Steroid drops for retinopathy?

Posted on 11 August 2026 by Keith Barrington

A just published, modestly sized, multicentre randomized masked trial from Sweden has investigated the efficacy of dexamethasone eyedrops to prevent the progression of pre-threshold RoP. Infants born before 30 weeks’ gestational age (GA) were eligible if they had prethreshold RoP, which was defined as stage 1 or 2 without plus disease in zone I, or stage 2 or 3 in posterior zone II without plus disease. (Hellstrom A, et al. Dexamethasone Eye Drops to Prevent Treatment-Requiring Retinopathy of Prematurity: The DROPROP Randomized Clinical Trial. JAMA Pediatr 2026).

Some previous observational data suggested a possible benefit, and the authors also quote a “supportive” animal study, that I think is of highly questionable relevance. In that study newborn mice had systemic dexamethasone during the hyperoxic insult, starting on day 7, and they had less new vessel formation. Other data suggest an inflammatory component to the progression of RoP, which might, therefore, be responsive to local glucocorticoids.

Dexamethasone is often prescribed after laser therapy, and some people had started using it prior to laser, and thought they saw improvement. This had lead to a small number of observational studies suggesting possible reduction in the progression of what is now called “Type 2 RoP”, that is, retinopathy that requires very close surveillance, but not immediate intervention. So DROPROP was born, (quite a good acronym) Hellstrom A, et al. Evaluation of timed dexamethasone eye drops to prevent proliferative retinopathy of prematurity: a study protocol for a randomized intervention, multi-centre, double-blinded trial (DROPROP). BMC Pediatr. 252025. p. 332..

This was the study protocol, all exams were recorded by RetCam and evaluated centrally.

100 babies were randomized 50:50, and they had very similar RoP stages at baseline, dosing was 1 drop per eye every other day for stage 1 or 2 ROP, and 1 drop per eye daily for stage 3 ROP. The primary outcome was progression to “type 1” RoP, that is need for immediate treatment, which could be either laser or antiVEGf injections.

The results showed that 38% of placebo infants, and 20% of dexamethasone-treated progressed to type 1. There appears to be a major error in the labelling of the figure A, as it shows about 65% compared to 37% had type 1.

There was some minor evidence of systemic absorption, with salivary cortisol being lower during treatment, and a possible minor impact on length growth. There was no evidence of intra-ocular hypertension or other adverse local effects.

Although a well-done study, unfortunately there were 7 infants who had invasive treatment despite not satisfying the pre-agreed criteria for therapy. Obviously we don’t know what would have happened to those babies had they been followed without intervention. An analysis of the results without those babies gives a similar relative risk of RoP, of almost exactly 0.5, with 95% CIs of 0.26 and 1.0 (that is my own calculation using Medcalc online, and obviously unadjusted).

The visual abstract accompanying the article is really designed for dummies, it is very stripped down, and includes an infantile cartoon of a retina. Do we really need 2 cartoons of droppers, one filled in in a grey shade and the other white? Surely a visual abstract could be a useful adjunct to an article without being so reductive. That visual abstract states “there was no statistically significant reduction in incidence of type 1 ROP” between groups.

The actual abstract of the article is more reasonable and nuanced “Timely administration of topical dexamethasone numerically reduced the risk of prethreshold ROP progressing to treatment-requiring type 1 ROP. Although the analysis did not reach statistical significance, these findings suggest that topical dexamethasone may be a safe, noninvasive strategy to reduce the need for invasive treatment.”

That is quite appropriate, although the use of the word “may” could apply to almost any intervention. What do we do with these results? Do we need more studies?

I am in 2 minds, I think that if my own baby had pre-threshold RoP and I saw these results, I would be very tempted to ask for the drops. There seems to be a likely benefit, and little risk. But widespread use of dexamethasone eyedrops in large numbers of babies will inevitably lead to more complications, so it would be nice to be somewhat more certain about the benefit. The 95% CI do, just, include the possibility of no effect, the adjusted Odds Ratio is probably between 0.17 and 1.12. Although it would be nice to have more stringently positive data, it might be difficult to convince many parents in a future trial to have the risk of receiving a placebo, and perhaps an increased risk of their infant being subjected to retinal laser ablation. It might, on the other hand, be more reasonable to randomize infants in whom the intervention, in case of progression to Type 1 disease, would be antiVEGf injection.

Laser treatment destroys the peripheral retina and leads to an extremely high incidence of high myopia, avoiding it is a worthwhile outcome. Anti VEGf treatment, in contrast, is relatively benign, despite some stated concerns about systemic effects, it appears to be extremely safe.

The next baby in my practice? I think if a baby has Type 2 disease, then a discussion with the parents and the ophthalmologists will be essential. Despite the evidence not being “iron clad”, the DROPROP regime seems reasonable, especially if the anticipated intervention is laser ablation.

Edit added 13 August.

Ann Hellstrom just sent a comment about this post, which you can read in the comments section. I must say, I had not read all the references in detail, and I didn’t realize that there was another animal study in the reference list which is much more relevant to this intervention. (Yagi H, et al. Timed topical dexamethasone eye drops improve mitochondrial function to prevent severe retinopathy of prematurity. Angiogenesis. 27: 2024. p. 903–17). This publication is a report of a prospective observational study of 5 preterm infants with off-label dexamethasone drops given for type 2 RoP, (all of them were stage 3, zone 2) all of whom regressed. It also reports studies in mouse oxygen-induced retinopathy with local dexamethasone application. The mouse disease has some similarities to human RoP, the immature retina is avascular, and undergoes vasoconstriction during hyperoxia, and when the mice are returned to normoxia, they develop new vessels (at least if you have exactly the right strain of mice!) Of note, the mice are exposed to hyperoxia along with their mothers who are lactating, the mothers sometimes die of hyperoxic lung damage, they usually become sterile, and they sometimes even cannabilise their pups!(Kim CB, et al. Revisiting the mouse model of oxygen-induced retinopathy. Eye Brain. 82016. p. 67–79). I also haven’t seen any evidence that the pups’ retinas develop fibrosis leading to retinal detachment, and there are, in addition, some differences in the vaso-occlusion phase, which is more central in mice, and more peripheral in humans. Nevertheless, that study by Yagi showed that giving the dexa drops to the mice during the avascular phase didn’t do much, and giving them after new vessels started to regress was ineffective. However, there was a significant reduction in neovascularization when given in the middle group, prior to peak new vessel formation.

In addition, I agree with Dr Hellstrom that antiVEGf injections are not completely benign, and shouldn’t be considered banal, but they are much less damaging to the eyes than laser retinal ablation. Avoiding laser with dexa drops is more of an advantage than avoiding antiVEGf treatment, but the long term outcome really needs to be investigated,

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Study Design: Hierarchical Composite Outcomes

Posted on 7 August 2026 by Keith Barrington

As frequent readers of the blog will know, there are major concerns about using the classical dichotomous composite outcomes for trials. One of the outcomes included is usually death, as it “competes” with many other outcomes, and the other components in the composite may range from the extremely important such as ‘NEC requiring surgery’ or ‘profound disability’ to the less important, such as culture-negative sepsis, or oxygen requirement at 36 weeks.

