Comment on my post about the Beneductus trial

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Tim Hundscheid and Willem P. de Boode

References

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

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

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

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

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

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

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

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

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

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

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The PDA, will we ever know what to do?

There are a few trials on-going, or near completion or, as this one, just published, that should give us insight into what to do about an open ductus in the very preterm. This trial has major limitations, but does give us some information. Hundscheid T, et al. Expectant Management or Early Ibuprofen for Patent Ductus Arteriosus. N Engl J Med. 2022.

Babies of under 28 weeks gestation were randomized at 24 to 72 hours of age if an echocardiogram showed a PDA of over 1.5 mm diameter, and a majority left to right shunt. They either had expectant management (no pharmacological or surgical PDA closure, which was followed by all except 1 of the 136 in this group) or a course of ibuprofen, followed by a second, and then possibly a third and fourth courses, with an option for ligation under limited circumstances, n=137 in the intervention group.

My first question is whether infants in the PDA closure group were more likely to survive or not, and I don’t know! There is nowhere I can find in the document or supplemental material the mortality before discharge in the 2 groups. The intervention group had much higher mortality before 28 days, 18% vs 9.6%, and somewhat higher at 36 weeks, 18% vs 14%, but death before discharge (which is listed as an outcome in the supplement) is nowhere reported.

I don’t know about you, but I can’t interpret, or care very much, about any of the other outcomes if I don’t even know if survival is different.

It looks like there was about the same NEC in the 2 groups, and more moderate to severe BPD in the intervention group, so there was more of the composite outcome “death prior to 36 weeks, or mod/severe BPD or NEC (stage 2 or 3)” in the ibuprofen group, 64% vs 46%.

There are a couple of other issues that are not clearly addressed in the publication, a substantial proportion of the babies received paracetamol (acetaminophen to the North Americans), 38 % of the ibuprofen group and 25% of the expectant group, but whether this was for analgesia or as therapy to close the PDA is not mentioned. There were also a lot of babies who received diuretics, over 40% in each group, but for what indication, at what time, and for how long isn’t clear.

The study was stopped before halfway, so it was drastically underpowered to answer the weird question of what ductal treatment with cox inhibitors does to outcomes up to 36 weeks. I say a weird question because it is one that I don’t really care about at all! Were the babies more or less likely to survive to go home if they were treated? Did they have worse pulmonary outcomes, i.e. home oxygen, or prolonged hospitalisation for pulmonary reasons, or poor feeding because of persistent respiratory distress?

For the outcome that was reported, expectant management was “not inferior” to intervention. In other words if you stop looking at the babies after 36 weeks PMA, then leaving the PDA alone is not worse than treating it, but you have to guess about what happens after 36 weeks.

IF there were few deaths between 36 weeks and discharge, then expectant management appears preferable, but the relevance of the parts of the primary outcome are questionable: at 36 weeks there were more intervention group babies who needed oxygen, but the median duration of oxygen therapy (40 vs 41 days) and of respiratory support (55 vs 56 days) were almost identical between the 2 groups. Why is there no report about outcomes that matter? How many went home on oxygen? Was hospitalisation prolonged in the group with more BPD? Were the same number of babies feeding orally when they were discharged? These are things which have impacts on families, far more than the diagnostic label of BPD, and none of them are mentioned in the publication. They have made many other rather strange choices in data presentation, for example, I know that one of the babies developed West syndrome (which was likely diagnosed after 36 weeks!), and, from the table of adverse effects, I know that one baby in each group had a wrist abscess, despite not knowing the survival!!

There is 2 year follow up planned, so hopefully we will eventually discover the survival rates in the 2 groups in the trial.

Another trial published this year had some similarities (Potsiurko S, et al. Randomized Noninferiority Trial of Expectant Management versus Early Treatment of Patent Ductus Arteriosus in Preterm Infants. Am J Perinatol. 2022). In a single centre trial from Lviv, Ukraine, VLBW infants of under 32 weeks gestation were randomized at less than 72 hours of age if their PDA diameter was over 1.5 mm. They received either attempted closure (with either rectal ibuprofen or intravenous acetaminophen, n=104, the choice of rectal ibu or IV acéta was apparently randomized), or expectant treatment, n=104. with 8 of the expectant group having “rescue” PDA treatment at about 7 days of age.

These were, on average more mature babies, with a lower incidence of BPD, and there were no important differences in either survival to discharge (about 80% in each group), or the need for oxygen at 36 weeks (28% with active treatment vs 22% with an expectant approach). The power of the trial for excluding even major differences in outcomes is, of course, limited, with this sample size.

Most importantly however, I think there has been a huge failure of peer review for this trial, which is written in some parts as, and stated in the title to be, a non-inferiority trial, but it is no such thing. It is a comparative trial that did not show a difference between the groups, that is NOT the same as showing non-inferiority!

The sample size calculation is very strange to start off with, it starts by assuming that there is an outcome difference in favour of expectant treatment (death or BPD of 35% compared to 55%), and then calculating for an alpha of 0.01 and a power of 90% that they would not show a difference of greater than 10% beyond this difference. Which gave them a very small sample size for a non-inferiority trial, of 84 per group.

That really isn’t what is meant by a non-inferiority trial! The point of a non-inferiority trial is to show that the two approaches are not very much different, and that the experimental arm is not worse than the usual care arm, by an acceptably small amount, with a certain confidence. So to calculate the sample size you should start with the assumption that the two treatments have about the same outcome, and then calculate how much worse the new treatment could be without exceeding your “acceptably small amount”. If you use the non-inferiority margin that these authors have claimed in the methods of 10%, and that the incidence of “death or BPD” with standard care is about 40%, then with an alpha of 0.05 and a power of 80% (which are much more conservative than the calculations these authors have used) the sample size required is 297 PER GROUP.

There is no mention in the results of the confidence interval of the difference between groups, which is essential to know if the non-inferiority margins were crossed or not. What I think they have actually shown is NOT non-inferiority, I have tried to visualize the results with the figure below, which shows the event difference between groups (death or BPD was 0.45 vs 0.39, or an event difference of 0.058, with 95% CI of -0.085 to 0.195, which overlaps both no difference and the non-inferiority margin of a 10% difference, and is therefore an inconclusive result.

You cannot say, based on this result, that expectant treatment is non-inferior to active PDA closure.

As a reminder, here are the possible outcomes of a non-inferiority trial, in a similar graphic form (from Mauri L, D’Agostino RB, Sr. Challenges in the Design and Interpretation of Noninferiority Trials. N Engl J Med. 2017;377(14):1357-67)

Another trial of early PDA treatment was published last year, (Roze JC, et al. Effect of Early Targeted Treatment of Ductus Arteriosus with Ibuprofen on Survival Without Cerebral Palsy at 2 Years in Infants with Extreme Prematurity: A Randomized Clinical Trial. J Pediatr. 2021;233:33-42 e2), this study randomized infants of under 28 weeks (minimum 24 wk) at 6 to 12 hours of age if they had a large PDA, which was calculated according to the postnatal age in hours (PNA), the minimum size to treat was 2.26-(0.078 x PNA)mm, so a 12 hour old baby with a PDA diameter >1.33 mm would be enrolled, or a 6 hour old with a diameter >1.8 mm.

A large proportion of the placebo babies received open-label ibuprofen after the initial course (62%, compared to 17% of the ibuprofen group), so the study is not very informative for other clinical outcomes, which really weren’t very much different between groups even though the PDA was more likely to be closed on day 3 and on day 14 in the ibuprofen group.

