Evaluation of the Growth Assessment Protocol (GAP) for antenatal detection of small for gestational age: The DESiGN cluster randomised trial.

BACKGROUND: Antenatal detection and management of small for gestational age (SGA) is a strategy to reduce stillbirth. Large observational studies provide conflicting results on the effect of the Growth Assessment Protocol (GAP) in relation to detection of SGA and reduction of stillbirth; to the best of our knowledge, there are no reported randomised control trials. Our aim was to determine if GAP improves antenatal detection of SGA compared to standard care. METHODS AND
FINDINGS: This was a pragmatic, superiority, 2-arm, parallel group, open, cluster randomised control trial. Maternity units in England were eligible to participate in the study, except if they had already implemented GAP. All women who gave birth in participating clusters (maternity units) during the year prior to randomisation and during the trial (November 2016 to February 2019) were included. Multiple pregnancies, fetal abnormalities or births before 24+1 weeks were excluded. Clusters were randomised to immediate implementation of GAP, an antenatal care package aimed at improving detection of SGA as a means to reduce the rate of stillbirth, or to standard care. Randomisation by random permutation was stratified by time of study inclusion and cluster size. Data were obtained from hospital electronic records for 12 months prerandomisation, the washout period (interval between randomisation and data collection of outcomes), and the outcome period (last 6 months of the study). The primary outcome was ultrasound detection of SGA (estimated fetal weight <10th centile using customised centiles (intervention) or Hadlock centiles (standard care)) confirmed at birth (birthweight <10th centile by both customised and population centiles). Secondary outcomes were maternal and neonatal outcomes, including induction of labour, gestational age at delivery, mode of birth, neonatal morbidity, and stillbirth/perinatal mortality. A 2-stage cluster-summary statistical approach calculated the absolute difference (intervention minus standard care arm) adjusted using the prerandomisation estimate, maternal age, ethnicity, parity, and randomisation strata. Intervention arm clusters that made no attempt to implement GAP were excluded in modified intention to treat (mITT) analysis; full ITT was also reported. Process evaluation assessed implementation fidelity, reach, dose, acceptability, and feasibility. Seven clusters were randomised to GAP and 6 to standard care. Following exclusions, there were 11,096 births exposed to the intervention (5 clusters) and 13,810 exposed to standard care (6 clusters) during the outcome period (mITT analysis). Age, height, and weight were broadly similar between arms, but there were fewer women: of white ethnicity (56.2% versus 62.7%), and in the least deprived quintile of the Index of Multiple Deprivation (7.5% versus 16.5%) in the intervention arm during the outcome period. Antenatal detection of SGA was 25.9% in the intervention and 27.7% in the standard care arm (adjusted difference 2.2%, 95% confidence interval (CI) -6.4% to 10.7%; p = 0.62). Findings were consistent in full ITT analysis. Fidelity and dose of GAP implementation were variable, while a high proportion (88.7%) of women were reached. Use of routinely collected data is both a strength (cost-efficient) and a limitation (occurrence of missing data); the modest number of clusters limits our ability to study small effect sizes.
CONCLUSIONS: In this study, we observed no effect of GAP on antenatal detection of SGA compared to standard care. Given variable implementation observed, future studies should incorporate standardised implementation outcomes such as those reported here to determine generalisability of our findings. TRIAL REGISTRATION: This trial is registered with the ISRCTN registry, ISRCTN67698474.

Introduction

In 2014, the World Health Organization (WHO) launched the Every Newborn Action Plan with the aim to end preventable perinatal deaths by 2030; reducing stillbirth is thus a global priority [1]. While national strategies to tackle stillbirth vary according to leading causes locally, the importance of risk stratification and screening strategies that target improved detection of small for gestational age (SGA) (birthweight <10th centile) and appropriate management and timely delivery has been emphasised for high-income countries [2,3]. Antenatal detection of SGA has been associated with a halved risk of stillbirth compared to undetected SGA [4,5]. A review of guidelines from 6 high-income countries described a consensus on recommendations for stratifying women by risk of SGA, but noted variation in other aspects of screening and management, such as the use of customised fetal charts to identify SGA and the role of universal third trimester ultrasound [6].

The Growth Assessment Protocol (GAP), developed by the Perinatal Institute [7], is a complex intervention that includes the use of customised centile charts for fundal height and estimated fetal weight (EFW) measurements (Gestation-Related Optimal Weight (GROW) charts), evidence-based protocols and risk assessment, training and accreditation of clinical staff, a rolling audit programme and benchmarking of performance [8]. A nonrandomised control trial in the United Kingdom (UK) of standardised fundal height measurements plotted on customised charts demonstrated an increase in antenatal detection of SGA (29% versus 48%, odds ratio 2.2; 95% confidence interval (CI) 1.1 to 4.5) [9]. A recent study in New Zealand reported an almost 3-fold increase in detection of SGA (22.9% versus 57.9%; p < 0.001) when comparing rates before and after implementation of GAP [10]. In the UK, national uptake of GROW charts or GAP increased between 2007 and 2012 with a concomitant 22% reduction of stillbirth rates in regions of high uptake [11]. However, a study comparing the trend of stillbirth rates during 2010 to 2015 in England and Wales to that in Scotland where uptake of GAP was very low reported a greater decline in Scotland [12]. The authors concluded that any association between GAP and reductions in stillbirth rates was coincidental rather than causal. To our knowledge, there has been no randomised control trial studying the impact of GAP versus standard care on detection of SGA. There is also paucity of data on the impact of GAP on service usage (e.g., number of ultrasound scans and induction of labour) and on unwanted potential effects, such as a possible increase in neonatal adverse outcomes related to iatrogenic late preterm/early term birth.

The primary aim of the DESiGN trial (DEtection of Small for GestatioNal age fetus) was to determine whether implementation of GAP results in improved ultrasound detection of SGA, when compared to standard care. We also planned to explore the effect on related maternal and neonatal outcomes and to conduct a process evaluation of fidelity, reach, dose, acceptability, feasibility, and resource use.

Methods

Study design and population

The DESiGN trial was a pragmatic, superiority, 2-arm, parallel group, open, cluster randomised control trial, including 13 maternity units in England [13]. All women who gave birth in participating clusters (maternity units) during the trial (between November 2016 and February 2019) were included. Baseline data were also collected on women who gave birth during the year prior to cluster randomisation. Pregnancies with significant fetal abnormalities, multiple pregnancies, and pregnancies ending before 24+1 weeks of gestation (referred to as weeks in the paper) were excluded. The study design and methodology of this trial have been prospectively registered (ISRCTN67698474), and both the study protocol (S1 Protocol) and the prespecified analysis plan (S1 Appendix) have been approved by the Trial Steering Committee.

We enrolled maternity units primarily in London given the lower uptake of GAP in this area at the time the trial was proposed compared to the whole of the UK, where uptake was 64% [14]. A cluster trial was undertaken because the intervention requires implementation of site-wide guidelines for screening and management of SGA and additional staff training. Within-site contamination would limit the validity of individual randomisation. The trial was pragmatic to capture the reality of the introduction of this complex intervention into clinical practice with support from the Perinatal Institute.

Randomisation and masking

Clusters were randomly allocated by the trial statistician to immediate implementation of GAP (intervention arm) or to continue standard care during the study period (standard care arm). Randomisation occurred in 3 strata according to time of inclusion in the study (8, 3, and 2 clusters, respectively); the randomisation of the first 8 clusters were further stratified by size of maternity unit (number of births during the year 2013 to 2014). Randomisation was by random permutation within strata, providing exact 1:1 allocation except in the second stratum of 3 clusters where it was determined at random which arm would receive 2 clusters. The random permutation was conducted in Stata v14 (StataCorp LP, College Station, Texas, USA). Due to the nature of the intervention, concealment was not possible.

Procedures

Data were collected from a prerandomisation period of 12 consecutive months, which differed by randomisation stratum, the washout period (variable duration) during which the intervention arm clusters were implementing GAP, and for an outcome comparison period (outcome period) of 4 to 6 months from 1 September 2018 to 28 February 2019. The outcome period commenced when women giving birth in intervention clusters had had time to receive full antenatal exposure to GAP. One cluster from the control arm provided outcome data earlier due to a previously planned introduction of GAP at the original trial end date. This was a consequence of the washout period being extended after delays in GAP implementation at the last cluster randomised to the intervention.

Data were obtained from 4 types of routinely collected electronic patient record system at each cluster: maternity, ultrasound, neonatal, and administrative [15]. Additional data were collected to assess compliance with the intervention in allocated clusters from review of a subset of women’s paper maternity records (n = 120 per cluster). Data were anonymised locally by the trial team before being sent centrally for data management, storage, and analysis.

Following randomisation, maternity units allocated to the intervention were expected to contact the providers of GAP to commence training and implementation support. The components of GAP implementation are detailed in Table 1, by stage of implementation. Following consultation with cluster sites, the e-learning training requirement was amended by the Perinatal Institute to allow compliance with e-learning certification to be achieved within 3 months of going “live.” The prespecified requirements that describe how an implementing cluster would be considered as GAP compliant are further detailed in the study protocol (S1 Protocol; page 74). These were GAP recommendations during this trial; there were changes introduced subsequent to this study [16].

Table 1

Expected components of GAP implementation.

Implementation Stage	GAP requirements
Preparation and planning	Nominated staff from each cluster to attend “Train the Trainers” GAP workshop. Cluster to conduct a baseline audit of SGA detection (10% of annual births). Cluster to prepare local guideline for the “Assessment of Fetal Growth” modelled on GAP recommendations.
Implementation	Cluster trainers to cascade face-to-face training to 75% of colleagues from each professional group (midwives, obstetricians, sonographers). GAP e-learning module to also be completed by 75% staff members from each professional group.
Ongoing use of GAP	Access to GROW chart online programme provided by the Perinatal Institute after cluster compliant with above requirements. Each pregnant woman assessed for risk of SGA at antenatal booking appointment using GAP tool. Customised GROW chart printed for each pregnant woman at antenatal booking appointment and used to assess fetal growth by plotting fundal height measurements or estimated fetal weight on the chart. Women at low risk of SGA expected to have a fundal height measured 3-weekly during pregnancy, commencing between 26 and 28 weeks. If plots deviate from what is expected (first plot below 10th centile, slow/static/accelerative growth), the woman should be referred for a fetal growth scan. Women at high risk of SGA expected to have an ultrasound scan to estimate fetal weight 3-weekly during pregnancy, commencing between 26 and 28 weeks. Where GROW chart EFW plots deviate from the expected trajectory (as per fundal height deviations), RCOG protocols should be followed for further investigation of suspected SGA [17]. Birthweight centiles are calculated at the time of birth using the GROW software. This also prompts the clinician to enter whether SGA was detected antenatally, to inform auditing of practice and national benchmarking. GAP users are encouraged to use the GAP online proforma to conduct analyses of ‘missed cases’ in which SGA was not detected antenatally.

EFW, estimated fetal weight by ultrasound; GAP, Growth Assessment Protocol; GROW, Gestation-Related Optimal Weight chart; RCOG, Royal College of Obstetricians and Gynaecologists; SGA, small for gestational age.

