Three trials with null results, how should we respond?

These 3 articles have just been published, all show no difference in long term outcomes between the randomized groups. What does that mean for the impact on therapeutic decision-making?

Natalucci G, et al. Neurodevelopmental Outcomes at Age 5 Years After Prophylactic Early High-Dose Recombinant Human Erythropoietin for Neuroprotection in Very Preterm Infants. JAMA. 2020;324(22):2324-7.

Rozé J-C, 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. The Journal of Pediatrics. 2020.

Tauzin M, et al. Neurodevelopmental Outcomes after Premedication with Atropine/Propofol versus Atropine/Atracurium/Sufentanil for Neonatal Intubation: 2 Year Follow Up of a Randomized Clinical Trial. The Journal of Pediatrics. 2020.

The first of them, Natalucci et al is a longer-term follow up of a trial that already reported their 2-year primary outcomes. It was an RCT of infants of 26 weeks gestation or more and less than 32 weeks, who received either 3000 iu of erythropoietin at < 3 hours of age and then 2 other doses at 12 to 18 hours and 36 to 42 hours. There was no impact on the Bayley MDI at 2 years, and now they have shown in the 77% of children left in the trial (total n= 345) that there was no difference between groups on a test of cognition, or in cerebral palsy, disabling CP, or hearing or visual problems. This study complements the PENUT trial which included babies down to 24 weeks gestation (up to < 28 weeks) and gave a dose of 1000 iu/kg every 48 hours for 6 doses and then 400 iu/kg 3 times a week until 33 weeks. That study also showed no benefit on long term outcomes.

The next study, Roze et al TRIOCAPI , randomized babies born between 24 and <28 weeks who did not have an IVH on initial head ultrasound. They had a screening cardiac ultrasound at 12 to 24 hours of age and, if the ductus was “large” (calculated as > 2.26 – (0.078 x postnatal age in hours) mm), they received either ibuprofen or placebo. The primary outcome was survival without cerebral palsy at 2 years of age; among the 228 babies randomized in the 2 groups, this outcome was not different by treatment group, at just over 71%. This was double what they were expecting in the control group, as outcomes have improved dramatically in France for these very immature babies, so they were somewhat underpowered. They did show a decrease in pulmonary haemorrhages in the first 3 days (those requiring an increase in FiO2 > 20% or an increase in mean airway pressure > 2cmH2O) from 8% to just under 2% with ibuprofen; at 3 days of age, they were much more likely to have closed the PDA (66% vs 17%). There were a large proportion of the babies, 62% of controls and 17% of the ibuprofen group, who received open-label ibuprofen after the first 3 days.

The third of these studies Tauzin et al, PRETTINEO is the first, I think, controlled trial of premedication for neonatal intubation that has published long term follow up and has a sample size large enough to have reasonable power. The drug regimes compared for non-emergency intubations in the NICU are mentioned in the title. Atropine at 15 microg1kg was given to everyone, followed by either propofol (2.5 mg/kg for babies >1kg, and 1 mg/kg <1kg) or atracurium 0.3 mg/kg and sufentanil (0.2 microg/kg >1kg and 0.1 microg/kg <1kg). The initial publication of the acute results showed about the same incidence of the primary outcome, prolonged desaturation, in the two groups. The propofol group required many more extra doses of medication to achieve “adequate anaesthesia”; they were also less well sedated and required a longer time to be intubated. However, they started to breathe again more quickly, the atracurium sufentanil group taking a median of 33 minutes compared to 14 with propofol. The follow-up data are mostly from the Ages and Stages Questionnaire, and showed no difference between the groups. However, of the 166 babies included in the follow-up only 118 had data from the ASQ included, the others haveing their data imputed, many more in the propofol group (40%) than the atracurium/sufentanil group (19%). With this limitation in mind, all of the ASQ scores were basically identical between groups.

What should we do when we have results like these 3 trials, showing no difference in the long term outcomes or mortality between two treatment approaches? I don’t thin kit necessarily means you should throw the treatment out of the door, if there are really no differences in long term outcomes between 2 treatments then there are a few questions we should ask:

How reliable are the results?

What differences between groups are compatible with the results?

How applicable is this to my practice?

What are the short term impacts of the treatment?

What are parents likely to prefer?

How reliable are the results? Is the trial likely to be unbiased? Or are there potential sources of bias in the trial design or reporting of the results? This is a huge subject, but some things can improve your confidence that there really is no difference between the groups, such as a trial with masked allocation (and masked intervention, if possible) funded by an independent source that was registered before the trial started and reports the same primary (and a limited number of secondary) outcomes as are in the registration documents.

What differences between groups are compatible with the results? A trial may be called a null trial because the results did not reach a threshold of “p<0.05” but the confidence limits of the trial should be examined, a small to moderate size trial may still be compatible with a large, clinically important, difference in the treatments.

How applicable are these results to my practice? If the comparison group is not managed as they are managed in my practice, if the eligibility criteria eliminate many babies that I look after, or if control group outcomes are dramatically different to my patients, then the applicability to my practice may be very limited.

What are the short term impacts? We have become so focused on long term outcomes, very often survival without disability, that the impacts of short term outcomes may get lost. So a treatment that doesn’t impact survival or long term outcomes might well have advantages that are worthwhile. Such as reducing severe IVH despite no change in developmental progress or reducing the need for retinopathy therapy despite no final impact on blindness. If those short term benefits are achieved without short term adverse effects, that might be an indication for using a treatment.

What are parents likely to prefer? Outcomes which are important to parents should be a major part of our considerations, even if long term benefits are few or unproven. To return to the example above, would a parent prefer that their baby does not have a severe IVH, even if that doesn’t necessarily improve their long term outcome? If so, then prophylactic indomethacin should be considered, especially as the large, high-quality trials (Ment Indo IVH Prevention Trial and TIPP) showed no substantial difference in adverse events.

To apply these question to our three new null publications.

How reliable are the results?

For the trial of Natalucci, I would say that I can’t find any important potential bias in this trial design, a multicentre double-masked trial with the primary outcome as initially specified.

The TRIOCAPI trial is also well done, again a multicentre masked RCT with a pre-specified primary outcome.

For the PRETTINEO trial, the low rate of follow up and the reliance on the imputed outcomes makes me rather hesitant, especially with the very low rate of follow up in the propofol group.

What differences between groups are compatible with the results? This is, of course, a consideration of power and of confidence intervals.

For the Natalucci trial the primary cognitive score was almost identical in the 2 groups, and the results were compatible with a true difference between groups of a 3 point decrease in scores to a 2 point increase (approx), and therefore very little chance of a significant adverse impact of Erythropoietin.

