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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Neonatal Research Shorts : February 2026

Posted on 17 March 2026 by Keith Barrington

Dereymaeker A, et al. Neonatal sleep physiology and early executive functioning in preterm children. Pediatr Res. 2026.

In this observational study, the authors recorded sleep architecture overnight shortly prior to discharge of 76 preterm infants, averaging 30 weeks GA.

The main finding was that infants with less sleep time (as a percentage of the recording) had more executive function problems. This was a single recording prior to discharge, and might not reflect total sleep problems during the hospitalisation, but is certainly suggestive that preterms need their sleep.

Take Home Message : Sleep may be important for development of normal executive function among preterm infants.

Assaad MA, et al. Incorporating stressors during simulated neonatal endotracheal intubation creates a stress response but does not affect performance: a randomised pilot study. Arch Dis Child Fetal Neonatal Ed. 1112026. p. F109–F14.

In this randomized study from our institution, my colleagues randomized simulated intubations by residents to having a lot of stress, which included an attending staff running into the room and breathing over their shoulder, they also had alarm and background noise, a nurse and an RT in attendance, and the manikin desaturated. The low stress simulation had no noise, a low fidelity manikin that couldn’t desaturate, and fewer personnel.

They showed that they were able to stress the trainees, as their heart rates went up more in the high-stress group, but that didn’t have an impact on success or time to intubation. Maybe that has something to do with an overall supportive and positive environment in our institution, trainees know that even if a procedure goes badly they won’t be yelled at! They also knew that no manikin would be seriously harmed in the making of this study.

Take Home Message : in a simulated intubation, more stressful situation did not impact competency.

Hulse WN, et al. Iron Deficiency Screening with Reticulocyte-Hemoglobin Content and 2-Year Neurodevelopmental Outcomes in Extremely Low Birth Weight Infants. Am J Perinatol. 2026(EFirst).

The measure of iron deficiency that the Utah group was investigating here was new to me. The average haemoglobin content in a reticulocyte (RET-He) is apparently one of the best ways of determining iron status, and has been shown in animal models to correlated with brain iron deficiency. The value should stay over 29 pg, it seems. There are good data from full term infants, that iron deficiency has impacts on neurodevelopment, including on executive function; but little similar data from the preterm. This observational study of very preterm infants <28 weeks GA compared Bayley version 3 scores at 2 years corrected age in 78 infants who were left after exclusions (of receiving erythropoietin or an analogue, being in a trial of EPO, or not having an RET-He measured).

There was no significant difference in scores between the babies who had at least one RET-He <29 and those in whom all the measured values were >29, but looking at the table, all the mean scores were higher in the babies without evidence of iron deficiency.

The correlation of average daily Fe dose with the Bayley cognitive score was statistically significant, but not very impressive.

But, there are so many influences on cognitive development in very preterm infants that are not directly related to iron intake or iron status, such as growth restriction, lung injury, infections, intermittent hypoxia, social status, number of books in the home, and maternal education. With this in mind, to find even a weak correlation, and a minor difference in Bayley scores is highly suggestive to me. The median daily Fe dose was 4.4 mg/kg/d (IQR 3.2-5.6) I was surprised to see that the range included a baby with a dose of 0 (!).

One concern I have about this paper is that the babies were born 2014-2018, and the latest follow up included was in 2020. I don’t know why there aren’t any infants from the last 6 years, but the babies benefited from delayed cord clamping, which, of course, increases initial iron stores.

The recommended range of iron intakes from ESPGHAN is 2-3 mg/kg/d, but that is based on no data about neurodevelopmental outcome in the very preterm. There is one study in late preterm infants which showed improved outcomes with iron supplementation compared to no supplementation, but the Systematic Reviews available (the latest Cochrane review is from 2012) include almost no information on the very preterm. The most recent SR that I found is from 2022, the authors restricted the studies to those with babies receiving human milk, and found only 3 RCTs comparing different doses of iron. Those 3 trials included a tiny number of babies, about 140 infants total, and only one of them had some follow up, which on post hoc testing showed a decrease in adverse motor outcomes (BSID II PDI score <85) in the higher dose group.

I was a bit surprised how little data we have on which to base the dose of iron that we give to our very preterm babies. It seems to me that it would be an easy study to design fund and perform. If simply increasing the standard dose of iron will improve developmental outcomes without having any adverse impact, that would have a major impact on a very easily performed intervention. Of note the little data currently available shows no increase in adverse outcomes with higher dose iron compared to a standard 2 mg/kg/d.

Take Home Message : the current standard dose of enteral iron supplement may be insufficient, but the data to support any dose are lacking. Probably, for now, the standard should be 3 mg/kg/d. More studies are desperately needed.

