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Cochrane Database of Systematic Reviews Protocol - Intervention

Setting and techniques for monitoring blood pressure during pregnancy

Authors' declarations of interest

Version published: 03 August 2017 Version history

https://doi.org/10.1002/14651858.CD012739

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view the current version 23 July 2020
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Abstract

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

To assess the effects of setting and technique of BP measurement for diagnosing hypertensive disorders in pregnancy on subsequent maternal and perinatal outcomes, women's quality of life or use of health service resources.

Background

Description of the condition

Hypertensive disorders of pregnancy (HDP) are common, with pre‐eclampsia complicating 2% to 3% of pregnancies, pre‐existing hypertension complicating 1% of pregnancies and isolated gestational hypertension complicating 5% to 6% of pregnancies (Hutcheon 2011). Hypertension is defined as a diastolic blood pressure (dBP) greater than or equal to 90 mmHg and/or a systolic BP (sBP) greater than or equal to 140 mmHg, with severe hypertension defined as a blood pressure (BP) greater than or equal to 160/110 mmHg and non‐severe (or 'mild‐moderate') hypertension as a BP of 140 to 159/90 to 109 mmHg (NICE 2010).

HDP are a leading cause of maternal and perinatal morbidity and mortality, particularly in low‐ and middle‐income countries (Duley 2009). NICE 2010 defines pre‐eclampsia as gestational hypertension with proteinuria and/or maternal end‐organ complication(s) (e.g. eclampsia) or fetal involvement, and this condition is the cause of most HDP‐associated morbidity and mortality (Khan 2006). Although there are still gaps in understanding around the pathophysiology of pre‐eclampsia, pre‐eclampsia has been established as a systemic syndrome, characterised by placental and maternal vascular dysfunction, which, if severe, may lead to adverse outcomes such as severe hypertension, stroke, seizures (eclampsia), coagulopathy, renal and hepatic injury, haemorrhage or death (Brown 2000). Two small yet landmark cohort studies have suggested that neurological complications of pre‐eclampsia/eclampsia, including stroke and posterior reversible encephalopathy syndrome, are more prevalent in women with systolic hypertension as opposed to diastolic hypertension (Martin 2005; Wagner 2011). These findings support the 2010 NICE guidelines recommending immediate treatment if sBP is 150 mmHg or above (NICE 2010). Perinatal mortality and morbidity is also high as a result of pre‐eclampsia; the blood supply to the placenta is disrupted, which may result in intrauterine growth restriction or fetal death secondary to placental abruption. Furthermore, pre‐eclampsia is an antecedent for one‐fifth of infants born prematurely (Hewitt 1988). Hypertension in pregnancy, independent of pre‐eclampsia, is also associated with increased risk of stroke and other maternal and perinatal complications including pulmonary oedema, placental abruption and perinatal death (Brown 2000).

Description of the intervention

Accurate and regular BP measurement is crucial to the diagnosis and management of HDP, which are often asymptomatic. Most deaths associated with HDP are considered preventable with timely and effective detection along with management of hypertension and associated complications (MacKay 2001). The 2006–2008 UK Confidential Enquiries into Maternal Deaths report found that the most common reason for substandard care in deaths secondary to pre‐eclampsia/eclampsia was failure to recognise and treat hypertension (Cantwell 2011). The 2012–2014 report found that although the proportion of women dying secondary to hypertensive disorders had decreased, in 93% of those women, improvements in the care may have made a difference in their outcome (Knight 2016). Therefore, BP measurement and subsequent management, including treatment of hypertension and timing of delivery, are critical in preventing avoidable maternal deaths.