The results of TRIOCAPI showed, again, almost identical rates of the primary outcome, but, as a smaller trial, the results are compatible with a 17% relative reduction or a 16% increase in the outcome of survival without cerebral palsy. The absolute risk difference in CP between groups was about 5% and the 95% limits of the absolute difference are between about a 9% lower frequency with indomethacin and a 6% higher frequency. The differences in disabling CP (GMFCS >2) were tiny (3 patients in the placebo and 2 in the indomethacin groups).

For PRETTINEO, the confidence intervals for the difference in “survival without neurodevelopmental delay” are very different if you include the imputed values or not, and therefore I would say that you can’t really rely on the confidence intervals.

How applicable is this to my practice?

The Natalucci trial is relatively applicable, but it excluded the highest risk babies of under 26 weeks. Survival and other outcomes among enrolled babies are not very dissimilar to mine.

TRIOCAPI again excluded the most immature babies <24 weeks, but included 24 week infants (French NICUs have a higher rate of comfort care in the delivery room at 24 weeks than we do, so the proportion of enrolled 24 week infants is somewhat lower), the main thing that makes me concerned about applicability is the very high rate of early PDA treatment among placebo group babies, which is much more, I guess, than a similar group of babies in my NICU. But, whether that would have an impact on the rate of CP or other developmental delays, I doubt.

PRETTINEO compared propofol premedication to a regime that is somewhat similar to what I use, which is atropine/succinylcholine/fentanyl. Succinylcholine has a much shorter duration of action than atracurium, so the babies start breathing gain much faster (sometimes it is too fast and we have to give a second dose), so I would say somewhat relevant.

What are the short term impacts?

Natalucci’s trial showed no adverse effects; the PENUT trial also showed no evidence of any adverse effect, the previous concern about a possible increase in retinopathy with some regimes is not born out by this new data. I can’t find a report of transfusion requirements in the Nataluci trial publications, but PENUT showed that the proportion of babies who never needed a transfusion increased from 13% to 28% with their erythropoietin regime and the median number of transfusions decreased from 4 to 2.

TRIOCAPI also showed little in the way of adverse impacts of early targeted ibuprofen treatment. There were a lot fewer pulmonary haemorrhages 2% vs 8% in the first 3 days of life, but somewhat more GI perforations, 8.8% vs 3.5%. The Cochrane review of prophylactic ibuprofen (not exactly the same I know, but ibuprofen given in very early life, also shows more GI perforations compared to no treatment, but is only based on 2 small trials with a total of 167randomized babies and 14 events, the confidence intervals are very wide and include no difference. GI bleeding is also more common in the Cochrane review, although that is supposed to be “statistically significant” it is largely based on 2 very small Thai trials that had enormous rates of GI bleeding.

PRETTINEO in their initial publication showed a high frequency of hypotension after propofol, which received treatment on 2 occasions, No other major difference in short term impacts was shown, the proportion desaturating during intubation was similar. There were many more intubations on the first attempt in the atracurium/sufentanil group.

What does mean for the clinical implications of these null studies?

Early Erythropoietin, doesn’t seem to offer any neuroprotection when you put it into the context of other trials. It does seem to reduce the proportion of babies who receive a transfusion and the total volume of blood transfused, without any adverse effects. I think that is an impact that might be valuable to some parents, and that therefore it would be reasonable to offer it as an option to parents with babies at risk of being transfused. If we couple it with delayed cord clamping and greater efforts to reduce blood losses, by taking initial blood work from the blood left in the placenta for example, we could probably do even better to reduce transfusions, which I know are extremely safe these days, but still not as safe as not having a transfusion!

Early targeted ibuprofen was something that we introduced into our unit as a pilot after the Kluckow trial, partly because we had been through a phase of having quite a lot of pulmonary haemorrhages. This trial means, I think that we should rethink that approach. It confirms that there are fewer pulmonary haemorrhages leading to respiratory deterioration with this approach, but there may be an increase in GI perforation. Is there a better way to target those at risk of pulmonary haemorrhage to change the risk:benefit ratio?

The PRETTINEO trial confirms to me that propofol is not a good idea, even though there was no adverse long term impact (with the limitations already mentioned) intubation took longer and more attempts and there was more hypotension. Maintaining the use of a regime with a short acting muscle relaxant seems to me optimal, as long as a potent analgesic is also used.

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What role for High Flow Nasal Cannulae?

There are a few new publications which might help us to answer the question posed in the title of this post.

When heated, humidified, high flow nasal cannulae were first being spoken about I remembered an old study using standard cannulae but with flow rates up to 2 litres per minute. In 13 infants with an average body weight of about 1500g, the authors measured intra-oesophageal pressures, using either 0.2 or 0.3 cm diameter prongs. (Locke RG, et al. Inadvertent administration of positive end-distending pressure during nasal cannula flow. Pediatrics. 1993;91(1):135-8).

As you can see from this figure you can get very high oesophageal pressures with 2 litres per minute of flow if you have tight-fitting nasal prongs. The average was 9.8 cmH2O, and the error bars are SEM, which means the SD was 3.6, so the upper limit of pressures generated could easily be 9.8+2SD= 17cmH2O! The lower limit would be about 2 cmH2O with a 2 litre flow, and as you can see a pressure of 0 when the smaller prongs were used. You can see from the title of the article that the PEEP delivered, at that time, was considered “inadvertent”!

Since then the use of heated humidified gases and systems specifically designed for high flow have been introduced. Unfortunately, the initial introduction of HFNC was without good trials evaluating risks and benefits. I, for one, was reticent to use them for quite a while. The only advantage I could see was that they seemed to be more comfortable for larger, more mature, kids, although the trials evaluating pain scales are contradictory. There does, however, seem to be less nasal trauma when they are used for younger preterm infants (<28 wk PMA), and parents generally prefer them, perhaps because it is easier to interact and play with their babies with HFNC than CPAP.

We started using them for older babies with mild to moderate BPD who still needed CPAP when they were getting to be over 34 weeks. One of the features of our unit is that babies on HFNC can be transferred to the intermediate care section of the unit, whereas if on CPAP they have to stay in an intensive cot. When we were short of beds we sometimes switched a baby from CPAP to HFNC to make room for a new admission. So the use of HFNC gradually crept up, which made us review our practices and ask a couple of questions based on more recent data than the article from 1993.

