinatal
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Stillbirth (intrauterine death of fetus at more than 24 weeks' gestation)
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Neonatal mortality (death of a baby born with signs of life within 28 days of birth).
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Postneonatal mortality (death of a baby greater than 28 days up to one year of life).
Fetal/neonatal
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Cord pH less than 7.1.
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Apgar less than seven at five minutes.
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Apgar less than four at five minutes.
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Any admission to neonatal intensive care or special care facility.
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Any resuscitation required.
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Intubation/ventilation required.
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Interval between randomisation and delivery.
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Gestation less than 28 weeks at delivery.
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Gestation less than 34 weeks at delivery.
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Birthweight less than 10th centile.
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Birthweight less than 5th centile.
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Birthweight less than 3rd centile.
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Low birthweight (less than 2.5 kg).
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Very low birthweight (less than 1.5 kg).
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Respiratory distress syndrome (as defined by trialists).
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Meconium aspiration (as defined by trialists).
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Seizures (as defined by trialists).
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Infection or sepsis (as defined by trialists).
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Neonatal cooling performed.
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Any Hypoxic Iscahemic Encepahlopathy (HIE) (grade I, II or III).
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Moderate or severe HIE (grade II or grade III).
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Interventricular haemorrhage (IVH) or germinal matrix haemorrhage (GMH).
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Bronchopulmonary dysplasia (BPD).
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Necrotising enterocolitis (grade II or above).
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Retinopathy of prematurity requiring treatment.
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Periventricular leucomalacia (PVL).
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Length of hospital stay.
Maternal
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Caesarean section.
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Induction of labour.
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Spontaneous vaginal birth.
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Operative vaginal birth.
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Breastfeeding.
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Maternal satisfaction with care.
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Antenatal admission (days).
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Any antenatal complication (pre‐eclampsia, thromboembolic disease, antepartum haemorrhage, infection, other).
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Administration of antenatal corticosteroids.
Long‐term outcomes
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Neurodevelopmental impairment at or after two years of age.
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Cerebral palsy at or after two years of age.
We will also report non‐prespecified outcomes if we consider them to be important.
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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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 and will include studies identified in abstract form.
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 consult a third assessor.
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 a third person. We will enter data into Review Manager software (RevMan 2008) 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 2009). We will resolve any disagreement by discussion or by involving a third assessor.
(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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adequate (any truly random process, e.g. random number table; computer random number generator);
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inadequate (any non‐random process, e.g. odd or even date of birth; hospital or clinic record number); or
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unclear.
(2) Allocation concealment (checking for possible selection bias)
We will describe for each included study the method used to conceal the allocation sequence in sufficient detail and determine whether 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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adequate (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
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inadequate (open random allocation; unsealed or non‐opaque envelopes, alternation; date of birth);
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unclear.
(3) Blinding (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 judge studies at low risk of bias if they were blinded, or if we judge that the lack of blinding could not have affected the results. We will assess blinding separately for different outcomes or classes of outcomes.
We will assess the methods as:
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adequate, inadequate or unclear for participants;
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adequate, inadequate or unclear for personnel;
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adequate, inadequate or unclear for outcome assessors.
(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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adequate (less than 5% of participants);
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inadequate (5% or more of participants);
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unclear.
(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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adequate (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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inadequate (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.
(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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yes;
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no;
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unclear.
(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 2009). 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
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 Handbook using an estimate of the intracluster correlation co‐efficient (ICC) derived from the trial (if possible), or from another source. If ICCs from other sources are used, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we identify both cluster‐randomised trials and individually‐randomised trials, we plan to synthesise the relevant information. We will consider it reasonable to combine the results from both if there is little heterogeneity between the study designs and the interaction between the effect of intervention and the choice of randomisation unit is considered to be unlikely.
We will also acknowledge heterogeneity in the randomisation unit and perform a separate meta‐analysis.
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 (5% or more of participants) 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. 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 T² is greater than zero and either I² is greater than 30% 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 we detect asymmetry in any of these tests or 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 2008). 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. We will treat the random‐effects summary 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, we will present the results as the average treatment effect with its 95% confidence interval, and the estimates of T² and I².
Subgroup analysis and investigation of heterogeneity
If we identify substantial heterogeneity, we will investigate it using subgroup analyses and 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 analyses.
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Gestation less than 28 weeks, 28 to 31+6 weeks, 32 to 36 weeks.
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Singleton and multiple pregnancies.
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Male and female babies.
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Underlying cause of fetal compromise: placental insufficiency, congenital abnormality, isoimmunisation, intrauterine infection, twin‐twin transfusion syndrome.
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Severity of fetal compromise: positive end diastolic flow in umbilical artery doppler, absent or reversed end‐diastolic flow in umbilical artery doppler, abnormal arterial or venous doppler.
We will use the following outcomes in subgroup analysis.
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Perinatal mortality.
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Serious neonatal morbidity (composite outcome including bronchopulmonary dysplasia (BPD), necrotising enterocolitis (NEC), intraventricular haemorrhage (IVH), retinopathy of prematurity (ROP), hypoxic ischaemic encephalopathy (HIE)).
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Death or disability at or after two years of age.
For fixed‐effect inverse variance meta‐analyses we will assess differences between subgroups by interaction tests. For random‐effects and fixed‐effect meta‐analyses using methods other than inverse variance, we will assess differences between subgroups by inspection of the subgroups’ confidence intervals; non‐overlapping confidence intervals indicate a statistically significant difference in treatment effect between the subgroups.
Sensitivity analysis
We will perform sensitivity analyses to explore the effect of trial quality on results, where there is risk of bias associated with the quality of some of the included trials. We will also use sensitivity analysis to explore the effects of fixed‐effect or random‐effects analyses for outcomes with statistical heterogeneity and the effects of any assumptions made such as the value of the ICC used for cluster randomised trials.
We will use the following outcomes in sensitivity analysis.
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Perinatal mortality.
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Serious neonatal morbidity (composite outcome including BPD, NEC, IVH, ROP, HIE).
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Death or disability at or after two years of age.