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Optimizing ventilation in established BPD

Posted on 13 March 2026 by Keith Barrington

Babies with established BPD (I won’t worry about the exact diagnostic criteria here, but very preterm infants who are still ventilated as they approach term are the group I am talking about) have somewhat reduced compliance, increased airways resistance, leading to long time constants, and rather heterogeneous lungs, often with apical emphysema and basal atelectasis. Ventilatory requirements are different to infants with, for example, HMD, who have predominately atelectatic lung disease, very low compliance, and airways resistance which is largely normal, apart from the resistance due to the endotracheal tube; such infants have very short time constants, so can be ventilated with very short expiratory times, and respond to increased PEEP with improving oxygenation. The limit of PEEP in such infants is when airway pressures are high enough to interfere with venous return, something which changes dramatically after surfactant administration, following which overdistension of the lungs is a risk to be avoided by rapid weaning of PEEP.

Selecting the optimal PEEP, respiratory rate, inspiratory/expiratory times and tidal volumes in established BPD is often tricky. The goals are to minimize on-going lung injury, maintain adequate oxygen delivery, and progress toward non-invasive support. Determining lung volumes is not easily done at the bedside, chest-xrays are insensitive, and may show both overdistension and atelectasis on the same image.


Shui JE, et al. Identifying optimal positive end-expiratory pressure with electrical impedance tomography guidance in severe bronchopulmonary dysplasia. J Perinatol. 2026. In this small study the authors used ventilation measurements from Electrical Impedance Tomography (EIT) during changes in PEEP to determine what PEEP led to the best ventilation without over-distension or atelectasis. BPD infants were very sick babies of 43 to 54 weeks PMA, they were on PEEP between 10 and 14 and mostly in a lot of of oxygen (one post-tracheotomy was in 25-30%).

The EIT belt is placed around the chest of the infant, as far as I can tell sedation and/or paralysis were not changed during the measurement, and PEEP was varied up or down over a total of 1 to 2 hours.

After processing, the EIT gives results like these. I’m not sure I understand what they mean by “variation in ventilation” which determines the shade of blue in the lower panel, and which is also called “ventilation change”

One thing you can see from the figures, and from the supplemental data, is that the dynamic compliance is at its highest when the infant is placed on what the determine from EIT to be the optimal PEEP. For the infant in the figure above for example, the compliance is 2 mL/cmH2O at a PEEP of 14, 2.3 at a PEEP of 10, and 1.8 at a PEEP of 6.

Another figure in the article, from a different patient, with x-rays included, again shows that the dynamic compliance is greatest at optimal PEEP.

Perhaps the EIT isn’t necessary, and one could do the same procedure just calculating the compliance at each step.

It would be nice to have a larger case series, and to compare different methods of determining optimal PEEP, but I think this might turn out to be a very useful technique. I’ll have to figure out how to get hold of one.

EIT can also be used to image perfusion of the lung,s as the amazing David Tingay, and his coworkers, demonstrated a few years ago (Tingay DG, et al. Electrical Impedance Tomography Can Identify Ventilation and Perfusion Defects: A Neonatal Case. Am J Respir Crit Care Med. 2019;199(3):384–6). There had been little follow up of that article until 2 publications from the same authors, from Aurora Colorado, one is a case report of repeated EIT in a single complex case, which has some fascinating videos in the supplementary materials (Enzer KG, et al. Electrical impedance tomography imaging of ventilation and perfusion in bronchopulmonary dysplasia. J Perinatol. 462026. p. 284–6) The other is a case series, which just appeared on-line with images from repeated EIT studies from infants with varying severity of BPD, and some controls. The images below are from an infant with severe BPD (still ventilated at 44 weeks PMA).

The bars below the images show the colours attributed for ventilation, or perfusion, or the ratio between Ventilation in litres/s and perfusion (Q) in litres/s. We don’t know the details of how the baby was being ventilated, but there seems to be a progressive improvement in V/Q matching over the studies.

The following figure shows results from 2 studies of an infant with mild BPD, and at the bottom a control infant. The second images of the BPD infant show ongoing differences from the control, but the VQ pattern looks almost normal, to my untrained eye.

I think this is the only non-invasive way of getting a V/Q image of the lungs, which might turn out to be very useful, if it can be rolled out with a simple to use commercial device.

I suggested, in response to the first paper, that the optimal PEEP might be determined without EIT by determining the PEEP which gives the highest dynamic compliance. That is exactly what these authors seem to have done in a group of babies with developing or established BPD who were ventilated. They had a protocol for varying the PEEP, after paralysing the infants with vecuronium, and giving them sedation. (Darwish N, et al. A non-invasive diagnostic tool for the assessment of optimal positive-end expiratory pressure (PEEP(OPT)) in infants receiving prolonged invasive ventilation. J Perinatol 2026).

