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‐measurement (using an automated BP device at home) versus conventional clinic BP measurement

Technique

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

2. Korotkoff phase IV (K4, muffling sound) versus Korotkoff phase V (K5, disappearance of sound) to represent diastolic BP

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

4. Multiple BP measurements at one clinic visit versus one BP 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 or diastolic BP, or both, versus mean arterial pressure

Primary outcomes

Systolic BP greater than or equal to 150 mmHg

Secondary outcomes

Random sequence generation (checking for possible selection bias)

For each included study, we described the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.

We assessed 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)

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

We assessed 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)

For each included study, we described the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We considered that studies were at low risk of bias if they were blinded, or if we judged that the lack of blinding would be unlikely to affect results.

We assessed 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)

For each included study, we described the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. 

We assessed 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)

For each included study, and for each outcome or class of outcomes, we described the completeness of data, including attrition and exclusions from the analysis. We stated 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. We contacted authors where there were missing data, and included them, were appropriate, information was provided.

We assessed 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)

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

We assessed the methods as being at:

• low risk of bias (where it was clear that the study reported all prespecified outcomes and all expected outcomes of interest to the review);

• high risk of bias (where authors did not report all the study's prespecified outcomes; did not prespecify 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)

For each included study, we described any important concerns we had about other possible sources of bias.

We assessed 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 made explicit judgements about whether studies were at high risk of bias, according to the criteria given in Higgins 2011. With reference to the risk of bias domains, we assessed the likely magnitude and direction of the bias, and whether we considered it likely to impact on the findings. 

If the quantity of data had allowed, we would have explored the impact of the level of bias by undertaking sensitivity analyses – see Sensitivity analysis. 

Dichotomous data

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

For one of the trials, we reported adjusted data to account for the stepped‐wedge cluster design (Vousden 2019). In data and analysis tables, we reported summary RRs, as planned, instead of odds ratios (ORs), as reported by trial authors.

Continuous data

For continuous data, we planned to use the mean difference if outcomes were measured in the same way between trials. We would have used the standardised mean difference to combine trials that measured the same outcome but used different methods.  

Cluster‐randomised trials

We identified one cluster‐randomised trial (Vousden 2019), which was not combined with any other trials in a meta‐analysis because it did not address the same comparison as any other trial. Within this trial, for our outcome of interest (maternal death), we used reported data (which had been adjusted using a 'bent stick' approach, adapted from the approach used for interrupted time series for a stepped wedge cluster‐randomised trial (Bernal 2017)). We entered these data into RevMan 5 using the generic inverse variance (Review Manager 2014). Although reported as ORs by the trial authors, we presented them as RRs, as the outcome was rare (maternal death), and thus the OR approximated the RR closely (McNutt 2003).

In future updates, if we identify both cluster‐randomised trials and individually randomised trials investigating the same comparisons, 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 the interaction between the effect of intervention and the choice of randomisation unit to be unlikely. 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.

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 did not identify any other unit of analysis issues in this version of the review. In future updates, we may include multi‐arm studies in relevant analyses, for example, ambulatory versus self (automated) versus conventional clinic BP measurement. We would include factorial studies in all relevant analyses, as two separate studies. For example, we may include ambulatory versus self BP measurement (SBPM), and appropriate cuff size versus universal cuff factorial studies in a meta‐analysis of ambulatory versus self in the appropriate cuff size group and the universal cuff group.

Maternal outcomes

1. Systolic BP greater than or equal to 150 mmHg

2. Maternal death

3. Pre‐eclampsia

4. Number of antenatal hospital admissions

5. Maternal admission to intensive care

6. Induction of labour

Neonatal outcomes

1. Stillbirth

2. Neonatal death

3. Perinatal mortality

4. Preterm birth

5. Neonatal unit admission

6. Neonatal unit length of stay

7. Endotracheal intubation and use of mechanical ventilation

We used GRADEpro GST to import data from RevMan 5, in order to create ’Summary of findings’ tables (GRADEpro GDT; Review Manager 2014). A summary of the intervention effect and a measure of quality for each of the above outcomes were produced using the GRADE approach.

The GRADE approach uses five considerations (study limitations, consistency of effect, imprecision, indirectness, and publication bias) to assess the certainty of the body of evidence for each outcome. The evidence can be downgraded from 'high certainty' 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.