ECMO for ARDS

Although this isn’t neonatal it is a great study with an unfortunate conclusion… There has long been controversy about the place of ECMO for adults with ARDS. To resolve this a French multicentre trial randomized adults who were very sick to ECMO or continuing standard therapy. (Combes A, et al. Extracorporeal Membrane Oxygenation for Severe Acute Respiratory Distress Syndrome. The New England journal of medicine. 2018;378(21):1965-75). Just under 1/3 of the patients were enrolled in non-ECMO centers, so the ECMO group was a transport and ECMO group for those patients.

After 2/3 of the sample size was enrolled the study was terminated “for futility”. They had hypothesized a 60% mortality in the controls and a 40% mortality in the ECMO group, for ethical reasons they allowed rescue ECMO in the controls if the physician felt they were still deteriorating and might benefit from ECMO.

At the point the trial was stopped, because they crossed the pre-specified ‘futility’ stopping boundary, there was a 35% mortality in the ECMO group, and a 46% mortality in the controls. 28% of the controls (35 patients) crossed over to ECMO, and of those 57% died.

I don’t know about you, but an 11% absolute reduction in mortality sounds huge to me, and if I was ever unfortunate enough to have severe ARDS, I think the ECMO group would suit me just fine.

Unfortunately, there will now be people saying there was no difference between the groups.  In fact one of the accompanying editorials in the FPNEJM says exactly that “the routine use of ECMO in patients with severe ARDS is not superior to the use of ECMO as a rescue maneuver in patients whose condition has deteriorated further”. That is not true, 35% mortality is superior to 46% mortality! The sentence should state “the routine use of ECMO in patients with severe ARDS is superior to standard care, with the use of ECMO as a rescue maneuver in patients whose condition has deteriorated further, but the difference does not meet conventional norms of statistical significance”.

Indeed if the 15 patients rescued by ECMO in the control group had been allowed to die without ECMO, and if they had indeed all died, then the difference would have been highly statistically significant (p=0.0004). You can see in the online supplement that those who crossed over were indeed extremely sick, all on 100% O2 with a PaO2 averaging 50 despite a PEEP of 10 and a PIP of 33 (Which would probably give an oxygenation index of about 100 if they had been babies!), so the idea that they might have almost all died without ECMO is reasonable, the mortality of this, rescue, group (57%) was substantially higher than the early ECMO group.

This was a very difficult trial to do, it took 6 years to get the 240-0dd patients enrolled, and the stopping boundary for futility was decided prior to starting the trial. I think the decision to stop can be justified, but I do wonder about the stopping boundary that was chosen. The trial showed a potentially substantial benefit of ECMO, and stopping a trial in those circumstances, even when the chance of showing p<0.05 at the end might be considered low, should be questioned. Realize that the relative risk of death was 0.76; a 24% relative reduction in mortality will now be considered “not significant”! I am in favour of sequential designs in general, they may preserve power while potentially decreasing sample size. The problem is in how the stopping boundaries are calculated. If a stopping boundary is calculated which leaves a good chance of a major clinically important benefit, like an 11% absolute mortality reduction, then we have to question the methods. The other editorial about the trial in the FPNEJM says some similar things Harrington D, Drazen JM. Learning from a Trial Stopped by a Data and Safety Monitoring Board. The New England journal of medicine. 2018;378(21):2031-2.

Perhaps the  best answer to all of this is to analyze trials using Bayesian methods, incorporating prior probabilities into the interpretation of new data to produce a posterior probability. At the end of which we can then say not “ECMO decreases mortality” but “the probability that ECMO decreases mortality is X, whereas the probability that ECMO increases mortality is Y”. A perfect example of exactly that technique is the late-hypothermia trial from the NICHD. (Laptook AR, et al. Effect of Therapeutic Hypothermia Initiated After 6 Hours of Age on Death or Disability Among Newborns With Hypoxic-Ischemic Encephalopathy: A Randomized Clinical Trial. JAMA. 2017;318(16):1550-60). The final conclusion of the trial could have been “p=NS, there is no effect of therapeutic hypothermia in this population”, but fortunately the authors had realized when planning the trial that adequate power for classical frequentist p-value testing would be unlikely and planned to perform a Bayesian analysis. That analysis showed that there was about a 75% chance that hypothermia was beneficial.