In terms of the impact of HFNC on the respiratory system, they do generate PEEP under certain circumstances, but it is variable from baby to baby, and from minute to minute. It depends on how tight they fit in the nostrils of the baby. and the flow rate and whether the mouth is open or not.

And here I can’t help myself, but I must insist: NARE IS NOT A WORD! Sometimes the nostrils are referred to as the “nares” (pronounced naireez) which is a Latin word occasionally used in English to refer to the two nostrils. One nostril in Latin is “naris”, so, if you wanted to, you could refer to a naris, but I would insist that the whole sentence is in Latin! Quid magnum naris! (what a big nostril!) We have a perfectly functional English word for the nostril, let’s use it!

As another aside, one thing I find cute in a French-speaking NICU is that nasal flaring is referred to as “flapping the wings of the nose” (battement des ailes du nez).

To return to medicine…

A recent article on the physiological impacts of HFNC has, for the first time in preterm babies, I believe, tried to actually measure one of the supposed mechanisms of action, that is, dead space washout. (Liew Z, et al. Physiological effects of high-flow nasal cannula therapy in preterm infants. Arch Dis Child Fetal Neonatal Ed. 2020;105(1):87-93) They did this in 44 low birth weight babies (500 to 1900g), testing different flow rates and comparing to nCPAP at 6 cmH2O.
Normally, when you inspire, you at first pull into your gas exchange sacs (terminal sacs or alveoli depending on GA) the gas that you just expired, from the tracheobronchial tree then the upper airways, before getting fresh atmospheric gas (there is, of course, a gradual mixing during inspiration). The idea of dead space washout with HFNC is that a high flow of gas into the pharynx, much higher than the infant’s minute ventilation, will wash out the pharynx with a fresh gas flow (21% oxygen or more and 0% CO2) and thus decrease the effective dead space. To measure this you could look at the moment by moment gas composition of the gas in the pharynx during the respiratory cycle, and determine the inspiratory concentrations of CO2 and O2. This group did almost exactly that, but taking into account the mixing of gases and the turbulence caused by the HFNC in the pharynx, they decided to measure the peak, end-tidal CO2. Which dropped progressively as gas flow increased.

As you can see the pEECO2, or end-tidal CO2, expressed as a percentage dropped from 2.3% at a flow of 2 to 0.9% at 8 litres per minute, confirming that there was indeed a wash-out of the dead space. In addition, minute ventilation fell, although not as consistently, as flows increased, which is what you would expect; if you wash out CO2, then PCO2 will fall, leading to a decrease in respiratory drive and then in minute ventilation until PCO2 comes back up to where it was, this is confirmed by the stability of the transcutaneous CO2 (about 46 mmHg in old units). This might mean that a baby who has a high work of breathing associated with BPD will have a reduction in their respiratory effort as flows increase, which is in fact what we sometimes see in the NICU.

As another aside, babies (and indeed adults) with chronically raised CO2 have intact CO2 responses. This has clearly been shown in adults with COPD who do NOT become “dependent on hypoxic drive” as stated in some texts, which has led in the past to restricted oxygen administration. Newborns also remain responsive to CO2, even when chronically hypercapnic. I studied this back when I was a fellow, in the last century, giving 2% CO2 to a few babies with BPD and chronic hypercapnia, they increased their minute ventilation, just as you would expect.

The pharyngeal pressures as shown in the table don’t clearly show the variability in the pressures obtained, which are better demonstrated in their graph:

A flow of 8 lpm/kg produced pressures between 2 and 14 cmH2O, at 2 lpm/kg pressures were between close to 0 and 7 cmH2O.

Are there any advantages to HFNC compared to CPAP? What are the disadvantages?

As mentioned above parents seem to prefer them, they also state that their child prefers them. In this randomized cross-over trial (Klingenberg C, et al. Patient comfort during treatment with heated humidified high flow nasal cannulae versus nasal continuous positive airway pressure: a randomised cross-over trial. Arch Dis Child Fetal Neonatal Ed. 2014;99(2):F134-7) parents rated their child’s “satisfaction” as an average of 8.6/10 compared to 6.9 for nasal CPAP, even though the PIPP scores were just about identical between the two groups.

That, I think, is an important difference, but must be offset by the fact that initial use of HFNC for early respiratory distress is more likely to fail than CPAP (Roberts CT, et al. Nasal High-Flow Therapy for Primary Respiratory Support in Preterm Infants. N Engl J Med. 2016;375(12):1142-51), and infants are more likely to fail extubation if they receive HFNC rather than CPAP (Uchiyama A, et al. Randomized Controlled Trial of High-Flow Nasal Cannula in Preterm Infants After Extubation. Pediatrics. 2020:e20201101. Manley BJ, et al. High-flow nasal cannulae in very preterm infants after extubation. N Engl J Med. 2013;369(15):1425-33).

This may not matter too much if you have CPAP available as a backup, but in some circumstances, failure of the HFNC might be associated with substantial pulmonary de-recruitment, and difficulty stabilising with CPAP.

In addition, we may be drowning the babies! (Reiner E, et al. Using heated humidified high-flow nasal cannulas for premature infants may result in an underestimated amount of water reaching the airways. Acta Paediatr. 2020), this was a study in an in vitro model so it is of limited applicability in terms of the actual numbers compared to the complex dynamics of a newborn’s upper airway, but a Heated humidified HFNC system deposited up to 44 mL of water over a 24 hour period in a feeding bottle being used as the model for the upper airway. A CPAP system with a heater wire in the inspiratory limb may well lead to less water deposition, but I don’t know that for sure and it would be interesting to know.

All of which leads to a few studies suggesting from several centres that when they started using more HFNC they had worsening pulmonary outcomes. Heath Jeffery RC, et al. Increased use of heated humidified high flow nasal cannula is associated with longer oxygen requirements. J Paediatr Child Health. 2017;53(12):1215-9. Hoffman SB, et al. Impact of High-Flow Nasal Cannula Use on Neonatal Respiratory Support Patterns and Length of Stay. Respir Care. 2016;61(10):1299-304. Multicentre databases have reported the same thing. Taha DK, et al. High Flow Nasal Cannula Use Is Associated with Increased Morbidity and Length of Hospitalization in Extremely Low Birth Weight Infants. J Pediatr. 2016;173:50-5 e1.