Unfortunately the figure they use doesn’t really do the article justice, as it shows the same dynamic compliance (Cdyn on the photo of the ventilator screen shown below) of 0.4 at each of the 2 PEEP levels shown in the 2 panels

But if you look at the 2 lines in the middle of the lower screen, the one in orange, showing the PEEP, and the one below in white, showing the compliance, you can just make out the stepwise increases in PEEP, and that the Cdyn seems to increase up to a PEEP of 10, then drops at the PEEP of 12.

Of course, if you have a paralysed patient, and you keep the delta-p constant, you don’t need to calculate Cdyn, you can just measure the tidal volume; the expired Vt dropped from 8.5 to 7.9 with the increase in PEEP from 10 to 12 (the Cdyn fell from 0.41 to 0.38 with that increase in PEEP, the numbers on the screen are given as a single decimal point, which is why you don’t see any change).

Calculating Cdyn, or interpreting tidal volume changes are much trickier in an infant who is breathing, as respiratory effort is very variable in our babies, you would really need to wait until the infant was apneic, or perhaps do a recording and average over a long period of sleep cycles and variable activity. I guess it is probably acceptable to use a medium-duration muscle relaxant in this way, if there is a good chance you can optimise assisted ventilation. Most of the infants in this publication had a change in their PEEP (either up or down) indicated by the study.

An alternative would be to insert an oesophageal catheter and measure the trans-pulmonary pressure, if you have the equipment and the expertise. Then you wouldn’t have to paralyse the infant.

I think it is likely that increases in PEEP which lead to decrease in Cdyn are evidence of over-distension, which is probably also the point at which there will be a circulatory impact of the positive intrathoracic pressure. Finding optimal PEEP should help to be able to ventilate these babies with less adverse effect, and optimal lung inflation.

What is the best way to find the optimal PEEP I am not sure, but the EIT technique was performed without paralysis, and they were able to find the PEEP that gave the highest compliance. Whether the EIT signal really adds to that process I am unsure.

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Managing Post-Haemorrhagic Hydrocephalus

Posted on 2 March 2026 by Keith Barrington

PHH, as I will call it, is an extremely important determinant of outcomes in a small subgroup of preterm infants. Infants with severe IVH who don’t develop PHH have outcomes that are little affected. As our group reviewed, even grade 4 IVH, if unilateral, and affecting 1 or 2 of the Bassan zones, has little impact on motor or cognitive outcomes unless complicated by PHH.

Andrew Whitelaw died recently (a touching eulogy is on the site of the Newborn Brain Society), I knew him personally, having worked as his resident during a summer in Jersey (Channel Isles, UK), when he covered for my consultant during their vacation. I remember meeting him on the beach with a surf board under his arm, and a pager tucked in his wet suit! Andy was interested in PHH throughout his productive career, and led some important trials in its management, he was the PI of the Ventriculomegaly Trial Group for their pivotal trial, Ventriculomegaly Trial Group. Randomised trial of early tapping in neonatal posthaemorrhagic ventricular dilatation. Arch Dis Child. 1990;65:3–10. That trial did not show any real benefit of routine early LP (or ventricular tapping) compared to “conservative” management of PHH. Of interest, the indications for permanent shunting were typical of the time it was done, “failure to control head size“, which clearly implies rather late intervention. Andy was also critically involved in the development of DRIFT treatment of PHH (DRainage, Irrigation and Fibrinolytic Therapy) for infants with bilateral ventricular enlargement to more than 4mm over the 97%le This involved inserting a ventricular reservoir, then injecting tPA into the ventricles, then perfusing the lateral ventricles with a solution designed to resemble CSF.

Although this invasive therapy has not been widely adopted, it did show improved long term outcomes in a small RCT.

More recently the ELVIS trial (Early versus Late Ventricular Intervention Study, in which Andy was a collaborator) showed improved 2 year outcomes in infants in whom intervention was started early. The protocol for the early intervention group included a trial period of lumbar punctures (maximum of 3) followed by reservoir placement with repeated drainage until CSF accumulation stopped or a shunt was inserted. The primary outcome for ELVIS was survival or needing a permanent VP shunt, which was not different between the groups. But, to be honest I don’t think there was any real chance that survival would be affected by earlier intervention, and, re-reading the original publication, I realize that it is difficult to figure out what the primary outcome rate was in each group, as it is never stated in the text, but from the figure, it looks like it was 19/64 early intervention babies (7 deaths and 12 VP shunts) and 22/62 in the late group (8 deaths and 14 shunts).

The 2 year outcomes, (Cizmeci MN, et al. Randomized Controlled Early versus Late Ventricular Intervention Study in Posthemorrhagic Ventricular Dilatation: Outcome at 2 Years. J Pediatr. 2020;226:28–35 e3) however show definite benefit in the early treatment group.