In the standard care arm, women received routine antenatal care as per the local guidelines for screening and management of SGA in each cluster. There was no prespecification of policies in this arm, except that these clusters should not implement GAP or use customised centiles for fundal height or ultrasound monitoring of fetal growth. At the time this trial started, standard care for screening and management of SGA was guided by an RCOG guideline [17]. This recommends stratification of pregnant women by presence of risk factors for SGA. Women at low risk of SGA are further screened using measurement of fundal height at each antenatal appointment after 24 weeks. Women with risk factors are either offered serial fetal growth ultrasound scans or further stratification using doppler assessment of the uterine arteries at 20 weeks of gestation, dependent on the number or significance of the risk factors present. RCOG does not guide frequency of serial growth scans. Following a request from reviewers, a summary description of recommended practice in standard care clusters is provided on S2 Appendix (page 2) based on review of local guidelines for screening and detection of SGA. The Saving Babies’ Lives care bundle is a complex antenatal intervention that started to be implemented nationally during the trial. Clusters in the standard care arm were exempted from compliance with element 2 (risk assessment and surveillance of fetal growth restriction) of the Saving Babies’ Lives bundle. However, it was considered unethical to stop clusters in the standard care arm that were willing to implement concomitant strategies for improved detection of SGA and prevention of stillbirths initiated locally or nationally, which could include the Saving Babies’ Lives care bundle [18].

Process evaluation of implementation

The process evaluation examined implementation compliance, acceptability, feasibility, contextual factors, and mechanisms of impact. To assess compliance with the intervention in implementing sites, we assessed fidelity, reach, and dose [19], by comparing site guidelines to those recommended by GAP, assessing compliance with training targets and by a review of 600 women’s maternity records (40 randomly selected singleton nonanomalous births in each of 3 months during the outcome period at 5 implementing clusters). Acceptability and feasibility of GAP implementation were explored through interviews with clinicians including clinical leads. A summary of implementation is provided in this report to support interpretation of the main findings (methodology provided in S2 Appendix; page 3). We also collected guideline on screening for SGA from clusters in the standard care arm. A more detailed process evaluation analysis will be reported separately.

Outcomes

The primary outcome of this study was antenatal ultrasound detection of SGA (after 24 completed weeks) defined for infants who are SGA (i.e., birthweight less than 10th centile) according to both population (UK1990 birthweight centiles) and customised (GROW) charts [20,21]. This definition was chosen because GAP targets detection of babies who are SGA by customised centiles, whereas standard care largely uses population centile charts. Antenatal detection of SGA was defined as ultrasound-derived EFW <10th centile by customised (GROW) charts in the intervention arm during the outcome period and by population [22] fetal charts for babies born in intervention sites during the prerandomisation period and all babies born in the standard care arm [20-22]. For calculation of ultrasound detection of SGA, data were obtained from electronic ultrasound records to identify EFW <10th centile and from electronic maternity records to identify birthweight <10th centile; these were calculated for all births in each cluster. A detailed description of methodology for calculating the rate of antenatal detection of SGA is provided in S2 Appendix (page 4).

The 26 planned secondary outcomes included the test positive rate for antenatal detection of SGA (defined by both definitions as per primary outcome), antenatal detection and false positive rate of antenatal ultrasound detection of SGA confirmed at birth by customised centiles and by population centiles, maternal outcomes (induction of labour, mode of birth, postpartum haemorrhage, severe perineal tear (third/fourth degree), epidural and episiotomy), neonatal parameters and measures of condition at birth (gestational age at birth, preterm birth, birthweight, Apgar score <7 at 5 minutes, arterial cord pH <7.1, respiratory support at birth), neonatal unit admission, major neonatal morbidity (defined as one or more of: receipt of supplemental oxygen at 28 days of age, necrotising enterocolitis, sepsis, neonatal retinopathy, hypoxic–ischemic encephalopathy, intraventricular haemorrhage), minor neonatal morbidity (defined as one or more of hypothermia, hypoglycaemia, nasogastric tube feeding), stillbirth, neonatal death, and perinatal mortality. Utilisation of ultrasound scan was a process outcome (proportion of pregnancies with a scan, proportion of pregnancies with a scan between 18+0 and 24+0 weeks, proportion of pregnancies with a scan after 24+0 weeks with EFW, number of scans per pregnancy after 24+0 weeks with EFW, proportion of pregnancies with no record of ultrasound). Timing of scans after 24 weeks (i.e., utilisation per week gestation) was described following a request from reviewers and the academic editor, with the aim of better understanding differences in practice between trial arms. These process measures were reported to provide context to results.

Statistical analysis

Data management was performed to harmonise and amalgamate datasets from all clusters. This process has previously been described in detail and published [15]. The approach for multiple imputation of missing data is summarised in the S2 Appendix (page 5).

Characteristics of the individual participants in the prerandomisation and trial outcome period were summarised for each trial arm using means and standard deviations, medians and interquartile ranges or frequencies and percentages, as appropriate. These results are reported using imputed data, where available; results from available case analyses are provided in the Supporting information.

Main analyses

The primary analysis was performed using a modified intention to treat (mITT) approach. This involved excluding any cluster in the intervention arm that did not contact the GAP provider to initiate implementation of the intervention due to changes in local strategy, since such changes are not considered informative of how GAP would have performed in the cluster. Due to the modest number of clusters, the analysis was performed using an unweighted 2-stage cluster-summary statistical approach [23]; detailed description provided in S2 Appendix (page 6). Intervention effects (absolute difference of intervention minus standard care arm) are presented with 95% CIs. A sensitivity analysis was also performed at the request of reviewers, excluding 1 cluster without ultrasound measurement data for the baseline period, which are imputed in our main analysis (S2 Appendix; page 5).

Prespecified secondary, subgroup, and sensitivity analyses

A secondary analysis was planned using a per protocol approach restricting analysis of the intervention arm to clusters that complied with the GAP preimplementation requirements (S1 Protocol; page 74) in full. A further secondary analysis was a full intention to treat (ITT) analysis in which data from all clusters were used as randomised, irrespective of whether or not GAP was implemented. A prespecified subgroup analysis was planned to explore the effect of the intervention on 21 clinical and neonatal outcomes, only in SGA infants. A sensitivity analysis explored the intervention effect when restricted only to women who had an ultrasound scan between 18+0 and 24+0 weeks (presumed fetal anomaly scan) at the cluster where she later gave birth, reflecting antenatal care primarily within a single cluster and consistent exposure to the intervention from 24 weeks. A reviewer requested a further post hoc sensitivity analysis of the stillbirth outcome, concerned that our 2-stage analysis approach may be unsuitable for rare outcomes. After preferred 1-stage methods were found unfeasible or did not converge, we applied the standard logistic regression approach but with robust standard errors to acknowledge clustering (see S2 Appendix, page 6 for details). We use the standard 5% significance level for testing across our secondary outcomes and subgroup and sensitivity analyses. Due to multiple testing, significant results for secondary outcomes should be treated with caution.

These analyses were conducted following a prespecified analysis plan (S1 Appendix). All prespecified subgroup and sensitivity analyses were detailed in the trial protocol (S1 Protocol) and approved by the trial steering committee. This study has been reported as per the Consolidated Standards of Reporting Trials (CONSORT) statement (S1 CONSORT Checklist).

Sample size calculation

The power calculation for this study determined a minimum target sample size of 12 clusters (6 per arm) based on information collected during protocol development [13]. We were unable to identify reports of an intracluster correlation coefficient for detection of SGA; therefore, a coefficient of the most approximate outcome (rate of fetal growth restriction) was used (0.019) [24]. A cluster size that included an average of 126 SGA infants (defined by customised and population centile charts) with 6 clusters per arm provides 84% power to detect an improvement in the detection of SGA, assuming 20% are detected using standard care and 33% detected using GAP (doubling of odds ratio for detection) at the 5% significance level (2-sided test) [13]. We made no explicit allowance for the additional baseline data from each cluster, their inclusion is likely to increase power. Power calculations were performed using the user-written programme “clustersampsi” for Stata.

Protocol changes

The trial protocol was amended during the study period for logistical and methodological reasons, including changes to data flow and storage, and following a change to the trial sponsor in 2017. A further change occurred prior to the randomisation of recruited clusters, whereby the definition of the primary outcome was refined. The registration of this change was delayed until after randomisation because of the change in study sponsor. Nevertheless, the amendment was approved before any women included in the primary analysis had given birth. These and other minor study amendments are recorded in the current version of the study protocol (S1 Protocol). All amendments were approved by the Research Ethics Committee and participating sites’ Research and Development departments. Approval was also sought from the trial steering committee, Confidentiality Advisory Group and funders, where appropriate. During data management and analysis, the definition of major neonatal morbidity changed in relation to the study protocol, as the data was insufficiently detailed to determine Bell stage of necrotising enterocolitis, culture status in sepsis, and need for ophthalmic intervention related to retinopathy.

Ethical approval

Ethical approval for this trial was obtained from the Health Research Authority (HRA) through the London Bloomsbury Research Ethics Committee (Ref. 15/LO/1632) and the Confidentiality Advisory Group (Ref. 15/CAG/0195). Individual informed consent was not obtained, but women could request to opt out from sharing their data. A key professional for each cluster provided written cluster consent prior to randomisation.

Patient and public involvement

Patient groups and stakeholders (representing both PPI and professional groups) were involved from the conceptualisation of this study. Patient groups were provided with a summary for the study and procedures in lay terms and asked their opinion about key points including the relevance of the study and the use of data without individual informed consent given the cluster intervention/design. Their feedback was used to inform the final study protocol and ethical application. Stakeholders such as Stillbirth Clinical Study Group from RCOG, SANDS Charity, and Tommy’s Charity were also involved in the conceptualisation of this study. We have a patient representative in our coinvestigator group who has provided their perspective throughout the study, including in interpretation and explanation of results to a lay audience.

Results

Among the 16 sites that were invited to participate in the trial, 13 were willing and enrolled in the study (Fig 1). Seven clusters were allocated to the intervention and 6 to standard care. Two sites randomised to the intervention did not contact the GAP provider to initiate implementation. The median washout period was 17 months (range 11 to 18), this included a median 9 months (range 6 to 12 months) interval between antenatal booking of women (presumed to be at 12 weeks) with the opportunity of exposure to GAP until commencement of the outcome period. Among the 209,314 pregnancies during the study period in the 13 participating sites, 201,209 were included in the study. For the primary analysis (mITT), the outcome period included 13,810 pregnancies in the standard care arm (6 clusters) and 11,096 pregnancies in the intervention arm (5 clusters). No women asked for their data to be excluded from the study.

Fig 1

Study population (CONSORT flow diagram).

GAP, Growth Assessment Protocol; ITT, intention to treat; mITT, modified intention to treat.

Demographic characteristics are provided in Table 2. In the prerandomisation period, age, height, and weight were broadly similar between trial arms, but there were fewer women: of white ethnicity (55.9% versus 62.8%), with obesity (15.7% versus 18.1%), and in the first (least deprived) quintile of Index of Multiple Deprivation (7.6% versus 17.4%) in the intervention arm than the standard care arm. Similar findings were observed in the outcome period. Demographic characteristics were also broadly similar using available case data (for variables that were imputed) and the ITT sample (13 clusters) (Tables A and B in S3 Appendix). A description of the full list of ethnicities used for the customised centiles calculator is provided in Tables C and D in S3 Appendix. There were 4 tertiary level clusters in the trial; these were balanced by randomisation of 2 clusters to each of the 2 trial arms.

Table 2

Clinical and sociodemographic characteristics according to treatment allocation (modified intention to treat analysis).