The primary outcome of this trial was the diagnosis of cerebral palsy at 2 years of corrected age. Survival to 2 years was a little more frequent in the placebo group, and CP was a little less frequent, but both differences could easily have been due to chance.

There are other trials of treating the PDA compared to a conservative approach, hopefully with designs which will inform us for the future which approach is preferable, based on clinically important effects such as survival to discharge and other outcomes which are of importance to babies and their families.

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Not Neonatology: Oh Canada…. Warbler

Still on my trip to Ecuador, where I saw my first ever Canada Warbler. I know it is just a name, but it was most pleasing to find this bird, which does indeed migrate to Canada each year but I had never encountered, and passes the Canadian winter here.

I have completely changed the design of my other blog keithbarrington.com hopefully it is easier to navigate and see anything that might interest you.

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Not neonatology: a trip to Ecuador

A break in blogging for a couple of weeks, while I take a trip to Ecuador, with the main purpose of birdwatching and photography. Ecuador is the country with the greatest avian biodiversity in the world, and with and amazingly knowledgeable guide, I’m having a great experience.

I am blogging about the trip as I go, mostly in order to post photos. Please visit https://keithbarrington.com/, in addition to the home page, I will add various other pages of photos, for now, there is just the page “All the Tanagers of the Trip” which you can find by clicking a link at the top of the page.

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How much protein should we provide to the preterm in the first days of life?

Extremely preterm infants become catabolic rapidly after birth, with the sudden interruption of their trans-placental nutrient supply to the fetus, who becomes a baby that has tiny stores of fat or glycogen. We progressed in neonatology from starving preterm babies in the first few days, to supplying them with just a glucose solution, to providing sick babies unable to full feed with TPN starting almost in the delivery room! This has been based on physiologic principles and the best guess of nutrient needs, and short term physiologic studies. In my NICU, we start with a solution of 3% AA in 10% dextrose, which the babies get at about 80 mL/kg/d (up to 100 if they have no arterial catheter) and so they receive amino acids at a rate equivalent to between 2.4 and 3 g/kg/d of on day 1, the next working day they have a formal TPN prescription, which will progress the amino acid amount up to 4 g/kg/d over a few days.

I have written recently about the PEPANIC trial, and have referred to trials of older children and adults, in whom early TPN after ICU admission increases complication rates, in particular hospital acquired sepsis. That is true even among adults who are considered malnourished on admission.

Extreme preterms are, of course, a different species, and we should not extrapolate any of those data to the preterm, but we can certainly learn from them.

In the ProVIDe trial, (Bloomfield FH, et al. Early Amino Acids in Extremely Preterm Infants and Neurodisability at 2 Years. N Engl J Med. 2022;387(18):1661-72), 434 ELBW infants (<1000g) who were admitted <24 hours and had a UAC placed, were randomized to either get 8.4% amino acid solution or 0.45% saline as the solution in their umbilical arterial catheter, running at 0.5 mL/h. Which would have given a 1 kg baby 1 g/kg/d more amino acids, and given a 500 g infant 2 g/kg/d of amino acids extra.

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Which is the first thing I don’t understand here, the authors state that they did it this way to ensure that the intervention babies received 1 g/d more protein; the babies should, with a birth weight averaging 780g have received on average about 1.3 g/kg/d more protein in the intervention group, for as long as the UAC was in place, to a maximum of 120 hours. But, in fact, they received a supplement which was inversely proportional to their birth weight I am not sure really how relevant this is to any kind of practice that I would consider instituting. I understand the technical simplicity of designing the study this way, but surely just adding an extra 0.5 mL/kg/h of the solution would have been simple and much more clinically relevant. Then every baby would have received 1 g/kg/d extra for the intervention period.

This makes it very difficult to figure out what this means; the results showed, overall, in the intervention group, very slightly lower mortality (18% vs 19.4%, consistent with random variation) before follow up, but worse, and slightly lower, Bayley language, cognitive, and motor scores. Here below are the scores on the 3 composites, showing the numbers tested (about 93% of the surviving infants), the mean score and 1 SD, with the intervention group first, the controls second and then the adjusted mean difference with the 95% CIs.

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The intervention group babies received an average of 0.8 g/kg/d of protein when calculated and averaged over the 1st week of life, but, as mentioned, that supplement will have been very variable. A 400 g baby, for example will have received 2.5 g/kg/d of additional amino acids, up to a total of 12.5 g/kg over the maximum 5 days of the study. This calculates to 1.4 g/kg/d when averaged over the 1st week. Others may have received very little; a 1kg baby having their UAC removed at 48 hours of life would have had an additional 2 g, or when calculated over the 1st week, 0.3 g/kg/d. It might seem strange to calculate the supplements over the first week, when the intervention lasted a maximum of 5 days, but the authors also did the calculations that way for the table in the supplement, which showed that all of the other nutritional intakes, of macronutrients and energy, were identical between groups.

The primary outcome was a new word, “neurodisability”, which really meant… it is not immediately obvious as it is not clearly defined in the publication, you have to download and read the protocol to be certain. To save you that extra work, I have copied the definitions below.

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As is usual in studies of follow up in the very preterm infant, the majority of abnormal outcomes were due to low Bayley scores. In the control babies, 5.5% had CP, 0.6% were “blind” and 1.2% were “deaf”, therefore, most of the 37% with so-called “neurodisability” were classified as such because of a low score on one or more of the Bayley 3 composites.

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This is the part of the results table showing the proportion of tested babies with scores below 85 (“mild”), and below 70 (“moderate or severe”), on each of the composites, and the adjusted relative risk and 95% CI. You can see that most of the 95% CI included no difference, apart from the proportion with a Bayley cognitive composite <70.

The finding which is emphasized in the graphical abstract above, “of moderate to severe neurodisability” was defined posthoc: “Because few disabilities were classified as severe or moderate, these categories were combined post hoc into a single category”.

Giving additional protein, with the same amount of energy, led to an increase in serum ammonia (with 95% CI which included zero) an an increase in urea concentrations, which suggests to me that the babies weren’t utilizing all the extra protein. At the same time there was a metabolic response, as more of the intervention group babies became hypophosphataemic and hypercalaemic, which is a phenomenon that occurs after birth most frequently in babies with Intra-uterine Growth Restriction, and has been called different things in the literature, but which is analogous to the re-feeding syndrome. Babies with this occurrence often also are hypokalaemic and hypomagnesaemic, and may be hyperglycaemic, but I can’t see if those are reported in this trial.

As I mentioned above, early TPN in the PICU leads to an increase in hospital acquired sepsis, which was true for the overall group in the PEPANIC trial, and was especially true for the babies of <1 week of age. In this new trial there were no major individual changes in neonatal complications, apart from an increase in PDA needing treatment, from 42 to 54%, (aRR=1.3, 95% CI 1.05- 1.6). There was only a small increase in the proportion of babies with at least one episode of culture proven late onset sepsis, from 31 to 36% (aRR=1.19, 95% CI 0.51- 1.96). There was a small transient impact on weight gain, with the intervention groups having slightly higher body weight z-scores at 4 weeks of age, but there was no difference at discharge or at 2 years. They also performed executive function testing (BRIEF-P) and a behavioural evaluation (CBCL), which showed no striking differences.