The adjusted OR for adverse outcome (death or any grade of CP or Bayley (version 2 or 3) motor or cognitive score <-2SD) was 0.24; 95% CI, 0.07- 0.87.

Based on these trial results and other observational data, we developed an intervention protocol which follows best practice, and is similar to suggestions in a fairly recent review (El-Dib M, et al. Management of Post-hemorrhagic Ventricular Dilatation in the Infant Born Preterm. J Pediatr. 2020;226:16–27 e3)

We use criteria very similar to the Yellow zone criteria to start LP attempts, with neurosurgical intervention if dilatation is persistent or progressive according to clear criteria.

One thing I appreciate about the group where I work is our production, and following of, such clinical protocols. We have large numbers of such protocols in every area of neonatal care, and try to ensure that they are followed unless there is a good clinical reason in an individual case for deviating. For such a difficult decision as this, requiring an understanding of the literature, the prognosis, and the therapeutic options, I can’t imagine nowadays trying to make a decision for each infant without the guidance of such a protocol. Which is why I was surprised that so many centres do not have such a protocol.

Coletti K, et al. Post-hemorrhagic ventricular dilatation: Comparison of management pathways among North American level IV NICUs. J Perinatol 2026. This article was from the Children’s Hospitals Neonatal Consortium, of mostly US NICUs (plus Toronto Sick Kids). Among the 40 NICUs that replied, only 12 had a written guideline, another 17 said they had a consensus. I find it hard to imagine what you would do in a NICU without a guideline: “if it’s Monday we intervene at at anterior horn width of 8 mm, but tomorrow it will be 6 mm (unless its the other neurosurgeon)”? Come on guys! What do you say to the parents? “We don’t know what to do, so we toss a coin”?

Even among those few with a guideline, there was a lot of variation, and most seem to have quite late thresholds for surgical intervention:

Mahaney KB, et al. Wide variation in death rates and post-hemorrhagic hydrocephalus (PHH) treatment in preterm severe intraventricular hemorrhage (IVH). J Perinatol 2026. These data from California show wide variation in the approaches to PHH, with many babies not having temporary interventions with reservoirs or subgaleal shunts prior to definitive VP shunting, which strongly suggests late intervention in most such babies. There were about 2000 deaths among about 5,500 babies with severe IVH, another 587 had a permanent VP shunt, 268 of them following a temporizing neurosurgical intervention. Another 89 had a temporary procedure and never had a shunt, either because they died, (n=16) or because, I suppose, it resolved or stabilized.

The evidence supporting early intervention for PHH is limited, it is true. If you want to be critical, you could argue that the improvement in the long-term outcomes in ELVIS is only statistically significant after adjustment for other risk factors. But even if that is your argument, it is important to come to a local, clearly-defined consensus. You also should take into account the observational data, comparing early to late intervention, such as this study comparing the Toronto Sick Kids results (at the time, a late approach) to results from Holland with an early intervention protocol, which was similar to that suggested by El-Dib and colleagues (Leijser LM, et al. Posthemorrhagic ventricular dilatation in preterm infants: When best to intervene? Neurology. 2018;90(8):e698–e706). The early intervention babies in that study had excellent outcomes, similar to babies without IVH.

At each stage in an ideal protocol there are important decisions to be made, to be discussed with parents: a trial of lumbar punctures; how many and when to to stop LPs; when to proceed to temporizing intervention; whether to insert an Omaya reservoir or a Ventriculo-Subgaleal shunt (which may be as much an institutional decision as a personalized one); and when to decide on definitive shunting, which will usually be a Ventriculo-Peritoneal shunt.

I don’t know how a parent could make most of these decisions without clear guidance from a treatment pathway agreed by all involved parties, especially neonatology and neurosurgery.

For babies without contra-indications, and especially for those without a major parenchymal injury, a protocol following the broad outlines of the El-Dib guidance referenced above will minimize secondary injury caused by ventricular dilatation. Of importance, there is no requirement for clinical signs of intracranial hypertension before intervention being indicated. Such signs occur very late in preterm infants, in the “Red Zone”, and should be avoided whenever possible.

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Give your opinion: what should we call the most immature babies?

Posted on 27 February 2026 by Keith Barrington

There is an upcoming workshop, sponsored by the AAP, and other groups, that is investigating what shared language should be used for the babies of less than 25 weeks gestation.