A dichotomous composite outcome treats all components as if they are equal; adding components to the outcome may increase the power (although not always) especially when some of the outcomes are rare. So studies investigating therapies in infants of 28 to 32 weeks will need to be enormous to show differences in mortality, as it is relatively uncommon, but if a second outcome of higher incidence is added, such as failure to extubate by 12 hours as an example, sample size may become manageable. Thus trials with multiple components of the primary outcome have been developed, sometimes being rather unwieldy. For example, the recent LIFT trial of lactoferrin prophylaxis (Tarnow-Mordi WO, et al. The effect of lactoferrin supplementation on death or major morbidity in very low birthweight infants (LIFT): a multicentre, double-blind, randomised controlled trial. The Lancet Child & Adolescent Health. 2020;4(6):444–54) used the following as its composite primary outcome “death or major morbidity, defined as: brain injury on ultrasound, NEC, (Bell stage ≥II), culture-proven late-onset sepsis, or RoP requiring treatment”. The now completed LIFT_Canada trial was designed to be identical to LIFT in order to be able to perform an IPD analysis, so we used the same composite outcome (Asztalos EV, et al. Lactoferrin infant feeding trial_Canada (LIFT_Canada): protocol for a randomized trial of adding lactoferrin to feeds of very-low-birth-weight preterm infants. BMC Pediatr. 2020;20(1):40). Other trials have had even more components to the outcome, which can make interpretation difficult, but might also actually decrease power, as large proportions of subjects will have at least one of the outcomes, and be counted as an adverse result, which might hide real important differences.

Among the problems with dichotomous composite outcomes are that if different parts of the composite change in different directions, then the overall analysis may be null, which might hide an important benefit, or adverse effect. The best example of this in neonatology is the SUPPORT trial, which showed a reduction in RoP (which was expected) but an increase in mortality (which was a surprise, but has been confirmed by other trials), when babies received oxygen targeting a lower saturation of 85-90% rather than a higher 91-95%. The primary outcome was not different between groups, even though most people would agree that dying is a worse outcome than “threshold retinopathy or retinal surgery or bevacizumab injection” (the definition of severe RoP used).

One way to address these problems is to use Hierarchical Composites, where the various parts of the composite are placed in ascending order of seriousness. The analysis requires either that the patients are entered as pairs, and each is compared to the paired patient in the other group, or, now more commonly, every individual in group 1 is compared to every individual in group 2. For each paired comparison, if one survives and the other dies then the survivor is declared the winner. If both die, then the outcome is a draw. If they both survive, then the second outcome in severity is compared, and a winner (if there is one) is then declared, and so on through the list of outcomes of diminishing importance. Eventually a winner or a draw is determined.

The analysis of such outcomes is still being developed, the simplest, I think, is the “win ratio” (Cunningham JM, et al. Win Ratio Method for Hierarchical Composite Outcomes in Randomized Clinical Trials. JAMA. 2026) that I have written about a few times. There are several examples of trials where the primary analysis of the outcome as being dichotomous has shown a null result, but the analysis using win ratio has been significant, demonstrating a real clinically important difference in the results between 2 interventions, missed by conventional methods. Several trials have more recently been designed to primarily use Win Ratio, or other hierarchical endpoint analyses.

That article by Cunningham discusses the analysis of a recent cardiovascular therapy trial (where these types of endpoints have been most widely used), and points out that the significant difference between results that the trial found (comparing 2 different treatments in Chagas’ disease cardiomyopathy) was not in mortality, or hospitalisation, as you can see from the figure below, but in the results of a blood test, measuring the change in NT-proBNP. The figure shows the number of wins for each group, the number of ties, and the overall difference between groups, which was almost entirely due to changes in the serum marker.

This points out a limitation of this kind of trial analysis, it is important to include items which are of clinical significance, that is, they are of significance to patients. I doubt that many people care too much about the relative changes in their NT-proBNP. Perhaps how far they could walk without being breathless, or something else of importance to the patient, should have been measured.

Indeed, how the components of the composite are chosen and their relative importance is a major question for future trials. As another article in JAMA points out (Ehrenzeller S, et al. Randomized Clinical Trials Using a Hierarchical Composite Primary End Point: A Scoping Review. JAMA Netw Open. 92026. p. e2625935), of the 92 trials they found which had used hierarchical composites, the large majority, 82%, included no information about how the hierarchy was developed.

It is essential that multiple different stakeholders are involved in developing future hierarchical composites, and that, importantly, parents and former sick newborns are given a free voice in suggesting their own priorities. (Callahan KP, et al. Integrating parent voices into research at the extremes of prematurity: what are we doing and where should we go? J Perinatol. 2024). Much as I admire the development of Core Outcomes Lists, often the processes involved have had parents and other partners choosing among our predefined list of possible outcomes. The parents voices project, though, has shown that some of the things that we include in lists of outcomes are of little importance to parents (Demers C, et al. Measuring family-important outcomes in large neonatal networks: where we are and where we need to go. Semin Perinatol. 2025;49(7):152149), such as needing oxygen at 36 weeks (!), and others that we rarely discuss, and don’t even measure (such as feeding problems post-discharge), are very important to them.

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Not neonatology. Trip to Costa Rica

Posted on 6 August 2026 by Keith Barrington

Our family vacation this year was to Costa Rica. One week just Annie and me, then another 2 weeks with Annie’s mother and 2 of our children. Costa Rica has a well-deserved reputation as a destination for holidays with abundant easy access to wildlife. 30% of Costa Rica is protected land, and vigorous laws have ensured the survival of endangered species, and the return of some that were previously endangered, such as the Costa Rican population of Scarlet Macaws.

There were many great experiences on the trip, hikes and spectacular scenery, as well as other opportunities to photograph the wildlife

Including this Mantled Howler Monkey carrying a baby who was peeking out of mom’s fur.

A tiny Volcano Hummingbird, only found at high altitude along the Talamanca Cordillera.

This Golden-browed Chlorophonia is also restricted to that range.

For those interested, I posted a few other photos on my other blog keithbarrington.com, including this iconic Costa Rican bird, the Resplendent Quetzal

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Routine vitamin K prophylaxis. Why are there so many refusals?

Posted on 6 August 2026 by Keith Barrington

This is still a fairly rare phenomenon in my hospital, but it does seem to increasing slightly here, as it is just about everywhere else.

The science is settled, transplacental transfer of vitamin K is extremely limited, hepatic stores at birth are very low, and human milk contains extremely low concentrations of vitamin K. In later life, most of our vitamin K2 is produced by intestinal microbiota, including by our friends the Bifidobacteria, as well as Bacteroides and Prevotella, but we don’t have many of those present at birth or over the first few days. Routine supplementation with intramuscular vitamin K is an intervention with amazingly positive risk/benefit balance, which has proven its worth over decades. Like many other preventive interventions, the success of routine vitamin K prophylaxis is probably part of the reason for the current situation. In addition, the relative rarity of what is now called Vitamin K Deficiency Bleeding (VKDB, which I think is a better name than Haemorrhagic Disease of the Newborn) means that most families will never have heard of a case.

