Computerised interpretation of the fetal heart rate during labour: a randomised controlled trial (INFANT)

Inclusion criteria

Women admitted to a participating labour ward who fulfilled all of the following criteria were eligible to be recruited and randomised.

• Women were judged to require EFM by the local clinical team based on existing guidelines, and the woman consented to have EFM, and EFM was possible.

  • Note that EFM is defined as the active decision of the health-care professional and the woman to initiate EFM for the purpose of fetal monitoring, usually because of perceived risk factor(s) that increase the likelihood of fetal compromise occurring in labour.

  • The decision to initiate EFM can occur at any time during labour. Some women with known factors that place them at higher risk of fetal compromise during labour would already know that EFM throughout labour was planned. Others started labour with intermittent monitoring and then were judged to require EFM at some point during the labour. Women were eligible to participate at any stage of labour.

• Women were pregnant with a single fetus or twins.

• Gestational stage was ≥ 35 weeks (≥ 245 days).

• There was no known gross fetal abnormality, including any known fetal heart arrhythmia such as heart block.

• Women were aged ≥ 16 years.

• Women were able to give consent to participate in the trial as judged by the attending clinicians.

Exclusion criteria

• Triplet or higher-order pregnancy.

• Criteria for EFM not met, including elective caesarean section prior to the onset of labour.

Information for women and obtaining informed consent

Information about the trial was provided to women during the antenatal period (see Appendix 1), after their booking appointment. This process was individualised for each participating centre depending on their routine practices. For example, in some centres, women were provided with information about the trial at their routine ultrasound scan appointment (18–22 weeks). All women had the opportunity to ask questions.

When a woman presented in early labour to the labour ward in a participating centre, she was given a copy of the participant information leaflet (see Appendix 2) and a verbal explanation of the INFANT trial. She was then asked whether or not she would like to participate in the study and, if she agreed, she was asked to sign an INFANT trial consent form. Then, if at any point EFM was commenced during labour, the midwife responsible for the woman’s care checked her eligibility to participate in the trial and that she was still happy to take part. This was documented, and then the woman was randomised by the Guardian system to either the decision support (intervention) arm or the no decision support (control) arm.

All women in labour admitted to the participating centres were expected to have their labour information recorded in the Guardian system, in accordance with the current practice in each centre. This did not change the way health professionals managed labour; it merely changed the way they managed the information generated by the process of monitoring labour and how they recorded this information. It was clearly stated that women were free to withdraw from the study at any time for any reason without prejudice to future care, and with no obligation to give the reason for withdrawal.

Written informed consent was obtained by means of a dated signature from the woman and the signature of the person who obtained informed consent (see Appendix 3); this would be the principal investigator (or a qualified health-care professional with delegated authority). A copy of the signed informed consent document was given to the woman. A further copy was retained in the woman’s medical notes, a copy was retained by the principal investigator and a final copy was sent to the trial co-ordinating centre.

A senior investigator was available at all times to discuss concerns raised by women or clinicians during the course of the trial.

Randomisation

The Guardian system prompted the health professional providing care to consider whether or not the woman was eligible for the INFANT trial when EFM had been used for > 5 minutes. Intermittent use of EFM for durations of up to 5 minutes could be employed for intermittent monitoring, but when used for longer periods of time this would indicate that a decision had been made to initiate EFM, in which case the woman may have been eligible to participate in the trial. If the health-care professional indicated that the woman was not yet eligible because an active decision had not been made to initiate EFM, then the Guardian system prompted the health-care professional again, if the CTG continued to be recorded for longer than 5 minutes in that or any subsequent episode of monitoring.

When the health-care professional indicated that a woman was eligible to participate, the Guardian system clarified that the necessary eligibility criteria for trial entry had been met (i.e. that the health professional gave the required answers to a number of questions posed by the Guardian system, and then the Guardian system randomly allocated the women in the ratio 1 : 1 to either ‘CTG with no decision support’ or ‘CTG with decision support’) (Figure 9). The allocations were computer generated in Stata^® version 10 (StataCorp LP, College Station, TX, USA) using stratified block randomisation employing variable block sizes to balance between the two trial arms by singleton or twin pregnancy, and within each participating centre. The procedures for randomisation were fully documented, reviewed and signed off prior to the start of the trial and monitored by the co-ordinating centre during the trial.

FIGURE 9.

Flow diagram.

Planned interventions

The intervention was the use of decision support software. In order to accurately reflect any potential impact of the decision support software in contemporary NHS practice, such as changes in midwifery presence during labour consequent upon knowledge of the allocation, it was desirable that clinicians were not masked to allocation.

Primary short-term outcome

The primary short-term outcome was a composite of poor neonatal outcome including deaths [intrapartum stillbirths plus neonatal deaths (i.e. deaths up to 28 days after birth) except deaths as a result of congenital anomalies], significant morbidity (moderate or severe NNE, defined as the use of whole-body cooling) and admissions to a neonatal unit within 48 hours of birth for ≥ 48 hours (with evidence of feeding difficulties or respiratory illness and when there was evidence of compromise at birth suggesting that the condition was the result of mild asphyxia and/or mild encephalopathy).

Note: we recognised that the signs of mild encephalopathy can be subtle and hence a number of babies identified as having this condition were likely to have a range of non-specific signs such as respiratory difficulty and poor feeding rather than features more specifically associated with encephalopathy. 38 Therefore, we included ‘admission to the neonatal unit within 48 hours of birth for ≥ 48 hours where there is evidence of compromise at birth’. Since this was a mature group of babies (born ≥ 35 weeks), any difference in the incidence of these admissions was felt likely to result from differences in perinatal asphyxia.

Primary long-term outcome

The primary long-term outcome was the Parent Report of Children’s Abilities-Revised (PARCA-R) composite score39,40 at the age of 2 years for a subset of 7000 infants.

Note: neurodevelopmental delay and cerebral palsy are the most important long-term adverse outcomes associated with perinatal asphyxia. However, the incidence of moderate or severe cerebral palsy is around 1.5–2.5 per 1000 live births, depending on the definition and the method of ascertainment. There is also uncertainty about the proportion of these cases that results from intrapartum asphyxia in mature infants; however, 30% appears to be a reasonable estimate. 4 Therefore, given the rarity of this outcome, it was unlikely that a clear difference could be demonstrated between the two groups in a trial of 46,000 births. In order to have reassurance that any benefits of the intervention, with respect to short-term outcomes, had not occurred at the expense of later neurodevelopmental delay, we measured neurodevelopment in a proportion of the surviving children at the age of 2 years.

Secondary short-term outcomes

Secondary long-term outcomes (infant)

Quality-of-care outcomes

• Adverse outcome (trial composite primary outcome plus metabolic acidosis) when it is judged that suboptimal care has occurred in labour: levels 1 to 3 separately and combined.

• Level 1: suboptimal care, but different management would have made no difference to outcome.

• Level 2: suboptimal care, and different management might have made a difference to outcome.

• Level 3: suboptimal care, and different management would reasonably be expected to have made a difference to the outcome.

Note: in all cases of adverse outcome (trial primary outcome plus a cord artery pH of < 7.05 with a base deficit of ≥ 12 mmol/l) and all neonatal deaths and intrapartum stillbirths care in labour was assessed, to determine if it was suboptimal, by panel review similar to that undertaken by the Confidential Enquiry into Maternal and Child Health (CEMACH). 26 Intrapartum notes were copied and anonymised, and all references to trial allocation removed. The notes were then examined by a panel of an experienced obstetrician, midwife and neonatologist to identify if there was suboptimal care, particularly in relation to interpretation of the CTG and actions that flowed from any identification of CTG abnormalities.