At present there are not as many responses as they would like from families, or from former preterm infants. I would encourage any readers of the blog, and especially those from the 2 groups I just mentioned, a few of whom, I know, follow this blog, to participate. The following is the generic notice that was circulated:

” We invite you to take a brief survey to provide feedback for an upcoming workshop about shared language for infants born at <25 weeks’ gestation. The workshop is sponsored by the American Academy of Pediatrics Section on Neonatal-Perinatal Medicine with representatives from the American College of Obstetricians and Gynecologists, Society for Maternal-Fetal Medicine, National Association of Neonatal Nurses, Association of Women’s Health, Obstetric and Neonatal Nurses, Vermont Oxford Network, Tiny Baby Collaborative, and NICU Parent Network. 

Survey participation is voluntary and confidential. The results may be used in workshop proceedings and future presentations or publications. For questions, you may e-mail matthew.a.rysavy@uth.tmc.edu. “

Survey link: https://uthtmc.az1.qualtrics.com/jfe/form/SV_dg9qrNqXGy5Orzw?list_source=ep

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Automated oxygen control; is it worth it?

Posted on 18 February 2026 by Keith Barrington

The history of automated controls of inspired oxygen goes back many decades, to before the invention of pulse oximetry. The first studies I remember used transcutaneous PO2 as the target variable, which had major limitations, as well as the advantage of being better at detecting hyperoxia, at least when it was working well.

There are numerous recent publications about automated FiO2 control, at the end of this post I have put a list of a selection of publications from the last 8 years or so. Such systems have usually been shown to reduce the time an infant spends outside of the desired saturation range, and to reduce the need for nursing intervention.

The different systems use different algorithms, and thus their efficacy in improving “time in range” differs. One of the publications below (Salverda et al) compared outcomes of 2 epochs using different controllers. They had previously noted a major difference in efficacy of the systems in reducing hyperoxia, with the OxyGenie system on the SLE6000 ventilator being much better at reducing hyperoxia than the CliO2 system on the Avea ventilator; but with similar efficacy in terms of percentage time in hypoxia. The clinical outcomes of the babies were different between the 2 epochs, with the OxyGenie epoch having fewer babies developing severe RoP, shorter duration of invasive ventilation, and shorter hospitalisation.

One big concern I have is that increasing FiO2 when an infant is apnoeic is unlikely to improve their oxygenation! Intermittent hypoxic episodes are mostly due to apnoeic pauses, and increasing the FiO2 during such pauses will likely have no impact on the depth of the hypoxia, but may lead to post-apnoeic hyperoxia. It is, unfortunately, difficult to tell if an infant is actually breathing. Central apnoeas are easy to detect, but obstructive apnoeas, and the obstructive component of mixed apnoeas, cannot be easily detected.

The algorithms should be designed to avoid changes in FiO2 during respiratory pauses, but rather to adjust FiO2 when the infant is breathing and their requirements for oxygen change. Exactly how to do that I am not sure; to determine whether an infant is actually breathing, a unidirectional noise-cancelling microphone attached to the chest, with the appropriate software for detection of breath sounds, is an idea I had many years ago and wasn’t able to pursue. Anyone who wants to investigate that idea, feel free.

Randomized trials, without crossover to periods of manual control, have been very few. One small trial listed below was from King’s College in London (Kaltsogianni et al), with only 70 babies in total, using the OxyGenie system on the SLE6000. Babies of GA 22-34 weeks (mean about 27) were enrolled, and randomized to automated vs manual control. The automated group had less hypoxia and less hyperoxia, and had improved clinical outcomes, shorter mechanical ventilation and less BPD.

What was needed was a large multicentre RCT. (Franz AR, et al. Automatic versus manual control of oxygen and neonatal clinical outcomes in extremely preterm infants: a multicentre, parallel-group, randomised, controlled, superiority trial. Lancet Child Adolesc Health. 2026;10(3):179–88) In this trial performed in China, Germany (80% of the subjects), the Netherlands and the UK, infants of 23 to <28 weeks GA were randomized, within 96 hours of birth, to either automated FiO2 control, using whatever ventilator system was available, or manual control, if possible using the same ventilator. A variety of systems were used, most commonly the Stephan Sophie ventilator, at just over half of the sites, followed by the Leoni+ at another 8 sites. The primary endpoint was a composite of any of the following: death, necrotising enterocolitis, or bronchopulmonary dysplasia up to 36 weeks PMA, or severe retinopathy of prematurity by 44 weeks PMA. I have no idea why death was only of interest up to 36 weeks, while the infants were followed in any case until 44 weeks. I don’t know if there were any deaths after 36 weeks.

The study was designed to have 2340 infants enrolled, but, because of recruitment difficulties, the analysis and the sample size had to be adjusted, and 1080 infants were finally included.