A new publication from Sweden (Simatou E, et al. Vitamin K Prophylaxis in Newborns and Bleeding in Infancy. JAMA Pediatr 2026) has the usual limitations of all large database studies, uncertainty about the accuracy of each individual data entry, diagnostic standards etc. But it points out that infants (>35 weeks GA) without a record of neonatal IM vitamin K prophylaxis (checkbox left empty) had a much higher rate of having an ICD-10 diagnosis of “any bleeding episode” prior to 6 months of age. They also had a much higher risk of having intracranial bleeding, or the combined outcome “death or bleeding”. When the analysis was restricted to the first 28 days of life the associations were even stronger. The greatest difference between groups with and without IM vitamin K administration documented was in “death or intracranial bleeding” in the 1st 28 days of life: 0.1% in infants with VitK, 1.5% in those without. Of course, most of those deaths would have nothing to do with vitamin K, but they should be equal in the 2 groups. However, when I look at these new Swedish data in detail, there are very many more deaths among the infants without a record of Vitamin K administration: 1300/100,000 compared to those who received vitamin K, 50/100,000, before 28 days of age (calculated by subtracting ICH from “death or ICH”) which I don’t fully understand.

Other data show that babies who don’t get vitamin K also are more likely to be born at home, more likely to not have Hepatits B or other immunizations (Loyal J, Shapiro ED. Refusal of Intramuscular Vitamin K by Parents of Newborns: A Review. Hosp Pediatr. 102020. p. 286–940 and, I would think, more likely to be exclusively breast fed, which increases the chances of VKDB, as there is much more vitamin K in artificial formula.

That review article on refusal rates (Loyal et al) also reviewed the published reasons parents gave for not wanting prophylaxis. they broke them into 3 categories. 1. Concern of harm from the injection (from the preservatives or from pain, or because the dose is too high, or it causes cancer). 2. Desire to be natural, often assuming that being “natural” meant that vitamin K insufficiency is not a problem. 3. Belief in alternative prophylaxis, either oral, or maternal or something else.

As I was preparing this, I came across an excellent review article (Mirone A, et al. Vitamin K Prophylaxis in Newborns: A Narrative Review of the Molecular Basis, Clinical Evidence, and Comparative Effectiveness of Intramuscular Versus Oral Administration and Parental Hesitation. Int J Mol Sci. 27 2026) which led to several of the references I have included.

What to do about this worrying and dangerous trend?

Education during pregnancy is essential, but I am doubtful that will have a major impact on the current trend. Education at birth is also important, and nurses have a major role to play (Holley SL, et al. Educating Parents on Vitamin K Prophylaxis for Newborns. Nurs Womens Health. 2020;24(4):283–93), but again I am sceptical that many minds will be changed.

I just did a quick search on Facebook about Vitamin K in babies, fortunately the very first result (maybe that’s just my algorithm) was from the excellent Jessica Knurick, whose clear evidence-based videos are always spot-on. The remainder range from clear support for the science to fear-mongering nonsense, including one from a prominent physician fear-monger who claims that God wouldn’t make babies short of vitamin K, I don’t know how he explains any congenital anomalies. Other posts frequently talk about how blood should be “thinner” at birth, often stating that vitamin K increases viscosity preventing the good cells from doing their work. Like a lot of medical pseudoscience on the internet, the nonsense is frequently repeated by other “influencers” who are usually selling something, even if its only subscriptions to their channel. They also often claim that physicians are making the vitamin K recommendation because of a personal gain. How we are supposed to be making money from recommending universal IM vitamin K prophylaxis, I don’t know.

One hospital in Tennessee, where there was a cluster of cases, introduced a mandatory information sheet detailing the risks of IM vitamin K refusal, and required signing an opt-out form, which is entered into the infants chart. Intramuscular vitamin K administration should be automatic, and require an opt-out for reluctant parents, whether requiring that parents read a document and sign a form will help, I am unsure. It has been proposed that parents should not even have the right to opt out (Isennock SM. The Legal Limits of Parental Autonomy: Do Parents Have the Right to Refuse Intramuscular Vitamin K for Their Newborn? HCA Healthc J Med. 42023. p. 5–11), as vitamin K is safe and effective and we need to protect newborns against badly informed parents; even though I have a little sympathy for that attitude, I don’t think its likely to get very far.

As I was preparing this I came across new publications about the resurgence of Tetanus (Edwards KM, Rathore MH. Resurgence of Tetanus-Why the Vaccine Remains Instrumental. JAMA. 3362026. p. 99–100), and meansles, on the CDC measles surveillance page, which notes that there are already more measles outbreaks and individual cases by June this year than in the whole of 2025, which was already 10 times higher than 2024.

I am really at a loss to know how to approach the uncertainties of certain parents, the few who are rabidly anti-science, and the many who are just confused and hesitant. Requiring social media companies to reign in the misinformation would be a good idea, but is not likely to get very far with extreme right wing conspiracy theorists being responsible for the most potent communication vehicles that humanity has ever known.

The first step for an individual case of vitamin K refusal has to be to recognise that all parents want the best for their babies, and that most of them will have no idea about the devastating consequences of VKDB. They will not understand the deaths and the brain injuries that can occur, or that they can be almost entirely prevented by a brief painful injection of a vitamin.

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Finally, a SMART approach for the PDA?

Posted on 3 July 2026 by Keith Barrington

One of the thorniest topics in neonatology currently. Some experts seem certain that we can define PDAs that benefit from early treatment. In contrast, the recent trials don’t show any clinical benefit in early treated groups compared to controls, and indeed usually show an increase in BPD with early treatment, and an increase in mortality with very early treatment. I have posted many times over the last few years about trials of PDA closure. See here https://neonatalresearch.org/2022/12/21/the-pda-will-we-ever-know-what-to-do/ and here https://neonatalresearch.org/2023/10/20/closing-the-pda-or-leaving-it-alone/ and here https://neonatalresearch.org/2024/01/26/is-there-any-indication-to-close-the-pda/ and here https://neonatalresearch.org/2025/12/10/should-we-ever-close-the-pda/.

Bedside echocardiography has been used to try and define characteristics of the baby and the ductus that might benefit from treatment, but the difficulties in interpretation mean that most of the trials have either just confirmed patency, or have just measured ductus diameter (which isn’t much above the limits of resolution of the devices) as a criterion for entry into the trial.

Studies of the natural history of the PDA in the very immature infant confirm that, sometimes, large diameter PDAs close spontaneously, whereas other PDAs of similar size may have large shunts and tend to remain open. If we could be smarter about this, maybe we could define criteria for a study which would only include those where the shunt is causing problems, the PDA will tend to stay open, and it really is contributing to the adverse outcomes of the baby.

The latest attempt to do so is the SMART-PDA trial recently published in Archives Mitra S, et al. Selective early medical treatment of the patent ductus arteriosus in extremely low gestational age infants: a pilot randomised controlled trial (SMART-PDA). Arch Dis Child Fetal Neonatal Ed. 2026. The protocol for this pilot was previously published, and the diagram below is taken from that prior publication

The trial was performed in 4 Canadian and 3 US NICUs with functional echocardiography programs. It only included infants with a GA of <26 weeks. Of note, the trial lasted until day 7 of life. after which open label treatment of control group (or indeed active treatment group) infants was permitted.

Eligibility for the trial required an open PDA, documented prior to 72 hours of age, after which treatment in the active treatment arm followed an algorithm, requiring at least a “moderate” shunt, with “moderate” or severe clinical signs, or a “severe” shunt as defined in the right-hand column below, regardless of clinical status.