Process outcomes (after trial entry)

• Total number of CTG abnormalities (blue, yellow and red levels of concern) detected by the decision support software.

• Number of blue levels of concern on the decision support software, indicating a mild abnormality on the CTG.

• Number of yellow levels of concern on the decision support software, indicating a moderate abnormality on the CTG.

• Number of red levels of concern on the decision support software, indicating a severe abnormality on the CTG.

• Number of women with at least one yellow level of concern on the decision support software, indicating an abnormality on the CTG.

• Number of women with at least one red level of concern on the decision support software, indicating a severe abnormality on the CTG.

• Time from first red level of concern to birth.

Note that it was important to collect and analyse process outcomes in the trial, as a failure to detect differences in clinical or quality-of-care outcomes between the two randomised groups may be because of poor adherence with the alerts of the system, rather than the system not correctly identifying abnormalities with the CTG. In addition, as the trial allocation was not masked, it was important to measure any change that resulted from clinicians being aware of whether or not the decision support system was in operation.

• Number of thumb entries per hour from time of trial entry to first yellow level of concern or until fully dilated (10 cm) if no abnormality detected or first yellow level of concern occurred prior to trial entry.

• Number of vaginal examinations.

• Epidural analgesia.

• Labour augmentation.

• Presence of meconium.

Note: some of these later process outcomes (e.g. the number of thumb entries per hour) were proxy measures to determine the presence of a health professional in the delivery room during the labour, which allowed us to quantify any differences between the groups with respect to support offered to women during labour. Although unlikely, knowledge of the trial allocation could have resulted in less frequent contact with the woman allocated decision support in labour. Less frequent contact would have resulted in a lower number of these process measures.

Calculation of proposed sample size

The proposed total sample size was 46,000 births.

The following data sources and assumptions were used in the calculation of the trial sample size.

Loss to follow-up

It was assumed that loss to follow-up for the short-term primary outcome would be negligible, as most of this information would be collected before the woman left the delivery room in which she had been recruited. For neonatal outcomes, a small number of babies were admitted to a neonatal unit separate from where they were born or planned to be born, in which case data were collected from these sites through the research midwives employed by the study in the participating centres. At the time of entry to the study all women were asked for permission for their contact details to be downloaded to the trial co-ordinating centre along with their clinical details from the Guardian system. The families selected for follow-up at 2 years were contacted by post 8 weeks after birth and informed that they had been selected for the follow-up study. Contact with families who agreed to take part was maintained during the period between birth and the follow-up assessment by sending a birthday card each year along with a FREEPOST change-of-address card to facilitate communication with University College London (UCL) Comprehensive Clinical Trials Unit about updated contact details.

Research governance

The sponsor of the trial was initially the University of Oxford (January 2009 to May 2012), but changed to UCL when the trial moved (May 2012 to June 2016). The trial was run on a day-to-day basis by the project management group. This group reported to the Trial Steering Committee (TSC), which was responsible to the research sponsor. At each participating centre, local principal investigators reported to the project management group via the project-funded staff based at the UCL Comprehensive Clinical Trials Unit.

Insurance

NHS indemnity operated in respect of the clinical treatment being provided. In addition, the sponsor had appropriate insurance-related arrangements in place.

Trial Steering Committee

The trial was supervised by an independent TSC. The precise terms of reference for the TSC were agreed at its first meeting. A TSC charter similar to that used by the Data Monitoring Committee (DMC) (see Data Monitoring Committee) was completed.

Data Monitoring Committee

An independent DMC was established for the trial. This was independent of the trial organisers. The terms of reference for the DMC were agreed at the first meeting. A DMC charter was completed following the recommendations of the DAMOCLES (DAta MOnitoring Committees: Lessons, Ethics, Statistics) study. 48

During the period of recruitment to the trial, interim analyses were supplied, in strict confidence, to the DMC, together with any other analyses the DMC requested. In the light of interim data, and other evidence from relevant studies, the DMC would inform the TSC if, in its view, there was proof beyond reasonable doubt that the data indicated that any part of the protocol under investigation was either clearly indicated or contraindicated, either for all women or for a particular subgroup of trial participants. A decision to inform the TSC would in part be based on statistical considerations. Appropriate criteria for proof beyond reasonable doubt could not be specified precisely. A difference of at least three standard errors (SEs) in the interim analysis of a major endpoint may have been needed to justify halting, or modifying, the study prematurely. This criterion had the practical advantage that the exact number of interim analyses would be of little importance, and so no fixed schedule was proposed. 49 Unless modification or cessation of the protocol was recommended by the DMC, the TSC, collaborators and administrative staff (except those who supply the confidential information) would remain masked to the results of the interim analysis. Collaborators and all others associated with the study were able to write, through the trial office, to the DMC, to draw attention to any concerns they may have about the possibility of harm arising from the treatment under study, or about any other matters that may have been relevant.

Publication policy

The chief investigator was responsible for co-ordinating the dissemination of data from this study. All publications using data from the study to undertake original analyses were submitted to the TSC for review before release. To safeguard the scientific integrity of the trial, it was agreed that data from the study would not be presented in public before the main results were published, without the prior consent of the TSC. The success of the trial depended on a large number of midwives and obstetricians. For this reason, chief credit for the results would be given not to the committees or central organisers, but to all who collaborated and participated in the study. It was agreed that authorship at the head of the primary results paper would take the form ‘The INFANT Collaborative Group’, to avoid giving undue prominence to any individual.

Survey

From 5 January 2010 to 18 July 2010, 469 women were recruited to the pilot phase of the INFANT trial from the Royal Blackburn Hospital. A total of 234 women were recruited to the CTG monitoring only (control) group and 235 were recruited to the CTG monitoring plus decision support (intervention) group. The eligibility criteria and process of recruitment are described in Chapter 2. In a subset of women approached to participate in the INFANT trial, we measured anxiety in the latent phase of labour when cervical dilatation was ≤ 3 cm with an effaced cervix. If the woman was recruited into the trial, we measured anxiety at a further two time points: during the active phase of labour when the cervical dilatation was 4–7 cm, and within 48 hours post partum. At each time point, the midwife asked women to rate their anxiety using a visual analogue scale – anxiety (VAS-A) from 1 (not at all) to 10 (very much so). Their responses were recorded on the VAS-A study form (Figure 10).

FIGURE 10.

The INFANT study visual analogue scale form.

Statistical analysis

The change in VAS-A scores in the two groups (control and intervention) (1) from the latent to the active phase of labour and (2) from the latent phase to the postpartum period was analysed using repeated measures analysis of covariance (ANCOVA). This enabled us to include all women in the analysis, even those with data at only one time point. The correlation between scores between phases was calculated using the Pearson correlation coefficient. Two-sided significance tests were used, taking a p-value of 0.05 as significant. The analysis was conducted using statistical software Stata version 11.1.

Qualitative study

Women from two of the study sites in the INFANT trial (Warrington Hospital and University Hospital of North Staffordshire) were approached to be interviewed about their experiences of birth and fetal monitoring by a single trained qualitative researcher. Women were approached after giving birth and before hospital discharge. A purposive sampling approach was used to ensure that equal numbers of women from the two arms of the trial were recruited, and that the number and severity of alerts was wide-ranging and well balanced between the two groups. The trial’s statistician identified potential women to be included and informed the qualitative researcher of their study number. The interviewer was masked to the women’s trial allocation and pattern of alerts until after the interviews were complete.