There were no major differences in any of the outcome measures, or in the primary, composite, outcome. The primary outcome was 2.7% less frequent among intervention group babies (Absolute difference). In a subgroup analysis, the FiO2 control with ventilator “3” (which they are careful not to name but was used in over half the infants, and therefore must have been the Stephan Sophie) was associated with a larger reduction in the primary outcome, from 41% to 35%, while the other 2 ventilators had slightly worse outcomes in the FiO2-control groups, by 2 or 4%. One always has to be very careful about such subgroup analyses, and the interaction term was not ‘significant’, but it does suggest the possibility that the impact of the automated control differed by algorithm. The BPD part of the primary outcome was significantly different by subgroup of ventilator/algorithm type, again showing a greater reduction with ventilator 3 (17% vs 23%) in the FiO2 control group.

This study did not measure the impacts on nursing workload, or alarm fatigue, 2 things that may be positively impacted by automated FiO2 control.

Currently none of these systems are available in north America, largely because of a lack of trials such as this. From my fairly limited review of this large literature, it seems that the most promising algorithms are the OxyGenie on the SLE6000, which was not used in this recent RCT, and the Stephan Sophie with SPO2C, which was. This trial, with its lack of a clinical benefit, at least showed no safety concerns.

It is hard to argue with a large multicentre trial such as this, but it is also hard to imagine that spending less time hypoxic, and less time hyperoxic, will not eventually be proved to have benefits for our patients.

A Selection of Recent Publications

Dani C, et al. Cerebral and splanchnic oxygenation during automated control of inspired oxygen (FiO2 ) in preterm infants. Pediatr Pulmonol. 2021.
Dani C. Automated control of inspired oxygen (FiO2 ) in preterm infants: Literature review. Pediatr Pulmonol. 2019;54(3):358–63.
Poets CF, Franz AR. Automated FiO2 control: nice to have, or an essential addition to neonatal intensive care? Arch Dis Child Fetal Neonatal Ed. 2016.
Wilinska M, et al. Automated FiO2-SpO2 control system in neonates requiring respiratory support: a comparison of a standard to a narrow SpO2 control range. BMC Pediatr. 2014;14(1):130. Kaltsogianni O, et al. Closed-loop automated oxygen control in preterm ventilated infants: a randomised controlled trial. Arch Dis Child Fetal Neonatal Ed. 2025.
Brouwer F, et al. Comparison of two different oxygen saturation target ranges for automated oxygen control in preterm infants: a randomised cross-over trial. Arch Dis Child Fetal Neonatal Ed. 2024;109(5):527–34.
Langanky LO, et al. Pulse oximetry signal loss during hypoxic episodes in preterm infants receiving automated oxygen control. Eur J Pediatr. 2024;183(7):2865–9.
Salverda HH, et al. Clinical outcomes of preterm infants while using automated controllers during standard care: comparison of cohorts with different automated titration strategies. 2022:fetalneonatal–2021–323690.
Salverda HH, et al. The effect of automated oxygen control on clinical outcomes in preterm infants: a pre- and post-implementation cohort study. Eur J Pediatr. 2021;180(7):2107–13.
Ali SK, et al. Preliminary study of automated oxygen titration at birth for preterm infants. Arch Dis Child Fetal Neonatal Ed. 2022:fetalneonatal–2021–323486.
Dargaville PA, et al. Automated control of oxygen titration in preterm infants on non-invasive respiratory support. Arch Dis Child Fetal Neonatal Ed. 2022;107(1):39–44.
Sturrock S, et al. A randomised crossover trial of closed loop automated oxygen control in preterm, ventilated infants. Acta Paediatr. 2021;110(3):833–7.
Sturrock S, et al. Closed loop automated oxygen control in neonates – a review. Acta Paediatr. 2019.
Gajdos M, et al. Effects of a new device for automated closed loop control of inspired oxygen concentration on fluctuations of arterial and different regional organ tissue oxygen saturations in preterm infants. Arch Dis Child Fetal Neonatal Ed. 2018.

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Prophylactic acetaminophen in the preterm

Posted on 17 February 2026 by Keith Barrington

In a newly published trial (Roze JC, et al. Prophylactic Treatment of Patent Ductus Arteriosus With Acetaminophen: A Randomized Clinical Trial. JAMA Pediatr. 2026) nearly 800 infants of 23 to <29 weeks GA were randomized within 12 hours of birth. There were few exclusions, basically only congenital anomalies and Twtin-Twin transfusion syndrome. The doses were different among the 27-28 weeks infants compared to those more immature, and continued for 5 days in both groups.

The primary outcome variable was survival without “severe morbidity” which was any one of : severe bronchopulmonary dysplasia, stage II or III NEC, grade III or IV IVH, or cystic leukomalacia. Severe BPD used the 2018 NIH consensus definition, i.e. invasive ventilation with more than 21% O2, or CPAP with more than 30% O2, or high flow at more than 3 lpm. Outcome was determined at 36 weeks or discharge home.

There was no outcome difference of importance between the groups, as you can see below.