The authors of that cooling study have also published an article about how you can use Bayesian methods to inform the stopping of an RCT (Pedroza C, et al. Advantages of Bayesian monitoring methods in deciding whether and when to stop a clinical trial: an example of a neonatal cooling trial. Trials. 2016;17(1):335)

It would be interesting to think what would have happened with the ECMO trial if they had used Bayesian methods. Especially given the prior (lower quality) evidence that there may be a reduction in mortality of adults with ARDS who are treated with ECMO. The previous study “CESAR” has been criticized because only 75% of patients randomized to referral for ECMO actually were cannulated, and perhaps respiratory management (in both groups) was not optimal, but it did show a similar-sized advantage of ECMO referral over conventional management. The prior probability of an ECMO advantage for your Bayesian analysis should probably therefore already have favoured ECMO, and  Bayesian analysis might well have shown a high probability that ECMO is preferable to conventional management for adults with ARDS.

I have never done intensive care in adults, but I was a pediatric intensivist for many years as well as a neonatologist, and I cared for a couple of kids with ARDS that we put on ECMO, with good results. I think there is certainly a place for ECMO in such kids, and this trial, to me, confirms that they probably benefit, and probably have a better chance of surviving with ECMO, if they are sick enough to be at substantial risk of death.

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At last, something men are better at than women!

That is, giving blood for babies, at least maybe.

The introduction to this new publication notes something that I was not aware of, that plasma donated by women is associated with a substantially greater frequency of transfusion related complications than man-plasma. It is thought to be due, perhaps to the leukocyte antibodies in higher concentration in female derived plasma, and the increase in risk is particularly in TRALI (transfusion related lung injury), and was first identified by the UK surveillance program, Serious Hazards of Transfusion, which I guess has the acronym SHAT.

The new article (Murphy T, et al. Impact of Blood Donor Sex on Transfusion-Related Outcomes in Preterm Infants. The Journal of pediatrics. 2018) examined the donor sex of blood given to preterm babies. We use a lot of blood in our tiniest babies, but not that much plasma; platelet transfusions are not uncommon and they contain a lot of plasma. In this study they only included babies who had received blood, and excluded those who had also had high plasma products. They ended up with a cohort of 170 babies under 32 weeks who had received blood, and divided them into groups of female only donors, male only donors and both. Initial comparisons were between the male only and the others, and that showed that babies who were received some female donor blood had more BPD, more composite morbidity and longer hospital stay than those who received exclusively man-blood.

If you think about it, getting out of the NICU having received blood from only male donors, compared to mixed male/female donors is more likely if you only have one or two transfusion donors. So the authors found that the mixed male/female donor group were more likely to have had more transfusions than the male-donor-only group. Perhaps they were therefore were sicker and had more complications. When they corrected for numbers of transfusions there was still a difference, with male-donor-only babies having better outcomes, but with smaller Odds Ratios and confidence intervals that now included no difference.

They then also compared those that had only female donors to the male-donor-only group, to compare recipients who had the same numbers of transfusions; the numbers are now getting smaller, about 60 per group. The odds ratios for BPD and any major morbidity (1.12 and 1.75) remain in the direction of worse outcomes with female-donor blood, but the confidence intervals are now quite wide and include no effect (or even a protective impact).

The data suggest then that it is possible that there is an impact, with man-blood recipients having better outcomes. Certainly a big enough impact to be worth investigating further. Donating blood also increases your life expectancy maybe if more men donated blood we could catch up to women, and provide safer blood to babies also!

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Placement of umbilical catheters

This is not a very new article, but it still appears to be on-line only. I wrote the draft of this post a while ago then forgot about it, but I think it is a valuable publication. Lean WL, et al. Accuracy of 11 formulae to guide umbilical arterial catheter tip placement in newborn infants. Archives of disease in childhood Fetal and neonatal edition. 2017.