	Prerandomisation period		Outcome period
	Standard Care (n = 29,404)	Intervention (GAP) (n = 26,546)	Standard Care (n = 13,810)	Intervention (GAP) (n = 11,096)
Imputed data
Age at conception (years), median (IQR)	31.6 (27.5, 35.2)	31.5 (27.6, 35.2)	32.0 (27.9, 35.4)	31.8 (27.9, 35.5)
Ethnicity, %
White	62.8	55.9	62.7	56.2
Black	16.2	12.7	15.1	12.6
Asian	13.3	19.4	13.5	20.3
Mixed	2.1	1.9	2.6	1.6
Other	5.5	10.1	6.1	9.2
Index of Multiple Deprivation Quintiles, %
1 (Least deprived)	17.4	7.6	16.5	7.5
2	12.5	10.8	12.7	10.6
3	16.1	23.2	16.6	23.6
4	28.5	34.7	28.7	35.4
5 (Most deprived)	25.4	23.7	25.5	22.9
Maternal Height (m), median (IQR)	1.64 (1.60, 1.69)	1.64 (1.59, 1.68)	1.64 (1.60, 1.69)	1.64 (1.60, 1.68)
Maternal Weight (kg), median (IQR)	66.0 (59.5, 76.0)	65.6 (57.4, 74.0)	67.0 (59.5, 77.9)	65.4 (58.0, 76.0)
Body Mass Index Categories, %
<18.5	3.9	4.1	3.4	3.4
(18.5–24.9)	50.1	53.9	47.2	51.6
(25.0–29.9)	28.0	26.3	29.5	27.2
(30.0–34.9)	11.9	10.5	13.1	11.3
(35.0–39.9)	4.2	3.5	4.6	4.4
≥40.0	2.0	1.7	2.2	2.1
Parity, %
Nulliparous	46.4	59.0	47.5	51.6
1	33.8	26.3	34.0	30.3
2	11.6	9.4	11.0	11.1
3	4.6	3.2	4.2	4.2
4 +	3.7	2.2	3.3	2.9
Nonimputed data
Smoking in pregnancy, % (n)	5.8 (1,646/28,252)	5.2 (1,090/21,149)	5.2 (698/13,466)	5.7 (569/10,010)
Missing smoking, n	1,152	5,397	344	1,086
Preexisting comorbidities, % (n)
Hypertension	2.0 (379/19,324)	1.5 (303/20,162)	1.3 (119/9,276)	1.4 (130/9,189)
Missing hypertension, n	10,080	6,384	4,534	1,907
Diabetes	0.9 (162/18,511)	2.5 (497/20,162)	1.0 (94/9,153)	3.4 (299/8,862)
Missing diabetes, n	10,893	6,384	4,657	2,234
Systemic Lupus Erythematous	0.18 (35/19,344)	0.03 (7/20,154)	0.17 (16/9,294)	0.02 (2/8,521)
Missing SLE, n	10,060	6,392	4,516	2,575
Antiphospholipid Syndrome	0.05 (9/19,285)	0.00 (0/11,629)	0.05 (5/9,294)	0.00 (0/4,904)
Missing APS, n	10,119	14,917	4,516	6,192
Pregnancy comorbidities, % (n)
Gestational diabetes	3.5 (833/23,957)	6.2 (1,242/20,087)	6.3 (713/11,416)	8.1 (707/8,699)
Missing GDM, n	5,447	6,459	2,394	2,397
Gestational hypertension	1.7 (308/18,506)	2.6 (401/15,215)	1.2 (136/11,418)	3.4 (219/6,498)
Missing Gest HT, n	10,898	11,331	2,392	4,598
Pre-eclampsia	0.7 (132/18,504)	1.8 (368/20,150)	1.2 (100/8,663)	2.4 (216/9,185)
Missing Pre-eclampsia, n	10,900	6,396	5,147	1,911
Eclampsia	0.29 (54/18,504)	0.09 (10/11,372)	0.30 (26/8,663)	0.08 (4/4,827)
Missing Eclampsia, n	10,900	15,174	5,147	6,269
Infant sex, male, % (n)	51.3 (15,086/29,397)	51.3 (13,586/26,494)	51.1 (7,053/13,798)	50.7 (5,590/11,023)
Missing Infant sex, n	7	52	12	73

Data are % (n/N); mean (SD); or median (IQR), unless otherwise specified. Where multiple imputation was used numbers are not provided, only percentages.

APS, Antiphospholipid Syndrome; GAP, Growth Assessment Protocol; GDM, gestational diabetes; Gest HT, gestational hypertension; SLE, Systemic Lupus Erythematous.

The proportion of women with an EFW measured by ultrasound after 24 weeks was similar in the intervention and standard care arms during the outcome period (64.0% versus 75.7%; unadjusted difference −11.7%, 95% CI −31.0% to 7.6%; adjusted difference −10.0%, 95% CI −36.2% to 16.1%; adjusted for baseline, age, ethnicity, parity, and stratification factor). In the prerandomisation period, the respective rates were 62.0% versus 43.7% (Table 3). Timing of ultrasound scan after 24 weeks (i.e., utilisation per week of gestation) was broadly similar between trial arms in the outcome period (Fig 2). A common pattern of offering scans at 28, 32, and 36 weeks was observed in both standard care and intervention arms. In the prerandomisation period, a higher proportion of scans at 36 weeks was observed in the intervention arm compared to standard care; no clear difference was observed in other gestations.

Table 3

Utilisation of ultrasound services according to treatment allocation (mITT analysis).

	Prerandomisation period		Outcome period		Intervention effect size—unadjusted (95% CI)	Intervention effect size—adjusted* (95% CI)	p-value
	Standard Care (n = 29,404)	Intervention (GAP) (n = 26,546)	Standard Care (n = 13,810)	Intervention (GAP) (n = 11,096)
Ultrasound
Proportion of pregnancies with a scan between 18+0 and 24+0 weeks, % (n)	66.2 (19,473/29,404)	82.2 (21,807/26,546)	88.4 (12,212/13,810)	84.2 (9,344/11,096)	−3.7 (−11.6, 4.3)	−10.7 (−36.7, 15.3)	0.35
Proportion of pregnancies with a scan after 24+0 weeks, % (n)	45.1 (13,273/29,404)	60.7 (16,111/26,546)	77.3 (10,677/13,810)	66.1 (7,331/11,096)	−8.4 (−24.9, 8.1)	−12.6 (−32.6, 7.5)	0.18
Proportion of pregnancies with a scan after 24+0 weeks with EFW, % (n)†	43.7 (12,860/29,404)	62.0 (11,629/18,751)	75.7 (10,450/13,810)	64.0 (5,145/8,043)	−11.7 (−31.0, 7.6)	−10.0 (−36.2, 16.1)	0.35
Number of scans per pregnancy after 24+0 weeks with EFW, mean (SD)	0.9 (1.3)	1.2† (1.3)	1.5 (1.3)	1.5† (1.4)	−0.1† (−0.8, 0.6)	−0.2† (−0.6, 0.1)	0.14
Proportion of pregnancies with no record of ultrasound, % (n)	27.1 (7,961/29,404)	11.8 (3,121/26,546)	5.8 (794/13,810)	9.2 (1,015/11,096)	2.2 (−5.9, 10.3)	2.6 (−5.3, 10.6)	0.45

Data are % (n/N) or mean (SD), unless otherwise specified. Effect size provided are differences (intervention minus standard care arm) for the outcome period. 95% CIs and p-values are derived from linear regression where the dependent variable for each outcome was the adjusted cluster summary; p-values are reported only for the adjusted analysis.

CI, confidence interval; EFW, estimated fetal weight using ultrasound; mITT, modified intention to treat.

* Adjusted for baseline, age, ethnicity, parity, and stratification factor.

† Excludes 2 clusters.

Fig 2

Ultrasound utilisation per week of gestation in standard care and intervention arms during the prerandomisation and comparison periods.

SGA, small for gestational age. *Pregnancies for which SGA screening remained relevant for each week gestation was defined as ongoing pregnancies (undelivered) that had not been antenatally detected as SGA (growth scans with estimated fetal weight >10th centile or no growth scans) up to that gestational age.

The primary outcome of antenatal detection of SGA infants by both customised and population centiles was similar between trial arms (unadjusted difference intervention minus control 1.2%, 95% CI −7.5% to 9.8%; adjusted difference intervention minus control 2.2%, 95% CI −6.4% to 10.7%; adjusted for baseline, age, ethnicity, parity, and stratification factor), as was the test positive rate (unadjusted difference 0.9%, 95% CI −0.6% to 2.5%; adjusted difference 0.8%, 95% CI −0.8% to 2.3%; adjusted for baseline, age, ethnicity, parity, and stratification factor) (Table 4). The association between antenatal detection of SGA at baseline and the comparison period across clusters is displayed in Fig J in S3 Appendix). Measures of diagnostic test performance (antenatal detection, false positive rate, positive predictive value, and negative predictive value) when SGA at birth is defined by customised centiles or by population centiles are provided in Table 4; there were no differences in antenatal detection between trial arms. There were also no differences in the rates of primary and secondary outcomes in most of the prespecified secondary and sensitivity analyses (Tables E, F, and G in S3 Appendix). In the full ITT analysis, the unadjusted difference (intervention minus control) for the primary outcome was −4.0% (95% CI −14.8% to 6.8%), and the adjusted difference was −3.5% (95% CI −14.0% to 7.0%; p = 0.52). There was no difference in the primary outcome in the sensitivity analysis excluding 1 cluster without ultrasound measurement for the prerandomisation period (adjusted difference intervention minus control 2.4%, 95% CI −6.1% to 10.8%; p = 0.58); results were in keeping with the main analysis. All minimum requirements for GAP compliance prior to “going live” were met except the e-learning target, which was only met in 1 cluster; therefore, per protocol analysis could not be performed. The intracluster correlation coefficient observed in the outcome period for mITT analysis was 0.008 (95% CI 0.002 to 0.039).

Table 4

Screening performance according to treatment allocation (mITT analysis).

	Prerandomisation		Outcome period		Intervention effect size—unadjusted (95% CI)	Intervention effect size—adjusted* (95% CI)	p-value
	Standard Care (n = 29,404)	Intervention (GAP) (n = 26,546)	Standard Care (n = 13,810)	Intervention (GAP) (n = 11,096)
Primary outcome (SGA by customised and population centiles)
Proportion of SGA (birthweight), %	7.2	7.6	7.2	7.6	-	-
Antenatal detection of SGA, %	19.1	24.4	27.7	25.9	1.2 (−7.5, 9.8)	2.2 (−6.4, 10.7)	0.62
Test positive rate, %	2.4	3.2	3.4	3.7	0.9 (−0.6, 2.5))	0.8 (−0.8, 2.3)	0.35
Secondary outcomes
SGA by customised centiles
Proportion of SGA (birthweight), %	11.2	11.0	11.6	12.2	-	-	-
Antenatal detection of SGA, %	14.9	19.7	21.5	22.3	2.9 (−3.2, 8.9)	3.2 (−3.1, 9.4)	0.32
Specificity†, %	99.2	98.9	99.0	98.9	-	-	-
Positive predictive value‡, %	68.9	67.1	73.3	72.9	-	-	-
Negative predictive value‡, %	90.2	90.7	90.6	89.8	-	-	-
False positive rate†, %	0.9	1.1	1.0	1.1	0.4 −0.4, 1.2)	0.3 (−0.5, 1.1)	0.41
False negative rate, %	85.2	80.3	78.6	77.7	-	-	-
SGA by population centiles
Proportion of SGA (birthweight), %	8.6	9.7	8.5	9.4	-	-	-
Antenatal detection of SGA, %	17.1	21.3	25.0	21.5	−0.5 (−9.1, 8.0)	0.8 (−7.0, 8.7)	0.83
Specificity†, %	99.0	98.8	98.6	98.2	-	-	-
Positive predictive value‡, %	60.9	64.2	62.5	54.8	-	-	-
Negative predictive value‡, %	92.7	91.8	93.4	92.1	-	-	-
False positive rate†, %	1.0	1.2	1.4	1.9	0.9 (−0.2, 2.1)	0.8 (−0.3, 1.8)	0.14
False negative rate, %	82.9	78.7	75.0	78.5	-	-	-

Data are % (n/N), unless otherwise specified. Where multiple imputation was used, numbers are not provided, only percentages. Effect size provided are differences (intervention minus standard care arm) for the outcome period. 95% CIs and p-values are derived from linear regression where the dependent variable for each outcome was the adjusted cluster summary; p-values are reported only for the adjusted analysis.