I still don’t know, after this trial, what is the optimal amount of protein to start in the TPN of the very immature baby, and actually, I don’t think the trial helps me very much. The control babies received, when averaged over the entire first week of life, an average of 2.9 g/kg/d of protein, and about 76 kcal/kg/d. Adding somewhere between 1 and 2.5 g/kg/d for the first few days in a manner which is inversely proportional to birth weight, without changing anything else, did not have any positive impact, and there is some suggestion of a negative long term change in development. So I won’t be doing that.

I would be fascinated to see an analysis of these data by the actual amounts of extra protein received. The highest risk babies (lowest birth weight) will have received relatively more additional protein, and, if the additional protein is the cause of those potential impacts on developmental progress, then it should be more evident in those infants.

There are very few studies to put this new trial in context, in terms of large randomized trials of early nutritional interventions in the very preterm with clinical outcomes. A study from Rhode Island, (Balakrishnan M, et al. Growth and Neurodevelopmental Outcomes of Early, High-Dose Parenteral Amino Acid Intake in Very Low Birth Weight Infants: A Randomized Controlled Trial. JPEN J Parenter Enteral Nutr. 2018;42(3):597-606) enrolled 168 babies under 1250 g birth weight, to receive either 1-2 g/kg/d on day 1 increasing to 4 g/kg/d by day 5, or 3-4 g/kg/d on day 1, increasing to 4 g/kg/d by day 2. The primary outcome was from a neurological exam and developmental assessment at 2 years, and it showed no difference between groups. The Cochrane review of higher vs lower amino acid intakes of amino acids included about 20 other studies which were of various different interventions, had differing outcomes, and were all small or tiny. It showed no clear difference in any outcome.

For the future, it would be illuminating to do a similar study to ProVIDe, but to add both protein and an additional energy source, adjusted to give the same per kg supplement to all babies. That might allow better protein utilization and avoid the increase in urea concentrations, at the same time enhancing phosphorus supply, especially among the infants with IUGR, should make this safer.

Should we go lower? Is it possible that babies would have better outcomes if we started with even lower protein intakes than the ProVIDe control group? The answer is, I think, yes, it is possible, but I think we will have to be very careful, we could perhaps randomize babies to intakes which are within the range of those in current use in our NICUs, say 1.5 g/kg/d as starting dose, compared to 3 g/kg/d, with appropriate energy intakes, which also could (and probably should) be different between groups. ProVIDe, and other data, suggest that our outcomes should include PDA, late onset sepsis, and long term developmental progress. Despite the lack of very strong data to support the current practice of extremely early TPN in the very preterm, I don’t think we should return to the days of starting TPN on day 3, with just dextrose administered initially, but rather acknowledge that we are not really sure what is the optimal approach to protein and other nutrient administration in the extremely preterm infant in the first few days of life. Overall, babies do much better in terms of survival, nutritional, growth, and developmental outcomes than they have have before. We are doing somethings right, we need to fine tune to get them “righter”!

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It’s Raining Antibiotics

Early onset sepsis is a serious condition with a substantial morbidity, and, thankfully, a relatively low mortality in recent years. Prompt recognition and early treatment are essential, but early clinical signs and risk factors tend to be non-specific. As a result many infants are evaluated for sepsis and treated empirically while waiting for culture results. The proportion is amazingly variable between hospitals, in an article from a couple of years ago the California Perinatal Quality Care Collaborative showed that the proportion of newborns receiving antibiotics ranged from 1.6% to 43% in various hospitals. Some of which was due to differences in hospital characteristics (and included preterm infants), but much was due to differences in practice patterns.

Among term infants and those very near to term (35 weeks and more) somewhere around 5 to 10 % currently have a sepsis evaluation, which almost always leads to temporary treatment with antibiotics. Despite the very high sensitivity of modern culture methods, it is difficult for some physicians to stop antibiotics when the cultures are negative, so “culture negative sepsis” is a frequent diagnosis. The actual incidence, or even the existence of such a phenomenon is uncertain, as very many studies have used the prolongation of antibiotics as a diagnostic criterion. Which leads to the following circular reasoning:

  • 1. Infants with the following criteria were evaluated for sepsis and then had more than 2 days of antibiotics, therefore they had “culture negative sepsis”,
  • 2. In the future we will use those criteria to define “culture negative sepsis” and treat the babies with a full course of antibiotics.
  • 3. Lo and behold, the babies do well, so we must be doing the right thing,
  • 4. We will continue to use the same criteria to diagnose “culture negative sepsis”

This is all compounded by the use of “inflammatory markers” such as CRP as part of the criteria. The criteria used in many centres are a combination of perinatal risk factors and higher concentrations of CRP, or perhaps procalcitonin, than the concentrations found in healthy normal babies without those risk factors.

Anyone reading this blog for a while will now my attitude to those markers. The new article that I will shortly discuss used a combination of “risk factors” and an elevated CRP >10 or procalcitonin (above “reference intervals for postnatal age”). About 10% of noninfected babies overall have a CRP over 10, I am not sure what the proportion is, however, of non-infected babies from births with “risk-factors” that have an elevated CRP. Especially as nowhere in this publication or in the attached protocol are the risk factors defined. One risk factor for sepsis, which is associated with a very high rate of empirical treatment, and a very low frequency of actual sepsis, is maternal chorioamnionitis. It is known that maternal fever and chorioamnionitis increase neonatal CRP even when the infant is not infected, as do fetal distress, prolonged rupture of membranes, prolonged labour, and meconium aspiration syndrome.

The trial I am discussing, (Keij FM, et al. Efficacy and safety of switching from intravenous to oral antibiotics (amoxicillin-clavulanic acid) versus a full course of intravenous antibiotics in neonates with probable bacterial infection (RAIN): a multicentre, randomised, open-label, non-inferiority trial. Lancet Child Adolesc Health. 2022;6(11):799-809.) with one of the longest titles of recent years, enrolled babies of at least 35 weeks gestation, who had an evaluation for early onset sepsis because of risk factors, or transient clinical signs, and who were well at 48 hours after the blood cultures were obtained, which were negative. As mentioned the risk factors are not defined in this publication, but the reference they give is to the NeoPINS study which defined the risk factors as any one of: maternal GBS positive; ruptured membranes >18h; GA <37 weeks; or maternal chorioamnionitis, defined as either fetal tachycardia or a maternal fever >38.5.

If this trial used those criteria, then 100% of the babies born at 35 and 36 weeks would have had a sepsis evaluation and antibiotics, which I think is crazy, to use the scientific terminology.

The combination of one of those risk factors with a negative culture, a baby who was well at 48 to 72 hours, and either a CRP >10 or a PCT over the postnatal age defined limits, made a baby eligible to be randomized to either continued IV antibiotics, or to switch to an oral suspension of amoxicillin and clavulanic acid.

The worst thing about this trial is labelling these healthy, probably uninfected babies, as having “probable bacterial infection”. They did not.

The primary outcome was the re-infection rate, defined as a clinical infection associated with either fever or hypothermia and an increase in inflammatory markers, prior to 28 days of age.

The primary outcome occurred in 1 of 252 IV and one of 252 po babies.

So if you don’t need antibiotics, it doesn’t matter whether you get them intravenously or orally.

The current AAP recommendations are to stop antibiotics in well-appearing infants after 48 hours if the cultures are negative and not to continue simply based on lab results (such as a raised CRP or abnormal white cell count). That is an evidence-based recommendation that I firmly agree with, and would have meant that the large majority of the infants in the RAIN trial, probably all of them, would have been sent home without antibiotics.