I actually wonder whether that may be because of the increased ease of use and apparent comfort of the babies on HFNC, which makes us less pressed to wean their support so we end up weaning more slowly and the babies are exposed to more positive pressure, potentially more oxygen, and maybe even more water droplets in the airway(?). The Cochrane review did not find any evidence of worse pulmonary outcomes with HFNC, but there really aren’t many trials comparing the long-term use over several weeks during the recovery phase of preterm lung disease compared to CPAP, so the Cochrane review doesn’t really cover that kind of usage. This small trial found no advantage of prolonged HFNC compared to CPAP for babies recovering from their RDS in terms of learning to feed Glackin SJ, et al. High flow nasal cannula versus NCPAP, duration to full oral feeds in preterm infants: a randomised controlled trial. Arch Dis Child Fetal Neonatal Ed. 2017;102(4):F329-F32.

So what are the indications for HFNC today?

  1. Initial respiratory support of the preterm infant? I think that very preterm babies (<32 weeks) are at higher risk of failing compared to CPAP and, as such babies are usually in a tertiary NICU with CPAP available, that should be their initial support. 32 to 35 week babies in a level 2 nursery could be managed initially with HFNC if CPAP is not easily available, but early contact with a referral centre should be instituted, in case of failure.
  2. Post-extubation support? This should be either CPAP for larger preterm babies or nIMV for smaller preterm babies. I don’t think HFNC is a good option for any baby immediately after extubation.
  3. Prolonged respiratory support? This is the one place where I think there may be a role for HFNC, parents prefer it and they see that their infants are more comfortable. I think that for the baby approaching 36 weeks, who is starting to be more interactive, if CPAP can’t be weaned off, then HFNC could be considered. The caveat is that we should have a protocol for weaning, with frequent evaluation of the baby and attempts at weaning, the dead space washout might reduce respiratory efforts in babies with low compliance or high resistance lungs, and they may therefore have less retractions and their nose wings might flap less (!), but beware being complacent about the baby who is stuck on HFNC, you may end up with more of them having respiratory support for longer.
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Probiotics and NEC, the latest answer?

The updated Cochrane review of probiotics for prevention of NEC, sepsis and mortality has been published.

Meta-analysis showed that probiotics may reduce the risk of NEC: RR 0.54, 95% CI 0.45 to 0.65 (54 trials, 10,604 infants; I2 = 17%); RD -0.03, 95% CI -0.04 to -0.02; number needed to treat for an additional beneficial outcome (NNTB) 33, 95% CI 25 to 50. Evidence was assessed as low certainty because of the limitations in trials design, and the presence of funnel plot asymmetry consistent with publication bias. Sensitivity meta-analysis of trials at low risk of bias showed a reduced risk of NEC: RR 0.70, 95% CI 0.55 to 0.89 (16 trials, 4597 infants; I2 = 25%); RD -0.02, 95% CI -0.03 to -0.01; NNTB 50, 95% CI 33 to 100. Meta-analyses showed that probiotics probably reduce mortality (RR 0.76, 95% CI 0.65 to 0.89; (51 trials, 10,170 infants; I2 = 0%); RD -0.02, 95% CI -0.02 to -0.01; NNTB 50, 95% CI 50 to 100), and late-onset invasive infection (RR 0.89, 95% CI 0.82 to 0.97; (47 trials, 9762 infants; I2 = 19%); RD -0.02, 95% CI -0.03 to -0.01; NNTB 50, 95% CI 33 to 100). Evidence was assessed as moderate certainty for both these outcomes because of the limitations in trials design. Sensitivity meta-analyses of 16 trials (4597 infants) at low risk of bias did not show an effect on mortality or infection.

I find this extremely interesting, but also somewhat concerning. The recent network meta-analysis that I posted about ( found the following:

Compared with placebo, a combination of 1 or more Lactobacillus species (spp) and 1 or more Bifidobacterium spp was the only intervention with moderate- or high-quality evidence of reduced all-cause mortality (odds ratio [OR], 0.56; 95% confidence interval [CI], 0.39-0.80). Among interventions with moderate- or high-quality evidence for efficacy compared with placebo, combinations of 1 or more Lactobacillus spp and 1 or more Bifidobacterium spp, Bifidobacterium animalis subspecies lactis, Lactobacillus reuteri, or Lactobacillus rhamnosus significantly reduced severe NEC (OR, 0.35 [95% CI, 0.20-0.59]; OR, 0.31 [95% CI, 0.13-0.74]; OR, 0.55 [95% CI, 0.34-0.91]; and OR, 0.44 [95% CI, 0.21-0.90], respectively).

The differences between the reviews, and between the interpretations of the evidence are fascinating. The Cochrane review did not include 12 trials which are included in the Network Meta-Analysis (NMA), with a total of 3580 subjects; most of those trials are listed in the excluded trials table as having been excluded because “most participants were not very preterm or VLBW”. Three of the trials in the NMA are not listed as excluded in the Cochrane review, one of them has 174 participants, and a mean GA of 29.5 weeks, and is probably eligible for inclusion in the Cochrane review, but has only been published as an abstract in conference proceedings, so may not have been found by their literature search. The other 2 trials, one large (n=524) and one small (n=62) appeared to be mostly larger preterm infants, so probably would have been excluded anyway.

The Cochrane review included 9 trials not in the NMA, it is not clear why they weren’t included, but those trials enrolled a total of 765 infants. Most are limited to VLBW infants, and many are not difficult to find (in JPGEN and PLOS1, for example).

The interpretation of the quality of the data are divergent, the NMA referring to moderate to high-quality data, while the Cochrane review refers to evidence of low certainty. In part, this is based on an analysis of the funnel plot, which looks a bit asymmetric and the statistical test for missing data was just below p=0.05. It is, of course, impossible to be sure if there is missing data or not, if you knew about it it wouldn’t be missing! The statistical test used has been evaluated by using simulations, which is I guess the only way to test such tests, but makes me a little uncertain how reliable it is.

The divergence of opinion also points out that there is some degree of subjectivity in deciding on the quality of the evidence.

Where I start to have concerns about the Cochrane review is that, when restricting the analysis to high-quality trials, there remains a major reduction in NEC, those trials number 16 with 4,597 infants enrolled. Also when analyzing mortality in only trials with a low risk of bias, they state that there was no difference, in fact, the mortality with probiotics was 5.9% and with placebo was 7%, which are 2 different numbers unless I am mistaken. You could say they are not statistically significantly different, or that there is a small difference which may be due to chance, the weighted RR from the meta-analysis is 0.86 (95% CI 0.69, 1.07).

I guess the main issue is : how confident do you have to be to introduce an intervention which has next to no risk, is very cheap, does not prevent you from introducing other interventions to reduce NEC risk, and which decreases NEC in a meta-analysis of high-quality trials? Even though the reductions in mortality and in invasive infection are not below a p-value of 0.05, the differences are in the right direction in the high quality trials.

