Comment on my post about the Beneductus trial

The authors of the Beneductus trial commented on my post about the trial, but it has somehow disappeared from the comment section of the blog, as they raise very valid points, I thought I would copy what they sent here as a new post.

First, I would like to say that I often try to write my posts to be provocative, and hopefully to make us all consider how best to treat newborn infants. Although I might criticise how a trial was done, I have huge respect for everyone who tries to do prospective research. We will never advance if everyone sits about writing blogs about others research, rather than doing the very difficult work, which always involves multiple compromises, of performing new trials. That being said, here is the text of the comment from Willem de Boode and Tim Hundscheid about the trial.

Thank you for your interest in our recent publication entitled ‘Expectant Management or Early Ibuprofen for Patent Ductus Arteriosus’. (1)

We have read your blog, posted on December 21, 2022 with great interest and would like to comment on this.

The first question you raised was about the mortality rate in the two study groups, more
specifically death before discharge. Although mentioned in Table S2 – Outcome parameters with definitions, the mortality prior to discharge is not reported in the paper. This is related to the fact that death before discharge was identical to the mortality at 36 weeks postmenstrual age. In the original Table depicting mortality before 28 days postnatal age, before 36 weeks postmenstrual age and before discharge, the latter was removed, since the data were exactly the same. In conclusion, there was no significant difference observed in mortality between the two groups; death occurred in 19 of 136 infants (14.0%) and in 25 of 137 (18.2%), respectively (absolute risk difference, -4.3 percentage points; two-sided 95% CI, -13.0 to 4.4).

In response to your other comments we would like to respond as following.

Paracetamol was given to 34 of 136 patients (25.0%) in the expectant management group, as compared to 52 of 137 patients (38.0%) in the early ibuprofen treatment group. So paracetamol was prescribed less frequently in the expectant management group. As the dosage used was the ‘normal’ analgesic dosage (20-40 mg/kg/day), which is lower than the dosage of 60 mg/kg/day investigated in randomised trials on PDA closure (2, 3), this is unlikely to have influenced our findings.

You questioned about the use of diuretics in this study. As described in the study protocol (4), patients randomised to the expectative management arm will not receive COXi, including for indications other than closure of the DA. No (additional) putative interventions to prevent or treat a PDA, for example fluid restriction or diuretics for that purpose only, are allowed. There was no significant difference in the use of diuretics between the study groups. The observed use of diuretics in this study population of extreme preterm infants is similar to published data. (5-7)

In your opinion the study was “drastically underpowered”. As mentioned in the paper as one of the limitations, ‘enrollment was stopped after only 48% of the planned sample size had undergone randomization’. However, this does not mean that the study was underpowered, let alone ‘drastically’ underpowered. The results are very clear and speak for themselves. With an absolute risk difference of -17.2 percentage points with a one-sided 95%-CI of -7.4 percentage points it can be concluded that expectant management for PDA in extremely premature infants was noninferior to early ibuprofen treatment with respect to necrotizing enterocolitis, bronchopulmonary dysplasia, or death at 36 weeks’ postmenstrual age.

Referring to the Figure in the blog of possible outcomes of a non-inferiority trial, our results are even consistent with the upper outcome, noninferiority and superiority, since the upper boundary of the one-sided 95% confidence interval didn’t overlap the value of 0%.

We’re sorry to hear that you consider our composite primary outcome as “weird”. We fully understand and acknowledge that parents of the infants that are treated on our NICU’s are not only interested in that outcome at that specific age. That’s why we’re very pleased to have a very inspiring and good collaboration with Care4Neo, the Dutch organisation representing the interests of preterm and newborn infants and their families. Care4Neo was also involved in this study and the publication.

As depicted in Table 3 and S7 there were no differences between the groups for need for
supplemental oxygen, and length of hospitalisation. There was a slight, significant difference in the time to full enteral feeding, which was shorter in the expectant management group (Table 3).

Every study will raise additional research questions, and the follow-up of the BeNeDuctus study population is of major importance. As published in the study protocol, all patients are evaluated at a corrected age of 24 months.

Regarding your opinion about ‘many other rather strange choices in data presentation’, such as West syndrome and wrist abscess in the list of adverse events, we would like to say that all reported adverse events are summarised in Table 4. It would be very negligent to exclude West syndrome, when this has been reported by one of the centres as an adverse event.

Hopefully we have clarified important issues to your satisfaction. In our opinion, the results are really important and the suggestion of potential harm of Ibuprofen should be taken seriously and investigated in more detail. Unfortunately, not all relevant results are immediately known and we would like to invite you to take notice of subsequent publications regarding the BeNeDuctus Trial in the near future.

Tim Hundscheid and Willem P. de Boode

References

  1. Hundscheid T, Onland W, Kooi EMW, Vijlbrief DC, de Vries WB, Dijkman KP, et al. Expectant Management or Early Ibuprofen for Patent Ductus Arteriosus. N Engl J Med. 2022.
  2. Harkin P, Harma A, Aikio O, Valkama M, Leskinen M, Saarela T, et al. Paracetamol Accelerates Closure of the Ductus Arteriosus after Premature Birth: A Randomized Trial. J Pediatr. 2016;177:72-7 e2.
  3. Ohlsson A, Shah PS. Paracetamol (acetaminophen) for patent ductus arteriosus in preterm or low birth weight infants. Cochrane Database Syst Rev. 2020;1(1):CD010061.
  4. Hundscheid T, Onland W, van Overmeire B, Dijk P, van Kaam A, Dijkman KP, et al. Early treatment versus expectative management of patent ductus arteriosus in preterm infants: a multicentre, randomised, non-inferiority trial in Europe (BeNeDuctus trial). BMC Pediatr. 2018;18(1):262.
  5. Hagadorn JI, Sanders MR, Staves C, Herson VC, Daigle K. Diuretics for very low birth weight infants in the first 28 days: a survey of the U.S. neonatologists. J Perinatol. 2011;31(10):677-81.
  6. Gouyon B, Martin-Mons S, Iacobelli S, Razafimahefa H, Kermorvant-Duchemin E, Brat R, et al. Characteristics of prescription in 29 Level 3 Neonatal Wards over a 2-year period (2017-2018). An inventory for future research. PLoS One. 2019;14(9):e0222667.
  7. Guignard JP, Iacobelli S. Use of diuretics in the neonatal period. Pediatr Nephrol. 2021;36(9):2687-95.