Many infants in the RAIN trial would not have had a sepsis work up at all if they had used a sepsis calculator instead of these simplistic perinatal risk factors (Achten NB, et al. Association of Use of the Neonatal Early-Onset Sepsis Calculator With Reduction in Antibiotic Therapy and Safety: A Systematic Review and Meta-analysis. JAMA Pediatr. 2019;173(11):1032-40), probably about half of them would never have been evaluated, and large numbers of the 35 and 36 week infants would have escaped antibiotics.

Systemic antibiotic therapy in the newborn, especially when prolonged, is not benign.

Messing up the neonatal microbiome, which has evolved along with us over many millions of years, should not be taken lightly. Oral antibiotics may even be worse than intravenous, depending on the IV antibiotics used, some have little intestinal excretion, whereas amoxicillin clavulanic acid is great at killing bifidobacteria.

The human intestinal microbiome is affected for months when you give that combination to adults. The long term impacts of giving systemic antibiotics, during the phase of initial development of the intestinal microbiome, are only now being appreciated. (Patangia DV, et al. Impact of antibiotics on the human microbiome and consequences for host health. Microbiologyopen. 2022;11(1):e1260).

Some of the derangement in the microbiome after neonatal antibiotic treatment has abated by 12 months of age (Reyman M, et al. Effects of early-life antibiotics on the developing infant gut microbiome and resistome: a randomized trial. Nat Commun. 2022;13(1):893), but the long term clinical impacts are numerous and important.

Neonatal antibiotic exposure has been linked with asthma, other forms of recurrent wheezing, colic, coeliac disease, abnormal development of recognition processes, reduced linear growth, and increased obesity, not to mention eczema, inflammatory bowel disease, and type 1 diabetes. (Duong QA, et al. Antibiotic exposure and adverse long-term health outcomes in children: A systematic review and meta-analysis. J Infect. 2022;85(3):213-300).

The RAIN trial showed that switching to oral antibiotics meant that the child could go home sooner, and had fewer iv attempts and therefore less pain, which are good things. But even better would be just stopping antibiotics when the baby doesn’t need them.

A mentioned above, all the RAIN trial really tells us is that if you don’t need antibiotics, then the risk of possible infection in the first month of life is the same if you give oral or IV antibiotics for a week.

I have corrected the title of the trial :

Efficacy and safety of switching from intravenous to oral antibiotics (amoxicillin-clavulanic acid) versus a full course of intravenous antibiotics in neonates who probably are not infected (RAIN), unfortunately without an untreated control group: a multicentre, randomised, open-label, non-inferiority trial.

Which we could rename as RAINING (Reduction of intravenous Antibiotics In Neonates, In a Non-infected Group).

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Do omega 3 fatty acids make preterm babies smarter?

It seems that they do, perhaps a little bit!

There are now a confusing array of trials of supplementation of polyunsaturated fatty acids in preterm infants. They have compared various control diets to differing PUFA supplements. Many of them have used a long chain omega-3 fatty acid, Docosahexaenoic acid (DHA), and sometimes also Eciosapentaenoic acid (EPA), rarely ALA (alpha-linolenic acid). Some of the studies have also used arachidonic acid, an omega-6 PUFA, and they all try to make sure that the essential FAs, linolenic and linoleic acid are supplied in sufficient quantities.

This new publication (Gould JF, et al. Neonatal Docosahexaenoic Acid in Preterm Infants and Intelligence at 5 Years. N Engl J Med. 2022;387(17):1579-88) notes in the introduction that the current dietary recommendations for DHA intake of about 20 mg a day, are lower than the usual in utero accretion of DHA, most of which goes to the brain and is incorporated into neuronal membranes and is needed for synaptic function. There are a couple of previous tiny trials of DHA supplementation in term babies which suggest that Bayley Scores and problem solving might be improved with a bit more DHA among formula fed babies. The new publication is a follow up study to N3RO which was a multicentre RCT in about 1200 preterm babies <29 weeks gestation with the primary outcome being BPD. BPD was actually more frequent with the DHA supplementation, against all expectations. DHA in that study was started by oral supplementation within 3 days of starting oral feeding, which supplied an additional 60 mg/kg/d.

As you can see from the main outcome table from the original publication which is below, there was less mild BPD, but more moderate or severe BPD, and more BPD overall, with DHA supplementation.

The new publication is of a study in a subgroup of 480 Australian babies from the original trial with similar numbers and similar baseline characteristics in the 2 groups. The primary outcome for this study was the full scale IQ on the WPPSI at 5 years corrected age. Because of COVID a few evaluations were performed outside of the originally specified time window, and a few were unable to be tested.

The main results are below:

What they call “General Cognitive Impairment” is a WPSSI score less than 85 (it is a standardized score, so that is 1 SD below the mean) and “Severe Cognitive Impairment” is <70. In a sample with a normally distributed result, one would expect 16% to have General and 2.5% to have Severe Impairment.

One can see that the full scale scores are shifted up a few points in the DHA group, so that the mean is a little higher and fewer infants fall below those thresholds, and that the main difference is in verbal comprehension.

What should we do with these findings? First of all let’s try and put them in the context of other trials, the MOBYDick trial supplemented breast-feeding mothers of babies <29 weeks. The babies’ intake of DHA was probably less than in N3RO: supplementation increased the percentage of DHA in breast milk from 0.3% to just under 1% of total fatty acids, which remained at about 35 mg/mL, in other words a baby getting 100 mL/kg/d of breast milk from a supplemented mother would receive somewhere around 30 mg/kg/day of DHA compared to about 10 mg/kg/d in the controls. That study also showed an increase in BPD with supplementation, which was why they stopped the trial early, as the results of the N3RO trial appeared, and in combination with the increase in BPD on interim analysis of this trial they realized they were extremely unlikely to show a benefit. The 18 month follow up of that study (Guillot M, et al. Maternal High-Dose DHA Supplementation and Neurodevelopment at 18-22 Months of Preterm Children. Pediatrics. 2022;150(1)) showed no real differences between groups, with a slightly higher Bayley language composite score in the DHA supplemented group. On a subgroup analysis of that trial the scores were more improved in the more immature babies, but the statistical test for interaction suggests that might just be a random difference between the subgroups.

Another much smaller trial of DHA and AA supplementation in around 100 VLBW infants followed the babies to 6 months with the Ages and Stages questionnaire, which was improved on one subscale in the supplemented group, then to 2 years with Bayleys, and then to 8 years for IQ testing. The Bayley and IQ results were similar between the groups.

The DINO trial was an RCT, also from Australia, which enrolled infants of up to 33 weeks gestation, with both maternal supplementation or supplementation in formula milk, with the primary outcome being developmental outcomes. They showed no overall difference in Bayley scores at 18 months were similar between groups, with perhaps higher MDI scores by about 5 points in the supplemented girls.

This seems overall to suggest that there might be a slight benefit, overall, on developmental progress, of supplementation of the diet with DHA in very preterm infants, and at the least, there is unlikely to be a negative effect. It may be that there is a pro-inflammatory effect while receiving supplementation though, leading to an increase in oxygen needs at 36 weeks, and therefore the diagnosis of BPD. There is almost no longer term pulmonary follow up reported, however. The new report does mention that almost half of the babies in N3RO had a respiratory hospital admission before 5 years of age, with an average of just over 2 admissions; there was no real difference between the groups.

These studies point out again the major limitations of using “BPD” as the indicator of lung damage in the preterm infant. There is relatively poor correlation between BPD and longer term pulmonary outcomes which are of importance. It seems that supplementation with DHA may increase “BPD”, but does not increase long term pulmonary morbidity. It might make the babies a little bit smarter though.