The authors, from the Royal Women’s Hospital in Melbourne, compared the accuracy of 11 formulae for deciding how far to insert an umbilical arterial catheter. There have been 11 formulae published and they worked out, based on 103 babies of various sizes who had catheters placed, how well the different formulae worked.

They found that many formulae in common use, especially those based on body weight rather than a body measurement, led to misplaced catheters very frequently. The formulae which worked best were the umbilicus to shoulder tip measurement which is ‘a’ in the figure, and one that I had never heard of which was 0.33 multiplied by the total length of the baby.

Measuring the total body length of a baby is rather inaccurate, and can be difficult when the baby is getting lots of attention or is unstable. I have always used the shoulder tip to umbilicus, since I was a fellow (and add 1 cm for the babies over 2 kg, but I don’t know where any of that comes from). This study confirms that that is one of the best methods, the difference between that method, and the more difficult body length method was minimal. I think it should clearly be the default for UAC insertion depth; I just have to remember to take the measurement before I gown up.

The second article is from the same group of people, and is also on-line first, since March this year  : Lean WL, et al. Accuracy of five formulae to determine the insertion length of umbilical venous catheters. Archives of disease in childhood Fetal and neonatal edition. 2018.  In this study they had 118 umbilical venous catheters, but only 70 in a position that they could use; the others being either displaced in the portal venous system or too low to be useful. None of the formulas they evaluated were much good, with at best 55% being well-placed. Shukla’s formula, based on body weight is as follows (((3xBW)+9)/2) +1. That is a bit unwieldy for daily use, and prone to errors. The next best had slightly more well-placed UV catheters but many more that were too low (37% vs 4%), that was umbilicus to xiphisternum plus 1cm.

My own practice has been umbilicus to xiphisternum plus 2cm (again I don’t know where that comes from), which would lead to more catheters being too high, but very few being too low, and I think, based on this article I will stick to that.

The big question that these studies pose hasn’t been asked: why are we so backward? Surely we should all be using point-of-care ultrasound to position our catheters correctly the first time. We could all choose the best formula (the best ones from these studies) and then quickly check where the catheter tip is, by ultrasound, to adjust within a few seconds if it is not right.

I say this not as a fanatic of point-of-care ultrasound, I don’t even remember how to switch on our machine, but after thinking about these 2 studies, it just seems evident that we could improve care if we had an immediate objective methods for determining catheter position. I will now have to learn how to do it myself.

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Integrating families more in their babies’ care is a good thing!

Giving families a much greater role in the care of their infants is a really important advance and much of what Karel O’Brien and the team at Mount Sinai have done is what should be done in all our NICUs.  O’Brien K, et al. Effectiveness of Family Integrated Care in neonatal intensive care units on infant and parent outcomes: a multicentre, multinational, cluster-randomised controlled trial. The Lancet Child & Adolescent Health. 2018;2(4):245-54.

The idea behind family integrated care (FIC) is to give families much more room to participate in the care of their infants in the NICU, including participating in medical rounds, and becoming an essential part of the care team, including writing in the medical chart. It might even include adjustments of oxygen concentration and administration of some medications. It certainly includes eliminating institutional barriers to parental presence (such as sending parents away during hand-over or rounds; which used to happen in many places). I think we should be giving parents clear, overt, authority also to stop people touching their baby who haven’t washed their hands, or if they are the 2nd, 3rd or 4th member of the team (or consultant service) to examine the baby during a short time, or when the baby has just gone to sleep. Parents often don’t feel they have the right to intervene at such times, but recognizing their role as parents and putting them at the center of the care team could well help their baby.

If we change our approach to the place of parents in the NICU, what measurable outcomes should such an approach aim to achieve? Parents of hospitalised children, especially those who are critically ill, often feel disempowered, and have difficulty finding their place as parents. When your baby’s life starts in an NICU those difficulties are amplified, and may be associated with longer term issues in parenting and stress. So a trial of integrating families more into the care of their infants should probably examine outcomes such as parental feelings of empowerment, satisfaction and stress, parental resilience, how parents adjust, later on, to having their baby at home, whether they felt competent to be parents at home after discharge, whether they were less likely to be re-admitted during the first year of life (especially for more minor illnesses). Weight gain during the first few days after randomization, I suggest, is not something I would expect to be affected, nor would it interest me very much.