BP measurement has traditionally taken place within an antenatal clinic environment, conventionally with one or two mercury sphygmomanometer (gold standard) measurements, taken to guide further investigation and management. In recent years there has been a shift away from mercury sphygmomanometry, owing to environmental and safety concerns of mercury in clinical settings and issues with user error (Nathan 2015). Likewise, some authors consider aneroid devices (which also rely on auscultation and therefore are also associated with user and calibration error) as unattractive options for BP measurement (Canzanello 2001). With this, there has been a move towards the use of automated devices, which rely on the detection of oscillometric waveforms produced within the cuff during BP measurement, giving a digital BP reading and minimising user error (Perry 1991). This shift has coincided with growing concern over the accuracy of automated devices, most of which have not been formally validated as accurate. This is particularly problematic in pre‐eclamptic women, in whom automated devices have been shown to significantly underestimate BP, possibly due to the pathophysiological changes of pre‐eclampsia that can alter the oscillometric waveform (Nataranjan 1999; Shennan 1993). The British Hypertension Society (BHS), the European Society of Hypertension (ESH) and the International Organisation for Standardisation each recommend that automated BP devices be independently validated to ensure accuracy according to a recognised protocol (ISO 2013; O'Brien 1993; O'Brien 2010). Even if a device is validated as accurate in a non‐pregnant population, these studies recommend formally validating it in a specific group of pregnant women before using it in pregnancy (O'Brien 1993; O'Brien 2002; O'Brien 2010).

How the intervention might work

Setting of BP measurement

Relying only on clinic or home BP readings may limit the diagnostic potential of BP measurement. White coat hypertension, or elevated BP in a hospital setting yet normotension in a home setting, may occur in nearly 30% of pregnant women. Its recognition can prevent unnecessary admission to hospital or antihypertension treatment; however, it is associated with an increased risk of developing hypertension in pregnancy and pre‐eclampsia, so clinicians should not ignore it (Bellomo 1999; Brown 2005). In women with hypertension in pregnancy (including pre‐eclampsia), the diurnal variation in BP may be altered (Hermida 2000). Alternatives to conventional clinical BP measurement include self (or home) BP monitoring (SBPM) and ambulatory BP measurement (ABPM). In SBPM, people are trained to use the device and interpret readings, in order to alert a health professional if abnormal readings are obtained, or readings can be automatically sent to a central facility for evaluation by a health professional (O'Brien 2001). In ABPM, a portable automated device performs repeated measurements typically over 24 hours during the woman's normal daily routine (Greer 1993). Both methods may increase reproducible measurements, minimise misleading results, identify impaired diurnal variation, and improve BP control and prediction of adverse clinical outcomes (Bellomo 1999; Halligan 1993; Higgins 1997).

Technique of BP measurement

It is well recognised that only BP devices that have been validated as accurate through formal validation according to recognised protocols should be used clinically. Even if validation has occurred, other variables outside of the test environment may influence BP measurement, including BP measurement technique. The BHS and ESH have published several recommendations related to BP measurement technique to ensure reliability: resting for at least five minutes prior to BP measurement, sitting upright with the arm supported and the cuff placed at the level of the heart, using the appropriately sized cuff, deflating the cuff at a rate of 2 mmHg to 3 mmHg, using Korotkoff phase V and recording BP to the nearest 2 mmHg (O'Brien 1993; O'Brien 2003). Unfortunately, correct technique may not be practised outside of the test environment, yet it may impact on BP measurement and therefore outcome. Universal cuffs (that can be used in women with a wide range of arm circumferences) may eliminate the potential error introduced by using an inappropriately sized cuff; however, their impact on outcome is not known.

Why it is important to do this review

As well as confirming or predicting disease, a screening and diagnostic test should also show clear benefit according to robust evidence, in terms of improved survival, function or quality of life. The Cochrane Review 'Ambulatory versus conventional methods for measuring BP during pregnancy' published in 2002 highlighted the absence of randomised controlled trial evidence comparing the two methods of BP measurement according to clinical outcome, use of healthcare resources and women's views (Bergel 2002).

The BHS and ESH have made recommendations on various aspects of BP measurement technique, and a number of studies have assessed the effectiveness of self‐blood pressure measurement (SBPM), ambulatory blood pressure measurement (ABPM) and aspects of BP measurement technique in non‐pregnant and pregnant populations. However, no systematic review has evaluated their impact on survival, health service resources or quality of life.

This review aims to identify all new published and unpublished randomised controlled trials of ABPM, SBPM and all aspects of BP measurement technique to establish the benefits and risks of each for pregnant women. This review will not assess the accuracy of BP devices, but rather the clinical performance of BP equipment that has been previously validated according to recognised protocols, in terms of technique and interpretation. For this reason, we will not include wrist and finger BP devices, as they have not undergone formal validation for use in pregnancy.

Objectives

To assess the effects of setting and technique of BP measurement for diagnosing hypertensive disorders in pregnancy on subsequent maternal and perinatal outcomes, women's quality of life or use of health service resources.