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Making intubation safer for the most fragile babies

Many, many years ago, when I was a young trainee physician, we learned almost everything “on the job”. I can’t remember the first patient I intubated, but there were no mannequins, and no simulations, the phrase “see one, do one, teach one” was perhaps an exaggeration, but not far from the truth. When I read, recently, the hilarious book ‘This is Going to Hurt’, by Adam Kay which recounts his time as s junior obstetric trainee doctor in England, it seems that a similar approach continued when he was training, fairly recently.

I don’t remember the first patient I intubated, it was certainly an adult, as I did jobs as a House Officer (intern), then a year as a Senior House Officer in adult medicine before switching to paediatrics. During that year I would often institute intensive care for the most critically ill patients, I remember inserting peritoneal catheters to start dialysis, putting in central lines to start intracardiac pacing, and intubating several patients. The first one, or maybe two, intubations were probably done with an anaesthetist standing by my shoulder coaching me. By the time I did my first neonatal job I was asked if I was able to intubate, and, as I answered in the affirmative, I was given first option on the intubations that occurred in the NICU during my calls. In those days we also intubated in the delivery room all babies born with thick meconium in the amniotic fluid, as we were convinced this would reduce the risks of severe meconium aspiration syndrome. We would repeatedly intubate and suck on the tube as we removed it, until the fluid that returned was clear, so sometimes needing 3 or 4 intubations and sometimes even more. We even tried to stop the babies breathing vigorously as we did the intubations! This meant that I rapidly became an expert at endotracheal intubation in larger babies, and gradually in smaller infants also.

Returning to the present, we now know a lot more about physiologic responses to intubation, and the adverse impacts of failed intubations and multiple attempts (Singh N, et al. Impact of multiple intubation attempts on adverse tracheal intubation associated events in neonates: a report from the NEAR4NEOS. J Perinatol. 2022). For example, having multiple attempts at endotracheal intubation in the delivery room increases the risk of intraventricular haemorrhage (Sauer CW, et al. Intubation Attempts Increase the Risk for Severe Intraventricular Hemorrhage in Preterm Infants-A Retrospective Cohort Study. J Pediatr. 2016;177:108-13), and many babies desaturate severely during intubation. It is critically important to make intubation as safe as possible for at-risk babies. At the same time we have to train new young paediatricians, many of whom will eventually work in hospitals with delivery rooms, where they will be responsible for neonatal resuscitation, and may provide coverage for level 2 neonatal units where intubation skills may be important. We have therefore, a dual responsibility, both to future babies, to ensure that our trainees can care for them adequately, but, most importantly, to the fragile babies currently in our NICU.

My colleagues and friends, the 3 authors of this study, Michael, Christian and Ahmed, (Assaad MA, Lachance C, Moussa A. Learning Neonatal Intubation Using the Videolaryngoscope: A Randomized Trial on Mannequins. Simul Healthc. 2016;11(3):190-3) have been performing a series of studies of the best way to teach intubation skills. Residents now intubate mannequins before they ever touch a baby, and they have a refresher course with a mannequin and the videolaryngoscope at the start of their first NICU rotation. They are supervised performing their first real-life intubations with video laryngoscopy, (Moussa A, et al. Videolaryngoscope for Teaching Neonatal Endotracheal Intubation: A Randomized Controlled Trial. Pediatrics. 2016;137(3):1-8), and most subsequent intubations in the NICU are performed by trainees using the videolaryngoscope. In addition, all intubations in the NICU (except in a major emergency) are premedicated, with atropine, fentanyl and succinylcholine (Barrington K. Premedication for endotracheal intubation in the newborn infant. Paediatr Child Health. 2011;16(3):159-71). Atropine reduces bradycardia, fentanyl reduces pain (and intubation is a very painful procedure) and improves physiologic stability, and succinylcholine shortens the overall duration of intubation (Barrington KJ, et al. Succinylcholine and atropine for premedication of the newborn infant before nasotracheal intubation: a randomized, controlled trial. Crit Care Med. 1989;17(12):1293-6) and reduces the number of attempts required.

Despite these standards, endotracheal intubation remains a procedure with high risk of desaturation, occasional bradycardia, and sometimes requires multiple attempts. Our group decided a few years ago that it wasn’t a good idea to have trainees performing their first intubations with the most fragile babies. We therefore restricted endotracheal intubation of the highest risk babies to only those who had demonstrated competence in the procedure with larger babies. Babies under 29 weeks gestation are only intubated by the “tiny baby” team members, which includes neonatologists and fellows, nurse practitioners, respiratory therapists who are members of the transport team, and residents. In order to be on the team, an intubator had to successfully complete at least 5 intubations on larger infants, 4 of which had to be with either 1 or 2 attempts. These criteria were entirely arbitrary. It was difficult to decide what the criteria should be as there was little previous information to base them on, and if we were too restrictive there would not be enough people around to ensure that there was an intubator on every shift! We have just published our experience with this approach, comparing pre- and post-institution of the tiny baby team. (Gariépy-Assal L, et al. A tiny baby intubation team improves endotracheal intubation success rate but decreases residents’ training opportunities. J Perinatol. 2022). We compared 3 periods, just prior to starting the team, a second period starting 6 months later, and a 3rd period starting 4 years later.

Here is an edited version of table 2 from the publication, showing the overall numbers and results of “ETI” endotracheal intubation, in the 1st 3 columns, then the results for the tiny baby team and the remaining infants. One thing you can see is the reduction in overall intubations, with more babies being managed non-invasively, a change which is most marked <29 weeks.

You can also see that the success rate, on first attempt, among the tiny babies increased when the team started and has remained higher, and the proportion needing more than 2 attempts dropped from 23% to just over 10%. Over these periods, if the first intubator was a junior trainee, they were only usually allowed one attempt, which is why the residents’ success rate is lower than the second attempt success rate in all categories. The number of intubations and the proportion performed by residents have both fallen overall, which has made it even more important to ensure that all forms of training are optimized for future paediatricians to be able to adequately perform the task. One change between T2 and T3 was that residents were prioritized for the intubations of babies >28 weeks. Coupled with enhanced simulation training, their success rate for the larger babies was improved in the most recent period.

This study wasn’t designed to look at the physiologic changes during intubation, but the NEAR for Neos registry has recently published data confirming that serious adverse events are more common with multiple attempts. (Singh N, et al. Impact of multiple intubation attempts on adverse tracheal intubation associated events in neonates: a report from the NEAR4NEOS. J Perinatol. 2022;42(9):1221-7). This is a multicentre registry with data contributed by many hospitals in the USA, Canada and Australia. Those data confirm that more than 1 attempt, and especially more than 2 attempts, are associated with serious adverse events. Severe “TIAE”, tracheal intubation associated events, include cardiac arrest and massage, airway injury, vomiting and aspiration, air leaks, and delayed recognition of oesophageal intubation.

They confirmed that the requirement for multiple attempts was much greater among the most immature babies, and also when the intubator was a paediatric trainee, and was much lower when the baby had received a muscle relaxant. Overall 22% of the intubations required more than 2 attempts.