Empowering parents therefore is something I very much believe in, that being said this trial has a number of quite large problems, which make the conclusion, that family integrated care improves weight gain of infants born at 33 weeks gestation or less, between when the infants become stable enough to be enrolled (on CPAP or without respiratory support) and 21 days later, somewhat questionable.

This was a trial that was mostly a cluster randomized trial, but Mount Sinai hospital in Toronto, where the FIC approach was developed, was not randomized, they were a priori placed in the FIC group. As they are the largest inborn NICU in Canada, with, I think, about 1300 admissions a year, mostly of preterm babies, that immediately might create a bias in the results.

Parents enrolled in the FIC group were screened to ensure that they committed to “having a primary caregiver at the infant’s bedside for a minimum of 6 h per day (between 0700 h and 2000 h), 5 days a week, and to attend medical rounds and education sessions for at least 3 weeks”. Parents enrolled in the standard care hospitals didn’t have to give any such commitment. This immediately introduces another bias in this trial, which is critical to the results, the parents were therefore likely to be different between groups. A couple where one parent works full time, and that already has a young child at home, might not be able to give such a commitment, for example. You could easily imagine many other scenarios where that commitment would be difficult or impossible. This is probably one of the reasons why recruitment among eligible patients was very much lower in the FIC centers (30%) than the standard care centers (44%). If you look at the numbers differently, about half of the eligible patients in the FIC group (about 900 of about 1800) “declined” compared to only 15% of the controls (about 155 of about 1000). They had to approach 1.5 times as many patients in the FIC hospitals to enroll the same final number of infants. You can see those data here:

Several of the secondary outcomes might therefore be very different because of baseline differences between the groups; if a mother can be present for at least 6 hours per day, compared to a family that could not make that commitment, then breast feeding might well be different regardless of randomization. Breast-feeding outcomes at discharge were indeed different, or at least they were different between the modest proportion of babies for whom this outcome was available; which was only 396 of the FIC babies and 624 of the controls (of about 890 in each group). The breast feeding outcomes were only available for the infants who were not back-transported to step down level 2 care, which is something that occurred at a much higher frequency in the FIC centers, such centers might well have very different outcomes for breast-feeding, than infants discharged directly home from a tertiary NICU. I think therefore that the data on breast-feeding outcomes are quite unreliable, even though they are important, and might well be affected by an FIC approach, these data don’t really give us the answer about whether this approach improves breast-feeding at discharge.

One could also question the primary outcome, weight gain (or to be specific, change in weight z-score between enrolment and 21 days). Final weight z-score at discharge home, head circumference at discharge home, those are things which have an association with long term outcomes, but weight gain between about 32 weeks and about 35 weeks has a more questionable clinical significance. Weight gain is very closely associated with nutritional supply, so any difference in nutritional practices between the randomized institutions will have a big impact on this outcome. I can’t see in the published article a presentation of nutritional intakes or practices or of the intra-cluster correlation coefficients; maybe the centers randomized to standard care had nutritional standards which were less “aggressive” than the FIC NICUs. This is at least a possibility.

The results as presented show a change in body weight z-score of 1.58 in the FIC group and 1.45 in the standard care group; this I find impossible to understand, did body weight really cross multiple percentiles in both groups, to be about 1.5 standard deviations higher in each group, over 21 days?

I don’t think so, I think the primary outcome is not presented correctly, in fact the infants, on average, lost weight in comparison with Fenton’s growth trajectories, in both groups; but with a possible advantage in the FIC group.

Let me explain; when I look in detail at the results, the babies were on average 14oo grams at 32 weeks post-menstrual age when enrolled, and the mean z-score for their weight was -0.9 at that point (the same in both groups). If the groups had really both improved their z-scores by about 1.5 over 21 days, that would put them at about a weight z-score of +0.6, on average, at 35 weeks, which is about 2750 g, or an increase in 1350 grams on average over 21 days, a weight gain of, on average, 64 g per day. If that was true it would be remarkable, but, I suggest, close to impossible, and it is not what they report.