This trial was designed and powered as a pilot, with the primary outcome being the feasibility of a future adequately powered trial, feasibility being determined by the following “The proportion of eligible infants recruited during the study period, (2) the proportion of treatment outside of protocol-mandated therapy among randomised infants and (3) the proportion of infants in the control group meeting pre-defined safety criteria.” Sample size was also determined by feasibility considerations and required 100 randomized infants.

The usual clinical outcomes were collected and analyzed using Bayesian methods, and a WinRatio hierarchical composite was constructed (not mentioned in the protocol).

As a moderately sized trial there were some small imbalances in baseline characteristics, more of the controls were 24 weeks or less, more controls had normal antegrade descending aortic flow, etc. but generally speaking the groups were quite balanced.

The feasibility outcomes all demonstrated that a future trial is entirely feasible, with a high recruitment rate, and only 1 control was a protocol violation and was treated to close the PDA before 7 days of age.

In terms of clinical outcomes there were 2 differences that stand out, the most striking being the reduction in pulmonary haemorrhage in the active treatment arm, 0/51 compared to 6/53, 11%; also NEC was 6% compared to 15%.

These data were also analyzed using a Win Ratio approach, with the outcomes of Death, Pulmonary haemorrhage, sepsis, NEC or RoP. If you don’t recall what that means, basically every individual baby in the SMART group was compared with every individual in the CONTROL group, and for each comparison a decision is made whether the SMART group infant is a winner (has better outcomes) or a loser, or if there is a tie. So for example if baby 1SMART and baby 52CONTROL both survive and neither have a pulmonary haemorrhage, but baby 52CONTROL has sepsis and baby 1SMART does not, then baby 1SMART is the winner. Finally you add up all the wins and the losses, and the ratio of wins to losses is calculated. The analysis in this paper then applies a Bayesian approach, which shows that SMART has a higher likelihood of being preferable than control.

This is a much better approach than just “death or complications” as a binary outcome, as it immediately gives survival a higher importance than the other outcomes, unlike “death or BPD” (for example) which gives them equal weight. It does require some partially subjective decisions, for example I would probably put the outcomes in the following decreasing severity order : septic shock, NEC grade 3, NEC grade 2, culture-positive sepsis without shock. Pulmonary haemorrhage, I certainly agree, is a very important complication, especially as defined here, associated with increased oxygen requirements leading to an MAP >12 and an FiO2 >60%. Putting it as the second most important adverse outcome seems reasonable.

Of note, 16 (/53, 30%) control infants had a “predefined safety event”, which seems to be either a severe pulmonary haemorrhage or persistent hypotension, 4 of them received PDA medications before 7 days to treat those events; a further 29 of the control infants received PDA medications after the 7 days, for a total of 64% of the controls receiving treatment. 35% of the SMART group didn’t satisfy the treatment criteria during the 7 day trial period.

This pilot gives adequate justification for a larger trial, it does not, I think, provide strong enough justification for routine implementation of the SMART protocol. The only significant benefit, an important one, was one of many secondary clinical outcomes, the reduction in pulmonary haemorrhage. Other trials of early PDA closure have also shown fewer pulmonary haemorrhages, in particular Martin Kluckow’s trial of early indomethacin (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). In that trial of infants <29 weeks GA, echocardiographic screening was much earlier, 3 to 12 hours of age, and infants were eligible for treatment on the basis of simply PDA diameter, and the absence of bidirectional shunting (diameter limits being >1.8 mm at postnatal age 3–5 h, >1.6 mm at post- natal age 6–8 h and >1.3 mm at postnatal age 9–12 h). The study was stopped early because Indomethacin was no longer available. Early pulmonary haemorrhage was much less frequent with early intervention among those with a large PDA, 1/44 va 10/48. But the primary outcomes, for which that trial was designed, were no different between groups.

As you can see from this Forest plot from the latest Cochrane review of early PDA treatment, there is an increase in mortality with very early ibuprofen, overall. Any future trial of very early treatment has to be adequately powered to ensure that there is no increase in death with treatment. This new trial had about 18% mortality in each group, so, to be fairly sure there wasn’t an increase in mortality, of about the amount shown in this SR, (about a 36% increase) with reasonable power (80%), a trial of over 400 patients per group is needed.

The risks of serious pulmonary haemorrhage start quite soon after birth, and I understand the logistical problems with randomizing and enrolling infants after a qualifying echocardiogram before the 72 hour limit in SMART-PDA. But to have the most benefit in reducing pulmonary haemorrhage, randomization before 36 hours would be preferable. It is easy for me to say that, as I don’t do functional echocardiography, so I wouldn’t be on the call schedule for urgent echos over the weekend!

This high quality pilot trial points the way to designing a definitive trial of smarter treatment of the PDA in extremely immature infants. Early screening, eligibility based on criteria which show a large shunt and which predict persistent patency of the PDA seems to be the way to go to answer some of the many questions that remain.

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A new standard for NOWS

Posted on 28 April 2026 by Keith Barrington

Neonatal Opioid Withdrawal is a major public health problem in the world. Large numbers of infants born after fetal exposure to opioids experience unpleasant symptoms, requiring non-pharmacologic and pharmacologic intervention.

Studies of different approaches for symptom control have the potential to improve outcomes for this fragile population.

To go back in the history a bit, the Finnegan scale was developed as a research tool, it is fairly cumbersome, with 21 items, several of which are rather subjective, and some are frequent in babies without opioid exposure. The threshold for treatment, of a score of 8, was entirely arbitrary, and has never been adequately tested or compared to other thresholds. It was developed in 1975, when the standards now required for development of such tools were not in place.

A big advance in the management of NOWS was the development of a different system; the ESC system, rather than being a “score” is a method of evaluation of an infants ability to function normally . Babies are assessed on their ability to breastfeed successfully, or eat at least 30 mL per feed, to sleep uninterrupted for at least 1 h, and to be consoled within 10 min. If any of these conditions are not met, non-pharmacological soothing methods are instituted, and eventually medications may be introduced. Rather than regular timed Finnegan scoring, the ESC system is a continuous longitudinal evaluation allowing intervention as soon as an infant is unconsolable, or feeds poorly, or has sleep interruption.

Large trials have shown that infants evaluated and treated according to ESC have shorter hospitalisations without an increase in adverse effects. Young LW, et al. Eat, Sleep, Console Approach or Usual Care for Neonatal Opioid Withdrawal. N Engl J Med. 2023.

Infants managed with ESC have much lower opioid exposure in the neonatal period, and nevertheless have no increase in adverse outcomes in the short or medium term.

I can’t see any justification for continuing to use the Finnegan score for these infants. Which made me a little surprised to see some of the data in this new publication. Devlin LA, et al. Symptom-Based Dosing for Neonatal Opioid Withdrawal: The OPTimize NOW Randomized Clinical Trial. JAMA2026.

One of the questions about the ESC approach was exactly when drug therapy is indicated, and how to manage it. This RCT compared 2 different approaches, shown diagrammatically below. This was a cluster randomized trial, with individual centres being the clusters, they were randomized to start with the symptom-based dosing approach to pharmacologic therapy, and then switch after 5 months to the scheduled opioid taper approach for a second 5-month period; or to commence with approach B and then switch to approach A.