I was disappointed to see that of the over 6,600 intubations, 3,800 of which were in the NICU, only 2,760 received sedation and a muscle relaxant. Of those that did receive the optimal combination, only 16% needed more than 2 attempts. This is not the first time this group has reported the benefits of sedation with paralysis for reducing “difficult intubation”, and, of all the dozen or so reports I have found of the use of muscle relaxants during intubation, they universally show a reduction in adverse outcomes, depending on what they were measuring, either serious adverse events, desaturation, duration of attempts, or number of attempts. I don’t think there is a good excuse for not giving newborn infants requiring non-emergency intubation in the NICU an adequate pre-medication with a potent rapidly acting analgesic (either fentanyl or remifentanil are the best options) and a muscle relaxant (either succinlycholine or mivacurium, unless you want more prolonged paralysis in which case rocuronium) with atropine to prevent reflex vagally mediated bradycardia. In one recent publication it was reported that it took an median of 16 minutes for the babies to receive the premedications, I find that a little bemusing. We have a “crash cart” in the NICU with the medications easily available, pre-printed charts with the doses already calculated for each step of 100 g of weight, and all the equipment that may be required. Once I say I want to intubate a baby, the crash cart and additional nursing staff arrive, and the baby is often receiving the atropine within 3 minutes, there aren’t many intubations that are so urgent that they don’t receive our cocktail.

The other thing that you can do to improve stability during neonatal endotracheal intubation is to provide a flow of oxygen. My mentor, Neil Finer, was ahead of his time in many ways, he was among the first to study premedication for neonatal intubation, and one thing that was standard in his NICU was the oxyscope, a laryngoscope with an oxygen channel, to which an oxygen source was attached during intubation. I think “Oxyscope” was a trade name which may have been replaced by “Oxiport”, and I am not sure is still being manufactured, but it provided a fresh gas flow near the larynx which decreased desaturation. (Ledbetter JL, et al. Reducing the risks of laryngoscopy in anaesthetised infants. Anaesthesia. 1988;43(2):151-3). Although not using that commercially-produced blade, a much more recent publication (Steiner JW, et al. Use of deep laryngeal oxygen insufflation during laryngoscopy in children: a randomized clinical trial. Br J Anaesth. 2016;117(3):350-7) has confirmed that taping an oxygen cannula to a standard laryngoscope blade also works, and that a video-laryngoscope blade with an integrated oxygen channel exists, which also decreased desaturation in larger children during intubation. These laryngoscopes have only been studied with 100% oxygen flows, usually about 2 litres per minute, and there are of course concerns about brief episodes of hyperoxia that might be associated with their use. However, hypoxia and subsequent re-saturation is probably rather worse for the generation of free radicals than a couple of minutes of hyperoxia, and using a fresh oxygen flow into the pharynx of an apnoeic infant is unlikely to lead to much hyperoxia anyway.

Another way of providing apnoeic oxygenation during intubation is with the use of high-flow nasal cannulae (HFNC), I already posted about the SHINE study from Melbourne using high-flow, here is another trial, a pilot from Dublin (Foran J, et al. Nasal high-flow therapy to Optimise Stability during Intubation: the NOSI pilot trial. Arch Dis Child Fetal Neonatal Ed. 2022:fetalneonatal-2022-324649), as a pilot there were only 43 babies, and 50 intubations included. Infants (who were all premedicated, as in the SHINE trial, with atropine fentanyl and succinylcholine, also known as suxamethonium) had HFNC placed at 6 lpm with 100% oxygen, which is different to the SHINE trial who used a flow of 8 lpm at the same FiO2 as the infant was already getting and only increased to 100% if they desaturated. Another difference is that SHINE was just during the 1st intubation attempt, whereas in this trial they removed the cannulae after the first attempt and put them back if another attempt was required. This new trial had as the primary outcome the duration of desaturation below 75%, which was shorter in the preterm babies (median 29s vs 43s) and not much different in the term babies, as I said, this was a small pilot.

Here is the profile of the median saturations in the <34 week and >33 wk groups.

It seems to show two things, that the babies clearly desaturate faster without oxygen (!) and that someone should have stopped the intubation attempts before they got out to 120 seconds!!! The NRP used to state that an intubation attempt should take a maximum of 20 seconds, Neil Finer showed that was unrealistic Lane B, et al. Duration of intubation attempts during neonatal resuscitation. J Pediatr. 2004;145(1):67-70, that even experienced fellows took an average of 22 seconds, and Colm O’Donnell, when he was in Melbourne (O’Donnell CP, et al. Endotracheal intubation attempts during neonatal resuscitation: success rates, duration, and adverse effects. Pediatrics. 2006;117(1):e16-21), showed that the Australian trainees were slower, averaging 38 seconds for residents, and 32 for fellows. The 7th edition of the NRP handbook continues to state that “the steps of intubation should be completed within approximately 30 seconds”. That is clearly unrealistic, given that the average time for consultant neonatologists to perform a successful intubation in O’Donnell’s study was 25 seconds SD 17s. In experienced hands only about a half of intubations are completed in 30 seconds.

Most babies these days will have a pulse oximeter in place, and hopefully functioning, during an intubation, even in the DR. I think that after 30 seconds there should be an evaluation of the babies status, and if the baby is desaturating and the intubation is not completed by 40 seconds a decision whether to continue or interrupt the intubation, by someone other than the intubator, should be made. This is actually one way that I find the videolaryngoscope useful, I can see if the trainee has a view of the larynx, and is about to insert the tube, compared to the situation with the larynx briefly flying past the screen, and the tube tip heading for the dark hole of the oesophagus.

I don’t know if the combined oxyscope/video laryngoscope would be more or less effective than HFNC to reduce desaturation and adverse events during intubation, but I think someone should find out!

In summary, making endotracheal intubation safer for our most fragile patients requires the following:

  1. Adequate training of all intubators with simulation and video-laryngoscopy
  2. Step-wise introduction of intubators, with video-laryngoscopy, supervision, feedback and repeated training
  3. Ensure that someone with proven competence performs the procedure, by limiting intubation of the highest-risk patients to a restricted list of intubators.
  4. Universal premedication, including muscle relaxation, unless there is a contra-indication, and have procedures in place to administer with minimum delay.
  5. Apnoeic oxygenation, with HFNC, or perhaps an video-oxyscope
  6. Video-laryngoscopy, if you have access to a laryngoscope blade of appropriate size
  7. Ensure supervision of the baby, and their status, by someone who is empowered to stop the procedure if it is going wrong, or is taking too long.
  8. Feedback and further training whenever things go wrong, and even if they don’t.

No more “see one, do one, teach one”!

Even in our NICU, with most of this in place, over 10% of the very immature babies need more than 2 attempts to intubate, we have to find ways to do better than that, to reduce the number and the consequences of failed intubation attempts. During the study that I referred to, of the tiny baby team, we did not have a video-laryngoscope blade that worked for the extremely low birth weight baby, newer technology, and perhaps ever-more realistic high-fidelity mannequins, may help us to further reduce failure rates.

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Time to stop placebo injections in neonatal research projects

Randomized controlled trials are the bedrock of evidence-based medicine. If a treatment has a good theoretical rationale, and preclinical data showing efficacy, the only way to prove efficacy in the human is to randomise patients to the treatment, compared to an alternative, which should usually be some sort of standard therapy, and compare clinically important outcomes. In order to be reliable, randomisation should be masked, which means that, once the patient is enrolled in the trial, and prior to pressing the “randomise” button, the investigators are unaware of which group they will be enrolled.