The article actually notes that the participants gained on average about 26 g/day, which would actually put them at just under 2 kg, on average, 21 days later; that is consistent with what the article reports as the percentage increase in body weight from enrolment to 21 days, of around 40% in both groups, a bit higher in the FIC group than the controls (42.6% vs 38.9%). What that means is that the z-score for the participants weight actually worsened from enrolment to 21 days. They went from an average of -0.9 to an average of about -1.3 for the z-score at 21 days, or a change in z-score of -0.3 (which is a long way from +1.5). Just to stay with the same z-score they would have had to gain about 31 g/day, so a small decrease in z-scores appears to be what they really showed, with what seems to be a lesser decrease in z-scores in the FIC group. I think therefore that the primary outcome is not presented correctly, although the results do seem to show a small weight gain advantage of the babies in the FIC centers, whether the z-score change is really different between groups is more questionable.

After messing around with these figures for a while I think that what they may have done is to recalculate the z-scores at 21 days after enrolment using the Fenton weight distributions as of the post-menstrual age of the date they were enrolled. So the controls for example, gained 24.8 grams a day between enrolment at an average of 32 weeks, and when they were re-weighed 21 days later. They were therefore at 35 weeks on average 1.962 kg body weight, which is equivalent to a weight z-score of 0.48 at 32 weeks. That is obviously an error if that is what was done, you can’t use weight z-scores calculated at 32 weeks for babies who were 35 weeks post-menstrual age!

The journal where this is published is not on my universities subscription list, and I had to wait a while to get the pdf via inter-library loans, which would be impossible if you weren’t part of a university; It also is not listed on Pubmed, and I can’t even get the supplementary appendix (to see what else is reported) without paying for it. Research funded by the Canadian Institutes of Health Research is supposed to be all publicly available, this currently isn’t. The CIHR rules are, unfortunately, not as stringent as the NIH, our rules are that within 12 months after publication, all research papers must be publicly available (either through the publisher’s website or an on-line repository). I think, as a side issue, that the CIHR should enforce immediate open-access of any research published using public funds (it would only add a few hundred dollars to studies costing tens, or hundreds of thousands of dollars or more). Both as a matter of good policy regarding the public’s capacity to read research that they funded, but also so that I can get a supplementary appendix!

In this study the parents in the FIC group (who started at slightly higher stress and anxiety scores than the standard care parents) had lower stress and anxiety scores at 21 days. Was that because of FIC, or because these parents were different to start with, or because of other factors in the NICUs that were in the FIC group? I wouldn’t be at all surprised if it was due to the FIC intervention…

What I am saying is this; integrating parents more in the care of their infants is a good thing. We should be ready to adjust our care models so that parents can do anything they want in the medical/nursing/respiratory care of their infants that is consistent with good safe practice. We should also avoid forcing parents to be “integrated” where they are not comfortable, not all parents want to be present during resuscitation, intubation, lumbar puncture and so on, and maybe some parents don’t want to write in the medical chart or present their infant during medical rounds.  But, for those who do, there are an increasing number of publications (many of them based on the initiatives of Karel O’Brien and her colleagues from Mount Sinai Hospital in Toronto,  such as this one from Glasgow in Scotland; Patel N, et al. Family Integrated Care: changing the culture in the neonatal unit. Archives of Disease in Childhood. 2018;103(5):415-9) which can give you interesting ideas about how to move forward,

Another recent publication shows that it is safe to have parents adjust the FiO2 of their babies (Martin-Pelegrina MD, et al. FiO2 control by parents of preterm infants admitted to a neonatal intensive care unit: A pilot study. Acta Paediatr. 2018) at least in a small pilot trial. After training the parents were allowed to adjust the FiO2, and the babies were less frequently hyperoxic, compared to controls.