As you can see the initial evaluation and intervention is the same in both groups. In the standard tapering, “B”, group, once the infant had symptoms which breached the threshold for pharmacologic treatment, they were immediately started on regular drug dosing, which was then adjusted and weaned progressively. In the A group, the symptom-based dosing group, an infant who was over the treatment threshold would receive a single dose of whichever was the hospitals usual approach for such an infant (morphine, buprenorphine or methadone) and then, if their symptoms improved, they would go back to monitoring without routine repeated doses. If they needed more than 2 consecutive doses at either 2, 3 or 4 hour intervals, they were started on regular dosing and then weaned after they were stabilised.

At least I think that was the protocol, because the figure has a note which states “Infants were eligible if they received less than 3 doses in the preceding 24-hour period and fewer than 2 consecutive short-interval doses” But fewer than 2 means 1, and I don’t know how you can have 1 consecutive dose? Similarly less than 3 doses means either 1 or 2 doses, which is actually not what is in the protocol.

The protocol, attached as a supplement, states that the infants were allowed up to 3 doses (not less than 3) in a 24 hour period, and if they needed a 4th dose, then they switched to regular dosing and weaning. The precise wording in the protocol is “if a 4th dose is required within any 24 hour period, the study site will move to scheduled opioid treatment per the algorithm used at the study site…”.

I think the note by the figure should say “less than or equal to 3 doses in the preceding 24-hour period, and less than or equal to 2 consecutive short-interval doses”. That would be then consistent with the text of the article which states “Each time the threshold for treatment was met, an as-needed dose was given as long as the infant had not already received 3 opioid doses in the preceding 24-hour period or 2 consecutive short-interval doses”.

In other words, I think what that means is that if an infant was not eating, or sleeping, or consolable, they would receive a dose of morphine (or an alternative). If 2 hours later they were still in that state, they would receive another morphine dose; but if they needed another one 2 hours later they were started on regular morphine, with a progressive wean once the symptoms were under control.

The primary outcome for the trial was the time until medical readiness for discharge, which meant more than 96 hours of age and more than 48 hours since the last opioid dose, or when the medical provider discharged them, whichever was first. This primary was only used for the babies cared for with the ESC approach, which was used in 15 hospitals, with 8 using the Finnegan score.

This is my first question “why on earth would any centre still be using the Finnegan for term babies with NOWS?” Especially a centre with enough babies, and enough academic interest, to get involved with this trial? None of the reviews I have read, or the studies that have been performed, show any advantage to the Finnegan based system. Infants treated using the Finnegan system receive more opioids, and stay in hospital much longer, with no decrease in adverse outcomes.

In the ESC centres there were a total of around 190 infants treated by each approach. The length of hospitalisation was 2.5 days shorter in the symptom-based group. The same proportion of infants received at least one dose of medication (40% in each group), but, among that subgroup, the number of doses was much less, duration of opioid treatment was 3 days shorter, and many fewer received secondary medications (which could be either phenobarbital or clonidine)

The results in the Finnegan hospitals confirm the much longer hospitalisation with the out-dated approach, the Symptom-based approach led to 1.5 days shorter hospitalisation, but stay was more variable, and the difference may have just been a random effect.

Just getting these babies home (or at least discharged from hospital) earlier isn’t, of course, the only important outcome. Safety outcomes were similar between groups, with the rare primary, critical safety adverse outcomes occurring only in the scheduled taper group, n=3, not significant. Hospital re-admissions and ER visits were also similar, but numerically less frequent in the symptom-based group.

This seems to me to be another major step forward in treatment of this condition. Infants with NOWS should clearly be managed with the ESC approach, and if they cannot E or S or C, then intermittent opioid dosing can be used without immediately starting a regular regime.

I don’t understand why phenobarbital is still being used as a secondary medication, it has numerous secondary effects, and even the sedation is short lived, with longer treatment leading to hyperactivity. Clonidine makes much more sense. I don’t know if we even need an RCT of phenobarbital, as its use doesn’t seem to have a rational basis. But trials of the appropriate threshold for introduction of clonidine could be valuable.

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Neonatal Research Shorts : March 2026

Posted on 27 March 2026 by Keith Barrington

Pineda R, et al. Language and sound exposure across neonatal intensive care hospitalization and relationships with early outcome. J Perinatol 2026. In this short term outcome study, 64 very preterm infants <29 weeks GA were evaluated at near-term age with the Neonatal Neurobehavioural Score (NNNS). They had previously had a recording of the ambient noise for 4 separate 16 hour periods during their NICU stay, which was analysed to determine the exposure to any noise, including electronic sounds (which I guess means alarms, and monitors beeping), or meaningful language or distant voices.

The NNNS scores on the multiple various scales are shown below, with the “Comparator Value” being the average scores of full term infants, with the SD.

The statistically significant correlations with sound exposure and NNNS scores are shown below

Exposure to speech was associated with less stress, exposure to louder noise with more hypertonia, and so on.

In terms of statistics, this might be a bit questionable, as there were 5 sound characteristics and 13 different scales compared, leading to 65 possible associations, and a high risk of a type 1 error Nevertheless, the importance of human voices and the adverse impact of electronic sounds, especially loud sounds is consistent with everything else we know.

Take Home Message : Please get your parents, and everyone else, to talk calmly to the babies, and reduce as far as possible background noise and electronic sounds. Supplying books to parents, so that they can read to their infants while in kangaroo care, rather than scrolling on their phones, can only be a good thing.

d’Haens EJ, et al. Short Antibiotic Treatment for Coagulase-negative Staphylococcal Sepsis in Premature Infants: A Multicenter Noninferiority Study. Pediatr Infect Dis J, 2026.

In this multicentre observational study, infants with uncomplicated CoNS sepsis were compared between those with >96 hours of antibiotics. Cases were defined by “Presence of clinical signs of infection more than 72 hours after birth, a positive blood culture showing CoNS, and an increased C-reactive protein (CRP) level >10 mg/L within 24–36 hours after the onset of sepsis” and uncomplicated sepsis meant “clinical recovery within 24–48 hours, no central venous line in place or removed after the onset of sepsis, no signs of necrotizing enterocolitis or infected thrombus, and no Staphylococcus lugdunensis bacteremia”. (Apparently S. lugdunensis is particularly virulent). Most were treated initially with flucloxacillin and an aminoglycoside.

The primary outcome was the incidence of relapse of infection, and it was performed as a non-inferiority retrospective observational study.

There was one relapse in the short treatment group of 172 infants, and 0/218 in the long treatment group; short treatment satisfied the non-inferiority criterion.

Take Home Message : 4 days of adequate antibiotic treatment might well be enough for uncomplicated CoNS sepsis.

Katheria AC, et al. Impact of Availability of Waiver of Consent on the Preterm Cord Milking versus Deferred Cord Clamping Trial (PREMOD2). Neonatology. 1232026. p. 162–6.

In the PREMOD2 trial, of delayed clamping vs cord milking for preterm infants at birth, some centres allowed waiver of consent and others did not. This study examines the differences in patient characteristics and the impact of the trial intervention between those 2 groups of centres.

When the study was designed and started, there was no evidence that one approach was preferable to the other, and some centres were doing DCC, others cord milking. If you remember, the trial found an increase in severe IVH with cord milking, leading to premature termination of the trial. There were 475 babies in total in the trial, 99 of them in hospitals that required pre-randomisation consent, the remainder in hospitals allowing waivers. “At hospitals permitting initial waiver, 3% of parents who were approached after the delivery intervention declined postnatal consent for data collection. At hospitals without initial waiver, 75% of deliveries were approached for participation. Among those approached, 49% of parents declined consent (range 39–61%)”.