Masking of the actual intervention is not always possible, for example when comparing different modes of assisted ventilation, and there is less empirical evidence that it makes a difference to results. In particular, in neonatal research I don’t think there is any comparative evidence that shows whether the results of masked trials are systematically different to unmasked trials of the same intervention. The placebo effect, or the improvement in outcomes of control groups, is often misinterpreted as being evidence that the human body has great powers of self-healing, some people even talk about “harnessing the placebo effect”. But, when the outcomes of interest are objective outcomes, the majority of the placebo effect is in fact, “regression to the mean”, or simply that extreme findings usually become less extreme with time, and that most patients recover from most illnesses.

As an example, an uncontrolled trial of a drug (or any intervention) for apnoea will usually show an improvement in apnoeic spells, for a number of reasons. Babies tend to be enrolled in studies when their apnoea is troublesome, and they will therefore, usually, have fewer apnoeas after enrolment. In addition, in this particular example, apnoeas get better with time, so any trial without controls will tend to show improvement over time. But there is really no reason to think that treating babies with a placebo will have any more effect on apnoeic spells than simply not treating them with anything, as long as an objective measure of apnoea is used. Uncontrolled trials of medications for hypotension, as another example, will enrol babies who have blood pressures lower than average; overall such babies will subsequently have higher blood pressures, even if the drug has no effect. But having no treatment, compared to having a placebo infusion will not change that occurrence, both non-treatment and a placebo will have identical effects.

In studies with objective outcomes therefore, one could question the importance of masking the intervention. In my Cochrane review of inhaled nitric oxide for term and late preterm infants, as one example, the outcome “death or ECMO” is very similar between the masked and the unmasked trials. There were a few of both, and I compared the RR and confidence intervals between the masked and the unmasked trials, the results being very similar with the RR for the outcome “death or ECMO” being 0.66 for the masked studies, and 0.7 for the unmasked trials.

This question becomes extremely important when the intervention is a parenterally administered medication. In babies with no IV access in place, or when the medication must be given by another route (IM, subcutaneous…) the tendency in older publications was to give placebo injections, which inevitably create pain. For example, in a trial of erythropoietin prophylaxis published in 1994, control babies received placebo subcutaneous injections 3 times a week for up to 6 weeks. It seems to me to be highly unlikely that subcutaneous saline has any impact on erythropoiesis, not even a “placebo effect”, so the up to 18 painful injections were completely unnecessary. The more recent trial of Juul et al (and some older trials by Ohls and colleagues) used placebo injections for the intravenous phase of the trial, and when an IV was no longer in place, they avoided placebo subcutaneous injections by using sham procedures, in which curtains were drawn around the bed, and a bandage placed where the injection would have been.

This may be inconvenient, compared to just supplying vials with masked information on them and giving the unknown contents by injection, and it may be more costly, but the huge advantage of not inflicting pain on control babies must surely be worth it. A recent article in Acta Paediatrica discusses this issue, and also concludes that placebo injections are neither necessary nor ethically acceptable.

One recent article, which describes a potentially important improvement in RSV prophylaxis, was this one Griffin MP, et al. Single-Dose Nirsevimab for Prevention of RSV in Preterm Infants. N Engl J Med. 2020;383(5):415-25. The authors randomized preterm infants not eligible for RSV prophylaxis in their home countries, to receive either nirsevimab or placebo, 969 received active drug and 484 were randomized to have an intramuscular injection of saline. IM injections hurt. We should only give an IM injection to a newborn infant if there is some benefit to them. The primary outcome of the study was RSV infections requiring medical assistance, which were dramatically reduced from 46 (9.5%) to 25 (2.6%), hospitalisations from RSV were also reduced, from 4% to just under 1%.

Nirsevimab is potentially a significant advance in RSV prophylaxis, a single injection appearing to provide protection for the entire RSV season. Nevertheless, 481 infants received an intramuscular injection of saline. There is no possible benefit to the infant of this painful procedure. The published protocol notes that the blinding was performed at each individual centre, therefore there was an individual who was unblinded at each participating centre. The unblinded individual could easily have been the healthcare worker giving the injection, who could have performed a sham procedure on the control babies.

Even if blinding of the intervention is considered essential (and I hesitantly suggest that it was not, surely RSV infections would be identical in an open-label untreated control group and a masked control group) the blinding could have been maintained by placing an adhesive dressing on the thigh of the control babies, rather than subjecting them to a painful IM injection.

Another recent example is this Rosenfeld WN, et al. Stannsoporfin with phototherapy to treat hyperbilirubinemia in newborn hemolytic disease. J Perinatol. 2022;42(1):110-5, full term babies with a diagnosis of hemolytic jaundice were randomized to stannsoporfin or control, with the primary outcome being changes in serum bilirubin concentration. The 30 control babies received IM saline. I can think of no good reason for subjecting the control babies to the pain of the placebo; surely the lab tech analysing the serum for bilirubin concentrations will not be influenced by knowing which group the infant was in? Even if it was thought that other important secondary outcomes might be influenced by knowing which group the infant was assigned to, the intervention could equally well have been masked by a sham procedure without painful injection. But the only secondary outcomes listed all depend on the serum bilirubin concentrations. There is a plan to perform long term neurodevelopmental outcome evaluation in the infants; I guess it was thought to be just about feasible (and I would challenge that assumption) that knowledge of treatment group could have an impact on neurological or developmental outcomes. Even if this is the reason for maintaining masking of the intervention, such masking does not require intramuscular placebo injections.

Surely it is time to abandon additional unnecessary pain in research participants. We could start with banning placebo skin-breaking injections. Studies in newborn infants, who obviously don’t know themselves which group they are in, could be performed unmasked if the primary outcome variable is objective. If there is some subjectivity in the determination of the major outcomes than masking can be maintained by the use of sham injections.

A major problem is the way painful procedures are evaluated by ethics review committees. One of the worst studies in terms of pain inflicted on the neonatal participants was another RSV prophylaxis trial, the MAKI trial, where infants were subjected to either monthly palivizumab, or monthly IM placebo injections, to a maximum of 5 intramuscular injections of saline. Unusually, this trial was also the source of an article trying to justify its ethical approval. That article concluded

The Institutional review board (IRB) concluded the study has high clinical relevance because the benefit of 50% chance of protection by palivizumab outweighs the risk of side adverse events due to intramuscular administration of placebo.

It is actually impossible to argue with that conclusion, the study was indeed of high clinical relevance, and the “risk of side adverse events” from up to 5 IM saline injections is negligible. But only if you think that pain is not an adverse event. If you include pain as an adverse event the “risk” of adverse events was 100%.

The authors try to justify the use of the IM placebo, without ever mentioning pain, as follows “A placebo controlled control group was necessary because the primary objective will depend on parent-reported daily scores of wheezing along with information from parent-reported questionnaires”. Firstly, I question that rationale, is there any reason to believe that parents would provide biased scores of daily wheezing based on whether the child actually had a placebo injection compared to being enrolled in an untreated control group? Even if there were some evidence of such an effect, the placebo injections could have been replaced by sham injections.

The book from the Institute of Medicine “Ethical conduct of clinical research involving children” has a chapter “Defining, Interpreting, and Applying Concepts of Risk and Benefit in Clinical Research Involving Children” describing how to determine risks, and tries to define “minor increase over minimal risk”, in research with children as research participants. It includes a table which illustrates the hidden way in which pain is taken into account. The table lists “routine history taking” and a “complete neurological examination” as procedures with minimal risks, which we surely cannot argue with. But in the same category is included “venepuncture/fingerstick/heelstick”.