When you add to the RCTs the real-world experience of introducing probiotics in multiple studies, from large databases in Germany, the USA, and Canada, and individual hospital experiences like ours, and Toronto and Norwich, I think it is hard to avoid the fact that probiotics are almost certainly effective in reducing NEC, and that large enough high-quality studies would likely show a decrease in mortality, which is already evident when the lower quality studies are included in the analysis. It seems likely to me that Bifidobacterium longum Subsp Infantis in a mixture with a Lactobacillus or another Bifido-may be the best, but that is less certain.

Do we really want to spend the next 2 million dollar grant for an RCT comparing probiotics to placebo? Surely cluster randomized trials comparing different preparations could be much more cost-efficient and could quickly give us much larger sample sizes, and would permit an answer to the question of which preparations are most effective.

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Quality of life cannot be predicted from a brain scan

…either ultrasound or MRI, or by EEG, or neurological examination, or even during follow-up by screening for disabilities.

That title is from a recently published editorial (Fayed N, et al. Quality of life cannot be predicted from a brain scan. Dev Med Child Neurol. 2020;62(4):412) which is available full-text open access, and which includes this pearl:

Even though levels of cognitive and motor problems can often be  based on magnetic resonance imaging results, abnormal electroencephalogram findings, and a neonate’s hospital course, the happiness and acceptance a child will achieve in their families and communities cannot.

I actually would argue that none of those 3 methods can be used to identify cognitive or motor problems with any reliable degree of certainty. The PPV of disabling cerebral palsy, for example, based on white matter injury shown on the MRI, is LESS THAN 50%.

Even if pre-discharge imagery were perfectly predictive of impairments, which is far from being the case, being impaired does not imply a poor quality of life. There is very little correlation between a life of quality and whether or not an individual is impaired. As these authors note:

disability severity has little relationship to life quality. Instead, emotional well-being, peer interactions, parental adaptation, and community support are much more powerful predictors of whether a child is likely to grow up to have a good life. When conveying a prognosis of severe disability and its consequences to child and family, the solution is a simple one. Refrain from confounding the concept of a good QoL with the prognosis of cognitive or physical disability.

We perform many investigations to try and predict the outcomes of our patients, sometimes with the idea that we should change the intensity of our care based on the results.

When you state the issue as clearly as these authors did in the title of their article it becomes almost self-evident; of course you cannot predict quality of life by looking at the brain. And if you cannot, then why are we doing so many scans?

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What happened to the HeROs?

I had to find a way of changing HeRO to Heroes as an excuse for posting a link to this video

But also the results of a long term follow up of the HeRO trial have been published. The original trial (Moorman JR, et al. Mortality reduction by heart rate characteristic monitoring in very low birth weight neonates: a randomized trial. J Pediatr. 2011;159(6):900-6 e1) was in babies of less than 1500 g. That trial found, of course, that babies who had their heart rate characteristics index displayed to the caregivers had a lower mortality than babies on the same monitors for whom the index was hidden. Further analysis of the data from that trial showed that mortality was lower only among those infants who actually had late-onset sepsis, and specifically within 30 days of a sepsis episode. Presumably, this is because sepsis episodes were detected sooner, and appropriate therapy started earlier. The improved survival after sepsis is illustrated in this figure

Organism-specific mortality based on heart rate characteristics (HRC) monitor display… Survival was higher in each organism group in infants with HRC displayed (solid line) compared with those with HRC not displayed (dashed line).

If that explanation of the results is true, you might also hope to find a reduction in long term adverse outcomes also. This new publication Schelonka RL, et al. Mortality and Neurodevelopmental Outcomes in the Heart Rate Characteristics Monitoring Randomized Controlled Trial. J Pediatr. 2020 investigated the developmental progress and neurological signs of a subgroup of the survivors, that is those with a birth weight under 1000g and born in one of the 3 hospitals who contributed the most to the enrolment. They were also centres with established expert follow-up. I want to repeat a comment I made on another recent post, the last of these babies was enrolled in May 2010, and therefore completed their Bayley version 3s and neuro exam at 18 to 22 months corrected age at the latest by July 2012. Why 7 years to publish these important data?

Survival in this subgroup of 638 infants was higher in the group with the HeRO score displayed, 76%, compared to 68% with the monitors hidden, relative risk of death 0.75 (95% compatibility limits 0.59-0.97).

Among surviving infants, the developmental and neurological evaluation showed the following:

Neurological abnormality or developmental delay, survivors only
Displayed Hidden RR (95% CI)
Overall proportion with at least one abnormality 48/242 (19.8) 37/206 (17.9) 1.10 (0.75-1.63)
 GMFCS level 2-5 (moderate/severe CP) 23/246 (9.4) 13/210 (6.2) 1.51 (0.78-2.9)
 Bilateral blindness 4/247 (1.6) 0/210 (0) 0 (0-0)
 Deafness 11/248 (4.4) 1/210 (0.5) 9.31 (1.21-71.55)
 Bayley cognitive <70 23/243 (9.5) 15/207 (7.3) 1.31 (0.70-2.43)
 Bayley language <70 36/241 (14.9) 28/206 (13.6) 1.01 (0.69-1.74)

As you can see there are not many differences between the 2 groups, and the small differences are all in favour of the control group. The exception being deafness which was surprisingly more frequent in the monitor displayed group.

Because there were more survivors in the monitored group you can express the data, if you wish, as ‘death or severe CP’ and ‘death or blindness’ and ‘death or a lowish cognitive score on the Bayley’, those results are highlighted in the abstract, but any regular readers of this blog will know my opinion about such composite outcomes. I think without trying to massage the data to find an outcome which is “statistically significantly” improved in the monitoring group, we can be reassured that there were more survivors in the monitored group and they had very similar outcomes to the controls. The authors of this study have done a lot of great work, on this project and many others, and I have a great deal of admiration for them, but I don’t understand why torturing the data to find a combination of outcomes that has a p-value less than 0.05 in favour of the HeRO system was thought to be so important. Improved survival with very similar long term outcomes is surely enough evidence on which to base decisions about an intervention, and in this case show that HeRO is the way to go.

As I also mentioned recently, I don’t think there is any intervention in neonatology that has increased survival and also worsened long term outcomes, and, most importantly, no intervention that increases survival but only of babies with a future quality of life that is worse than being dead. Surveillance of long-term outcomes in a trial such as the HeRO trial, and timely publication, is important for quality assurance and to ensure that we optimize interventions, and continue the enormous progress we have made in neonatology.