Methods

Criteria for considering studies for this review

Types of studies

We will include all randomised controlled trials (including cluster‐randomised controlled trials) that use either automated BP devices previously validated in a pregnant population or calibrated mercury or aneroid sphygmomanometers and appropriate cuffing. We will exclude cross‐over randomised controlled designs and quasi‐randomised designs. Outcomes will not be part of the criteria for including studies. We will request the full report of trials in abstract form. If access to the full report is not possible, we will exclude these trials. We will also exclude non‐randomised studies because randomised trials are more likely to provide unbiased information and are feasible to achieve the objectives of this Cochrane Review.

Types of participants

Pregnant women (including all gestations of pregnancy) and postpartum women (within 42 days of the end of pregnancy).

Types of interventions

Setting

  1. Ambulatory measurement (using automated devices that provide a large number of device‐initiated BP measurements over a period of time, usually a 24‐hour period) versus conventional clinic BP measurement

  2. Self (automated BP measurement at home) versus conventional clinic BP measurement

Technique

  1. Auscultatory technique (using calibrated aneroid or mercury sphygmomanometer) versus automated technique (using oscillometric devices)

  2. Korotkoff phase IV versus phase V to represent diastolic BP

  3. Resting for at least five minutes from arrival at clinic prior to BP measurement versus immediate measurement on arrival in clinic

  4. Multiple measurements at one clinic visit versus one measurement at one clinic visit

  5. Appropriately sized cuff versus universal cuff (cuff designed to be used in all women, regardless of arm circumference)

  6. Systolic BP versus diastolic BP

  7. Systolic and/or diastolic BP versus mean arterial pressure

Types of outcome measures

Primary outcomes

Systolic BP greater than or equal to 150 mmHg

Secondary outcomes
Maternal outcomes

  • Maternal death: death during pregnancy or up to 42 days after end of pregnancy, or death more than 42 days after the end of pregnancy

  • Maternal morbidity

    • Pre‐eclampsia

    • Eclampsia

    • Cerebrovascular accident

    • Renal failure

    • Hepatic failure

    • HELLP syndrome

    • Disseminated intravascular coagulation

    • Pulmonary oedema

    • Placental abruption

    • Obstetric haemorrhage

Neonatal outcomes

  • Death

    • Stillbirth (death in utero at or after 20 weeks' gestation)

    • Neonatal death (deaths in the first 28 days after birth)

    • Death within the first 28 days after birth

  • Neonatal morbidity

    • Preterm birth (birth before 37 completed weeks' gestation)

    • Admission to a special care nursery for more than seven days

Use of health service resources

  • Maternal

    • Number of clinic visits

    • Number of antenatal hospital admissions

    • Induction of labour

    • Operative delivery

    • Intensive care admission (admission to intensive care unit and length of stay)

    • Ventilation

    • Dialysis

  • Neonatal

    • Admission to special care nursery and length of stay

    • Endotracheal intubation and use of mechanical ventilation

Measures of maternal quality of life

  • Women's experiences and views of the interventions

  • Measures of anxiety levels and self‐confidence

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.

Search results are screened by two people and the full text of all relevant trial reports identified through the searching activities described above is reviewed. Based on the intervention described, each trial report is assigned a number that corresponds to a specific Pregnancy and Childbirth review topic (or topics), and is then added 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 accounted for in the relevant review sections (Included, Excluded, Awaiting Classification or Ongoing).

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

We will endeavour to contact the study authors if the information we require is not included in the full article.

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 Cochrane Pregnancy and Childbirth.

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, through consultation with a third person.

Data extraction and management

We will design a form to extract data. We will extract information on study design and setting, trial dates, participant characteristics, study eligibility criteria, details of the intervention(s) and comparison(s), the outcomes assessed, sources of trial funding, and any conflicts of interest declared by the trial investigators.

For eligible studies, at least two review authors will extract the data using the agreed form. We will resolve discrepancies through discussion, or, if required, through consultation with a third person. We will enter data into Review Manager 5 software (RevMan 5) and check for accuracy (RevMan 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.

If we find cluster‐randomised trials, we will consider recruitment bias, baseline imbalance, loss of clusters, incorrect analysis and comparability with individually randomised trials. If necessary we will consult the Pregnancy and Childbirth Group's statistician regarding the possibility of using a statistical method that allows for analysis at the level of the individual while accounting for the clustering in the data.