The interviews collected views of the whole birth experience but included semistructured prompting to explore women’s feelings about monitoring and their understanding of the INFANT trial. The interviewer and another senior qualitative researcher undertook the analysis jointly. An initial thematic analysis was undertaken using NVivo (QSR International, Warrington, UK) software to support the coding process. This was followed by a framework analysis, summarising the experiences and attitudes of each woman and mapping these against the woman’s characteristics (hospital of birth, study allocation, maternal age, gestation at trial entry and number of yellow and red alerts).

Quantitative study

The VAS-A score sheets were completed by 275 out of 469 (59%) women [CTG monitoring only: 142 out of 234 (61%); CTG monitoring plus decision support: 133 out of 235 (57%)]. In the control group, data were available for 128 (55%) women from the latent phase, 104 (44%) for the active phase and 81 (35%) for the postpartum period. In the intervention group, data were available for 124 (53%) women for the latent phase, 106 (45%) for the active phase and 81 (34%) for the postpartum period.

The VAS-A scores are shown in Table 5. The scores were approximately normally distributed. In each group, anxiety levels increased from a score of around 5 points in the latent phase to around 6 points in the active phase, then dropped below 5 points in the postpartum period. There was no difference between groups in the change in anxiety from the latent to the active phase (p = 0.84) or from the latent phase to the postpartum period (p = 0.88). The scores were positively correlated: 0.48 between latent and active phase, 0.41 between the latent phase and the postpartum period, and 0.44 between the active phase and the postpartum period.

Qualitative study

A total of 18 women were interviewed, including six with their birthing partner, who was either their partner or mother. Table 6 provides a list of the women interviewed with details of their hospital of birth, trial group, age, gestation at trial entry and number of alerts. Four women had no alerts, seven had at least one yellow but no red alerts and seven had at least one red alert. The number of red and yellow alerts were evenly distributed across the trial groups.

Levels of understanding

Among participants, there was a patchy understanding of what the trial was about, beyond a general view that it was seeking to understand people’s experiences in labour and improve care for other women in the future. This is a finding that is widely reflected in the literature. 54–56 Women were frequently unclear about what is ‘normal’ monitoring of the baby in labour and what is part of the trial, and whether or not they would have been monitored anyway:

It was nothing, you know, that was intervening with anything, so I hadn’t minded at all. I just hadn’t been totally aware that I’d be hooked up to a machine the whole time. I just thought it was if you needed to be on the machine, they’d then monitor it through the computer . . . I wasn’t sure whether I had to be on the machine for the sake, you know, for the baby’s sake and whatnot or whether it was because I was, because of the study. I wasn’t too sure what it was that I had to actually be on it for.

Participant 02, control arm

My understanding at the time of it was really just that it would be somebody maybe 1 or 2 years after the birth would be following up with a questionnaire and maybe a phone call or something just to see what my experience was . . . I don’t recall the monitoring being part of the study but a huge deal wasn’t made of it anyway, but as I say it wouldn’t have been a problem if it was, but I was going to be monitored anyway with being induced.

Participant 05, control arm

Participant 05 (control arm) also said, ‘I didn’t remember them saying which group I was in. Is there different groups?’. Similarly, participant 14 (control group) said, ‘I don’t remember anything to do with groups’. Furthermore, she did not clearly recall any monitoring at all. This participant had a vague recollection of ‘bands’ being used for monitoring her baby’s heart, and that the baby’s heartbeat had dropped at one stage, but said, ‘I definitely don’t remember anything being put round me’ other than her transcutaneous electrical nerve stimulation machine. Similarly, a woman in the intervention arm (participant 18) said, ‘Groups? They might have mentioned it but I don’t remember it’.

One couple (04, control arm) knew they had been allocated to a group but were unaware of how and why they had been selected for participation. The male partner had spent quite a lot of time trying to work out for himself what the monitor readings meant:

It would be nice to know.

You know, why your specific case was chosen. Was it just it was randomly chosen or was it because they wanted to, to look at it for a certain reason?

Or is it just that we were placed in this particular bracket, you know?

Well, was it just random that our, you know, results were picked out? Or was it because, like we think, [female] had a rapid delivery? Or, you know, or something come up on the results why they decide?

However, other participants in both groups were aware that there were different arms and demonstrated an awareness of which arm they were in as well as how they were allocated to a group:

Basically what they told us, well it says in the leaflet as well, that you might not be selected for the trial on a computer. Basically she tapped in some information on the screen and then it come up whether you’d be selected for it. And she typed it in and she said we weren’t selected for it.

Participant 01, control arm

It was frequently suggested by participants that being given information about the trial towards the end of pregnancy rather than during the labour episode may improve understanding, as it was difficult for people to absorb the information or give it any priority during labour. This approach of providing information during pregnancy should have been happening in the centres, and a few women did recall discussing it at antenatal appointments or seeing posters about it in previous visits, but others did not. Women also mentioned feeling ‘vague’ or ‘confused’ about the information provided during labour because of the pain relief medication they had taken.

There was little evidence that feeling underinformed had led women to regret taking part. This was because EFM was commonly seen as routine care and not particularly invasive. Even women who disliked not being able to mobilise because of the monitoring failed to express major concerns about the information and consent process.

One exception to this was a woman in the decision support arm who said that she felt ‘mithered’ by having to answer all the questions needed to take part in the trial:

I didn’t want to be asked; I just wanted to be left alone to get on with going through the labour . . . I just wanted to be left alone and that took like 15, 20 minutes to do all that so like she was asking me questions and I was contracting as well . . . I signed it because I thought – and I said this to my mum this morning – the only reason that I signed it was because I thought if the midwife thinks that we’re co-operating with this then she’ll give us some drugs [laughter]. She’ll give me some more drugs, that’s what I thought . . . It was something that was so shoved in my face and I didn’t really have a choice basically . . . because I wanted to keep my midwife nice and sweet.

Participant 15, decision support arm

She complained that she ‘hated’ being monitored because it restricted her movements. It did not make her feel more anxious, but she regretted taking part because she felt that it spoilt her otherwise good experience of a spontaneous vaginal birth. She was so bothered by the restrictions on movement that she requested that the monitoring be stopped. It is clear from her interview that she did not understand that she would have had monitoring anyway and that it was not a consequence of taking part in the trial. She said that monitoring should be used ‘only if it’s an emergency for the baby’ and did not understand that the purpose of monitoring was to detect concerns before they become emergencies. When this was discussed during the interview she commented:

So in that case it does change my views differently then, then yes, if I would have known it was something to do with protecting the baby then yes I would have had it on in labour.

Participant 15, decision support arm

Monitoring and reassurance

Women in both groups of the trial reported finding monitoring reassuring. There was no difference in the pattern of responses between the two groups, or between women with few alerts and those with many.

For example, one woman said:

That showed what the heartbeat was doing, you know, ranging from sort of whatever it was, 100 to 150. And there was a guide next to it to say what’s acceptable and what’s, you know, risky. [um] So that was quite reassuring, wasn’t it?

Participant 04, control arm, no alerts

Oh, I thought it was brill, to be honest, because as I say a lot of the time I felt a little bit out of the loop. From where I was sitting I could see all the screens and what was going on so I found that, you know, sort of quite comforting.

Participant 03, decision support arm, no alerts

Being able to monitor what was happening with [baby 1] and sort of midway through what was happening with [baby 2] with their heart rates and things made me very reassured.

Participant 22, control arm, 13 yellow and two red alerts

I did quite enjoy having the monitors on actually. . . . you can just see, see sort of their heartbeat and how strong your contractions were, whereas normally you couldn’t, you haven’t got that.

Participant 09, decision support arm, eight yellow and two red alerts

Several women (or their partners) said that the monitor also helped reassure the partner. This generated a sense of involvement because they could observe a contraction and support their partner appropriately. Participant 19 (decision support arm) said that her partner ‘kept checking the paper. I think he was fascinated by it’.