Before anyone comments that SUPPORT showed increased survival with worse retinopathy in the higher saturation group, that is true, but blindness was not different between groups, and the NeoProm group showed no adverse impact of higher saturations on any long term outcome despite better survival in the high saturation group.

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CRP can suggest that babies are not infected, when you already know!

I wrote a blog post about 3 years ago about a study examining procalcitonin use in neonatal early-onset sepsis. You can see from my post that the authors didn’t, to my mind, show any utility of procalcitonin (PCT) either alone or in addition to the CRP for diagnosis of EOS. They have just published a secondary analysis of the trial (Stocker M, et al. C-Reactive Protein, Procalcitonin, and White Blood Count to Rule Out Neonatal Early-onset Sepsis Within 36 Hours: A Secondary Analysis of the Neonatal Procalcitonin Intervention Study. Clin Infect Dis. 2020) which shows the following:

Normal serial CRP and PCT measurements within 36 hours after the start of empiric antibiotic therapy can exclude the presence of neonatal EOS with a high probability. The negative predictive values of CRP and PCT do not increase after 36 hours

Which is all well and good, but not much use. Blood cultures are almost always positive by 36 hours, so by the time the PCT and CRP are useful you already know if the baby has sepsis or not! The actual time to positive cultures has just been reviewed, (Marks L, et al. Time to positive blood culture in early-onset neonatal sepsis: A retrospective clinical study and review of the literature. J Paediatr Child Health. 2020;56(9):1371-5). Using the Bactec system they found that 98% of positive blood cultures in babies with EOS were positive at less than 24 hours, and the only one that was positive later was taken after antibiotics had been started. In their review of the literature, blood cultures for EOS were positive by 24 hours in 92% to 100%. In my practice, we now stop antibiotics if cultures are negative at 36 hours, the idea being that in the rare case of a culture being positive between 36 and 48 hours we can restart the antibiotics without actually missing a dose, but the dose which would normally have been given at 48 hours is avoided if the cultures are negative. Given this new publication, we can probably stop even earlier, at least for EOS, and limit antibiotic courses to one or two doses for the majority of babies who are screened but do not have EOS.

The Bactec system and other similar systems are extremely sensitive to even very low bacterial counts as long as 1 mL of blood is used, they screen the culture medium continuously and an alarm bell rings in the lab if they become positive, bringing a laboratory technician scurrying over to get the result and phone it to the NICU. I actually don’t know how it all works, but that is the image I have in my mind. We have a very efficient lab that always telephones when a blood culture is positive, but just as a backup we ensure that someone checks with the laboratory directly before stopping antibiotics. Reducing unnecessary antibiotic use is an important goal, this most recent publication again fails to show that CRP or procalctinon measurements, single or repeated, assist in achieving that goal.

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Breast milk fortifiers, a new systematic review

A systematic review has just been published which compares the outcomes of milk fortification with bovine-milk derived fortifier and human-milk derived fortifier. (Grace E, et al. Safety and efficacy of human milk-based fortifier in enterally fed preterm and/or low birthweight infants: a systematic review and meta-analysis. Archives of Disease in Childhood – Fetal and Neonatal Edition. 2020:fetalneonatal-2020-319406)

The main conclusion is that the evidence is very weak, but I think that even that exaggerates the quality of the evidence! The extensive literature search, using terms designed to select randomized trials in which one group received bovine-milk derived fortifier (BMDF) and the other received human-milk based fortifier (HMDF), led to the inclusion of two trials with a total of only 332 infants. Unfortunately, those 2 trials studied different interventions, and in my mind should not have been meta-analysed.

We already know from published data, that using artificial formula, rather than pasteurized donor human breast milk increases Necrotising Enterocolitis. That is so whether the formula was used as a supplement to insufficient maternal breast milk, or as an alternative for babies not receiving maternal milk. Here is the relevant figure from the Cochrane review (Quigley M, et al. Formula versus donor breast milk for feeding preterm or low birth weight infants. Cochrane Database Syst Rev. 2019;7:Cd002971) for the outcome NEC.

(I have mentioned before that if you want to access the Neonatal Cochrane Reviews full text free of charge you can do so via this Vermont Oxford Network page; if you find the review you are interested in and click on the link then the Cochrane library page somehow knows that Vermont sent you, and VON support universal access to the neonatal reviews.)

So given that we already know this with a moderate degree of certainty, any study which tries to determine the importance of the type of fortifier on NEC, or other outcomes, should compare only the fortifier, and ensure that the milk received was human milk (maternal or donor).

But one of the 2 trials included in the new SR was Sullivan S, et al. An Exclusively Human Milk-Based Diet Is Associated with a Lower Rate of Necrotizing Enterocolitis than a Diet of Human Milk and Bovine Milk-Based Products. The Journal of Pediatrics. 2010;156(4):562-7.e1. In that trial, there were 3 groups, one of which received artificial fortifier as the supplement to breast milk and BMDF, the two groups who received HMDF also received donor human milk as the supplement to mother’s own milk. So it was not a trial of human-milk derived fortifier alone, but a trial of HMDF and donor breast milk supplements, compared to BMDF and artificial formula supplements.

In fact, if you work in a centre that has access to pasteurized donor human milk it is unethical to randomize infants to receive artificial formula as a supplement.

The only justification for giving a preterm baby at risk for NEC artificial formula, rather than donor human milk, if it is available, is parental refusal. And even then, if a parent refused for a baby at very high risk, I think it is questionable whether such a refusal should be accepted.

The other trial (O’Connor DL, et al. Nutrient enrichment of human milk with human and bovine milk-based fortifiers for infants born weighing <1250 g: a randomized clinical trial. Am J Clin Nutr. 2018;108(1):108-16) was very different to Sullivan et al, in that study all the babies received breast milk, either maternal or donor, and were randomized to either HMDF or BMDF (in this case powdered BMDF). This study only included 127 babies, so didn’t have much power to show a difference in NEC, but in fact, the 2 groups had exactly the same number of cases of proven NEC.

The evidence has never shown that adding a powdered multi-component fortifier to mothers milk has an adverse impact on Necrotising Enterocolitis rates, and until recently the only fortifier available was BMDF. That doesn’t mean we have good evidence that they are definitely safe, the Cochrane systematic review shows that the studies that looked directly at the issue only had a rate of NEC of about 2.5%; there was no evidence of a higher risk with the fortifier, but they note that the evidence is weak. The relative risk of NEC comparing fortifier to no fortifier was 1.37 (95% limits 0.72 – 2.63), which means of course that there remains a risk that fortification might substantially increase NEC.