In hospitals with a waiver, enrolled infants were more likely exposed to maternal chorioamnionitis (35% vs. 22%), less likely to have complete antenatal steroids (75% vs. 85%), and less likely to have received antenatal MgSO4 (79% vs 97%) compared to the others. Antenatal steroids and chorioamnionitis impacted the risk of having a severe IVH, mostly in the Cord Milking (UCM) group.

As you can see, in the cord milking group, antenatal steroids reduced the risk of severe IVH to 7%, compared to 14% without completed antenatal steroids, and Chorioamnionitis increased the risk from 3% to 22%.

Not having a waiver of consent therefore impacted the apparent difference between UCM and DCC, with waiver centres showing a decrease, and non-waiver centres showing no difference. This is probably because of the different risk profile among babies born in the different groups.

Our results highlight the importance of methods to enroll representative samples of the populations, to whom the studied interventions will ultimately be applied. Infants born to mothers that can be approached antenatally may have different comorbidities and co- treatments than the infants for whom the evidence will ultimately be applied… Relevant regulatory frameworks in countries including the USA and Australia have been previously described to support ethically appropriate modifications of the consent process for research on the safety and efficacy of common delivery room interventions. Based on the experience of PREMOD2, such methods may prevent false reassurances about safety or efficacy when unwarranted

There are previous data which confirm that parents questioned after the fact were supportive of this kind of waiver of consent. Even though 50% of those approached prospectively (in this trial) refused consent. I think that says something about how difficult it is in the midst of the stress of a threatened preterm delivery to explain comparative trials of differing approaches in common clinical use, which are both considered acceptable interventions.

Take Home Message : Waivers of consent, when ethically appropriate, allow randomization of subjects that more closely reflect the entire population. They may reveal effects of interventions which would otherwise be missed.

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Steroids and BPD, what do we really know?

Posted on 26 March 2026 by Keith Barrington

My first foray into systematic review and meta-analysis was about 25 years ago with this article Barrington KJ. The adverse neuro-developmental effects of postnatal steroids in the preterm infant: a systematic review of RCTs. BMC Pediatr. 2001;1:1. As you can see it was the very first article in the new journal BMC Pediatrics, I had submitted to BioMed Central, BMC, because it was a new open access model of publishing, (which authors didn’t have to pay for!) and then they asked me if I minded them transferring it to BMC Pediatrics.

At that time there was evidence that infants exposed to dexamethasone had an increase in the frequency of Cerebral Palsy. Unfortunately, in the RCTs, many of the control infants received dexamethasone. Which makes evaluation of the impacts of the steroid in the long term very difficult, if not just about impossible. This was the Forest plot of the impacts of steroids (all dexamethasone except for the study by Fitzhardinge et al, which was a mega-dose of hydrocortisone).

As noted in the figure legend, the study by O’Shea et al, which was a 42 day course of dexamethasone starting on day 15-25, was the only modestly sized trial without any crossover, control babies were not allowed to receive postnatal steroids.

Unfortunately, since then we have very unreliable data, because we can’t help ourselves, and frequently treat the babies randomized to control with steroids. In the trials in my SR/MA, Shinwell’s trial, 33% of surviving controls received dexamethasone, and in the Jones trial, 40% of the surviving controls received at least one course of dexamethasone.

This also means that we don’t know what the long term impacts of postnatal steroids are on the lungs! It is very disappointing, that so few of these trials have had long term pulmonary outcomes reported. If we are giving steroids to improve respiratory health in the long term, surely measuring that would have been reasonable? One of the few trials to measure long term pulmonary outcomes was that Jones trial, with its 40% contamination rate. They followed the subjects out to 13 to 17 years of age. And found no benefit of postnatal steroids at any point in their follow up.

I don’t really care if a baby is still in oxygen at 36 weeks. And neither do their parents!

Do postnatal steroids decrease the number of babies whose respiratory health adversely impacts their life? Or their family? Needing oxygen at home, needing respiratory interventions at home, re-admission to hospital, frequent cough or wheeze, impacts on feeding or on physical activity, recurrent stridor…. Those are things that bother parents, and we have no idea if postnatal steroids improve any of them. (Thivierge E, et al. Pulmonary important outcomes after extremely preterm birth: parental perspectives. Acta Paediatr. 2023;112(5):970–6).

I’m coming back to this issue because of a new ST/MA which has been published. (Raghuveer TS, et al. Systemic steroids and bronchopulmonary dysplasia: a systematic review and meta-analysis. J Perinatol. 2026). The search strategy found 44 studies. Their analysis found no change in mortality after adjusting for steroid contamination, and no change if the analysis was limited to the 24 trials with no steroid contamination. I was surprised that they were able to find 24 trials with no steroid treatment of the controls, and indeed I was right to be surprised.

Some of those trials did in fact have contamination of the controls with steroid treatment. Yeh 1999, for example, had several babies, 12% of controls, who received steroids after the first 28 days. Among the studies that report neurological outcomes, only O’Shea et al (which they call Kothadia, the first author of the initial publication), among the trials with data on CP, was not contaminated by steroid use in the controls. There also seem some errors with the actual results, in Stark et al table 2 reports 12 placebo and 8 dexamethasone babies with moderate to severe CP, and the text adds that 4 placebo and 5 dexa babies had mild CP, for a total of 16 vs 13 cases; the Forest plot in the appendix has only 6 vs 8 cases of CP. Also Yeh’s study, in table 4, reported 12 placebo and 25 dexamethasone babies with CP, while this new Forest plot has 17 vs 9. I’m sure they read the original publications carefully, so I don’t understand where those discrepancies come from.

However, the biggest problems with the outcome data continue to be the very small numbers of infants followed, and the use of steroids among controls. In Stark’s NICHD trial, for example, 50% of control babies received dexamethasone. It is impossible to say anything reliable about the long term impacts on CP or development, or pulmonary outcomes with this extremely serious limitation. When it comes to long term toxicities, analysis by Intention to treat is no longer the only analysis that should be performed. An analysis by treatment actually received, should have been performed. It seems likely that steroids given early in postnatal life, might have more marked effects on neurodevelopmental outcomes, and that bigger doses will have greater impacts. Meta-regression examining the impacts of those factors would be very useful, especially if the dose of dexamethasone actually received was available, and entered into the analysis.

I can find such evidence in any published article that shows an improvement in long term respiratory health with postnatal steroid use compared to untreated controls.

This is vitally important. Steroids reduce inflammation and thus the number of babies who need oxygen at 36 weeks. But there are known adverse impacts of systemic steroids on lung growth and development. I don’t remember ever quoting previously a systematic review of animal studies on this blog, but this one is great! Lok IM, et al. Effects of postnatal corticosteroids on lung development in newborn animals. A systematic review. Pediatr Res. (96) 2024. p. 1141–52. Despite the limitations of the initial studies, the differences in methodologies and in outcome measures, making meta-analysis very limited, and for some measures, impossible, it is quite clear there are serious negative effects of steroids in immature mammals on alveolarization, the radial alveolar count, for example, a well-validated measure of alveolar development, is substantially decreased by postnatal steroid use, but, it seems only in healthy animals, not after a lung injury (of various types).