Monitoring and restriction of movement

On those occasions when objections were raised about monitoring, this was most usually because of the restrictions it placed on movement. Some women said that they did not find the monitor restrictive or uncomfortable, including participant 19 (decision support arm). When asked if she could move around she said:

Yes, I was on my side for most of it, they said that’s the most comfortable position for me so I just stayed on my side.

Did you mind being monitored at all?

No, no anything that helps really.

When you say helps, in what way?

I mean, well like just in case there’s any complications, I’d rather be monitored and have them spot them, so.

You found it sort of reassuring?

Yes, yes extra reassurance.

However, other women talked about wanting to alleviate pain by moving around or to be able to go to the toilet. The monitor restricted this movement and some women felt that the monitor straps were uncomfortable. Some women expressed a preference for a wireless monitor. One woman had heard that this was available in other hospitals. Women who disliked being monitored expressed varying degrees of resignation, assuming that they would have their movement restricted anyway (e.g. because of an epidural) or that the disadvantages of limited movement had to be balanced against the benefits for the baby and their own peace of mind:

The fact that it restricted me, that was a bit of a pain, but I don’t know whether I would have moved round that much or, you know. Because I mean I could have sat on the ball, you know, the blow up ball . . . rather than the chair, which is one of the things they recommend. But I didn’t want it. I just wanted to sit on the chair . . . No, it’s reassuring, I think because you know you don’t want your baby’s heart rate to go down. And it was quite good as well in that my husband could see when the contractions were coming on . . . I think we, it made no difference to us taking part, you know, it wasn’t detrimental, it wasn’t, I was going to be monitored anyway whether I took part in the trial or not.

Participant 20, decision support arm, three yellow alerts

And the reason I agreed, why I thought it was brilliant, was because it’s extra checks, it’s extra checks for him. And I think well he’s going to be monitored closely from now on which is amazing but, you know, because I’d do anything for him, you know, healthy baby, and if it picks up on something, fantastic, and it’s doing research for everything else, so yes . . . So it turned out that I was on this monitor for this and my heart and everything so I couldn’t move off the bed for all them hours, they wouldn’t let me move. So I couldn’t walk round, so my plan had gone way out the window. I wasn’t walking round, I’d not had my bath at all, I’m stuck on this bed, I’ve been induced. . . . The birth plan was just sit on the ball, stay upright and move as much as you can. That was basically it. And nothing happened like that and I’m saying ‘Can I get off this bed?’ ‘No, you’re being monitored for this and you’re being monitored for your heart, you’re being monitored, baby’s being monitored because of the poo because that’s dangerous, no you can’t move off this bed’. I was like ‘Ohhhh’, so I just lay down the whole day. Which was really nice and very boring.

Participant 11, control arm, three yellow alerts

Monitoring and anxiety

Women did describe anxious moments during their labour; however, these did not seem to be associated with monitoring, but were more related to the urgent comments and behaviour of staff as they responded to the monitoring results or to other clinical concerns.

There was only one clear exception to this:

So it was quite good because obviously people could see what was going on . . . because the doctor come in and said I’ve been watching you on the screen . . . Sometimes, I kept hearing her say when the heartbeat, because they kept saying she’s being naughty, they just kept saying that, and it was flashing messages up to them and I heard her say a couple of times ‘I think that heartbeat’s okay for the minute’ but that was telling her it was, so . . . They did talk about it quite a bit, they used it as a guide but said they would use their own judgement to make any decisions . . . In a way I don’t know if it’s a good thing or a bad thing, though, because right towards the end because her heartbeat had been playing up all day, we were all focused on it . . . Everyone was just focused on this monitor and the heartbeat, so I think that got a little bit stressful, because I did end up telling him [partner] ‘Stop telling me what’s happening or talking about it’ because it was making me panic . . . He says to me afterwards that he was, it was the most scared he’d ever been in his life but at the time he seemed really quite cool and took it all in his stride but obviously he was just putting a show on for me.

Participant 16, decision support arm, four yellow alerts

Nonetheless, participant 16 concluded: ‘The study didn’t really affect the birthing experience at all so that, you know, I’d do it again, that’s fine’.

This woman’s interpretation was that the staff used the decision support to justify postponing any intervention. She was glad not to have a caesarean section, but she felt that she could have had an instrumental delivery earlier: ‘I do think that because her heartbeat had been playing up so long throughout the day and things weren’t moving on for me that they should have looked at me a bit earlier and made a decision a bit earlier’. The woman’s mother, who was present during the labour and birth, and was interviewed with her, was even more convinced of the need for an early delivery:

It was about half nine and I can remember the midwife saying, ‘We’re going to leave you till eleven and if nothing’s happened by eleven we’ll get the doctor and we’ll see about taking you to theatre. But then when 11 o’clock came they had a look at you and you’d dilated quite a bit by then so they said we’ll leave you another hour, that took you to 12.00 and then again we’ll leave you another 2 hours, and that annoyed me because that’s what they kept saying. Although, you know, she was well into labour I think they should have took her for a C-section at about 11 o’clock, I do.

Mother of participant 16, decision support arm

This example suggests that CTG with decision support could lead to some cases of raised anxiety levels. There were two examples in the control group in which monitoring without decision support also caused some anxiety. Participant 08 reported that her mother had been worried at one point, although she herself was relaxed and asleep:

My mum was watching where they was monitoring me and I think I fell asleep so as I had diamorphine. And at one point, because they had one on me and one obviously for the baby’s heartbeat, and the baby must have moved so it went to zero and my mum thought it was me. She said she couldn’t see my chest rising or anything and thought I wasn’t breathing and she looked at this monitor and seen zero and she was like, ‘She’s not breathing, she’s not breathing’ and I woke up and I was like ‘What?’ [laughter].

Participant 08, control arm

The partner of participant 21 (five yellow alerts and one red alert) recalled his own fears:

Yes it was helpful, but it was also, I think, in some respects that she couldn’t see it was as well because there was quite a few scary moments.

You see, I couldn’t see that because it was . . .

Yes, I mean his heart, I could see his heartbeat going down and she couldn’t see it, so I was a bit worried there.

But as soon as his heartbeat started going down they all, them sitting on their desk came in to have a look.

They were both surprised at the amount of paperwork the monitoring generated for the midwife, and felt that this detracted staff from providing reassurance and support:

You need somebody that’s talking to you, explaining things and actually maintaining the relationship with you as opposed to just doing, writing down and checking the monitors and things like that because otherwise you end up panicked and it’s not good.

Participant 21, control arm, 5 yellow alerts and 1 red alert

Data collection schedule

Information was to be collected at the following times:

• electronically during labour via the Guardian system

  • all women

• Post Birth Data Collection (PBDC) Form M (Mother) (see Appendix 8)

  • all women receiving a higher level of care, surgery or a procedure in theatre following delivery

• PBDC Form B (Baby) (see Appendix 5)

  • all babies receiving a higher level of care or surgery following birth

• PBDC Chart B (Baby) Neonatal Encephalopathy Data (see Appendix 6)

  • all babies receiving a higher level of care and classified as having NNE

• Death of a baby in the INFANT study form (see Appendix 7)

  • all intrapartum stillbirths and neonatal deaths up to 28 days after birth

• Parent’s Questionnaire at 24 months (health and development outcomes)

  • a subset of 7000 participants consenting to follow-up

• Parent’s Questionnaire at 12 and 24 months (health economic items)

  • a subset of 700 participants within the follow-up sample of 7000.