I don’t know why they inverted the groups between part A and B of the figure, which misled me briefly, as you can see there is a minor difference in NEC in the most immature infants, and among females, but this may well be a random variation.

It is also revealing that Acetaminophen was not very effective at closing the PDA :

Among babies who had an echocardiogram at 7 days of age, the rate of PDA closure was 43% in the more immature controls, and 61% with active medication. In comparison, prophylactic ibuprofen seems probably a little more effective for PDA closure; the Cochrane review of prophylactic ibuprofen shows closure of the PDA on day 3 to 4 of life of 58% in the controls compared to 83% with ibuprofen, from meta-analysis of 9 studies with a total of about 1000 babies.

21% of controls and 14% of acetaminophen infants had medical PDA “backup” treatment, which started a median of 7 days after birth, with a 1st quartile of 3 days. So, many of those “back-up” treatments started during the initial randomization period. A total of around 3% in each group had, eventually, formal closure (surgical or catheter) of the PDA.

The more immature GA stratum had the poorest response to acetaminophen, but still had many more PDAs closed at 7 days of age with acetaminophen than placebo. Apart from numerically fewer cases of NEC in this subgroup, with 95% confidence intervals which include no difference, there is no apparent difference in outcomes, either in the components of the primary or any of the secondary outcomes. Among the secondary outcomes, in the more immature group, there were also numerically fewer pulmonary haemorrhages, 4.5% vs 8%, and fewer babies who had catecholamine support or postnatal steroids in the first 7 days with acetaminophen treatment. But again, for all of these findings, the confidence intervals include no difference.

This trial confirms what we have been seeing in many recent studies. There is no advantage to routine PDA closure. There are still those who seem certain that there are some PDAs that should be closed in small preterm infants. My response remains that it may be true, but we really need a way to define that subgroup of infants, and then find the most effective, least toxic way of closing their PDA.

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Not just neonatology, trip to Rwanda

Posted on 17 February 2026 by Keith Barrington

I was very fortunate to be able to take a trip to Rwanda to participate in their neonatal training scheme, in what was termed a “respiratory bootcamp”.

Rwanda is a small country of 23000 km2, with a young population of over 14 million, and 400,000 births annually. Which I can’t help comparing to Quebec, with an area of 1.5 million km2, a population of 9 million and annual births of 80,000.

There has been remarkable progress in perinatal health care and outcomes over the last decade, with a marked improvement in the proportion of deliveries attended by a trained birth assistant, and taking place in an institution (now >95%), with a dramatic reduction in maternal mortality from over 1000 to about 300/100,000 births. This has been accompanied by a decrease in stillbirth rates, and in neonatal mortality. There are now 3 NICUs in Kigali, and another in development in Butare, with 4 neonatologists in the country, all in Kigali. Their young fellowship program will soon have the first locally trained neonatologists. I feel privileged to have been a small part of this program.

In addition to visiting the NICUs and spending time with fellows, nurses and staff, I was able to take a tour of the country, visiting the 3 of their 4 national parks where there is accommodation. The fourth is currently being developed. I started in Volcanoes national park, where I was able to pursue one of my interests, viewing wildlife and bird photography. You can click on any photograph to see it full-sized.

Regal Sunbird
Scarlet-breasted Sunbird
Northern Double-collared Sunbird

These 3 are all Sunbirds, a large family with very colourful males, and almost uniformly drab females, who eat nectar, filling a similar ecological niche to the Hummingbirds of the Americas.

In Volcanoes park, a small troupe of Golden Monkeys were eating and watching us carefully, but I decided against buying the permit to view the Mountain Gorillas, maybe next time. I also visited some wetlands in the region, and photographed the birds below, among many others.

Black Crake
Hadada Ibis
Pied Kingfisher

Then on to Nyungwe national park, which is in the South-west corner of the country

Augur Buzzard
Yellow-eyed Black Flycatcher
Black-headed Waxbill

And has troupes of Black-and-white Colobus and Blue Monkeys

Black-and-White Colobus
Blue Monkey

We visited another wetlands as we headed back eastwards

Fulvous Whistling Duck
Southern Red Bishop
Black-headed Gonolek
Swamp Flycatcher

Then on to Akagera national Park, the oldest and largest in Rwanda

Masai Giraffes and Plains Zebras in a Valley of the Akagera park.

Long-crested Eagle
Bare-faced Go-away Birds on termite nest
Cape Buffalo and Yellow-billed Oxpecker
Cardinal Quelea
Woolly-necked Storks
White Rhinoceros and Western Cattle Egret
White-browed Coucal
Rufous-breasted Heron
Blue-headed Coucal
Woodland Kingfishers
African Fish Eagle

I was able to return to Akagera for another day, later in my trip

Black Cuckooshrike
Pin-tailed Whydah
African Openbill
Lilac-breasted Roller

In Kigali, close to the airport, there is a preserved wetlands, which has been turned into an Eco-park.