Another measure of alveolarization, that I didn’t know about, is the mean alveolar chord length, which increases when there are fewer alveoli, That measure also shows substantial adverse effects of postnatal steroids in animals (mostly rodents) with normal lungs, but less evidence of such toxicity if they are given after a lung injury,

The conclusion of this review is

Postnatal corticosteroids have a negative effect on body weight and lung development resulting in persistent alveolar simplification

Although postnatal steroids reduce “BPD” there is no evidence that they improve important clinical features of lung injury. The animal data in fact suggest a major risk of adverse impacts on lung growth and alveolarisation.

Moderately large RCTs of dexamethasone with ≤ 33% treatment of controls with steroids (O’Shea, Yeh and Shinwell) have all shown an increase in CP with the steroid treatment. All of the larger RCTs performed since my 25 year old SR/MA have been contaminated by 40% or more of treatment of controls with steroids (which is basically just Stark and Doyle). Its really disappointing, looking back, that even though there was a serious concern raised so many years ago, none of the more recent trials have seen fit to analyze cerebral palsy as an outcome, and none have reported CP according to dose actually received.

This latest meta-analysis blithely reports that the steroids do not show evidence of increased risk of “NDI”, and focuses on a reduction in oxygen needs at 36 weeks. Wouldn’t it be great to know if we are actually helping our patients when we prescribe steroids for them?

Unfortunately the data we have do not show any improvement in pulmonary health with postnatal steroids, and there remains a major concern about the potential impacts on motor development and cerebral palsy.

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Registration of clinical trials.

Posted on 20 March 2026 by Keith Barrington

Since 2005 the International Committee of Medical Journal Editors has required that a condition of publication of a prospective controlled trial is that it should be registered in an accessible database prior to starting the trial. It is understandable that for a few years afterwards, trials that had been commenced prior to this standard might not have been pre-registered. I don’t think there is any reasonable excuse for not pre-registering prospective trials in more recent years.

Since 2013, the World Medical Association’s declaration of Helsinki has also clearly stated “Every research study involving human subjects must be registered in a publicly accessible database before recruitment of the first subject”.

Despite this obvious, basic, and easily complied with standard, many trials are still being performed without prior registration.

I recently wrote, for example, to the editors of “Neonatology” about this article Atef Abdelsattar Ibrahim H, et al. The Effect of Oral Immunotherapy on Preterm Neonates: A Promising Adjuvant Therapy in a Clinical Trial Study. Neonatology. 122.2025. p. 641–9. Which was a trial of oral colostrum. There were several major concerns that I had. The first was that the trial was registered after completion. This is inconsistent with the clear requirements of the ICJME and the WMA, and the stated criteria in the instructions of authors of “Neonatology”. The editorial board seem to be unaware of their own requirements.

In addition, the methods section of the trial does not describe the intervention. At all. It isn’t stated in the text that there were 3 groups, or that the groups had either no colostrum, 3 days of colostrum or 10 days of colostrum. The volume, frequency, and method of administration are not described.

In addition, the rate of early onset sepsis was enormous at 56% among the controls (and 10% in the 10 day group, 32% in the 3 day group) which is reported as if it was an outcome of the study. I think it is fairly obvious that a postnatal intervention cannot affect the incidence of early-onset sepsis, which should have been considered as a baseline imbalance.

Some of the presentation of results is just plain weird. I’ll give a years free subscription to “neonatalresearch” for anyone who can explain to me what the following figure means! The figure legend states “b ROC curve of time to reach the full enteral nutrition for sepsis (sensitivity and specificity are expressed in %). c ROC curve of time to reach the full enteral nutrition for prolonged length of hospital stay (sensitivity and specificity are expressed in %), ROC curve for prolonged length of stay as regards GA (gestational age) (sensitivity and specificity are expressed in %).

The response of the editorial board of Neonatology was very disappointing. They stated that the authors had not been aware that they needed to pre-register their study. they also stated that the rate of sepsis was consistent with other studies in LMICs, and sent me a reference which included data about Late-Onset Sepsis. It seems that the referees and editorial board of Neonatology are also unaware of their own requirements.

One journal which has rejected multiple articles because of a lack of pre-registration is the BMJ. They recently published a study describing what happens to such articles (Blanco D, et al. Analysis of non-prospective trial registration in clinical trials submitted to The BMJ: observational study. BMJ. 392.2026. p. e086467). It turns out most authors just submit them elsewhere, “Many trials rejected by The BMJ for non-prospective registration in an ICMJE accepted registry were later published in high impact journals claiming adherence to the ICMJE recommendations, often without disclosure of registration deficiencies.”

The accompanying editorial in the BMJ, written by the same authors, offers suggestions:

Rather than simply describing the problems we encountered, we wanted to offer some practical steps to help improve transparency around trial registration. Journals can play a central role by requiring authors to provide clear, precise, and verifiable registration information in journal submission systems and in manuscripts. This should include the full dates (day/month/year) of submission to a trial registry, registry approval, and first participant enrolment, according to the latest registry entry. Journals should also require the trial registry name and registration number, a hyperlink to the registry entry, and a clear statement indicating whether the trial was prospectively registered in an ICMJE accepted registry. Trial registries must harmonise their language and terminology so that users can easily identify key milestones, such as the date of first submission, approval, and first patient enrolment, as well as clearly determine registration status.

On publication, prospective or retrospective registration in an ICMJE accepted registry should be clear from reading the abstract alone, with all registration information also reported in the full manuscript text. As Douglas Altman so wisely said in the 1990s, “Readers should not have to infer what was probably done, they should be told explicitly.” With the provision of these details, readers can make informed judgements about the credibility and transparency of the research for themselves.

Prior registration is an important safeguard that allows readers to be confident that the interventions, analysis, and outcomes were decided prior to seeing the results. Without pre-registration all of these things can be changed post hoc, which makes all of the medical research endeavour unreliable. Meta-analyses, on which many treatment decisions are made, based on such results may lead us to treat individual future babies with inappropriate, ineffective or dangerous therapies. Even individual small trials, which sometimes are the only evidence we have, must be pre-registered, and failure to do so, and failure of journals to insist that trials are pre-registered, puts our fragile patients at risk.

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Neonatal Acute Respiratory Distress Syndrome, what is it and how should we treat it?

Posted on 20 March 2026 by Keith Barrington

ARDS is a fairly common problem in the adult and the paediatric ICU; following trauma, or systemic sepsis, or other extrapulmonary insults, usually inflammatory in nature, or as a complication of direct pulmonary insults, such as pneumonia or aspiration of gastric contents. It is characterised by acute respiratory distress, diffuse pulmonary infiltrates on the x-ray, without signs of cardiac compromise, an oxygenation defect, and a major decrease in lung compliance. Various definitions have been proposed, none of which are entirely satisfactory, but many cases in the PICU are fairly clear.

It also occurs in newborn infants; many of us will have seen, for example, an infant with systemic sepsis who develops a secondary respiratory deterioration within the first day or so, with a “white-out” on the xray, and a serious deficit in oxygenation, with very stiff lungs. One question then is, how to define the entity, ARDS in the newborn (nARDS)? The consensus definition from Montreux is shown below

As with any definition there are some problems with this. For example, that publication also states that “the mandatory criteria for diagnosis of RDS are respiratory distress appearing within the first 24 h of life, with complete, sustained, and prompt response to surfactant or lung recruitment or both”. Which suggests that almost any infant who has a partial response to surfactant could then be defined as nARDS.