Derivation of variables

Protocol violation

A protocol violation is the intended failure to comply with the final study protocol as approved by the REC and research and development departments, an example being serious non-compliance with the protocol resulting from fraud or misconduct that affects participant rights, safety and/or the integrity of the resultant data. Any violations were reported to the sponsor and REC as soon as possible.

Protocol deviation

A protocol deviation is an unintended failure to adhere to the final study protocol.

In this trial, the following were defined as protocol deviations.

Primary analysis strategy

For the primary analysis, participants were analysed in the groups into which they were randomly allocated (i.e. comparing the outcomes of all women and babies allocated ‘CTG with no decision support’ with ‘CTG with decision support’), regardless of the allocation received.

The two groups were compared by calculating the treatment difference adjusted for the stratification factors used in the randomisation (centre and singleton/twin pregnancy). The adjusted analysis took account of the correlation between treatment groups introduced by stratifying the randomisation (which forces outcomes between treatment arms to be similar apart from any treatment effect). 62 Both adjusted and unadjusted estimates were presented for all outcomes, but the primary inference was based on the adjusted analysis.

The unit of randomisation was birth episode, which raises the issue of non-independence of observations. Some women had more than one delivery over the study period and may have been randomised into the trial more than once if they were eligible, but this was estimated to be very unlikely. Based on national statistics and average interpregnancy intervals in the UK, we anticipated that around 10% of women in this cohort would have a subsequent delivery within the study period, but a smaller proportion would have two consecutive births monitored by CTG. 63,64 In addition, around 1.5% of women would be expected to have twin deliveries,65 but this proportion was likely to be lower in this cohort as some twin births will occur before 35 weeks’ gestation and a large proportion of twin term births are by elective caesarean section.

We anticipated the proportion of non-independent observations within and between pregnancies to be much lower than 10%; however, some outcomes can have a large intracluster correlation coefficient – in particular the 2-year outcomes collected via the parent questionnaire – so clustering was taken into account in the analysis. 66,67

Representativeness of trial population and participant throughput

The flow of participants through each stage of the trial was summarised using a CONSORT diagram. 68 We reported the numbers of women who:

• were randomly assigned

• received the intended intervention

• withdrew before or during CTG monitoring

• were included in the primary analysis at discharge

• were lost to follow-up

• were included in the analysis at 24 months.

Baseline comparability of randomised groups

Participants in the original two randomised groups were described separately with respect to:

• maternal age

• ethnic group

• singleton or twin pregnancy

• gestational age at trial entry

• BMI at booking visit (if recorded)

• smoking history at booking visit (if recorded)

• parity

• obstetric history

• cervical dilatation at trial entry (if recorded)

• intrauterine growth restriction (IUGR) suspected at labour onset

• labour induction.

Numbers (with percentages) for binary and categorical variables, and means (and SDs) or medians (with lower and upper quartiles) for continuous variables were presented; no tests of statistical significance were performed nor were CIs calculated for differences between randomised groups on any baseline variable.

Losses to follow-up

The numbers (with percentages) of losses to follow-up among women selected for the 24-month assessment were reported and compared between the two trial arms, and the reasons recorded. Any deaths (and their causes) were reported separately.

Description of available data

The pattern of missing data for primary and secondary outcomes, from baseline to the end of follow-up, was summarised for the two treatment groups, with differentiation between fully and partially completed forms/Guardian fields and those that were missing completely.

Not all data are routinely collected by all hospitals, for example BMI, smoking history, cervical dilatation, cord artery pH and base deficit. These data were reported separately for the subset of hospitals that do collect them routinely.

Description of compliance with intervention

A summary of the intervention received was provided, which included intermittent use of the decision support software and/or withdrawal of consent during labour.

Unmasking of randomised treatments

In order to accurately reflect any potential impact of the decision support software in contemporary NHS practice, such as changes in midwifery presence during labour consequent on knowledge of the allocation, the clinicians were not masked to allocation. The local community midwives and participants may also have been aware of the allocation. All other persons involved in the trial (except for the trial statistician and trial programmer), including the UCL trial co-ordinating centre, did not have access to the aggregate list of randomisation codes. K2 Medical Systems remained masked until the data were frozen at the end of the trial.

Statistical methods used for analysis of primary outcomes

The numbers (percentages) of babies with poor neonatal outcomes were presented for each group and the RR plus 95% CI calculated. RRs were estimated using generalised estimating equations (GEEs), or a similar method, adjusting for the stratification factors used in the randomisation (centre and singleton/twin pregnancy). This method of analysis accounted for the correlation in outcomes between twins and siblings delivered in a subsequent pregnancy during the trial period. A log binomial model was planned to be used in the first instance but, if convergence was not achieved, then a log-Poisson model would be used with a robust variance estimator. 69 The mean (SD) PARCA-R composite score was presented for each group and the mean difference between groups plus 95% CI was calculated and compared using GEE (Gaussian model with identity link), adjusting for stratification factors.

Significance levels

For the analysis of the primary outcomes, a p-value of 0.05 (5% significance level) was used to indicate statistical significance. Comparisons of all other outcomes including the components of the primary outcome were reported in full for completeness and transparency. For all other analyses, a p-value of 0.01 (1% significance level) was used to indicate statistical significance, to take into account the number of comparisons. Two-sided statistical tests and corresponding p-values were presented throughout.

Missing data

Missing data for the short-term primary outcome were likely to be negligible, as most of the data were collected electronically on the Guardian system before the woman left the delivery room. If any data items were missing on the PBDC forms, completed for babies and women admitted to a higher level of care, every effort was made to extract these data from the hospital involved.

For any partially completed PARCA-R scales in the 24-month parent questionnaires, the following strategies for estimation of the total and subscale scores were employed when items were missing:

• Non-verbal cognition scale (PARCA-R: ‘Your child at play’ Q1–33)

  • pro rata estimation if < 10% of (up to three) items are missing

  • if Q6 is ‘No’, and Q6a is missing, code ‘No’ for Q6a

  • if Q6 is ‘Don’t know’, and Q6a is missing, code ‘Don’t know’ for Q6a.

• Vocabulary subscale (PARCA-R: ‘What your child can say’)

  • non-ticked items were coded to zero.

• Sentence complexity subscale (PARCA-R: ‘Your child’s understanding Q1–18)

  • if Q1–6 were missing, coded to zero and analysed as ‘Not Yet’

  • if Q6 is ‘Often’ or ‘Sometimes’ and any of Q7–18 were not completed, coded to zero.

Prespecified subgroup analysis

To examine whether or not the effect of decision support was consistent across specific subgroups of women and babies, the following subgroup analyses were planned and carried out:

• singletons versus twins

• suspected IUGR at labour onset compared with no growth restriction

• BMI group [underweight (< 18.5 kg/m²), normal (18.5–24.9 kg/m²), overweight (25–29.9 kg/m²), obese (≥ 30 kg/m²) or unrecorded]

• centre.

For the trial composite primary outcome, results were presented in forest plots showing the RR plus 95% CI for each subgroup, by treatment group, with the p-value for the statistical test of interaction. 70 For the PARCA-R composite score, the difference between the mean treatment effects was reported, within each subgroup, with a 95% CI and the corresponding p-value. 71

Using these statistical methods, we performed subgroup analyses for all prespecified neonatal outcomes and instrumental vaginal deliveries. In addition, we analysed process outcomes by centre.