CI, confidence interval; GAP, Growth Assessment Protocol; mITT, modified intention to treat; SGA, small for gestational age infant.

* Adjusted for baseline, age, ethnicity, parity, and stratification factor.

† Excludes 1 cluster.

‡ Prerandomisation values exclude 2 clusters, but outcome period excludes only 1 cluster.

There were 2 statistically significant differences among the 26 secondary outcomes explored. When compared to standard care, the intervention was associated with a lower rate of overall stillbirth (unadjusted difference −0.05%, 95% CI −0.21% to 0.11%; adjusted difference −0.07%, 95% CI −0.14% to −0.01%; i.e., 0.7 fewer stillbirths per 1,000 births; adjusted for baseline, age, ethnicity, parity, and stratification factor) and of perinatal mortality (unadjusted difference −0.05%, 95% CI −0.27% to 0.17%; adjusted difference −0.09%, 95% CI −0.17% to −0.004%; i.e., 0.9 fewer perinatal deaths per 1,000 births; adjusted for baseline, age, ethnicity, parity, and stratification factor) (Table 5). The post hoc sensitivity analysis of stillbirth led to an unadjusted odds ratio (95% CI) for the intervention effect of 1.30 (95% CI 0.68 to 2.47), and adjusted odds ratio of 0.77 (95% CI 0.30 to 1.99); we do not attempt to reexpress this effect as a difference between arms as the methodology to do so with imputed data is not yet established.

Table 5

Secondary clinical outcomes according to treatment allocation (mITT analysis).

	Prerandomisation period		Outcome period		Intervention effect size—unadjusted (95% CI)	Intervention effect size—adjusted* (95% CI)	p-value
	Standard Care (n = 29,404)	Intervention (GAP) (n = 26,546)	Standard Care (n = 13,810)	Intervention (GAP) (n = 11,096)
Maternal outcomes
Induction of labour, %	25.1	26.3	26.9	29.5	2.8 (−4.2, 9.8)	1.7 (−0.4, 3.8)	0.11
Mode of birth, %
Spontaneous vaginal delivery	58.1	58.7	54.5	54.0	1.5 (−4.5, 7.5)	-0.1 (−2.6, 2.4)	0.94
Operative vaginal delivery	13.7	15.3	14.1	14.4	0.3 (−3.1, 3.6)	-0.1 (−1.6, 1.4)	0.87
Elective cesarean section	12.3	12.2	13.9	14.6	−0.9 (−5.7, 3.8)	−0.6 (−1.5, 0.4)	0.24
Emergency cesarean section	15.6	13.6	17.2	16.7	−0.8 (−4.4, 2.8)	0.6 (−1.6, 2.8)	0.59
Postpartum haemorrhage (>1,500 mls), %	2.7	2.3	2.7	2.5	−0.4 (−1.2, 0.3)	−0.1 (−0.5, 0.3)	0.66
Third/fourth degree tears, %	2.2	2.4	1.9	1.8	0.0 (−0.8, 0.7)	−0.1 (−0.6, 0.4)	0.78
Epidural, %	36.5	27.9	36.4	28.2	−13.0 (−33.7, 7.7)	5.6 (−1.4, 12.7)	0.12
Episiotomy, %	17.7	23.1	17.6	21.8	16.4 (−10.1, 43.0)	−2.3 (−6.4, 1.9)	0.28
Neonatal outcomes
Gestational age at birth, weeks mean (SD)	39.5 (2.0)	39.5 (2.0)	39.4 (1.9)	39.4 (2.0)	−0.1 (−0.2, 0.1)	0.0 (−0.1, 0.1)	0.80
Preterm birth (<37 weeks), %	5.6	6.0	6.1	6.4	0.3 (−1.3, 1.8)	0.0 (−0.8, 0.9)	0.94
Birthweight (g), mean (SD)	3,348 (559)	3,325 (558)	3,326 (552)	3,297 (567)	−24.1 (−87.2, 39.0)	−7.7 (−21.9, 6.4)	0.28
Condition at birth
Apgar score <7 at 5 minutes, %	2.0	1.9	2.2	1.7	−0.5 (−1.1, 0.1)	−0.2 (−0.4, 0.1)	0.29
Arterial cord pH <7.1, %	2.3	2.8	2.0	2.9	0.7 (−1.0, 2.4)	0.3 (−0.4, 1.0)	0.44
Respiratory support at birth, %	4.4	6.3	4.1	4.8	1.2 (−3.5, 5.8)	−1.0 (−2.7, 0.7)	0.26
Neonatal admissions
Neonatal unit admission (inc HDU and SCBU), %	14.9	8.1	16.2	7.4	−8.3 (−27.5, 10.8)	0.4 (−0.8, 1.7)	0.48
Major neonatal morbidity
Any major neonatal morbidity, %	4.5	6.2	5.5	4.7	−1.5 (−4.9, 1.8)	−1.2 (−3.4, 1.0)	0.28
Any neonatal brain injury (HIE + IVH), %	0.44	0.44	0.41	0.34
Supplementary O2 >28 days, %	0.16	0.16	0.09	0.15
Necrotising enterocolitis, %	0.18	0.15	0.12	0.08
Sepsis, %	4.50	6.13	5.37	4.60
Retinopathy of prematurity, %	0.11	0.12	0.17	0.06
Minor Neonatal morbidity
Any minor neonatal morbidity, %	2.8	4.5	2.6	3.0	0.5 (−1.4, 2.4)	−0.0 (−1.6, 1.5)	0.96
Hypothermia, %	0.14	0.41	0.17	0.14
Hypoglycaemia, %	1.43	1.72	1.19	0.86
Nasogastric feeding, %	2.37	3.62	1.98	2.62
Perinatal loss
Stillbirth, %	0.30	0.40	0.36	0.31	−0.05 (−0.21, 0.11)	−0.07 (−0.14, −0.01)	0.03
Neonatal death, %	0.07	0.13	0.04	0.07	0.01 (−0.08, 0.10)	−0.02 (−0.08, 0.04)	0.56
Perinatal mortality, %	0.37	0.49	0.41	0.37	−0.05 (−0.27, 0.17)	−0.09 (−0.17, −0.004)	0.04

Data are % (n/N) or mean (SD), unless otherwise specified. Where multiple imputation was used, numbers are not provided, only percentages Effect size provided are differences (intervention minus standard care arm) for the outcome period. 95% CIs and p-values are derived from linear regression where the dependent variable for each outcome was the adjusted cluster summary; p-values are reported only for the adjusted analysis.

CI, confidence interval; GAP, Growth Assessment Protocol, HDU, high dependence unit; HIE, hypoxic ischemic injury; IVH, intraventricular haemorrhage; mITT, modified intention to treat; SCBU, special care baby unit; O2, oxygen.

* Adjusted for baseline, age, ethnicity, parity, and stratification factor.

In the subgroup analysis of outcomes for SGA infants (defined by both population and customised centiles; n = 1,802 pregnancies of which 31 were stillborn), SGA infants in the intervention arm were born 2 days earlier, had a lower mean birthweight, and lower rates of stillbirth compared to SGA infants from standard care (Table 6). There were no differences in other neonatal or maternal outcomes in the subgroup analysis, including preterm birth (<37 weeks; Table 6) and late preterm birth (34+0 to 36+6 weeks; post hoc analysis, 9.1% versus 8.4% for intervention and standard care arms, respectively; adjusted difference 0.3%, 95% CI −1.9% to 2.6%). The change in mean gestational age at birth reflects fewer SGA babies born at or after 39 weeks in the intervention arm compared to standard care arm (post hoc analysis, 56.3% versus 61.2%; adjusted difference −8.3%, 95% CI −14.9% to −1.7%). Clinical outcomes using available case data and for women with a scan recorded in the cluster between 18+0 and 24+0 weeks are reported in Tables H and I in S3 Appendix, respectively).

Table 6

Subgroup analysis: Clinical outcomes among SGA babies by population and customised according to treatment allocation (mITT analysis).

	Prerandomisation period		Outcome period		Intervention effect size—unadjusted (95% CI)	Intervention effect size—adjusted* (95% CI)	p-value
	Standard Care (n = 2,134)	Intervention (GAP) (n = 1,932)	Standard Care (n = 995)	Intervention (GAP) (n = 807)
Maternal outcomes
Induction of labour, %	33.0	32.2	35.1	36.8	2.1 (−9.2, 13.3)	3.6 (−2.6, 9.8)	0.25
Mode of birth, %
Spontaneous vaginal delivery	54.2	52.2	53.6	48.7	−3.5 (−12.4, 5.3)	−3.3 (−7.4, 0.7)	0.11
Operative vaginal delivery	13.2	15.8	13.2	16.1	3.7 (−1.3, 8.7)	0.6 (−3.0, 4.2)	0.75
Elective cesarean section	9.2	10.3	10.6	9.4	−1.6 (−6.3, 3.1)	−1.7 (−5.1, 1.6)	0.32
Emergency cesarean section	22.6	21.0	21.4	25.3	2.3 (−4.6, 9.2)	2.4 (−0.9, 5.8)	0.16
Postpartum haemorrhage (>1,500 mls), %	1.3	1.4	1.3	1.7	0.4 (−0.6, 1.4)	0.4 (−0.5, 1.3)	0.39
Third/fourth degree tears, %	0.9	1.1	0.8	1.4	1.1 (0.0, 2.3)	1.1 (−0.1, 2.2)	0.08
Epidural, %	36.9	30.6	36.5	29.4	−12.9 (−31.3, 5.5)	−0.8 (−6.7, 5.0)	0.78
Episiotomy, %	17.0	25.3	18.2	22.9	17.6 (−6.0, 41.1)	−4.0 (−8.9, 0.9)	0.11
Neonatal outcomes
Gestational age at birth, weeks mean (SD)	38.9 (3.0)	39.0 (2.9)	38.8 (3.0)	38.6 (3.1)	−0.3 (−0.6, 0.1)	−0.3 (−0.5, −0.1)	0.002
Preterm birth (<37 weeks), %	13.8	12.8	13.7	16.5	3.0 (−1.92, 7.9)	2.3 (−1.5, 6.2)	0.23
Birthweight (g), mean (SD)	2,492 (534)	2,496 (532)	2,482 (550)	2,436 (550)	−55 (−131, 21)	−58 (−99, −18)	0.005
Condition at birth
Apgar score <7 at 5 minutes, %	4.4	5.0	5.2	4.1	−0.9 (−2.53, 0.7)	−0.5 (−1.7, 0.8)	0.45
Arterial cord pH <7.1, %	3.1	3.8	2.8	3.7	0.6 (−1.9, 3.0)	−0.3 (−1.4, 0.8)	0.58
Respiratory support at birth, %	8.6	10.6	7.1	8.0	1.6 (−4.3, 7.5)	−1.3 (−4.4, 1.8)	0.40
Neonatal admissions
Neonatal unit admission (inc HDU and SCBU), %	25.2	17.0	22.9	15.0	−5.3 (−23.4, 12.8)	1.5 (−2.4, 5.4)	0.46
Major neonatal morbidity
Any major neonatal morbidity, %	8.4	11.5	8.4	9.2	0.0 (−4.3, 4.3)	0.5 (−3.2, 4.2)	0.80
Any neonatal brain injury (HIE + IVH), %	1.31	1.03	0.89	1.15
Supplementary O2 >28 days, %	0.66	0.63	0.39	0.46
Necrotising enterocolitis, %	0.94	0.99	0.19	0.35
Sepsis, %	8.27	11.33	8.21	8.95
Retinopathy of prematurity, %	0.39	0.33	0.21	0.10
Minor neonatal morbidity
Any minor neonatal morbidity, %	8.9	12.6	6.3	8.8	3.2 (−1.9, 8.3)	1.9 (−3.1, 6.9)	0.46
Hypothermia, %	0.71	2.16	0.90	0.98
Hypoglycaemia, %	5.62	5.89	3.38	3.18
Nasogastric feeding, %	7.76	10.77	5.21	7.39
Perinatal loss
Stillbirth, %	1.67	1.86	2.19	1.39	−1.03 (−1.88, −0.18)	−0.76 (−1.50, −0.03)	0.04
Neonatal death, %	0.36	0.68	0.18	0.38	0.04 (−0.44, 0.52)	−0.11 (−0.60, 0.38)	0.67
Perinatal mortality, %	2.04	2.24	2.37	1.77	−0.99 (−2.06, 0.08)	−0.69 (−1.47, 0.09)	0.08

Data are % (n/N) or mean (SD), unless otherwise specified. Where multiple imputation was used, numbers are not provided, only percentages. Effect size provided are differences (intervention minus standard care arm) for the outcome period. 95% CIs and p-values are derived from linear regression where the dependent variable for each outcome was the adjusted cluster summary; p-values are reported only for the adjusted analysis.