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 being at:

  • 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.   

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 being at:

  • 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.

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 being at:

  • low, high or unclear risk of bias for participants;

  • low, high or unclear risk of bias for personnel.

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 being at low, high or unclear risk of bias.

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 studies reported attrition and exclusions as well as 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 trials report, or authors supply, sufficient information, we will re‐include missing data in the analyses that we undertake.

We will assess methods as being at:

  • 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.

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 being at:

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

  • high risk of bias (where authors did not report all the study's pre‐specified outcomes; did not pre‐specify one or more reported primary outcomes; incompletely reported outcomes of interest, rendering them unfit for analysis; failed to include results of a key outcome that they would have been expected to report);

  • unclear risk of bias.

Other bias (checking for bias due to problems not covered by the domains described 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, assigning it as being at:

  • low risk of other bias;

  • high risk of other bias;

  • unclear risk of other bias.

Overall risk of bias

We will make explicit judgements about whether studies are at high risk of bias, according to the criteria given in Higgins 2011. With reference to the risk of bias domains, 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 trials measure outcomes in the same way between them. 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 Section 16.3.4 or 16.3.6 of Higgins 2011 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 if we consider unlikely the interaction between the effect of intervention and the choice of randomisation unit.

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

Other unit of analysis issues

We will include multi‐arm studies in all relevant analyses, for example, ambulatory measurement versus self (automated) versus conventional clinic BP measurement. We may potentially use each arm in two analyses. We will include factorial studies in all relevant analyses (as two separate studies). For example, we will include ambulatory measurement versus self measurement and appropriate cuff versus universal cuff factorial studies in a meta‐analysis of ambulatory versus self in the appropriate cuff group and the universal cuff group.

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, that is, we will attempt to include all participants randomised to each group in the analyses, and we will analyse all participants 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 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 at any suggestion of asymmetry, we will perform exploratory analyses to investigate it.

Data synthesis

We will carry out statistical analysis using RevMan 5 (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, that is, where trials are examining the same intervention, and the trials' populations and methods are sufficiently similar. If there is sufficient clinical heterogeneity to suggest that the underlying treatment effects differ between trials, or if we detect substantial statistical heterogeneity, 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 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 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.

  1. Women at low or average risk of hypertension in pregnancy (unselected) versus women defined as being at high risk of hypertension in pregnancy (these will include women selected by the trial authors on the basis of an increased risk of hypertension in pregnancy, e.g. women with previous pre‐eclampsia).

  2. Women with hypertension, without other signs of pre‐eclampsia versus women with established pre‐eclampsia/eclampsia.

  3. Low‐ and middle‐income country setting versus high‐income country setting.

We will use the primary outcomes (blood pressure above a pre‐defined target) in subgroup analysis.

We will assess subgroup differences by interaction tests available within RevMan 2014, reporting the results of subgroup analyses along with the Chi2 statistic and P value as well as the interaction test I² value.

Sensitivity analysis

We will perform sensitivity analysis for the studies at high (or unclear) risk of selection bias (allocation concealment and sequence generation) and attrition bias. If studies are at high or unclear risk of bias for one or more of these domains, we will exclude them from the sensitivity analysis. It is likely that most studies will not have blinded participants, so this will not be one of our key domains for sensitivity analysis.

Summary of findings table

We will use 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. We have selected the following outcome for use in GRADE, for all the comparisons.

Maternal outcomes

  1. Systolic BP greater than or equal to 150 mmHg

  2. Maternal death

  3. Eclampsia

  4. Cerebrovascular accident

  5. Renal failure

  6. HELLP syndrome

  7. Pulmonary oedema

Neonatal outcomes

  1. Stillbirth (death in utero at or after 20 weeks' gestation)

  2. Neonatal death (deaths in the first 28 days after birth)

  3. Preterm birth (birth before 37 completed weeks' gestation)

  4. Admission to a special care nursery for more than seven days

We will use the GRADEpro Guideline Development Tool to import data from RevMan 2014 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, which considers five dimensions (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of the body of evidence for each outcome. We may download the evidence from 'high quality' by one level for serious (or by two levels for very serious) limitations, depending on assessments for risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates or potential publication bias.