Prespecified sensitivity analysis

Following early DMC meetings, it was reported that the number of babies admitted to a neonatal unit within 48 hours for ≥ 48 hours exceeded the number anticipated in the sample size calculation by an order of magnitude. Following a review of cases by the masked review panel at the end of the trial, the number still exceeded that anticipated in the sample size calculation, although to a lesser degree. Hence this component far outweighed the other rarer components, such as stillbirth, neonatal death and moderate or severe NNE, and strongly influenced the composite primary outcome. To explore the impact of this on the main findings, a sensitivity analysis of the primary composite outcome was performed, including only the most severely affected babies admitted to a neonatal unit and allocated a score of ≥ 7 points on the Primary Outcome Review Scoring Sheet by the masked review panel.

Statistical software employed

Stata/SE version 13 for Microsoft Windows was used for this analysis.

Statistical methods used for analysis of secondary outcomes

Generalised estimating equations, or a similar method, was used for the analysis of secondary outcomes, adjusting for the stratification factors used in the randomisation procedure (centre and singleton/twin pregnancy). For normally distributed continuous outcomes, we presented the mean and SD for each group, calculating the mean difference plus 99% CI using a Gaussian model with the identity link. For the length of labour, we presented the geometric mean ratio (GMR). For binary and categorical outcomes, we presented counts and percentages for each group and calculated the RR with corresponding 99% CI using a binomial or Poisson model with the log-link. For the number of thumb entries per hour from trial entry to the first yellow level of concern or full dilatation, the rate ratio plus 99% CI was calculated using a Poisson model with the log-link. For skewed continuous outcomes, we presented the median and IQR (or entire range, whichever was appropriate) for each group and compared the difference in medians between groups using quantile regression. We were unable to adjust for the correlation among twins and siblings using this method.

Deviation from analysis described in protocol

For the count variables, median differences were all zero with zero CIs, although some were statistically significant and adjusted quantile regression models were not performing well (lack of convergence), so rate ratios were presented as the effect measure instead of median differences. Medians (IQR) were still presented for each variable as planned. In addition, the hazard ratio was presented for the time from the first red alert to birth instead of the median difference, in keeping with the comparison of rates for the rest of the process outcomes. This was agreed at the INFANT project management group meeting on 23 October 2014.

The outcome time from the first red level of concern to delivery was changed to time from the last red level of concern to delivery. This was agreed at the INFANT coinvestigator group meeting on 15 July 2015 following a review by Professor Philip Steer. It was found that the first red level of concern was frequently an artefact and, therefore, did not accurately capture information relating to prompt action at or around delivery following a red alert.

NHS health-care resource use

A comprehensive list of health-care resource use information for mothers and their babies was collected for the study. Data collection began when women arrived in hospital in labour and ended when postnatal care for both mother and baby was complete. For most women, this was following hospital discharge. A subset of women who consented to be followed up post birth were sent a questionnaire regarding health-care resource use and maternal HRQoL information at 12 and 24 months’ follow-up.

Labour-related resource use data included procedures undertaken for mothers and infants before discharge and were collected using the Guardian system. Additional information, such as maternal transfers after birth, whether or not babies or mothers had been admitted to a higher level of care unit and neonatal deaths, was collected using bespoke data collection forms. These were overseen by the trial’s co-ordinating research midwife, who ensured that all care was documented. The forms were then posted to the INFANT trial administrative centre for data entry.

Health-care utilisation at 12- and 24-month follow-up was identified using a postal questionnaire that collected information about acute and community care, secondary care and maternal HRQoL. It included outpatient appointments and inpatient stays (e.g. for operations), follow-up care and numbers of visits to relevant health-care professionals. The questionnaires were sent to a subsample of mothers of surviving infants who consented to follow-up and who gave birth in the first year of the trial. The 12-month follow-up questionnaire collected resource use data between post-birth discharge and 1 year, and the 24-month questionnaire asked about resources consumed in the previous 12 months. Two postal reminders were sent by the trial management team for questionnaires not returned. All data collected using the postal questionnaire were double data entered and cleaned prior to analysis. Table 36 presents categories of NHS health-care resource use collected during the study.

To estimate whether or not the use of decision support software in INFANT would incur additional NHS resources beyond the implementation of the Guardian system, the health economics team met with a representative from K2 Medical Systems to identify a base-case cost for the software. All sites (and hence all women) participating in the trial used the Guardian system, but we identified three additional aspects to cost for the decision support tool.

The first was the price to be paid by the NHS for the new software. A price for the decision support software had not been determined at the time the study was concluded. We understand that this price would be determined using a particular commercial strategy by K2 Medical Systems and would probably be selected in view of the trial results. Therefore, for the base-case scenario it was initially assumed that the software would be made available free of charge to the NHS. Scenarios to address this were identified for a multiway sensitivity analysis, to include any cost shifting in actual practice.

Second, an annual maintenance fee would be needed for software updates and other related information technology issues. A maintenance fee for the whole Guardian system had already been paid by the trial sites so it was assumed that further maintenance needed for the software would be included. Although the fee could potentially increase as a result of the installation of the decision support software, in the base case it was assumed that the fee would not change.

Finally, training of NHS staff members to develop familiarity and technical competence with the software was reviewed. All training received by staff during the preparation of the trial was delivered during working hours and was fitted into regular working patterns. Therefore, staff did not have to take additional time off work to learn how to use the decision support tool. It was assumed that a similar model would be used across the NHS and that no separate training costs were required. Consequently, in our base case, none of the three identified elements would incur additional NHS resource use, so no specific costs for the use of decision support software in INFANT were assigned. Scenarios to address this were identified for a multiway sensitivity analysis, to include any cost shifting in actual practice.

Unit costs

Sources and associated estimates of unit costs for the different categories of health-care resource use are presented in Table 36. Information was primarily extracted from secondary national sources including the Personal Social Services Research Unit75 and NHS Reference Costs. 74 The unit costs associated with induction, episiotomy, perineal tear, manual removal of the placenta, blood transfusion and neonatal death were not available in any of the secondary data sources consulted. Therefore, we replicated the ‘bottom-up’ costing survey conducted in a recent cost-effectiveness analysis of the Birthplace in England programme to estimate the unit costs for these items. 73 A bottom-up costing proforma was circulated to all trial midwives to complete. These were then followed up with face-to-face interviews. The proformas represented a detailed approach to capturing all possible NHS resources used in the care of the mother and baby during the period between admission and discharge. A working document was generated to capture the generalisability and variability of the procedures. For each scenario, the trial midwife was asked to describe in detail the ‘standard procedures’ that would be undertaken for labour and birth events and, when possible, the typical ratios of ‘staff-to-woman’ care. Scenarios were then varied between the least and the most complex, and included a description of the associated change in activity, staffing level and related resource use. Each of the interviews included approximately 1.5 hours of structured time. The data were then compiled into comparative resource use spreadsheets and were cross-referenced. The original unit costs (calculated for the Birthplace in England study) were then revised to be trial specific. The cost associated with total body cooling was not available in the Personal Social Services Research Unit or NHS reference costs data and was extracted from a study investigating the cost-effectiveness of total-body hypothermia plus intensive care versus intensive care alone to treat NNE. 76

All costs were expressed in 2014–15 GBP inflated to this base using the most up-to-date Hospital and Community Health Service inflation index. 77 Costs incurred between 12 and 24 months’ follow-up were discounted at an annual rate of 3.5%, as recommended by current guidance. 78

Cost analysis

Categories of resource use and associated costs are presented separately for mothers and their babies. Quantities of resource use in each category were multiplied by the corresponding unit cost to estimate the cost in a particular category. This was then averaged across each trial arm to obtain a mean cost per mother or baby. Costs from post-birth discharge to 12 months, and then from 12 to 24 months’ follow-up, were combined to estimate the overall costs at 2 years post birth. The total costs for the following categories are presented separately for the mother–baby dyad: trial entry to hospital discharge, community professional visits and secondary care. Given that we present the economic evaluation as a cost–consequences analysis, and that the numbers of participants used to estimate costs to hospital discharge and to 2 years’ follow-up were different, an overall total cost over the trial period was not calculated. Analyses were by ‘intention to treat’, indicating that the costs incurred were attributed to the original trial arm.