This brings up another question I think, what do we need to know in order to change the culture in our NICU? I am not convinced, from these data, that FIC impacts weight gain; that does not stop me from wanting to make the NICU more welcoming, and more “integrating” of the parents of the babies I look after. It doesn’t stop me (and the rest of my team) from wanting to integrate many of the ideas of family integrated care into our practice at my hospital.

In fact, even if there was no difference between groups, and if, after eliminating Mount Sinai (the non-randomised center) from the results, and trying to correct for all the baseline differences between enrolled and non-enrolled parents, if after doing all that there was no impact on weight gain, or on other clinically important outcomes, then I would say that would be good evidence that we should be doing this.  We should be allowing the integration of parents into the day to day medical, nursing, respiratory, physiotherapy, and feeding intervention care of their babies in the NICU; with training and supervision, at least as much as they want, and as much as they are capable of doing.

We also as a side note (and not related to this study) must not judge parents who feel unable, unprepared, or uncomfortable in performing these tasks. As mentioned above, I am not sure all parents want to do all of the things demanded by FIC; that doesn’t make them bad parents. If I think of how I was as an (unusual) NICU parent 14 years ago. I could not have spent 6 hours per day in the NICU, it was a pretty boring place most of the time! In the beautiful new unit where I now work, with the amazing private rooms with parents’ spaces etc, I would probably have spent a lot of my time on my laptop, writing blog posts, while my baby slept. I would appreciate the power to stop residents and others (even occasionally nurses) from touching my baby without adequate hand hygiene, but I don’t think I could have tolerated being there for 6 hours every day. I am not sure I would even have wanted to have the right to change the inspired oxygen concentration. Even though with my patients I fiddle with the FiO2 and the ventilator settings all the time (just ask my RT’s who get very irritated at times!) On the other hand, 12 hours a day looking after 30 babies and their families is just fine…

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Just needle it! #NeoEBM

I didn’t post much about last year’s PAS (and I am not sure I will have the energy in future years either) there are often disappointments and surprises, abstrracts presented as platforms in important sessions that should not have been, and others that should have been given a platform that were hidden in a corner of a poster session. Organizing a huge conference like PAS, there are bound to be missteps like that, some of which are just differences of opinion, some of which everyone agrees to. Last year there was a really important, simple, randomized clinical trial that didn’t get the forum it deserved. But it has now been published in full, and it is a gem. Murphy MC, et al. Effect of needle aspiration of pneumothorax on subsequent chest drain insertion in newborns: A randomized clinical trial. JAMA Pediatrics. 2018.

Colm O’Donnell has a gift for asking simple clinical questions that can have big impact on practice. For example “can we really tell if a baby is hypoxic by looking at their colour?” The answer is clearly no, which is why we now place pulse oximeter probes as soon as we can during resuscitation.

This study was designed to ask another simple clinical question that has not been asked (or at least not answered) previously. “If a baby has a pneumothorax that appears to be symptomatic, do they need a chest tube, or can just draining it with a needle be enough?”

I was brought up in an era of neonatology (pre-surfactant) where inserting chest tubes was a nightly occurrence. We put chest drains in at least 25% of our ventilated babies, and often had to put tubes in both sides.

When I arrived in Edmonton as a fellow, the practice was to put a prophylactic chest tube in the contralateral side whenever we had a unilateral pneumothorax, because the incidence of contralateral pneumothoraces was so high, and the acute hemodynamic and ventilatory consequences of a pneumothorax were dramatic. So the thought was that you were better to prophylactically drain the other pleural space before it happened.

My co-fellow, Tony Ryan, and I studied all of our cases, and it was clear that if you had a pneumothorax on one side and if you also had Interstitial Emphysema (PIE) on x-ray, then the majority of babies did indeed develop a pneumothorax on the other side. For those babies who did not have PIE many of them never had a second pneumothorax, so we were able to avoid contralateral drains in those babies without radiologically evident PIE.

Since then, life has changed, for the better. Few ventilated babies now develop pneumothoraces, and the nights of putting multiple chest tubes in the same baby are a distant bad memory (I did get rather good at it though!).