From a purely “risk” point of view, if pain is not considered a risk, then I guess that makes sense, but surely examining a baby and sticking a needle into them should be considered differently? The table also includes, as a minor increase over minimal risk, a lumbar puncture. Lumbar puncture is an extremely low risk procedure in the otherwise stable newborn, why is it given a higher risk status? Is it because we know it hurts, a lot? The only place pain is mentioned in that table is for two other “minor increase over minimal risk” procedures: skin punch biopsy and bone marrow biopsy, where “topical pain relief” is added as part of the name of the procedure. One might wonder why pain relief is not mentioned for heelstick or for lumbar puncture. In another part of the book it is stated “children should always be given the option to receive a topical anesthetic to reduce needle-stick pain”, but I can find no mention of routine analgesia prior to painful procedures in the newborn. The only mention of intramuscular injections is that they are more risky in children with hemophilia

A new publication from Ruth Grunau and the group in Vancouver who have performed amazing research into the adverse impacts of pain, and how to minimize it, has just appeared. McLean MA, et al. Association of Neonatal Pain-Related Stress and Parent Interaction With Internalizing Behaviors Across 1.5, 3.0, 4.5, and 8.0 Years in Children Born Very Preterm. JAMA Netw Open. 2022;5(10):e2238088. This study examined child behavioural patterns at the ages mentioned in the title, and determined the association with painful procedures in the neonatal unit. There was a clear correlation, after correcting for multiple other factors including gestational age, between having more painful experiences and having more internalizing behaviours, across all of those ages. They also showed that a more supportive, positive, and less stressed family environment could mitigate those impacts.

This study, among many others, emphasizes that we need to do all we can to reduce pain in the neonatal period, and any additional avoidable pain should be prohibited. This must include the use of placebo injections in research, which can always be avoided.

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Protein pump inhibitors cause coeliac disease and asthma, and they are unnecessary.

OK, that title is perhaps slightly too definite, the publications that I wanted to discuss are observational studies, which can only prove associations, but it would be hard to perform the prospective controlled trials that would be necessary to prove (or disprove) causality. A trial for PPIs and coeliac disease would need an RCT of about 2400 per group, which will clearly never be done; for asthma the sample sizes I calculated were even larger, around 5000 per group.

So what this first study shows (Boechler M, et al. Acid Suppression and Antibiotics Administered During Infancy Are Associated with Celiac Disease. The Journal of Pediatrics. 2022) is that from a huge database, the military healthcare system database, the Hazard Ratio of having coeliac disease was 3.37, and after adjustment was 2.23, for infants who had a prescription for a PPI prior to 6 months of age; a risk that was also shown for histamine receptor blockers (adjusted HR 1.94) and antibiotics (1.14). Having all 3 was the worst risk (adjusted HR 5.43). They also showed that the longer the infant received a prescription for acid suppression, the higher the risk. In this database about 2% of all the babies got a prescription for a PPI during the 1st 6 months of life.

The other article is also from an administrative database and shows, using propensity score matching, an increase in the frequency of asthma diagnoses and of prescriptions for asthma medications among children who had a PPI prescription. (Wang YH, et al. Association Between Proton Pump Inhibitor Use and Risk of Asthma in Children. JAMA Pediatr. 2021;175(4):394-403), with the hazard ratio being about 1.5 for the various drugs, being highest in the first 6 moths after prescription and then decreasing.

In a recent study from Scandinavia rates of PPI prescriptions were given to up to 8% of all infants under 1 year of age in Denmark in 2017. There must be a global epidemic of hyperacidity. (Lyamouri M, et al. Proton pump inhibitors for infants in three Scandinavian countries increased from 2007 to 2020 despite international recommendations. Acta Paediatr. 2022;111(11):2222-8).

Why on earth are so many babies and infants receiving a PPI? We seem to have become intolerant of babies spitting up, or being irritable, or having colic, all of which can be rather disturbing things for new parents, but which do not usually need, or respond to, any medication!

In the NICU this is usually done because someone thinks a baby has pathological reflux, and gets a label of Gastro-Oesophageal Reflux Disease, which then leads to treatment with a protein pump inhibitor and/or other medications. A recent review article (Sawyer C, et al. Neonatal gastroesophageal reflux. Early Hum Dev. 2022;171:105600) is generally well done, I thought, but it is not intended just for the NICU or for preterm and former preterm infants.

Overall, available evidence does not support the routine use of PPIs or H2RAs to treat classically associated GERD symptoms in post-term infants, although some sub-populations may benefit from treatment. Outside of proven acid-reflux, treatment with a PPI should be time limited and all caregivers should be aware of possible side-effects. Acid-suppression therapy should not be used in preterm infants given the risk of severe side effect.

To put it simply, I think of this as follows:

  1. The only reliable clinical sign of reflux in the newborn is regurgitation, but having regurgitation does not mean that a baby has significant reflux, most babies regurgitate. No other clinical sign discriminates between babies with more or less reflux, either the total number of episodes, or the number of acid reflux episodes. When the nurse tells you they think the baby has significant reflux, either based on using a clinical score, or based on their personal evaluation, there is no correlation with objective measures of reflux.
  2. You cannot diagnose reflux with a laryngoscope.
  3. Diagnosis of abnormally frequent reflux requires objective evaluation, using multi-luminal impedance with pH monitoring.
  4. Most reflux in newborn infants is not acidic, as shown by such studies.
  5. Diagnosis of GOR DISEASE requires evidence, in addition, that the reflux is actually causing clinical problems; this is rarely due to acid in the newborn.
  6. Apnoea spells are not triggered by reflux, for the great majority of cases, but sometimes reflux may be triggered by apnoeas, especially obstructive apnoeas.
  7. Bronchopulmonary dysplasia is not clearly worsened or caused by reflux.
  8. Blocking gastric acid production does not decrease reflux, it just changes it from being majority non-acid to being a very large majority non-acid. It is possible that PPI use actually increases reflux, in several animal models they cause relaxation of the lower oesophageal sphincter.
  9. Gastric acid is there for a reason. Blocking it changes the intestinal microbiome, and increases the risk of respiratory infections, systemic sepsis and NEC. PPIs reduce calcium, magnesium, and iron absorption, and seem to cause coeliac disease, asthma, and increase the risk of fractures.

In summary, only prescribe acid blocking medications if there is some clear evidence that the baby will be improved with less gastric acid production. A rare occurrence.

The review article that I mentioned and linked to also discusses the evidence against using prokinetics, which I totally agree with:

None of the[prokinetic agents] have been shown to reduce GERD symptoms in preterm infants. Similar to other medical therapies for GERD, most are not well studied in neonates and are associated with significant and concerning side effects. Side effects of metoclopramide and domperidone are primarily neurologic including irritability, drowsiness, apnea, and possible irreversible tardive dyskinesia. Erythromycin is associated with infantile pyloric stenosis and cardiac arrythmias. Given the lack of evidence for efficacy and the potential for significant side effects, the use of prokinetic agents to treat neonatal GERD is not recommended.

The review does discuss the idea that bovine protein intolerance is a factor in GOR; in my evaluation there is some soft evidence for this in older infants, and as a result a therapeutic trial of elimination of cow’s milk protein is sometimes included in treatment guidelines, but, as far as I know, there is no such evidence in the newborn, especially in the preterm newborn.

An article I discussed previously noted that lansoprazole was a drug with a major decrease in use between 2010 and 2018, but over the whole period covered by that study about 5% of all the ELBW babies received at least one course of treatment. There were also about 10% of the ELBW infants received ranitidine, which was taken off the market towards the end of that study, let’s hope its use wasn’t replaced by more PPIs!

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