A conditional two-stage top-down costing approach was designed to cost prescribed medications for mothers or their babies. In the first stage, the proportion of mothers or babies with prescribed medications and the number of courses received were compared between trial arms. Were statistically significant differences to be observed between the groups, a microcosting method would be followed to cost the type of medication and the number of courses received on an individual basis. No statistically significant differences in the medications or the number of courses prescribed were observed between the groups and the cost of medication was excluded from the analysis.

Statistical analysis

Health-care resource use between treatment arms was compared using RRs for binomial variables and mean differences for continuous covariates. Costs and EQ-5D-3L scores were compared using mean differences between treatment arms. Parametric and non-parametric methods accurately estimate the true SEs of means when large sample sizes for continuous variables are used even when the data are highly skewed. 81 Hence, mean resource use, cost and EQ-5D-3L score differences, and their associated uncertainty between the INFANT decision support and no decision support groups were estimated using parametric methods. In line with the statistical analysis of the primary outcomes, differences between treatment arms were adjusted using a random intercept binomial (for RRs) or linear (for mean differences) model adjusting for the stratification factors at randomisation (centre and twin birth) and clustering because of twins and multiple-birth episodes. A 95% significance level was used in all the comparisons made.

In all categories except for two health-care resource categories (manual removal of the placenta and infant resuscitation), the level of missing data was < 5%. Therefore, the cost analysis to the point of hospital discharge was conducted using a complete case analysis. Nevertheless, the 12- and 24-month follow-ups suffered from a larger number of missing data (specifically for resource use and EQ-5D-3L) and a multiple imputation framework with a chained equation was implemented. 82 This was developed using recent guidance for handling missing data in cost-effectiveness analysis. 83 We constructed an imputation model that included covariates with complete data on trial entry characteristics (maternal age at trial entry, twin pregnancy, gestational age at trial entry, whether the mother was nulliparous or multiparous, the baby’s birth weight and mode of delivery), EQ-5D-3L scores and all individual categories of resource use variables at 12 and 24 months’ follow-up. We used prediction mean matching, estimated 50 different imputations and the imputation model was implemented separately by trial allocation. Mean estimates and estimates of SEs were combined between imputed data sets using Rubin’s rule84 and were also adjusted using a random intercept binomial (for RRs) or linear (for mean differences) model adjusting for the stratification factors at randomisation (centre and twin birth) and clustering because of twins and multiple-birth episodes.

Presentation of the results

The findings of the clinical study in Chapter 6 showed no differences in the composite primary outcomes at birth, or in PARCA-R composite scores at 2 years. Given these findings, we chose to present the results of our economic evaluation (using the clinical outcomes reported previously) with a cost–consequences analysis. Our statistical analysis plan refers to the estimation of a cost-effectiveness analysis, but with no differences in costs or effects between the groups, there was no evidence of differences between the groups to generate this. A cost–utility analysis could not be conducted, owing to the lack of HRQoL data at baseline and postnatally, to derive quality-adjusted life-years. Given the overall trial results, we considered that presenting the data in a disaggregated manner to show the costs and benefits (consequences) for different time periods provides the most useful information to complement the clinical findings.

The study was conducted at multiple labour ward sites across England, Scotland and the Republic of Ireland, with differing configurations of care and economies of scale strengthening the generalisability of our results. A useful ancillary benefit of this study is that it provides detailed costs of intrapartum care, which contributes to the broader field of evidence available for health economic evaluations in the perinatal research arena.

Findings

Both the clinical and cost–consequences analyses did not identify statistically significant differences between the trial arms. There were also no differences in the direction of costs, namely a consistent pattern of cost increase in one trial arm compared with the other. Within the cost categories there were small differences, such as secondary care for mothers post birth, but, overall, the differences between groups did not reflect a direction. We had anticipated that a decision support tool to prevent poor perinatal outcomes might have lifelong effects, that these could be modelled using decision-analytic or Markov models, and that ‘obstetric litigation costs averted’ would have been a key cost driver. Nevertheless, there were no differences in cost or effectiveness to model between the arms of the trial to 24 months post birth and for the longer term. Research was undertaken during the study to identify a composite ‘quality of care’ variable that would identify substandard (and potentially negligent) clinical care during birth. The consistent and methodical documentation of birth information captured in the Guardian system and decision support software (INFANT) might assist an interrogation of the ‘quality-of-care’ for clinical staff and may be useful in future studies. The software did not assist research for a longer-term cost-effectiveness study here but it has the potential to shorten an obstetric litigation process and even potentially to alter the outcome of some cases. This hypothesis is currently untested and may be relevant for future research.

The trial was not designed to assess the cost and benefit of the Guardian system and the value it provides for labour ward staff. No research was undertaken to explicitly cost Guardian separately from the decision support tool (INFANT). However, we did probe whether or not the combined information display (at the patient’s bedside, centrally or remotely) and the interaction with the decision support tool caused a cost shifting or change to practice for staff for efficiency purposes. We conducted informal interviews at 11 out of 23 sites, which were all sites where research midwives agreed to discuss the health economics component including whether or not the sites had:

• installed Guardian for the study and had changed to be wholly paper-free, using it for all births since the start of the trial

• installed Guardian for the study, but did not use it consistently in the ward

• used Guardian prior to and after the trial for all births.

In summary, feedback from the interviews was consistent across the sites. Interactions with Guardian and the decision support (INFANT) system produced negligible changes and affected clinical staff differently. Midwives generally reported no change to practice but stated that the alarms during the second stage of labour sometimes distressed patients and might require additional checks or review, or even the option to switch off the software. There were a few reports of increased visits to the ward by clinical staff, querying yellow and red alerts. Most midwifery co-ordinators reported that the convenience and accessibility of the display platforms increased time efficiency for staff co-ordination and allocation. Clinicians reported that, although the duration of their staff shift did not change, they had greater flexibility around location (with an increased freedom to be desk based, enabling work time to be more productive). Central hospital information technology staff identified an increase in their staff time dedicated to the labour ward, providing technical support to the midwifery and medical staff. It was difficult to separate out the impact of Guardian and decision support (INFANT) for this particular activity, as both collect and display information. However, there did not seem to be a striking change to the workload models for clinical staff, for cost shifting or efficiency. Having documented the findings of this research question, we did not attribute a cost impact.

Limitations

As discussed, the economic evaluation presented here was originally intended to be a cost-effectiveness analysis. The incremental cost-effectiveness ratio (ICER) was to be expressed as an incremental cost per poor perinatal outcome prevented (at hospital discharge following birth). Two longer-term cost-effectiveness analyses were planned: (1) to estimate the cost-effectiveness of the decision support software (INFANT) when surviving children reached 2 years of age and (2) to incorporate lifetime cost and health consequences of the decision support software (INFANT) for the mother and child within an economic modelling framework. Given that there were no statistically significant differences between costs and outcomes at post-birth discharge or at 24 months, we would not add value to this research with a longer-term framework. A cost-effectiveness analysis in the short term to include the cost of the software would only make the INFANT software more expensive and, thus, less cost-effective. Our original plan to perform multiway sensitivity analyses, to estimate and value the initial and annual maintenance fees for the decision support tool (INFANT), would make the decision support arm more expensive. As stated earlier, several strategies had been developed to estimate the additional software costs (apportioned per birth) via estimates of installation and maintenance fees or via a commercial strategy by K2 Medical Systems, but given the findings in the trial, we did not pursue a final cost estimate for the INFANT software.