Why not just switch to HMDF anyway? The available HMDF is a liquid, and as such dilutes the mother’s own milk that is given to the baby, for example, the standard fortification of mothers milk requires that there is a dilution of 40 mL of mothers milk by 10 mL of the liquid fortifier.

The ways the various products are produced are quite different, for example, the pasteurization of Prolacta is done by a Vat method, which destroys some of the good proteins (such as lactoferrin) in the human milk. Local milk banks usually use Holder pasteurization which has much less effect on those proteins, and some banks use very short time, higher temperature pasteurization which is probably even better.

I also don’t think there is any good reason to believe that the increase in NEC seen with artificial formula is because of the source of the protein, it could well be other features of preparation, sterilization, manipulation etc. Preterm newborns extremely rarely have evidence of cows milk protein intolerance, in fact, foreign proteins usually induce tolerance when you give them to preterm infants. The focus on where the proteins in the milk come from may be entirely misleading. If we concentrated on why formula increases NEC compared to human milk we might gain some further insights into the pathophysiology of the disease.

Human-milk based fortifier is extremely expensive, but even if it cost the same as the BMDF I think there should be robust evidence before switching to using it. It will require diversion of a significant proportion of our currently available breast milk to create enough fortifier for every baby, and it will reduce the amount of the mother’s own breast milk that a baby receives, by dilution.

In summary, the only data that compares BMDF to HMDF in babies receiving maternal breast milk supplemented with donor milk when required (the current standard of care) does not show any difference in Necrotising Enterocolitis. Given the small sample size of that trial and the importance of NEC, I think that performance of a large multi-centre trial is urgent. It should be performed in infants at significant risk who are also receiving all evidence-based preventive methods, multicomponent probiotics and feeding protocols.

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Evidence-Based Neonatology: more and more evidence, better and better care

For another project, which I will explain later, I have been trying to find recent large multicentre trials in very preterm babies. I searched PubMed for “Randomized Controlled Trial’, and “Multicentre study”, then filtered by Human and Newborn and Preterm and just looked at the last 10 years. So far here is the impressive list of Acronyms for the trials in approximately reverse chronological order: See how many you can recognize! There will be a prize for anyone who gets them all!


The prize I have in my mind is my admiration! There were one or two that I had to search hard to find the acronym, and there are a couple of trials which aren’t in the list because I could not find one at all (such as the budesonide/surfactant trial).

The reason I have been trying to list all the recent large trials is to see if I can develop a database of evidence-based treatments for the most immature babies that we treat, of 22, 23 and 24 weeks gestation. The physiological immaturity of these babies is so extreme that for some interventions it is likely that their response may be different.  I am searching to see which trials included such immature babies, and whether there are any data presented for infants under 25 weeks. So far… not much, but when I complete the search I will write it up as a publication, and let you all know on this blog.

If any readers know of a large RCT which included extremely immature babies and which is not on the list, please let me know, especially if data are presented for the gestational age stratum <25 weeks.

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My new watch has a pulse oximeter?!

I recently bought a smartwatch, I won’t say which model because what I found is now available on several makes of watch. I discovered when playing around with the Apps that there was one which claimed to measure blood oxygen levels. After clicking “go” I received a measurement about 30 seconds later, which was probably inaccurate, I usually have a saturation of about 98% at sea-level, and it only read 92%.

Which made me wonder what is the purpose of this?

It also made me realize that I have been doing neonatology a long time; I was around when pulse oximeters were invented and I published one of the first studies to evaluate their use in the NICU (Barrington KJ, et al. Evaluation of pulse oximetry as a continuous monitoring technique in the neonatal intensive care unit. Crit Care Med. 1988;16(11):1147-53). I even studied using them in rabbits! (Barrington KJ, et al. Pulse oximetry during hemorrhagic hypotension and cardiopulmonary resuscitation. J Crit Care. 1986;1:241-6). I wondered if they would be useful during low perfusion states, and I thought that a pulse oximeter would be great during cardiac massage, as you would be able to tell if you were achieving pulsation at the site it was placed, and also what the saturation of the blood being delivered would be.

The low perfusion part of the rabbit study was interesting, as the oximeter remained accurate until there was very little perfusion, then it just stopped, which was an improvement in the previous technology of Transcutaneous PO2 monitoring, which become progressively inaccurate as perfusion falls.

But when performing CPR on the rabbits after inducing cardiac arrest I was initially very excited when it seemed to work well, and routinely gave a saturation of about 85% with the same frequency as the cardiac massage! Wow, publication in Nature on the way, I thought. Then I realized that when you do cardiac massage on an adult rabbit, the front legs, where I had placed the probe, move, a lot. You’ll probably all have to take my word for that unless you happen to have tried to resuscitate a rabbit. So I then stopped doing the massage and just rhythmically shook the rabbit’s paw; it continued to get a nice beeping sound and a saturation around 85%. I then put the probe on a piece of red rubber tubing that was lying around, and shook that rhythmically, and found the same thing.

That was my introduction to movement artefact in pulse oximetry. It also got me thinking about how oximeters function and details of their design (I’ll get back to the watch soon).

Pulse oximeters work by shining light of different wavelengths onto a tissue and measuring the relative absorption of the light at those 2 wavelengths. Clinical pulse oximeters do this with transmitted light, whereas my watch is obviously doing this with reflected light. Most clinical pulse oximeters use 2 wavelengths of near infra-red light which are on either side of an isobestic point. That is a point at which the absorption spectra of haemoglobin and oxyhaemoglobin cross. As long as you have 2 wavelengths with different relative absorptions by oxygenated and de-oxygenated blood it will work, but by using 2 wavelengths that have inverted relative absorptions you can make the calculations more accurate.

It was a Japanese engineer Takuo Aoyagi (who died earlier this year aged 84) who realized in the 1970s that the pulsations he was seeing in his signals were entirely from arterial blood, and so if he screened out the constant part of the signal, and only analyzed the pulsatile part of the signal, he could calculate the proportion of pulsatile haemoglobin that was oxygenated or de-oxygenated.

That is why movements will give you an apparent signal, because there are fluctuations in the light absorption, it also explains why the specific pulse oximeter I was using read 85%, because at the 2 wavelengths that the company used (which are all slightly different because of patent issues) when the absorption of light at the 2 wavelengths was 1:1 that corresponded to 85% of the haemoglobin being oxygenated and 15% being de-oxygenated.