CI, confidence interval; GAP, Growth Assessment Protocol; HDU, high dependence unit; HIE, hypoxic ischemic injury; IVH, intraventricular haemorrhage; mITT, modified intention to treat; SCBU, special care baby unit; O2, oxygen.

* Adjusted for baseline, age, ethnicity, parity, and stratification factor.

Assessment of implementation (fidelity, dose, and reach) of GAP was performed at all implementing clusters. Implementing sites had guidelines in which concordance to the Perinatal Institute guidance ranged from high to low. All clusters achieved the face-to-face training target, but only 1 cluster achieved the e-learning target. Of the 595 women whose maternity records were reviewed, 84.9% were correctly risk stratified according to GAP guidelines (range between clusters 78.6% to 87.5%) and 88.7% had a GROW chart in their notes (range between clusters 62.2% to 98.3%). Intervention dosage varied; 30.7% (range between clusters 8.2% to 53.2%) of low-risk women had at least the minimum recommended number of fundal height measurements plotted on their GROW chart and 8.5% (range between clusters 0.0% to 16.7%) of women with risk factors for SGA had at least the minimum number of growth scans as recommended by GAP (Table 7). Detailed qualitative data with clinicians and other staff exploring implementation will be reported separately. In the standard care arm, there was wide variation in term of guidance for screening for SGA including variation in timing and interpretation of fundal height measurement, factors indicating high-risk status and number and frequency of ultrasound for high-risk women.

Table 7

Assessment of implementation strength: reach, dose, and fidelity.

Implementation Outcome	Measure of outcome	Overall results	Median cluster score (range)
Fidelity (the extent to which core components were consistently implemented)	Concordance of cluster guidelines for SGA detection to those recommended in GAP	High fidelity (2 clusters), medium fidelity (2 clusters), low fidelity (1 cluster)*
	>75% of staff members from each professional group (midwives, sonographers, obstetricians) trained in face-to-face methods	All 5 clusters compliant
	>75% of staff members from each professional group (midwives, sonographers, obstetricians) trained using e-learning methods	One cluster met training target (4 clusters did not).
	Proportion of women risk stratified according to GAP guidelines	84.9%† (505/595)	84.2% (78.6%–87.5%)
Reach (participation in the intervention by clinicians)	Proportion of women with a GAP-GROW chart in the notes	88.7% (528/595)	94.2% (62.2%–98.3%)
Dose (proportion of each component delivered)	Number of fundal heights plotted for low risk women, median (IQR)‡	3 (2–4)	3 (1–4)
	Proportion of low-risk women with a GROW chart who had at least the minimum expected number of fundal height measurements performed and plotted on GROW‡	30.7% (114/371)	31.4% (8.2%–53.2%)
	Proportion of low-risk women referred for growth scan when definite plot deviation‡	74.2%§ (69/102)	66.7% (40.0%–80.9%)
	Number of fetal growth ultrasound scans completed for high-risk women, median (IQR)‡	3 (2–4)	3 (2–4)
	Proportion of high-risk women with a GROW chart who had at least the minimum expected number of growth scans performed and plotted on GROW‡	8.5% (17/201)	5.3% (0.0%–16.7%)

Data are % (n/N) or median (IQR).

GAP, Growth Assessment Protocol; GROW, Gestation-Related Optimal Weight chart; SGA, small for gestational age.

* High fidelity (only occasional differences where GAP recommendations were partially included); medium fidelity (with partial or no inclusion of GAP recommendations in less than half of the recommendations); low fidelity (with partial or no inclusion of GAP recommendations throughout the guidelines, affecting over half of the recommendations).

† Around 18/90 women who were not correctly risk stratified by GAP guidelines were correctly risk stratified according to local policy.

‡ Risk status is as classified by clinician at booking.

§ Approximately 11.2% (16/102) additional women did have a growth scan, but documented as another indication, e.g., reduced fetal movements.

Discussion

The DESiGN trial has found that GAP was not superior to standard care for the antenatal detection of SGA, confirmed at birth by both population and customised centiles. All intervention clusters achieved the preimplementation requirements for access to GROW software, except for the e-learning target. In intervention clusters, GAP was implemented with varied levels of fidelity (high rates of face-to-face training, varied concordance of cluster site guidelines with GAP, high concordance with GAP risk stratification protocols), high levels of reach (majority of women had a GROW chart), but variable dose (low number of fundal height measurements plotted, number of growth scans below that which is recommended by GAP, high rates of referral for suspected SGA).

To the best of our knowledge, the DESiGN trial is the first randomised control trial that compared the effect of GAP and standard care on the ultrasound-detection of SGA. The intervention was not superior to standard care when implemented in this study setting. It is important to note that at the time of the DESiGN trial, there was concurrent national implementation of the “Saving Babies” Lives’ care bundle, which aimed to reduce rates of stillbirth through 4 components (smoking cessation, risk assessment for and surveillance of fetal growth restriction, raising awareness of reduced fetal movements, and effective fetal monitoring during labour) [18]; this has been shown to increase use of ultrasound and improve the detection of SGA [25]. The outcome period of this trial was in 2018/2019, at least 2 years after the implementation of the care bundle. While the NHS England and NHS Improvement (London) Clinical Leadership Group exempted the 5 London-based clusters in the standard care arm of this study from implementing the care bundle component related to fetal growth restriction during the study period, most units chose to implement at least some of the care bundle strategies. In previous observational studies reporting increased antenatal detection of SGA or reduced stillbirth following GAP implementation, preimplementation groups were not affected by this care bundle. This may explain some of the differences observed in antenatal detection of SGA between this and previous studies; the different study design between this randomised control trial and previous studies, which were all observational, may also explain the different results observed.

Our process evaluation highlights variation in implementation of GAP, which was also reported in the SPiRE Study [25], where 15 of 19 included maternity units had implemented GAP. The SPiRE study group found that most of the 15 local guidelines collected from GAP-implementing sites were only partially compliant with 4 out of 5 components that feature both in the fetal growth restriction element of the Saving Babies’ Lives care bundle and in GAP guidelines [26]. We also observed partial concordance with GAP guidelines in this trial, demonstrated through variable implementation fidelity.

In England, multiparous women are routinely offered fewer antenatal appointments than required for compliance with GAP fundal height measurement frequency, this may partly explain why the number of fundal heights plotted is lower than that recommended by GAP (every 3 weeks). Implementation dose in terms of number of scans conducted for each woman at high risk of SGA was lower than that which is recommended by GAP (3 versus 4 scans for women with term birth). This may be explained by common practice in England whereby serial growth scans are offered at 28, 32, and 36 weeks, rather than 3-weekly. Indeed, post hoc exploration of implementation dose data has shown that 74% of high-risk women in the intervention arm of this study had 2 or more growth scans after 24 weeks, suggesting a less frequent surveillance programme than recommended by GAP. The exploratory analysis of timing of ultrasound utilisation requested by the reviewers/academic editor also supports this hypothesis and describe a similar surveillance pattern in the standard care arm. The costs related to GAP include both the annual charge from the Perinatal Institute to access the programme, training costs, and any potential increase in use of clinical resources; these need to be considered when evaluating utility of GAP. A detailed economic analysis will be reported separately.

We observed a lower rate of overall stillbirth and perinatal mortality, as well as SGA stillbirth in the intervention arm compared to standard care arm during the outcome period. The fact that this was not achieved though the expected pathway of improving detection of SGA at birth, our primary outcome, does raise the possibility of a chance finding, and the finding was not confirmed in the (albeit post hoc) sensitivity analysis. Although we are limited in our ability to ascertain the drivers of this potential effect, it is plausible that the lower proportion of births at or after 39 weeks observed among SGA babies in the intervention arm may have mediated this effect. There is conflicting evidence regarding the benefit of offering earlier iatrogenic birth to women with SGA fetuses as while it may prevent stillbirth/perinatal mortality [27], adversely, it may increase rates of short-term neonatal morbidity and poorer developmental outcomes in childhood [28,29]. Complex interventions such as GAP may have effects that do not necessarily lie on the expected pathway; however, we note the need to replicate these findings before they can be considered robust given the number of secondary outcomes in this study.

We have not performed statistical testing to assess for changes between prerandomisation and outcome period as per prespecified analysis plan; however, we did observe some differences. In particular, the use of ultrasound seems to have markedly increased during the study in standard care clusters, which likely relates to the rollout of the Saving Babies’ Lives care bundle, at least in part. The SPiRe Study reported increased utilisation of ultrasound with implementation of the care bundle; the association was related to the overall care bundle and not to any specific component. Despite exempt from the fetal growth restriction component of the care bundle, clusters in this trial may have increased the utilisation of ultrasound by other related strategies such as the reduced fetal movements component.

The antenatal detection of neonates confirmed to be SGA at birth by customised centiles (secondary outcome) in this study was not higher in the intervention arm, which suggests the choice of growth chart may have limited influence in detection of SGA. Previous observational studies explored the value of customised centiles alone (not as part of GAP). We recognise that these studies have reported that population and customised charts have similar performance in detecting adverse perinatal outcomes after accounting for false positive rates for term births [30] and that the stronger associations between customised centiles and adverse perinatal outcomes (when compared to population centiles) were explained by confounding with preterm birth and maternal obesity [31], even though this is challenged by other authors.

The strength of this study is that, to the best of our knowledge, it is the first randomised trial assessing the effect of the GAP. DESiGN was a pragmatic trial capturing the real-life challenges of implementing complex interventions into clinical care and included a robust process evaluation and examination of implementation strength and variability. The trial has primarily used data from routinely collected electronic patient records, which has allowed cost-efficient inclusion of data from a large number of pregnancies. The primary outcome was antenatal ultrasound detection of SGA (after 24 completed weeks). We defined this as infants who are SGA (i.e., birthweight less than 10th centile) according to (i) population (UK1990 birthweight centiles) and (ii) customised (GROW) charts; this is considered to identify those at highest risk of adverse perinatal outcomes [32]. This is an important strength as both GAP and standard care target the detection of these infants.

