Use of biochemical tests of placental function for improving pregnancy outcome

  • Protocol
  • Intervention

Authors


Abstract

This is the protocol for a review and there is no abstract. The objectives are as follows:

To assess whether clinicians' knowledge of the results of biochemical tests of placental function is associated with an improvement in fetal or maternal outcome of pregnancy in high-risk, low-risk or unselected pregnancies.

Background

In a healthy pregnancy the placenta is a metabolically active endocrine organ secreting many different hormones and metabolites into maternal blood; this profile may alter with pregnancy complications (Conde-Agudelo 2013). The outcome of pregnancy is closely linked to placental function; placental dysfunction has been documented in complications of pregnancy including: fetal growth restriction, small-for-gestational-age infants, pre-eclampsia, preterm birth, reduced fetal movements and stillbirth (Brosens 2011; Ness 2006; Pinar 2014; Warrander 2012).

Biochemical tests of placental function measure released placental factors in maternal biofluid(s) including urine and blood. A previous Cochrane systematic review found no evidence that measuring oestriol improved pregnancy outcome (Neilson 2012). Since Neilson 2012 was published, there has been increased interest in measurement of biomarkers of placental function. Our review updates the Neilson 2012 review on this topic, and includes more recently developed biomarkers.

Description of the intervention

Prior to the widespread use of ultrasound to assess fetal biometry or biophysical profile from the mid-1970s onwards, biochemical tests of placental function including: oestriol, human placental lactogen (hPL) and human chorionic gonadotrophin (hCG) were used in antepartum assessment of the fetus in late pregnancy (Greene 1965). These biochemical factors were measured in maternal plasma, serum or urine. Levels of these factors may change throughout pregnancy; factors which are synthesised by the placenta tend to increase in proportion to placental mass throughout pregnancy. Important exceptions to this are hCG which peaks in the first trimester and free placental growth factor (PlGF) which declines after 36 weeks (Saffer 2013). Therefore, performance of specific biochemical factors may depend on the gestation at sampling.

Recently, biochemical markers related to placental function have been used as part of maternal serum screening for Trisomy 21 in the first and second trimester including alpha fetoprotein (AFP), hCG, unconjugated oestriol, pregnancy-associated plasma protein A (PAPP-A) and inhibin. Observational studies have demonstrated that in the absence of chromosomal or structural anomalies, dysregulation of these placental biomarkers is associated with altered risks of fetal death, fetal growth restriction, small-for-gestational-age infants or pre-eclampsia (Dugoff 2004; Smith 2007; Smith 2007a). These were either case-control or cohort studies which focused on samples obtained in first trimester screening. Serum PAPP-A below 5th centile (0.42 MoM) was associated with an increased risk of spontaneous loss before 24 weeks' gestation (odds ratio (OR) 2.50, 95% confidence interval (CI) 1.76 to 3.56), stillbirth (OR 2.15, 95% CI 1.11 to 4.15), small-for-gestational age below 10th centile (OR 2.47, 95% CI 2.16 to 2.81) and pre-eclampsia (OR 1.54, 95% CI 1.16 to 2.03); hCG below 5th centile was related to small-for-gestational-age infant below 10th centile (OR 1.55, 95% CI 1.33 to 1.80) (Dugoff 2004). Measurements obtained in the second trimester (15 to 21 weeks) found that women with increased AFP greater than 95th centile had an elevated risk of stillbirth (OR 2.79, 95% CI 2.09 to 3.73); this was also true for hCG greater than 95th centile (OR 1.93, 95% CI 1.39 to 2.66) (Smith 2007a).