In the new NORD trial the investigators from a multicenter group of NICUs randomized 70 babies with a radiologically confirmed pneumothorax if they had respiratory distress (intubated, CPAP or more than 40% O2). The study was performed with a delayed consent procedure, and infants either had drainage conventionally with an intercostal drain or needle aspiration as a one time only procedure, followed by waiting to see if they needed a chest drain.

It was my usual practice to insert a drain except in the most unstable babies for whom a needle aspiration might be performed first, usually followed immediately by a chest tube. In this trial, there were 33 infants randomized to needle aspiration 18 of them needed a chest tube within the next 6 hours, and 23/33 needed one at some time during hospitalization, presumably within the next few days. Which means that quite a lot of needled babies avoided having a chest tube, which I think is a significant benefit to them.

I wonder if, based on my previous experience, babies that had PIE visible on the chest x-ray would be more likely to need a chest tube. If you could predict which babies were most likely to need a later chest tube, maybe you could select them to have an immediate chest drain after needle aspiration. In the mean time based on this trial, needle aspiration of pneumothoraces should be the usual first procedure, if a baby stabilizes after needle aspiration we can just wait and see what happens.

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PAS 2018: the wrap-up.

A general comment about these PAS 2018 blog posts. I think we should be very careful about changing practice based on an abstract. We should respect peer review, with all its limitations, and we should always consider new research in terms of the quality of the trial, and how it fits in to the overall evidence base that already exists.

Sometimes there is little that already exists, and you could say, for example with the SAIL trial, that if you have already started using sustained inflations in the resuscitation of very preterm babies then you should reconsider your approach and probably stop doing it, at least as a routine. This was a high-quality trial with no real previous data on the overall clinical outcomes with sustained inflations in this population.

In contrast  for propranolol use in early retinopathy, there are previous data, but they are limited and of variably poor quality, and the quality of this new small trial is difficult to determine from the abstract. I think it would be a serious error to start routinely using propranolol in this population, there are a large number of unanswered questions, and potential risks. It is a trial that should be used to give support to a large multicenter RCT.

STOP-BPD is somewhere in the middle. A high quality trial with important clinical outcomes, and nothing quite similar in the literature, but there are many other trials of post-natal steroids and some other relatively similar trials going on right now. My response will be to wait and see, and try and analyse how this trial fits into the totality of the literature.

There were many other presentations that I found interesting at PAS. A study from Alabama with Colm Travers as the first author (1413.115) showed that it is possible to predict bradycardic episodes in preterm babies with apnea by training a neural network on previous heart rate patterns that preceded bradycardic episodes. Once trained the network could predict when the next brady was happening. I wonder how this would work if you looked at respiratory patterns, I remember some articles from the 1980’s (Waggener et al for each of them I think) where passing respiratory signals through a comb signal demonstrated multiple, otherwise difficult to see, respiratory pattern oscillations. When all the different oscillatory frequencies were at their lowest at the same time the babies had apneas. There may be some relationship between these 2 findings.

Peter Dargaville from Hobart, Tasmania, had several posters/presentations about automated oxygen control. One of them in particular (1413.112, first author Andrew Marshall) relates a little to my previous comment, they added a trick to their oxygen controller that immediately starts to increase the FiO2 at the onset of an apnea (or about 5 seconds later), rather than waiting for the infant to desaturate. Using this trick the periods of time when the infants were hypoxic was shorter. In manual FiO2 control the hypoxia lasted 30 seconds, with standard automated control it was 20 seconds, and with the added apnea-response element it was 12 seconds.This is a great trick, but I am not sure its the right thing to do. Obviously if you are not breathing, increasing the FiO2 isn’t going to do anything, so they are doing this to get the babies to re-saturate faster when they start breathing again. Is that what we really want? Release of oxygen free radicals during re-oxygenation might be worse if you reoxygenate faster, and increasing the FiO2 during apnea often leads to post-apneic hyperoxia, (I published an abstract about that several years ago, and there has since been a full publication from another group). In this study they calculated the number of seconds multiplied by the saturation percentage above target range, and there was more hyperoxia in the 60 seconds after the apnea when the new apnea-response element was switched on. I have thought about this a lot in the past, I think we should have studies looking at the best way to intervene for apneas, maybe the best way to intervene would be to immediately start assisted ventilation with the same FiO2 that the baby normal receives, but after how long? Does stimulation work (I think it probably does) and should we give a transient increase in FiO2 during recovery, or not? How can we reduce post-apneic hyperoxia? Anyway, this is a really interesting study showing you can integrate signals of respiratory activity into the FiO2 controller.