White-collared Oliveback
Black-and-white Mannikin
Gabar Goshawk
Red-chested Sunbird
Village Weaver and nest
Little Bee-eater

If you are interested, there are many other photos on my other blog, keithbarrington.com

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How much oxygen for the resuscitation of the preterm?

Posted on 29 December 2025 by Keith Barrington

I like a good acronym, so my initial response to the new TORPIDO trial was very positive! TORPIDO 30/60 was a large multicentre RCT comparing initial FiO2 concentrations for resuscitation of the preterm infant (Oei JL, et al. Targeted Oxygen for Initial Resuscitation of Preterm Infants: The TORPIDO 30/60 Randomized Clinical Trial. JAMA. United States2025). The first TORPIDO study (Targeted Oxygen in the Resuscitation of Preterm Infants and their Developmental Outcomes) was a comparison in 290 infants <32 weeks GA, of 21% starting O2 concentration vs 100% starting concentration (Oei JL, et al. Targeted Oxygen in the Resuscitation of Preterm Infants, a Randomized Clinical Trial. Pediatrics. 2017;139(1)) . It had to be stopped early because it became difficult to enroll patients as we became reluctant to use 100% oxygen. Although underpowered, there was a numerically greater mortality in the 21% oxygen group, especially among the infants <28 weeks.

This contributed to an apparent increase in mortality among lower FiO2 regimens when all the Individual Patient Data were included in a Network Meta-Analysis, NETMOTION. (Sotiropoulos JX, et al. Initial Oxygen Concentration for the Resuscitation of Infants Born at Less Than 32 Weeks’ Gestation: A Systematic Review and Individual Participant Data Network Meta-Analysis. JAMA Pediatr. 2024).

That NMA suggested that the higher starting oxygen groups (90% or higher), had a lower mortality than low starting concentration (30% or less), while intermediate, >30% to <90%, was similar to low starting concentration. Of note, the 1st TORPIDO study was the largest in that NMA.

Unfortunately, 10 of the 12 trials in that NMA were very small, 31 to 95 subjects, the 2 larger ones were modestly sized (287 and 193). For such an important outcome, and an easily applied, no-cost intervention, better, larger trials were needed.

The new TORPIDO 30/60 trial started in 2018, well before NETMOTION was performed. According to the choices made by the authors of NETMOTION, it would have been considered a comparison of intermediate (60%) to low (30%) oxygen. At the time of designing it, it was considered unlikely that very high starting oxygen concentrations would be a good idea, so the choice of a comparison between 30 and 60% was entirely reasonable.

The new trial results show no difference in the primary outcome, or in any indices of brain injury on ultrasound.

There were some differences in immediate responses in the delivery room, “Newborns in the FIO2 of 0.6 group, compared with the FIO2 of 0.3 group, were less likely to receive chest compressions (2% vs 5%) or epinephrine (1% vs 2%) and more likely to reach SpO2 > 80% by 5 minutes (58% v 44%) (Table 3) and had higher initial SpO2.” Which are interesting differences, but did not translate to any measurable difference in clinical outcomes.

This suggests to me that we have to push this further, and compare a starting FiO2 of 60% (which seems no worse than anything lower, and might have some short term advantages) to a starting FiO2 of 90 or 100%. It seems weird, after all this time, to talk of going back to 100% oxygen for initiating resuscitation. It seems only a few years ago (but I guess it is more than 2 decades now) that I had to approach the hospital administration at my previous post to have pressurized room air and air/oxygen mixers installed in the delivery room, so that we could start resuscitation with 21%, and titrate if needed. The DR, in a relatively new building, had been built with just piped oxygen for neonatal resuscitation. The administrators of the Royal Victoria Hospital in Montreal were very responsive, and immediately approved the budget when I presented the evidence.

Most of my readers will know that the evidence for room air resuscitation in full term infants was quite strong, and that routinely starting with 21% oxygen was associated with a 27% lower mortality than 100 % oxygen, as this ILCOR meta-analysis showed. https://publications.aap.org/pediatrics/article/143/1/e20181825/76868/Room-Air-for-Initiating-Term-Newborn-Resuscitation

But if the data for preterm infants is taking us back to much higher oxygen concentrations, I guess we will have to decide whether 34 week infants should be treated like the 35 weekers, or like the more immature infants. Just like my comments about cooling, I think it is unlikely that the risks change dramatically at midnight between 34 weeks 6 days, and 35 weeks. We will need more granular information in order to make decisions for infants in the late preterm age ranges. Hopefully. those doing the trials will provide Individual Patient Data, that will allow analyses according to gestational age, and other risk factors.

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