Recently, placentally-derived factors in maternal blood including hPL (Dutton 2012), placental protein 13 (PP-13) (Schneuer 2012), soluble FMS-like tyrosine kinase (sFLt-1) (Smith 2007), PlGF (Benton 2012), and various metabolites (Horgan 2011), have been measured by a variety of different experimental approaches including: enzyme-linked immunosorbent assay, mass spectrometry or developed point of care tests. Elevated sFlt-1 in the first trimester is associated with a reduced risk of a small-for-gestational-age infant (OR 0.92, 95% CI 0.88 to 0.96), and stillbirth associated with a placental cause (OR 0.77, 95% CI 0.61 to 0.95). Likewise, high PlGF in the first trimester is associated with a reduction in small-for-gestational-age infant (OR 0.95, 95% CI 0.90 to 0.99) (Smith 2007). Measurement of PlGF in the third trimester differentiated placental intrauterine growth restriction (IUGR) (n = 9) from constitutionally small fetuses (n = 7) with 100% sensitivity and 86% specificity (Benton 2012).

Currently, ultrasound assessment of fetal well-being provides only modest benefits in selected populations (Alfirevic 2010; Alfirevic 2010a). This has increased interest in other methods of predicting or identifying fetal compromise. It is hypothesised that measurement of biochemical factors in maternal blood or urine reflects placental function, which is closely linked to fetal outcome compromise.

How the intervention might work

Many pregnancy complications are related to abnormal placental function; methods which assess placental function may identify pregnancies where placental dysfunction is sufficiently severe that it leads to fetal demise. It is hypothesised that revealing the results of these biochemical measurements to clinicians may improve detection of complications, which could improve pregnancy outcome by targeting intervention (e.g. delivery). However, it is also possible that the intervention could have negative effects including: increased maternal anxiety due to increased testing or abnormal results, or increased intervention such as induction of labour or caesarean section.

Why it is important to do this review

Observational studies relating abnormal levels of placentally-derived factors to increased risk of stillbirth, fetal growth restriction and pre-eclampsia have re-ignited interest in biochemical markers of placental dysfunction. Therefore, it is important to determine the value of biochemical tests of placental function in improving fetal and maternal outcome of pregnancy.

Objectives

To assess whether clinicians' knowledge of the results of biochemical tests of placental function is associated with an improvement in fetal or maternal outcome of pregnancy in high-risk, low-risk or unselected pregnancies.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised, cluster-randomised or quasi-randomised trials that assess the effects of biochemical testing of placental or feto-placental function in pregnancy. We will not include cross-over randomised trials, as this is not an appropriate study design for this question. We will include studies reported only as abstracts, provided there are sufficient data to evaluate study quality.

Types of participants

All pregnant women, regardless of whether deemed to be high risk or low risk for pregnancy complications (e.g. fetal growth restriction, perinatal mortality or pre-eclampsia), or unselected participants by the study investigators. Women who have pregnancies complicated by chromosomal or structural anomaly will be excluded.

Types of interventions

Studies will be eligible if they compared women who had placental function tests and the results were available to their clinicians with women who either did not have the tests, or the tests were done but the results were not available to the clinicians. The placental function tests could be any biochemical test of placental function carried out using the woman's maternal biofluid, either alone or in combination with other placental function test/s.

Types of outcome measures

Primary outcomes
  • Death of a baby (stillbirth or neonatal death)

  • Small-for-gestational age (below 10th centile on customised birthweight chart, or as defined by trialists)

Secondary outcomes
For the baby
  • Stillbirth

  • Neonatal death

  • Umbilical artery pH < 7.0

  • Neonatal intensive care unit admission

  • Neonatal intensive care for more than seven days

  • Preterm birth (before 37 weeks' gestation)

  • Very preterm birth (before 32 weeks' gestation)

  • Need for ventilation

  • Organ failure

  • Serious neonatal morbidity (e.g. necrotising enterocolitis, chronic lung disease, intraventricular haemorrhage, sepsis, seizures)

  • Fetal abnormality

  • Neurodevelopment in childhood (cerebral palsy, neurodevelopmental delay)

For the women
  • Elective delivery (induction of labour or non-labour caesarean section)

  • Caesarean section

  • Intensive care admission

  • High-dependency unit admission

  • Hospital admission for ≥ seven days

  • Pre-eclampsia

  • Eclampsia

  • Maternal death

  • Women's perception of care

Search methods for identification of studies

Electronic searches

We will search the Cochrane Pregnancy and Childbirth Group’s Trials Register by contacting the Trials Search Co-ordinator.