When pulse oximeters were used under anaesthesia, movement artefact was not a big deal, but for continuous monitoring on moving patients, it required progressive improvements in technology to reduce the artefacts, which are still a problem for very active patients.

Also, it is worth remembering that it is the pulsatile part of the signal which is being analyzed, so if you have venous pulsation that will interfere with the result. I had a patient recently with severe pulmonary hypertension and the pre-ductal saturation was often  5-8% lower than the postductal, the patient had a closed ductus. On the echocardiogram, there was tricuspid regurgitation, which I think was causing venous pulsation and erroneously low oximeter readings in the upper limb, but wasn’t severe enough to be transmitted to the foot. In the past, we sometimes had an oximeter integrated into the monitor in one place, and a stand-alone monitor for the second site. Because the technologies differ between machines, sometimes you could change the gradient just by switching the probes around!

To get back to the watch, I am not really sure that this is a good idea; I also don’t know if it is accurate. Using reflected rather than transmitted light, and not having wavelengths that are chosen specifically for their use in oximetry, not having any idea if they can account for methaemoglobin or carboxy- or fetal haemoglobin etc etc.

I can imagine many people finding a saturation a bit low, like mine, will freak out and phone their doctor or go to the Emergency Room, and not just shrug it off like me as being probably inaccurate. We don’t need extra pressure on medical services right now! I read something about it perhaps being useful to detect sleep apnea, but for that, you would have to have it in continuous mode (if that exists) and wear it while you are asleep, which my watch battery would have a problem with, it would be very low the next morning.

The manufacturers, of course, come up with some weasel words about ‘not being intended for medical use, including self-diagnosis or consultation with a doctor, and are only designed for general fitness and wellness purposes’ but that just sounds like the usual get-out-of-jail free statements that health supplements use.

Now, how can I get my saturation higher? Maybe if I take high dose vitamin D, or find somewhere to insert a jade egg… hmmm.

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Does LISA protect your brain?

A few years ago now a multicenter RCT among infants of 23 to 26 weeks gestation showed that LISA was possible in even these most immature infants., NINSAPP.

Kribs A, et al. Nonintubated Surfactant Application vs Conventional Therapy in Extremely Preterm Infants: A Randomized Clinical Trial. JAMA Pediatr. 2015;169(8):723-30. 211 infants were randomized if they were stabilized on CPAP at 10 to 120 minutes of age and were needing more than 30% oxygen. The original publication was a “negative trial’ in that the primary outcome (survival without BPD) was not very different between groups; although more frequent with LISA than with intubation for giving surfactant (67% compared to 59%) the risk difference of 8% could have been due to chance (95% compatibility limits 21% reduction to 5% increase of “death or BPD” with LISA).

One finding of the study was that almost all of the 23 and 24 week babies randomized to LISA were intubated later (14/15 at 23 weeks and 24/26 at 24 weeks), as well as 3/4 of the 25 week and 1/2 of the 26 week infants. The eventual median duration of mechanical ventilation was therefore only 2 days different between the groups. Of note the incidence of severe intracranial bleeding ‘grade 3 and 4 IVH’ was 22% among the controls, and of cystic PVL was 11%. Both of these frequencies are very high and were much higher than the LISA group, 10% for severe IVH and 4% for PVL. In recent years in the Canadian Neonatal Network the combined incidence of severe IVH and PVL has been between 17 and 19% for babies of 23 to 26 weeks GA, even allowing for some overlap in the NINSAPP babies some of whom might have had IVH and PVL, their frequency of serious brain injury was much higher among the controls than among our intubated babies. Did they by chance have a group of controls who had more brain injury than usual? Or was it truly the impact of LISA? Or was it because the routine was to perform intubation without pre-medication in the control group? (Which causes major hemodynamic fluctuations and is much more likely to need multiple intubation attempts).

It is hard to imagine how the occurrence of cystic PVL would be affected so dramatically by 2 fewer days of mechanical ventilation.

Long term follow-up of the infants has just been published (Mehler K, et al. Developmental outcome of extremely preterm infants is improved after less invasive surfactant application (LISA). Acta Paediatr. 2020.)  156 babies were evaluated at 2 years corrected age (86% of the survivors). Strangely these data are 5 years old now, as babies were recruited up to 2012, so the last follow up would have been in 2015.

The primary outcome of the follow-up study is vaguely defined as “neurodevelopment” and refer to the Bayley version 2, but do not mention a neurological exam.

Disability was defined if the mental development index (MDI) or psychomotor development index (PDI) was <85 but ≥70, severe disability was defined for MDIs or PDIs <70. Indices between 85 and 115 indicated normal development, indices >115 were defined as development above average. Developmental delay referred to any MDI or PDI <85.

This is the main table of the results which shows a very high frequency of what they call “severe disability” among infants of 25 and 26 weeks GA randomized to the intubation group. Firstly, I would like to re-iterate, a low score on a Bayley is not a disability. The Bayley Scales of Infant Development are a screening tool meant to identify children who require further evaluation, many of those with low scores at 24 months do not have impairments when evaluated later.

A systematic review of LISA was published in 2017, it included 6 trials Aldana-Aguirre JC, et al. Less invasive surfactant administration versus intubation for surfactant delivery in preterm infants with respiratory distress syndrome: a systematic review and meta-analysis. Arch Dis Child Fetal Neonatal Ed. 2017;102(1):F17-F23) and  did not show an impact of LISA on intraventricular haemorrhage or PVL, but the other trials included very few infants at high risk, mostly specifically excluding infants below a certain GA.

Is it possible that LISA (or alternatively MIST, minimally invasive surfactant treatment) protects the brain? I would say that the data from NINSAPP are unconvincing; it was a well-performed study, but was too small, with an unusually high incidence of brain injury in the control group, and non-optimal intubation practices in those infants. Slightly delaying intubation in 23 and 24 week infants may have some benefits, and performing the procedure after the early perinatal hemodynamic changes. But it seems to me inherently unlikely that such a big difference in ultrasound brain inujry findings and in longer-term developmental scores would result from avoiding intubation overall of 25% of mostly 25 and 26 week infants and a median of 2 fewer days mechanical ventilation.

It would be good to be proved wrong (I think that happened once before😁). I am afraid to say it, more research is needed, to confirm or question these findings.

Also, and I know most of us are too busy and there are mutiple reasons why publications get delayed, but reporting dramatic differences in outcomes 5 years later does a disservice to our community, earlier reporting of these results could have helped to ensure that other trials get funded, and that other researchers include longer term neurological and developmental outcomes in their study designs.

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