The lucinactant study group is pursuing its studies of aerosolized surfactant. Neil Finer and colleagues (abstract 2899.821) performed this blinded study looking at 2 different doses of lucinactant (40 or 80 mg/kg) in babies 28 to 32 weeks who were on CPAP for HMD. 44% of controls failed CPAP and 32% of those who received 80 mg/kg of phospholipids by aerosolization. More work to be done yet, but this is looking interesting.

There was a good observational study on premedication for intubation from the NEAR4Neos database (abstract 1414.123, first author Yuri Ozawa). It confirms what some of us have been saying for years. Not only is pain relief the humane thing to do for intubation, adequate therapy, that is “sedation” plus paralysis, makes the procedure more likely to be succesful on the first attempt and associated with fewer adverse physiologic changes. In this abstract “sedation” meant a sedative or a narcotic, which I think is a mistake. Non-analgesic sedatives should not be used for this procedure, and the authors should divide the data into analgesic or anesthetic regimes on the one hand, and sedatives (such as midazolam) on the other. In this study babies who received only “sedatives” were worse off, with fewer 1st time successes and more desaturation. An observational study to be sure, so interpret with care.

I guess I could continue for a while, there was a lot of resuscitation research, for example, including several projects presented from Edmonton, in simulation, in animal models and in babies. If you go to the website and search for Georg Schmolzer under presenters you can find those. There were many interesting things about the microbiome in preterm babies also, under the “program” heading you can filter for microbiome, you will get 67 hits, but then finding the preterm stuff isn’t difficult.

I can’t see how to place a link directly to any of the abstracts, https://www.xcdsystem.com/pas/program/2018/ is the best I can do; this URL will take you to the welcome page, and you can then find the abstracts if you know the presentation number by clicking on program, then “filter” then typing or pasting the presentation number if you know it.

 

 

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PAS 2018 No7: Protecting tiny noses

#NeoEBM My blog posts are automatically tweeted. A group of twitterers got together at PAS and suggested that this hashtag should become a marker of neonatal Evidence Based Medicine posts. Great initiative! Now I have to find out how to do this…

Peter Davis was, as usual, omnipresent in the neonatal clinical research arena of PAS. You wouldn’t know that from the App but try searching for him on the website and you will find 15 abstracts on which he was an author. Interestingly though, you won’t find the MIST/LISA workshop that Ahmed Moussa from our hospital organized, and which is the only hit on the mobile App.

As I have for all of these posts, I have had to use both the website and the mobile App to write this one.

One of these abstracts trials is a modestly (but adequately) sized randomized trial of using hydrocolloid dressings to protect the noses of babies on CPAP who were less than 1250g birth weight or less than 30 weeks. Just over 100 babies were enrolled, and the incidence of nasal injury was substantially lower using the dressing (34%) than not (56%).

You can’t see the remainder of the results on the website as they are in tables that are invisible. But on the mobile App you can see that the demographics of the 2 groups were similar and other outcomes such as BPD and duration of CPAP were the same.

This is how the dressing was cut and applied with the use of Hudson Prongs.The illustrations are also not visible on the website, and you have to download them to see them on your phone, but then if you are very clever you can email them to yourself, and insert into a blog post! Many of the babies had their noses photographed in order to have an independent evaluation of the cuteness of the noses, or maybe it was to examine the nasal injury.

The big problem with this trial is the acronym, which is not as imaginative as we expect from Melbourne. PRONOSE is easy to remember, and tells you what the trial was about, but is that really what we want from an acronym?

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