I am also unsure, for some problems, if it helps to have this diagnosis. As one example, the document above discusses meconium aspiration syndrome as a cause of nARDS. I am sure that many of the pathophysiologic processes of MAS and nARDS do indeed overlap, but there are also very specific features of MAS. With meconium in the airways and distal lung, leading to surfactant displacement and inactivation and chemical pneumonitis, in association with frequent asphyxial impacts on the circulation and lung, there are management approaches which may be very different to other causes of nARDS. Trials of treatment in MAS will not necessarily be extrapolatable to other causes of nARDS, and vice versa. For example, lung lavage with diluted surfactant might be an appropriate option for MAS, but is unlikely to be helpful for other causes of nARDS.

Similarly for pulmonary haemorrhage, it is clear that surfactant dysfunction is common in clinically important haemorrhages, (in the lab, haemoglobin and fibrinogen are very useful to inhibit surfactant function) and surfactant replacement therapy often leads to acute improvements in clinical status. Should trials of therapy for nARDS include PH, or enrol them as a separate subgroup?

The reason for discussing these issues is the appearance of a new RCT comparing conventional ventilation to high frequency oscillation. (Li J, et al. High-Frequency Oscillation vs Mechanical Ventilation for Neonatal Acute Respiratory Distress Syndrome: A Randomized Clinical Trial. JAMA Netw Open. 92026. p. e260268). This is a single centre study from Chongqing in China, infants from 25 to <36 weeks were eligible if they were diagnosed with nARDS and were then randomized, to either be switched from the CMV to HFOV, or to remain on CMV. The primary outcome was “overall BPD”.

There are a huge number of problems with this publication. One good point is that the study was prospectively registered prior to commencing the study, as has been the required standard since 2005. Many studies are still being published that do not follow this simple rule, more on this soon.

In the first version of the registration documents this was a multi-centre trial with a sample size of 1000 infants. Shortly after that the sample size was reduced to 600, but there are about 30 different centres listed (perhaps this was just a “wish list”), the final publication had 386 infants included from a single centre. The sample size calculation was based on an effect size of 17% difference in BPD between groups, leading to a calculated need for 160 subjects per group. The actual mean GA of the participants was 31 weeks.

The published primary outcome of the trial, BPD, is presented with 2 different definitions, the NICHD 2001 definition, and the Jensen et al definition from 2019, both of which are analysed and presented. In the registration documents, however, only the NICHD definition is used. But whichever definition is used these only apply to infants of <32 weeks gestation. In other words nearly half of the babies in this study could not have BPD by either definition! This is not just semantics, defining BPD at 36 weeks GA is already problematic enough, but diagnosing it at 1 week of age in a 35 week GA infant is nonsensical. The authors themselves state in the discussion “it makes no sense to look for BPD in neonates born after 28 weeks”! This sounds to me like a quotation of a comment from one of the reviewers, but the authors have simply included that phrase in their discussion without otherwise discussing the implications for their study.

We only know the mean GA in each group, 31 weeks as noted above, so the proportion of infants <32 weeks isn’t precisely clear, but probably somewhere around half.

The fact that JAMA allowed the authors to add a second definition of BPD, and report both of them as if they were both the primary outcome of the study is extremely disappointing. In addition, BPD is calculated as the proportion of enrolled infants, even though there was significant mortality (19% with HFOV, 16% with CMV). We don’t know if the infants died before or after they reached 36 weeks, so we can’t even calculate the rate of BPD among surviving infants, which given the GA range of the babies in this study is not such a big deal!

Infants were screened and enrolled in the trial at an average of 4.8 hours, which is well before they had a diagnosis of nARDS. According to the CONSORT flow diagram, there were 632 infants of <34 weeks GA during the study period. 180 had RDS, and 12 did not meet criteria, with another 23 “unavailable”, 24 parents didn’t consent, Leaving 386 infants enrolled in the study who were randomized. All the randomized infants (except 11 CMV infants who “did not receive CMV”, not explained why) entered one of the treatment arms. I would guess that many babies enrolled (at 5 hours of age) never developed nARDS, what on earth happened to them?

This means that the incidence of nARDS in the centre reporting this study is enormously high, orders of magnitude higher than any previous report. Previous epidemiologic reports (De Luca D, et al. Epidemiology of Neonatal Acute Respiratory Distress Syndrome: Prospective, Multicenter, International Cohort Study. Pediatr Crit Care Med. 232022. p. 524–34. Chen L, et al. Clinical characteristics and outcomes in neonates with perinatal acute respiratory distress syndrome in China: A national, multicentre, cross-sectional study. EClinicalMedicine. 552023. p. 101739.) show a rate of about 1.5% of NICU admissions. One of those epidemiologic studies’ first authors was an author of this new trial.

I certainly do not understand how the incidence of nARDS can be more than double that of RDS among preterm infants. About 60% of each group are stated to have had early onset sepsis, which is also an enormously high proportion, but no diagnostic criteria are given.

The publication states that the study was masked to investigators and parents, which is clearly nonsense, unless parents were not allowed to visit, and the investigators had to stay outside of the NICU. Like almost all mechanical respiratory support interventions it is impossible to blind the intervention. This doesn’t really matter, masking of the randomisation process, so that the group assignment is unknown at the time of enrolment, is far more important anyway

There were 11 babies, analysed in the CMV group, who had been randomized to HFOV but treated with CMV because of lack of equipment. Again I can’t understand why JAMA would allow this, those infants should either have been included in the HFOV group, according to intention to treat principles, or just eliminated from the trial (which would have been quite reasonable).

Babies were allowed to be crossed over if they were not doing well, and they were appropriately analysed in the randomised group. The criteria for failure were different between groups, however, requiring persistent life-threatening hypoxia in the HFOV group (<50% saturation for more than 3 hours) compared to modest desaturation (<90% for >3h) in the CMV group. In either group persistent PCO2 >60 was also a criterion.

There are several other strange features of this study, the average mean airway pressure (MAP) at enrolment was >11 cmH2O, but the starting MAP in both of the groups was reduced to 8. The CMV group also have both a mandatory starting pip (16 cmH2O) and a set tidal volume (5 mL/kg). The copy-editor clearly didn’t do their job either, there are numerous weird phrases such as “Only pressure-regulated volume control is provided by any type of neonatal ventilator.” I think that means that any neonatal ventilator was allowed in the CMV group, and I don’t think they really mean PRVC. But I don’t know if they were using volume-targeted ventilation or pressure controlled.

I know I am being even more picky that usual with this study! It is easy to be critical, and much harder to do prospective research. One reason for focusing on this study, though, is that I have seen it quoted approvingly in a few places, as if it gave evidence supporting the use of HFOV in RDS. The authors themselves make many comparisons between their trial and other published research, and meta-analyses, which are all in infants with probable RDS. But this is, supposedly, a different patient group, with a different primary pathophysiology. The available data from trials in preterm infants with acute pulmonary dysfunction (as the Cochrane review puts it) show no advantage to initiating assisted ventilation with HFOV over CMV.

How to treat nARDS is an important issue, unfortunately this trial just muddies the waters. With uncertainties over the diagnosis, the outcomes, some suboptimal features of the design and the interventions, it doesn’t help me at all in a choice of ventilatory strategy for a baby with nARDS.

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