The study is limited by different components of missing data. The trial suffered a large loss to follow-up; 46% of women contacted at 12-month follow-up and 38% of women contacted at 24-month follow-up returned questionnaires. Although numerous methods and substantial effort was invested to increase the response rate, it was an unsurprising outcome. Labour is a life-changing but acute event, and the majority of the women in this study had uncomplicated pregnancies and a fairly straightforward labour (albeit requiring EFM during the event). Most also had healthy babies so we surmise that they would not have felt an innate need to personally ‘invest’ in the study, in a manner equivalent to suffering a severe long-term illness. We also identified women pregnant with their second baby while completing questionnaires about their first, reflecting a progression in their life stage from the original birth event. Our only contact with the women was via postal address and, with limited resources, once this connection was lost as a result of residential change, we were not able to trace them further. Finally, conversations with research midwives revealed that, although recruitment into the trial was explicitly and clearly communicated to women and their partners, and consent was required for participation, many would not have identified the use of the decision support software (INFANT) separately from their overall birth experience. It was primarily used by midwives and would have been associated with other clinical activity, such as documenting patient information into the system.

As described throughout this chapter, we resolved the issue of missing data in different ways. We ensured that missing data are noted in detail throughout, in the flow chart (see Figure 41), in each table of resource use and in the final cost analyses (see Tables 37 and 38). For the 12- and 24-month follow-ups, we account for missing data using multiple imputation techniques.

National Perinatal Epidemiology Unit, University of Oxford (from January 2009 to May 2012)

• Vicki Barber, Trial Director

• Emma Haines, Data and Administrative Co-ordinator

• Andy Kirk, Webmaster and Design Co-ordinator

• Louise Linsell, Senior Medical Statistician

• Katie Lean, Recruiting Midwife Co-ordinator

• Linda Mottram, Trial Co-ordinator

• Liz Schroeder, Perinatal Economist

• Clare Shakeshaft, Study Co-ordinator.

Comprehensive Clinical Trials Unit, University College London (from 1 May 2012 to 1 June 2016)

• Julie Bakobaki, Clinical Project Manager

• Philip Bakobaki, IT Developer

• James Blackstone, Data Manager

• Mary Yip Braidley, Trial Manager

• Jackie Coleman, Trial Co-ordinator

• Jade Dyer, Data Manager

• Abigail Howarth, Data Co-ordinator

• Dawn Letchford, Data Entry Assistant

• Victoria McCudden, Clinical Project Manager

• Guy Schroeter, Clinical Project Manager

• Heather Short, Trial Manager

• Irene Simmonds, Trial Manager.

Data collection

A prospective economic evaluation is being conducted alongside the trial, with the aim of estimating the cost-effectiveness of the intelligent decision support software. Information on resource utilisation will be collected through the Guardian data collection system, hospital-patient administration and maternity information systems. Observational research methods will be used to collect additional costs in intrapartum, postpartum or neonatal care for the first analysis (study aim 1).

Postal questionnaires sent to parents at 1 year and 2 years post discharge collect resource use data for the health service over that period (study aim 2).

Decision-analytic modelling methods (or Markov methods if required) synthesising primary INFANT and secondary cost and epidemiological data will be used to estimate the cost-effectiveness of longer-term outcomes (study aim 3).

A stand-alone study exploring litigation for obstetrics in the NHS and the potential effect that this intervention may have, using current primary data sources provided by the NHS LA and outcomes from the trial will also be undertaken (study aim 4).

The recruitment of study participants and data collection for the health economics can be viewed in the following flow chart (Figure 42).

FIGURE 42.

Flow chart depicting recruitment and data collection for INFANT health. a, +/– represents with or without additional data collected by the midwife as necessary. b, Only mothers recruited during the first year of the trial so that follow-up of this group can be completed around the time that the trial stops recruiting. c, x represents the actual numbers that would be collected.

Trial design

INFANT is a multicentre individually randomised controlled trial of 47,112 women who are judged to require continuous electronic fetal monitoring in labour. It is a two-arm parallel trial with one arm allocated to CTG monitoring with decision support and one arm allocated to CTG monitoring only. At 2 years after trial entry, a random sample of 5000–7000 children (2500–3500 in each group) are followed up at 2 years. This sample is taken from within the sample recruited during the second year of the trial so that follow-up of this group can be completed around the time that the trial stops recruiting.

For the economic evaluation, a subsample of approximately 750 infants from each trial arm randomly selected within the second year, as well as all babies with the primary outcome who survive to hospital discharge, are followed up at 1 and 2 years for resource use data in order to estimate the incremental cost per disability free life-years gained at 2 years. Decision-analytic modelling techniques will be used to extrapolate cost-effectiveness over a lifetime.

Time horizon and perspective of the INFANT economic evaluation

The economic evaluation will be conducted from a health service perspective and therefore only direct costs to NHS hospital providers will be included. Societal costs, such as travel time and lost productivity to families will not be captured. (Estimates of the longer-term costs of care including litigation costs are discussed in Economic evaluation design issues for INFANT study aim 3 (modelling longer-term outcomes) and Economic evaluation design issues for INFANT study aim 4 (modelling clinical scenarios that will impact on obstetric litigation claims).

Sample size and power

The sample size of the INFANT economic evaluation is based on the primary clinical outcomes of the INFANT trial, which is currently a pragmatic approach to the determination of sample size and power calculation. Different techniques have been proposed for the estimation of statistical power and sample size for economic evaluation in randomised trials, but current practice tends to prefer power calculations based on primary clinical outcomes. This is partly because of the complexity of trying to predict the main outcome of interest to economists, which is the joint distribution of the difference in costs and benefits between treatment arms. 6

Study end points

In the baseline study (study aim 1), we are using an intermediate outcome (poor perinatal outcome prevented at hospital discharge) and hence additional resource use and unit cost data are needed to capture longer-term costs and outcomes. This is the purpose of the study at 2 years where the outcome measure is quantified in terms of disability free life-years gained (study aim 2) and for the extrapolation of longer-term outcomes expressed as QALYs over a lifetime or to 18 years (study aim 3).

Database design and management

Collection and management of the economic data are fully integrated with the management of the clinical data and, as such, there will be no distinction between the data sets for study aim 1. Ongoing data quality monitoring occurs timeously to address missing and poor-quality data issues. Data queries are consistently managed to maximise data completeness and quality. The data formatting procedures needed for the economic analysis were prespecified such that the transfer of all necessary data for the economics study is timely, and the design and piloting of the data capture system is complete. Double data entry for the 12- and 24-month parental questionnaires is in process.

Trial costs/resource use

The economic evaluation focuses on main cost drivers (such as days spent in intensive care) as well as resources that are expected to differ between the trial arms. All resource use including intervention related resources will be included in the cost analysis. Table 46 documents the resource use data identified for the health economics component.

For each resource, the level of aggregation will be prospectively determined. As an example, inpatient hospitalizations might be considered in disaggregated units, such as staff time, or in highly aggregated units, such as numbers of hospitalizations or days in the hospital. A mixed case approach to costing will be used, dependent on resource use patterns expected, and availability of national standardised cost data (from Department of Health reference costs, typically used in economic evaluations). Items will be captured in disaggregated units where relevant, and such costing is typically labelled ‘bottom up’. This will be achieved by asking midwives/clinicians to document relevant staffing, medications and equipment. They will then be sent a micro-costing sheet to correct with their own resource components (Table 47) which will be very detailed, capturing all resource components that might be used. Further information will also be captured during formal interviews to include cost of the intervention itself, including the potential impact on staff working patterns.