We were unable to assess the impact of complete attainment of the GAP preimplementation requirements because only 1 implementing cluster achieved the training target for e-learning. The optimal interval between commencing GAP use and assessment of its effect is unknown. This study had a median interval of 9 months (range 6 to 12) from antenatal booking of women with the opportunity of exposure to GAP until commencement of outcome data collection. While the learning process of care providers may delay full programme effectiveness, an alternative “pioneering effect” may be working in the opposite direction [33]. Other limitations include issues related to the availability, or format, of data that are inherent in the use of routinely collected data, though we followed clear protocols in harmonisation and linkage of data from multiple electronic systems to minimise any variations in data quality between the randomised arms [15]. Missingness for characteristics (including customisation factors) was dealt with by multiple imputation, which is dependent on the assumption that results after inclusion of variables in the imputation model will be consistent between those with and without missing data. It is unlikely that randomisation to GAP or standard care would alter completeness of routine data collection in any cluster; therefore, this assumption is likely to be met. Ethnicity documented in hospital systems was often not as granular as that required by the customised calculator. One prespecified subgroup analysis exploring the effect of intervention in women stratified as high risk and low risk separately was not possible given lack of detailed data on some risk factors used to stratify women. The number of units randomised was modest and power was somewhat reduced by the failure of 2 units to contact the provider of GAP leading to their exclusion from our main analyses; however, the observed intracluster correlation coefficient was lower than that assumed for the power calculation; this would have preserved power to some extent.

We are not aware of other studies of GAP implementation that report as detailed assessment of the standardised implementation outcomes (fidelity, reach, and dose) as that performed in this trial [19], and by which we can benchmark these findings. While it is possible that the variable dose of implementation may explain the results of this trial, DESiGN was a pragmatic trial intended to reflect implementation in the real world. It is therefore possible that the implementation variability seen in this trial reflects the reality of implementing a complex intervention in a health service with competing needs on resources. A recent observational study of GAP implementation across the UK also described variation in implementation using nonstandardised outcomes. Their analysis demonstrated a greater reduction of stillbirth rates in maternity units that had completely implemented GAP (defined by reporting the birthweight and outcomes of more than 75% of births via the GAP online tool) compared with those that did not implement GAP [34]. A third of maternity units (31%; n = 29/94) implementing GAP achieved only partial implementation. The rate of stillbirth was no different between maternity units with partial or no implementation of GAP. The collective evidence from these studies highlights the challenges and variation in implementation of GAP.

This pragmatic study provides the only evidence from a randomised control trial regarding the effect of GAP, to the best of our knowledge. The GAP programme was not superior to standard care in the detection of SGA at birth by both population and customised centiles in this setting. Given the variable implementation observed, it is imperative that future studies assessing implementation of GAP or other interventions to improve perinatal outcomes, use standardised implementation outcomes (fidelity, reach, and dose) in order to determine the generalisability of our findings, identify barriers to implementation, and hence better inform policy for improving perinatal outcomes.

Dissemination to participants and related patient and public communities

Participating institutions and maternity units will be informed of the results soon after acceptance and any embargo period. We expect participating maternity units to share results locally in their communities aiming to also reach women that were pregnant during the study period. We will communicate with relevant stakeholders including SANDS and Tommy’s Charities. The main results of the current research will also be disseminated to related patients and the public through blogs, press releases, newspapers, and conferences.

The DESiGN trial Study Protocol.

(DOCX)

Click here for additional data file.

Statistical analysis plan.

(DOCX)

Click here for additional data file.

Additional methodology.

(DOCX)

Click here for additional data file.

Supplementary tables and figures.

(DOCX)

Click here for additional data file.

CONSORT Statement Checklist.

(DOCX)

Click here for additional data file.

15 Sep 2021

Dear Dr Vieira,

Thank you for submitting your manuscript entitled "Effect of the Growth Assessment Protocol (GAP) on the detection of small for gestational age: the DESiGN cluster randomised trial." for consideration by PLOS Medicine.

Your manuscript has now been evaluated by the PLOS Medicine editorial staff as well and I am writing to let you know that we would like to send your submission out for external peer review. Before doing so, we will require clarification regarding the start date of the trial (specified as November 2015 in the Abstract, and November 2016 in the Methods) since PLOS Medicine requires that all trials are prospectively registered. It would be appreciated if you could contact me directly by email lgaynor@plos.org with this information as soon as possible.

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Louise Gaynor-Brook, MBBS PhD

Associate Editor, PLOS Medicine

27 Oct 2021

Dear Dr. Vieira,

Thank you very much for submitting your manuscript "Effect of the Growth Assessment Protocol (GAP) on the detection of small for gestational age: the DESiGN cluster randomised trial." (PMEDICINE-D-21-03941R1) for consideration at PLOS Medicine.

Your paper was evaluated by four independent reviewers, including a statistical reviewer, and was discussed among all the editors here and with an academic editor with relevant expertise. The reviews are appended at the bottom of this email and any accompanying reviewer attachments can be seen via the link below:

[LINK]

In light of these reviews, I am afraid that we will not be able to accept the manuscript for publication in the journal in its current form, but we would like to consider a revised version that addresses the reviewers' and editors' comments. Obviously we cannot make any decision about publication until we have seen the revised manuscript and your response, and we plan to seek re-review by one or more of the reviewers.

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Comments from the Academic Editor:

This was a very challenging study and unfortunately has limited implications for practice due to the significant logistical challenges. That said it includes some very important messages and articulates many of the challenges associated with complex intervention implementation, and there are important lessons for future studies in this area. There are several issues highlighted by the reviewers which need additional attention - particularly the issue around standard care and the fact that ultrasounds use went up only in the standard care arm. Further detail on the timing of USS scan and detail on acquisition and more importantly validation of the primary outcome is also required.

Requests from the editors:

General comments:

Throughout the paper, please adapt reference call-outs to the following style: "... for high income countries [2,3]." (noting the absence of spaces within the square brackets).

Data availability:

PLOS Medicine requires that the de-identified data underlying the specific results in a published article be made available, without restrictions on access, in a public repository or as Supporting Information at the time of article publication, provided it is legal and ethical to do so. Since the data are not freely available, please provide an appropriate contact (web or email address) for enquiries (please note that this cannot be a study author).

Title: Please revise your title according to PLOS Medicine's style. Please place the study design in the subtitle (ie, after a colon). We suggest “Evaluation of the Growth Assessment Protocol (GAP) for antenatal detection of small for gestational age: the DESiGN cluster randomised trial” or similar

Please remove the study summary (lines 56-71) and replace with an Author Summary (see below) to follow your Abstract.

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In the last sentence of the Abstract Methods and Findings section, please describe 2-3 of the main limitations of the study's methodology."

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Please begin your Abstract Conclusions with "In this study, we observed ..." or similar, to summarize the main findings from your study, without overstating your conclusions. Please emphasize what is new and address the implications of your study, being careful to avoid assertions of primacy.

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Line 223 - please clarify what is meant by ' The utilisation of ultrasound has also been described’

Results:

Please provide the actual numbers of events for the outcomes (this may be in the Tables, and not necessarily each time they're mentioned).

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Please remove all subheadings within your Discussion e.g. Main findings

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Comments from the reviewers:

Reviewer #1: Thank you for allowing me to review the submitted manuscript. The authors are to be commended on try to prospectively study such a complex intervention at scale. There are however a few areas of concern that I think need to be addressed.

Methodololgy

-Despite reading reading this section several times I'm still nor entirely certain how the antenatal detection rate was devised. Was this from retrospective plotting of utlrasound EFWs onto chart or from a sample of notes. For readers to form opinions on the study then this section needs to be very clear and unambigous which it is not in my view currently.

-Standard care. There is no attempt to define what GAP is being compared and it is therefore difficult to judge whether GAP had a realistic chance of success (see below) following intervention. In my view the authors should provide more detail on what standard care is and whether this was within certain parameters or very variable. It is interesting to note that the standard care arm seemed to changes more significantly in terms of scan frequency than the GAP arm. There is also no attempt to describe whether units were secondary or tertiary or involved in other measures to improve SGA detection.

Results

The primary outcome table 3 is not very easy to read or interpret in its current format and I would suggest reviewing the row legends.

Is there any capacity to perform a sensitivity analysis using scans performed within 3 weeks of birth rather than performed throughout the 3rd trimester.

Discussion

Whilst the populations are similar there are some signficant differences and these are not discussed. From my reading of table 1 it would appear that the sites where the intervention occurred had more pakistani women and this might potentially allter the sensitivity of grow/standard care.

Table 2 demonstrates some surprising findings that are difficult to understand/believe for example the number of women not receiving anatomy scans between 18-24 weeks seems very low. There is also a huge increase in >24 weeks scan frequency in the standard care arm which is not even mentioned. This increase means that 77% of women in standard care have a scan though there is no description of when during the third trimester these scans occur. The big problem here in my mind is that the primary function of GAP is not managing women who are having growth scans, but improving the detection of SGA in low risk women, by more accurately targetting scans. However when scan frequency is so high it seems unlikely any package of measures will have an effect on SGA detection rate. The authors should discuss this as it is a mojor limitation of the primary outcome.

With such high % of scan usuage it is surprising that the detection rate was so low which suggest lots of process problems as briefly discussed in terms of historical scan timing. It is however difficult to judge the effecrtiveness of GAP if the recommended scan frequency has not been implemented. Of interest there does not seem to be a big difference between customised and non-customised outcomes in any metric. This is potentially the most interesting finding as although I'm not convinced the authors have adequately tested GAP, they have demonstrated that customisation does not really make a difference to any outcome. This should be highlighted and discussed in my view.

I note the stillbirth seems lower in the intervention arm, but no mention is made in the discussion about the pre-implementation phrase during which the standard care group had higher levels.

Summary

This study has potential practice chaging findings and I am very keen to see it published, but currently there are some significant changes requred in my view prior to publication.

Reviewer #2: Statistical review

This paper reports a cluster randomised trial investigating implementation of the Growth Assessment Protocol on detection of small for gestational age during pregnancy.

The trial was reported well and I had only minor comments.

1. Abstract "(instead of patients or subjects)" - presume this was leftover text?

2. Abstract - providing a brief summary of the low observed false positive detections of SGA might be of interest to aid interpretation of the results.

3. Page 14 line 314 'with obesity (15.7% vs 18.1%)' I initially read this as restricted to women of white ethnicity - a colon after 'less women' might help avoid misreads.

4. Page 15 line 343 - I feel it should be pointed out here that two marginally significant secondary outcomes out of 26 is consistent with what would be expected by chance if there were no benefit of intervention for any of the outcomes (to be fair the authors do point out this in the methods).

5. Discussion: Table 2 seems to show huge improvements in control clusters during the outcome period, compared to the baseline period. This might be worth reflecting on in the discussion. It wasn't clear to me why there were generally big differences between control and intervention clusters in the pre-randomisation period though?

James Wason

Reviewer #3: This is a well designed and executed study assessing the utility of the GAP program is the detection of fetal growth impairment (Defined as SGA, <10thcentile). The study was complicated by the roll-out of the Safer Baby Bundle, albeit the participating hospitals were exempted. The authors acknowledge that there would have been some contamination from that roll-out.

The methodology is well described and appropriate. The results are appropriately reported.

I would make the following comments:

1. The standard care hospitals appeared to have a significant change in key outcomes from the pre-randomisation phase to the outcome period (ie % pregnancies with 18-24 week scan; % pregnancies with a scan >24 weeks; % pregnancies with a scan >24 weeks +EFW; % pregnancies with no scan). these changes suggest changes in care provision between these two times, in the direction of improved care. The authors don't discuss this effect. Could this not explain why there is no difference in outcome between the two groups of hospitals? A discussion of this would be useful.