The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co-ordinator and contains trials identified from:

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

  2. weekly searches of MEDLINE;

  3. weekly searches of Embase;

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

  5. 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.

We will not apply any language restrictions.

Data collection and analysis

Selection of studies

Two review authors (Alexander Heazell (AEPH) and Melissa Whitworth (MKW)) 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 senior review author (Lelia Duley (LD) or Jim Thornton (JT)).

Data extraction and management

We will design a form to extract data. For eligible studies, AEPH and MKW will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult LD or JT. We will enter data into Review Manager software (RevMan 2014) 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

AEPH and MKW 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 LD or JT as a third assessor.

(1) Random 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:

  • 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 will describe for each included study 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)

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:

  • 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 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:

  • low, high or unclear risk of bias.

(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)

We 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 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 which 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)

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:

  • 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)

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:

  • 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 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 - see Sensitivity 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 standard errors using the methods described in the Handbook [Section 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. 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 will also acknowledge heterogeneity in the randomisation unit and perform a sensitivity analysis to investigate the effects of the randomisation unit.

Cross-over trials

Studies with a cross-over design will be excluded, as this design is not appropriate for this question.

Studies with multiple treatment groups

If we identify relevant multi-arm trials, we will include these if any pair-wise comparisons of the intervention groups are relevant to this review and meet the inclusion criteria. We will report all the intervention groups involved in the index study in the 'Characteristics of included studies' section, but will include only those intervention groups relevant to the analysis. We will address pair-wise comparisons from multi-arm trials in meta-analyses, if they are eligible. We will ensure that data from individual participants are only included once when pooling data. If there are multiple intervention groups in a particular meta-analysis, we will combine all relevant experimental intervention groups of the study into a single intervention group and combine all relevant control intervention groups into a single control group (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.

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 I² is greater than 30% and either 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. 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 the Review Manager software (RevMan 2014). 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 95% confidence intervals, 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 subgroup analyses based on:

  • risk at trial entry: women at high risk, women at low risk; women with mixed low and high risk or unselected risk; women with risk status unknown;

  • risk of bias: low risk of bias; high risk of bias; risk of bias unclear;

  • type of placental function tests;

  • timing of placental function tests divided by trimester.

Subgroup analysis will be restricted to the review's primary outcomes.

We will assess subgroup differences by interaction tests available within RevMan (RevMan 2014). We will report the results of subgroup analyses quoting the χ2 statistic and P value, and the interaction test I² value.

Sensitivity analysis

We will explore the effect of trial quality by sensitivity analysis. Where there is risk of bias associated with a particular aspect of study quality (e.g. randomised controlled trials versus quasi-randomised controlled trials) or statistical treatment of data, we will perform by sensitivity analyses to explore this looking at primary outcomes only.

Acknowledgements

Alexander Heazell is supported by funding from Tommy's - the baby charity.

As part of the pre-publication editorial process, this protocol has been commented on by two peers (an editor and referee who is external to the editorial team), a member of the Pregnancy and Childbirth Group's international panel of consumers and the Group's Statistical Adviser.

Contributions of authors

Dr Alexander Heazell (AEPH) conceived the idea for the review. All authors contributed to the design of the review and writing the protocol. AEPH is the guarantor for the review.

Declarations of interest

Jim Thornton and Melissa Whitworth: None known.

Lelia Duley has been awarded an NIHR research grant for a programme of work on care at very preterm birth.

Alexander Heazell has received research grants from Alere (UK) and Action Medical Research to investigate placental factors in maternal serum in women with reduced fetal movements.

Sources of support

Internal sources

  • No sources of support supplied

External sources

  • Tommy's the Baby Charity, UK.

    Salary support for Dr Alexander Heazell

Ancillary