The lack of mortality between 36 weeks and discharge is reassuring, but surely it should have been in the initial publication? This is not, unfortunately infrequent, there are a few other trials where it has been difficult to find the mortality after 36 weeks, even though such deaths are uncommon, they can make a difference to the interpretation of the results. The stop-BPD trial for example, had “statistically significant” difference in mortality at 36 weeks, but not at discharge, and not at 2 years follow-up, there were actually in that study 17 deaths between 36 weeks and discharge (8 vs 9 in the 2 groups) so the p-value was just over .05 at discharge, after being just under .05 at 36 weeks. Another illustration of why we should stop using simple p-value thresholds to decide if something is real or not!

It also is not necessary to adjudicate all outcomes at the same moment! Even if BPD is decided at 36 weeks, mortality before discharge can still be the primary survival outcome, and even if some babies with BPD die between 36 weeks and discharge it is simple to count them as a death, and as a BPD outcome.

Which brings me to the issue about my calling ‘death or BPD at 36 weeks’ a “weird” primary outcome. What I meant is that I don’t decide whether to give a medication or not based on what the baby will be doing at 36 weeks. The decision is based on whether the baby is more or less likely to survive, and, if they survive, how they will evolve over their time in hospital, and after.

Determining the severity of lung injury by need for oxygen (or respiratory support) at 36 weeks is a very common practice in randomized trials and in epidemiologic studies of preterm babies. This comment is, therefore, not really directed at the investigators of the Beneductus trial alone, but at all of us as we go forward in neonatal research. I note again, that even though the proportion of infants with “BPD” was lower in the expectant treatment group, they only had (as a median) 1 day less oxygen treatment than the ibuprofen group. The big difference in BPD (33% vs 51%) despite almost no change in median duration of oxygen therapy suggests strongly that a lot of the babies labelled as “BPD” came out of oxygen very soon after 36 weeks.

In day to day practice, I don’t actually care if a baby comes out of oxygen before or after 36 weeks, and parents don’t care either (we asked them: article in submission, I will blog about that study when it is finally accepted). What matters to parents is whether the baby goes home in oxygen, whether their discharge is delayed by respiratory concerns, whether they sleep and eat normally after discharge, whether they have to make multiple hospital or doctor’s office visits for their respiratory problems. I was very happy to see that the Care4Neo group was involved in the study, it is essential for the future that such groups are involved, and in particular that they are involved in the development of our primary outcome variables.

I recognize of course, that we need interim outcomes, and that all trials cannot be done with the primary outcome being respiratory symptoms up to adolescence!! Surely we should be analyzing the impacts of our interventions on outcomes which are important to babies and their families, those interim outcomes should be determined with parent groups. They might well be interested in home O2 therapy, delayed discharge for respiratory reasons, and home gavage, perhaps. Oxygen need at 36 weeks has very limited predictive capacity for future respiratory health. (Barrington KJ, et al. Respiratory outcomes in preterm babies, is bronchopulmonary dysplasia important? Acta Paediatr. 2022).

I think the Beneductus trial does show that there were no clear benefits of treating the PDA, and that a dedicated group of researchers can construct a trial in which there is a group in which almost no-one receives a cox inhibitor. The trial does suggest that such an approach is not worse than early routine ibuprofen for a large PDA with left to right shunt, but there are still concerns about power, despite what is written in the comment: post-hoc power analysis is useful, but after early termination of a trial must be interpreted carefully. At least in this instance the trial was not terminated after examining the data, which is always dangerous, but because of enrolment difficulties and funding issues.

The follow up of the Beneductus trial will be very informative, I would be surprised if there were any neurological or developmental differences between groups, so other health outcomes will be very interesting. If they show no advantage on longer term respiratory health (addressing outcomes of importance to families) then it would suggest that it doesn’t matter whether you treat the PDA with cox inhibitors or not.

Which makes me wonder if there might be still be a role for the drugs in babies at very high risk of pulmonary haemorrhage. A few years ago we introduced a protocol of very early screening and treatment of PDA, largely based on the trial of Martin Kluckow (Kluckow M, et al. A randomised placebo-controlled trial of early treatment of the patent ductus arteriosus. Arch Dis Child Fetal Neonatal Ed. 2014;99(2):F99-F104) showing less hemorrhage with treating a group who were at high risk of hemorrhage, based on having a PDA diameter above the 50th percentile for their postnatal age. Which means, of course that about half of the screened babies are eligible. In the Beneductus trial, using a PDA diameter of 1.5mm, about 2/3 of screened babies were eligible. I wonder if we can refine the criteria and target a subgroup where treatment will lead to the advantage of fewer pulmonary haemorrhages, which, even if we cannot prove an improvement in long term outcomes, is still something that I would like to avoid!

About Keith Barrington

I am a neonatologist and clinical researcher at Sainte Justine University Health Center in Montréal
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