2. The authors report tht the rate of stillbirth and perinatal mortality were reduced in the intervention group of hospitals but not the standard care group. What they don't comment on is that the rates fell to those of the standard care hospitals. Nonetheless, this is an important finding. As the authors comment, the whole point of detecting SGA is to reduce stillbirth. I think this finding should be in the Abstract and in the Main Findings section with further discussion in the Implications.

3. The intervention led to earlier birth than standard care. This is a common finding among studies exploring better detection of SGA. Indeed, in this study the false positive rate increased in both groups too. Earlier delivery of SGA, but not false positive AGA, effect has potential to cause longer term cognitive harm. This was recently reported in JAMA (Selvaratnam 2021;326(2):145-153). A comment on the possibility of harm - not just lack of utllity - would be important.

Reviewer #4: This cluster randomized trial evaluated the effectiveness of implementing the GAP program for antenatal detection of SGA births in maternity care hospitals in the UK. The research question is a highly important one, as this program appears to have been widely adopted into routine care across the UK without high-quality evidence of its effectiveness, and findings from this study suggest that the program may not in fact be achieving its intended objective. The trial was a pragmatic one, evaluating the effectiveness of the program as implemented in a real-world setting (as opposed to evaluating the efficacy of the program if implemented under optimal conditions), which is most relevant to informing roll-out of the program nationally and internationally.

The study findings are a challenge to interpret because of several issues arising during the trial, most notably, the concurrent national introduction of the Saving Babies Lives care bundle. The adoption of this care bundle means that the type of care provided to the standard of care comparison group likely changed across the study period, making it unclear to what clinical care settings the adverse outcome rates in the comparison group are generalizable to, and decreasing the value of the information on baseline rates. I do sympathize with the investigators, as the unfortunate timing of introduction of this care bundle was beyond their control, and as a new trial to address this question now seems unlikely, believe the trial nevertheless provides the best available information to help assess the merits of this program.

Main comments

1) My first concern relates to the two stage cluster-summary statistical analysis approach used, primarily as it relates to the less common secondary outcomes. If I understand correctly (without remote access to the textbook cited in the Supporting Information), the first stage of the two-stage cluster analysis calculates a summary value for each site (i.e., a site-specific mean rate (percent) of each outcome), adjusted for the listed covariates, and these rates (percents) are then put into a linear regression model estimating the difference in rate (percent) between treatment and control groups in stage 2. My concern is that for uncommon secondary outcomes, the site-specific rates estimated in step 1 will be very unstable because of low numbers of events at each site. For example, with 11,096 births in the intervention arm, and a stillbirth rate of 3.1 per 1000, there will only be ~34 stillbirths across all 5 intervention sites, meaning that the site-specific rates are being estimated from only 6-7 events per site. One stillbirth more, or less, per site will have an outsized impact on a site's rate, which in turn, will have a major impact on the comparison of rates between sites given the small number of sites.

I am not a trial statistician, but it would seem to me that for rare outcomes, an approach should be chosen that does not depend on accurate estimation of the hospital-specific rates. I agree that a multi-level model might be challenging given the small number of clusters, but is it not possible to build a single model using the original individual-level data that controls for clustering by hospital using GEE (or even an indicator variable for hospital), and uses marginal estimation to calculate risk differences between treatment arms (e.g., as per the approaches compared here: https://bmcmedresmethodol.biomedcentral.com/articles/10.1186/s12874-016-0217-0). Please better justify the choice of analytic approach as it relates to rare outcomes.

2) On a related note, please expand the description of the analytic approach in the Supporting Information to clarify how the two-step approach accounts for differences in cluster sizes. That is, the site-specific rate from a large site will be more precise than that from a small site; were the summary values in the second step weighted to account for the number of births at that site?

3) The amount of missing data in this trial is concerning. Although I agree that using existing hospital databases can be a reasonable strategy for efficiently collecting participant and outcome data for a large number of trial participants, the amount of missing data in this trial was much higher than I typical expect from clinical perinatal databases (e.g., 37% missing values for a key pregnancy complication such as pre-eclampsia during the outcome period in the standard of care group), and for variables that should not have missing data (e.g., vital status at discharge [neonatal mortality, stillbirth], based on the lack of 'n' provided in Table 4). This raises concerns for me about data quality and the appropriateness of multiple imputation given high rates of missingness. What efforts were made to reduce missing data and ensure data quality? Were chart audits considered to eliminate missing data for important health outcomes such as stillbirth and neonatal mortality?

4) The Supporting Information section on data management states, "For one cluster, ultrasound measurement data were not available for the baseline period. The proportion of SGA infants detected antenatally (by both definitions) at baseline for this cluster was imputed based on a model fitted to data from the other clusters predicting the number of infants detected based on the number of pregnancies with an ultrasound scan after 24 completed weeks". Imputing values for an entire site with missing data does not seem like a good solution given the between-site variation observed in the study. Did the study team consider conducting a chart review for a random sample of deliveries from this site to at least have some real data from the site to include in the imputation model? Further, more information on this lack of a key outcome variable seems important given the adjustment for baseline values in the final model: a) was this cluster in the treatment or control group, and b) were sensitivity analyses done excluding this cluster from analyses?

5) While appreciating that an economic analysis is likely beyond the scope of this manuscript, it does seem important to include some mention of the costs of this intervention. If a program is free, shows no evidence of causing harm, and there is a suggestion that it might improve an important health outcome like perinatal mortality, one might argue that it is not unreasonable to still implement the program despite the lack of evidence for its effectiveness, given the potential for benefit. However, if the program uses a meaningful amount of resources, then implementation of this program is much less justifiable, given that it would be detracting resources from other proven interventions. Can the authors comment in general terms on the costs of GAP implementation for those readers less familiar with the program? If implemented outside of the trial setting, does the Perinatal Institute provide its services for free, or are hospitals required to pay for the Institute's support? How much staff time was required/recommended for training and implementation? For ongoing running of the program?

6) The trial findings were not entirely unexpected, given previous literature demonstrating that customised growth charts (the core element of the GAP protocol) are not meaningfully better at identifying high-risk infants than non-customised ultrasound fetal growth charts (customised charts generally only appear to be better at identifying high risk infants when compared to birthweight charts [i.e., charts derived from the weights of live births rather than estimated fetal weights from ongoing pregnancies], which do not reflect the charts used antenatally to monitor fetal growth and are biased at preterm ages because of the correlation between preterm birth and fetal growth restriction). Citing some of this literature in the Discussion, particularly those studies comparing ultrasound estimated fetal weights classified using customised and non-customised standards, seems relevant to help interpret the plausibility of trial findings. E.g., Am J Obstet Gynecol 2018:218:S738-S744; Am J Epidemiol 2011;173:539-543.

Minor comments

1) It would be helpful to include a diagram of the study timeline in the Supplementary Material (pre-intervention, implementation, washout, and outcome collection periods by calendar time at each of the sites) - the description in the main body of the text was somewhat hard to follow, and given the concurrent roll-out of the Saving Babies Lives care bundle, it would be helpful to know the calendar timing of outcome collection at trial sites in relation to this bundle.

2) Please confirm that the study outcomes were included in the imputation models in the description of multiple imputation in the Supporting Information.

3) Presentation of results: an "adjusted difference 2.2%, 95% CI -6.4% to 10.7%" could be interpreted by some to be a relative change (i.e., an increase of 2.2%) rather than an absolute change in percentage points (which I believe is the correct interpretation based on a linear regression model). If so, the authors may wish to rephrase this as "2.2 more SGA infants detected per 100 births" for clarity for this and all outcomes.

4) The stillbirths are of considerable interest, and although the authors were appropriately cautious in interpreting the results for this outcome given the number of secondary analyses conducted, I believe that readers may be tempted to focus on this outcome. Including more information on these cases would be helpful, such as presenting the counts in each group (and counts of missing data), as well as a summary of cause of deaths.

5) The references in the Supporting Information appear to be incomplete; please update instances of "ref Mx" and "ref data Mx" (page 3) with the appropriate citation.

Any attachments provided with reviews can be seen via the following link:

[LINK]

20 Nov 2021

Submitted filename: Response to comments 20211117.docx

Click here for additional data file.

8 Jan 2022

Dear Dr. Vieira,

Thank you very much for submitting your manuscript "Evaluation of the Growth Assessment Protocol (GAP) for antenatal detection of small for gestational age: the DESiGN cluster randomised trial." (PMEDICINE-D-21-03941R2) for consideration at PLOS Medicine.

Your paper was re-reviewed by three reviewers, including the statistical reviewer, and discussed among the editorial team and with an academic editor with relevant expertise. The reviews are appended at the bottom of this email and any accompanying reviewer attachments can be seen via the link below:

[LINK]

The reviewers have identified unresolved issues relating to the statistical analysis and a lack of detail regarding what constituted standard care. As such, we are unable to accept the manuscript for publication in its current form, but we would like to consider a revised version that fully addresses the reviewers' comments. Obviously we cannot make any decision about publication until we have seen the revised manuscript and your response, and we plan to seek re-review by one or more of the reviewers.

In revising the manuscript for further consideration, your revisions should address the specific points made by each reviewer. Please also check the guidelines for revised papers at http://journals.plos.org/plosmedicine/s/revising-your-manuscript for any that apply to your paper. In your rebuttal letter you should indicate your response to the reviewers' and editors' comments, the changes you have made in the manuscript, and include either an excerpt of the revised text or the location (eg: page and line number) where each change can be found. Please submit a clean version of the paper as the main article file; a version with changes marked should be uploaded as a marked up manuscript.

In addition, we request that you upload any figures associated with your paper as individual TIF or EPS files with 300dpi resolution at resubmission; please read our figure guidelines for more information on our requirements: http://journals.plos.org/plosmedicine/s/figures. While revising your submission, please upload your figure files to the PACE digital diagnostic tool, https://pacev2.apexcovantage.com/. PACE helps ensure that figures meet PLOS requirements. To use PACE, you must first register as a user. Then, login and navigate to the UPLOAD tab, where you will find detailed instructions on how to use the tool. If you encounter any issues or have any questions when using PACE, please email us at PLOSMedicine@plos.org.

We expect to receive your revised manuscript by Jan 31 2022 11:59PM. Please email us (plosmedicine@plos.org) if you have any questions or concerns.

***Please note while forming your response, if your article is accepted, you may have the opportunity to make the peer review history publicly available. The record will include editor decision letters (with reviews) and your responses to reviewer comments. If eligible, we will contact you to opt in or out.***

We ask every co-author listed on the manuscript to fill in a contributing author statement, making sure to declare all competing interests. If any of the co-authors have not filled in the statement, we will remind them to do so when the paper is revised. If all statements are not completed in a timely fashion this could hold up the re-review process. If new competing interests are declared later in the revision process, this may also hold up the submission. Should there be a problem getting one of your co-authors to fill in a statement we will be in contact. YOU MUST NOT ADD OR REMOVE AUTHORS UNLESS YOU HAVE ALERTED THE EDITOR HANDLING THE MANUSCRIPT TO THE CHANGE AND THEY SPECIFICALLY HAVE AGREED TO IT. You can see our competing interests policy here: http://journals.plos.org/plosmedicine/s/competing-interests.

Please use the following link to submit the revised manuscript:

https://www.editorialmanager.com/pmedicine/

Your article can be found in the "Submissions Needing Revision" folder.

To enhance the reproducibility of your results, we recommend that you deposit your laboratory protocols in protocols.io, where a protocol can be assigned its own identifier (DOI) such that it can be cited independently in the future. Additionally, PLOS ONE offers an option to publish peer-reviewed clinical study protocols. Read more information on sharing protocols at https://plos.org/protocols?utm_medium=editorial-email&utm_source=authorletters&utm_campaign=protocols

Please ensure that the paper adheres to the PLOS Data Availability Policy (see http://journals.plos.org/plosmedicine/s/data-availability), which requires that all data underlying the study's findings be provided in a repository or as Supporting Information. For data residing with a third party, authors are required to provide instructions with contact information for obtaining the data. PLOS journals do not allow statements supported by "data not shown" or "unpublished results." For such statements, authors must provide supporting data or cite public sources that include it.

We look forward to receiving your revised manuscript.

Sincerely,

Louise Gaynor-Brook, MBBS PhD

PLOS Medicine

plosmedicine.org

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Comments from the reviewers:

Reviewer #1: Thank you for the detailed responses and changes made to the manuscript in response to mine and others reviews.

My remaining area of concern regards the information on standard care provided in the mansuscript in line 215-229 and in the response to review.

The authors state that-

"This is a pragmatic based trial on 'standard care'; we believe attempting to 'standardise' standard care in this study would create an artificial comparison and potential for change of practice given the study processes (contamination). Even though we agree it is challenging to ascertain based on our trial to what is an 'optimal' standard practice, we do believe practice in standard care clusters reflected national practice in maternity units not implementing GAP, including national variation."

-and then go on to state that a detailed review of the standard care local guidelines is already available in a prior publication (not referenced). Having looked for this I cannot easily find it to assess whether the reader can determine the range of standard care applied, but still think more information needs to be provided in this manuscript. Given there are only a small number of units in the study standard arm it would not require much additional work to include for example how many units employed uterine artery Dopplers or not, whether surveillance scan frequency was 3, 4 weekly or longer or prespecified at certain gestations, and gestation of last planned surveillance scan. This information could all be included in a simple supplementary table. Due to the international reach of PLOS med and the fact that this study's findings will be of interest to a range of healthcare systems outside of the UK I do not think quoting the RCOG guidelines and potential adherence to this is sufficient and still requires further work.

Reviewer #2: Thank you to the authors for addressing my previous comments well. I have no further issues to raise.

Reviewer #4: I appreciate the authors' thoughtful and detailed responses, which have satisfactorily answered most of my initial concerns.

I do, however, remain concerned about the use of the two-stage approach in the context of rare events (i.e, estimation of site-specific rates based on very low counts of events). The authors describe the two-stage approach in their Statistical Analysis (supporting information) as: "Firstly, the cluster summary values were adjusted for the ethnicity, age and parity of the individual participants (these are residuals from comparing the observed summary values with those predicted from a model fitted to all participants)... In the second stage, linear regression analysis (ANCOVA) was undertaken in which the adjusted cluster-summary values for an outcome in the trial outcome period were compared between intervention and standard care arms..." It is thus unclear to me how the response to reviewer comments can then claim "However, we disagree that the method requires accurate estimation of hospital-specific rates"-- unless I am misunderstanding, the adjusted hospital-specific rates are precisely what is being compared between groups, so an inaccurate or unstable rate would be expected to influence results. Especially if there is uncertainty in the literature as to which is the best approach, it would be helpful to include results showing the results when using a one-stage approach as supporting information. Confirmation that findings are robust to the type of analytic method would greatly strengthen confidence in the study conclusions.

Any attachments provided with reviews can be seen via the following link:

[LINK]

11 Feb 2022

Submitted filename: Response to comments 202200209.docx

Click here for additional data file.

14 Apr 2022

Dear Dr. Vieira,

Thank you very much for re-submitting your manuscript "Evaluation of the Growth Assessment Protocol (GAP) for antenatal detection of small for gestational age: the DESiGN cluster randomised trial." (PMEDICINE-D-21-03941R3) for review by PLOS Medicine.

I have discussed the paper with my colleagues and the academic editor and it was also seen again by three reviewers. I am pleased to say that provided the remaining editorial and production issues are dealt with we are planning to accept the paper for publication in the journal.

The remaining issues that need to be addressed are listed at the end of this email. Any accompanying reviewer attachments can be seen via the link below. Please take these into account before resubmitting your manuscript:

[LINK]

***Please note while forming your response, if your article is accepted, you may have the opportunity to make the peer review history publicly available. The record will include editor decision letters (with reviews) and your responses to reviewer comments. If eligible, we will contact you to opt in or out.***

In revising the manuscript for further consideration here, please ensure you address the specific points made by each reviewer and the editors. In your rebuttal letter you should indicate your response to the reviewers' and editors' comments and the changes you have made in the manuscript. Please submit a clean version of the paper as the main article file. A version with changes marked must also be uploaded as a marked up manuscript file.

Please also check the guidelines for revised papers at http://journals.plos.org/plosmedicine/s/revising-your-manuscript for any that apply to your paper. If you haven't already, we ask that you provide a short, non-technical Author Summary of your research to make findings accessible to a wide audience that includes both scientists and non-scientists. The Author Summary should immediately follow the Abstract in your revised manuscript. This text is subject to editorial change and should be distinct from the scientific abstract.

We expect to receive your revised manuscript within 1 week. Please email us (plosmedicine@plos.org) if you have any questions or concerns.

We ask every co-author listed on the manuscript to fill in a contributing author statement. If any of the co-authors have not filled in the statement, we will remind them to do so when the paper is revised. If all statements are not completed in a timely fashion this could hold up the re-review process. Should there be a problem getting one of your co-authors to fill in a statement we will be in contact. YOU MUST NOT ADD OR REMOVE AUTHORS UNLESS YOU HAVE ALERTED THE EDITOR HANDLING THE MANUSCRIPT TO THE CHANGE AND THEY SPECIFICALLY HAVE AGREED TO IT.

Please ensure that the paper adheres to the PLOS Data Availability Policy (see http://journals.plos.org/plosmedicine/s/data-availability), which requires that all data underlying the study's findings be provided in a repository or as Supporting Information. For data residing with a third party, authors are required to provide instructions with contact information for obtaining the data. PLOS journals do not allow statements supported by "data not shown" or "unpublished results." For such statements, authors must provide supporting data or cite public sources that include it.

To enhance the reproducibility of your results, we recommend that you deposit your laboratory protocols in protocols.io, where a protocol can be assigned its own identifier (DOI) such that it can be cited independently in the future. Additionally, PLOS ONE offers an option to publish peer-reviewed clinical study protocols. Read more information on sharing protocols at https://plos.org/protocols?utm_medium=editorial-email&utm_source=authorletters&utm_campaign=protocols

Please review your reference list to ensure that it is complete and correct. If you have cited papers that have been retracted, please include the rationale for doing so in the manuscript text, or remove these references and replace them with relevant current references. Any changes to the reference list should be mentioned in the rebuttal letter that accompanies your revised manuscript.

Please note, when your manuscript is accepted, an uncorrected proof of your manuscript will be published online ahead of the final version, unless you've already opted out via the online submission form. If, for any reason, you do not want an earlier version of your manuscript published online or are unsure if you have already indicated as such, please let the journal staff know immediately at plosmedicine@plos.org.

If you have any questions in the meantime, please contact me or the journal staff on plosmedicine@plos.org.

We look forward to receiving the revised manuscript by Apr 21 2022 11:59PM.

Sincerely,

Louise Gaynor-Brook, MBBS PhD

PLOS Medicine

plosmedicine.org

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Requests from Editors:

General comments:

To help us extend the reach of your research, please provide any Twitter handle(s) that would be appropriate to tag, including your own, your coauthors’, your institution, funder, or lab.

Data availability:

The Data Availability Statement (DAS) requires revision. Please remove “request made to the Chief Investigator (Prof Dharmintra Pasupathy) as, in the interests of transparency and reproducibility, a study author cannot be a contact person for the data or be responsible for approving access to data.

Abstract:

Abstract Background: please temper assertions of primacy by adding ‘to the best of our knowledge’ or similar with relation to ‘there are no reported randomised control trials.’

Abstract Methods and Findings:

Please clarify whether this should be November 2015 or 2016 (noting discrepancy between the Abstract and Methods section)

Please add a sentence to summarise the secondary outcomes

Please revise to <10th centile

Please define CI at first use

Author Summary:

Please temper assertions of primacy by adding ‘to the best of our knowledge’ (or similar) with relation to ‘This first randomised control trial’

In the final bullet point of ‘What Do These Findings Mean?’, please describe the main limitations of the study in non-technical language.

Methods

Thank you for providing a CONSORT checklist. When completing the checklist, please use section and paragraph numbers, rather than page numbers which will likely no longer correspond to the appropriate sections after copy-editing.

Results:

Line 367 (and throughout) - please revise to ‘there were fewer women..’, ‘fewer stillbirths’, etc

Where adjusted analyses are presented, please specify which factors are adjusted for, and provide the unadjusted analyses.

Discussion:

Line 443 - please temper assertions of primacy by adding ‘to the best of our knowledge’ or similar

Tables:

Tables 2, 3, 4, 5, S3A, S3B, S3C, S4A, S4B - When a p value is given, please specify in the table legend the statistical test used to determine it.

Tables 3, 4, 5, S1C, S3A, S3C, S4B - Please present numerators and denominators for percentages

Supplementary Table 2 appears to be missing

Comments from Reviewers:

Reviewer #1: Thanks for including the information requested which as suspected has revealed that there is no single "standard care" in the different sites not randomised to GAP. This likely means that GAP has been compared to multiple different preexisting detection rates. However, I think as this information is now clear for the reader there is no reason for the manuscript to go forward for publication in my view and look forward to the interest and debate it will create.

Reviewer #2: I presume I've been asked to re-review (after commenting that I was happy with the R2 version) is to comment on the two-stage vs one-stage approach. I'm afraid I am not knowledgable about that: I asked a colleague who works on cluster randomised trials and they are not aware of any investigation that has shown an issue with two-stage approaches. They did not feel there was a reason to favour using a one-stage approach instead of a two-stage.

I think the authors having added an additional analysis and discussion has addressed this issue to my satisfaction, but the other reviewer perhaps knows more about the issue than I do.

Reviewer #4: I have no further suggestions for the manuscript; this revised version of the manuscript addresses my previous concerns.

Any attachments provided with reviews can be seen via the following link:

[LINK]

27 Apr 2022

Submitted filename: Response to comments 20220426.docx

Click here for additional data file.

29 Apr 2022

Dear Dr Vieira,

On behalf of my colleagues and the Academic Editor, Prof. Jenny Myers, I am pleased to inform you that we have agreed to publish your manuscript "Evaluation of the Growth Assessment Protocol (GAP) for antenatal detection of small for gestational age: the DESiGN cluster randomised trial." (PMEDICINE-D-21-03941R4) in PLOS Medicine.

Before your manuscript can be formally accepted you will need to complete some formatting changes, which you will receive in a follow up email. Please be aware that it may take several days for you to receive this email; during this time no action is required by you. Once you have received these formatting requests, please note that your manuscript will not be scheduled for publication until you have made the required changes.

In the meantime, please log into Editorial Manager at http://www.editorialmanager.com/pmedicine/, click the "Update My Information" link at the top of the page, and update your user information to ensure an efficient production process.

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To enhance the reproducibility of your results, we recommend that you deposit your laboratory protocols in protocols.io, where a protocol can be assigned its own identifier (DOI) such that it can be cited independently in the future. Additionally, PLOS ONE offers an option to publish peer-reviewed clinical study protocols. Read more information on sharing protocols at https://plos.org/protocols?utm_medium=editorial-email&utm_source=authorletters&utm_campaign=protocols

Thank you again for submitting to PLOS Medicine. We look forward to publishing your paper.

Sincerely,

Louise Gaynor-Brook, MBBS PhD

PLOS Medicine