Maureen Hack’s contributions to neonatology, or at least, some of them.

Since the death of Maureen Hack last week, I have been thinking a little about some of her important contributions to neonatology. In part because whenever I present, or write, about the prediction of outcomes in very preterm babies, I include a table from one of her publications. (Hack M, et al. Poor Predictive Validity of the Bayley Scales of Infant Development for Cognitive Function of Extremely Low Birth Weight Children at School Age. Pediatrics. 2005;116(2):333-41.)

Bayley MPCWhat Maureen and her team did was to compare the scores on the mental development Index (MDI) of the Bayley Scales of Infant Development version 2 at 20 months of age in a cohort of 200 very low birth weight babies, to the scores on the Mental Processing Composite (the MPC in the table) of the Kaufman Assessment Battery for Children performed at about 8 years of age. The MPC is a test of cognitive function. The Bayley MDI is often referred to as a test of cognitive function also, and children with a low score are often referred to as “cognitively impaired” which is a terminology which drives me bonkers as it is very inaccurate. As this table shows better than anything. Children with a 20 month Bayley MDI more than 2SD below the mean, that is less than 70, only 1/3 of the time had low scores on the MPC. The results also show that infants with neurological impairments and a low Bayley score were more likely to have a low MPC at 8 years than those without.

Very very few children (3) who were above that threshold at 20 months had poor cognitive function at 8 years. Which I think shows the real, limited, value of performing a Bayley at this age, as a test to identify infants who may need intervention, and conversely, those who will probably do just fine.

You can see the difference in the proportion of infants of VLBW who are defined as having a problem from the total percentages of low scores: at 20 months of age using the Bayley 2 MDI, 39% had low scores. At 8 years of age it is only 16%. Which has huge implications if you think that “cognitive impairment” is important, which I think most of us do.

Maureen was also one of a small group of investigators who have followed very premature babies out to adolescence and adulthood, and have also included a control group. One of the many striking publications from her cohort, born in 1977 to 1979, was this one, (Hack M, et al. Outcomes in young adulthood for very-low-birth-weight infants. The New England journal of medicine. 2002;346(3):149-57.) The VLBW subjects, were functioning very well in general, most having finished high school (66% of boys and 81% of girls) somewhat fewer than the controls (75% and 90%) and another 9% of the VLBW boys and 5% of girls were trying to get high school equivalency certificates. Many were in higher education, although fewer than the controls.

One of the things that I found most striking in her data, was the social deprivation of the group that Maureen was studying, one part of the evidence of that was the rate of incarceration of both the VLBW and the controls. 26% of each group had been in jail or youth detention at some point (including overnight). In addition VLBW boys were less likely to have actually broken a law, VLBW girls were less likely to be sexually active, and both sexes were less likely to have taken illegal drugs.

One of Maureen’s older studies that I think is still very pertinent is from 1989, (Hack M, et al. Differential effects of intrauterine and postnatal brain growth failure in infants of very low birth weight. American journal of diseases of children. 1989;143(1):63-8). She showed that VLBW infants who had postnatal growth failure, especially in terms of head growth, had substantially worse outcomes, and this was not necessarily the case for VLBW infants who were growth restricted at birth. Which points out the importance of good postnatal nutrition, aimed at ensuring good head growth.

Maureen and her group enrolled and studied  another cohort, this time of extremely low birth weight infants (<1000g) born in 1992 to 1995.

Litt JS, et al. Academic achievement of adolescents born with extremely low birth weight. Acta Paediatr. 2012;101(12):1240-5. The average IQ in adolescence of the ELBW infants was 87, again the importance of a matched control group was demonstrated by this study, the controls had a mean IQ of 96. There were many more mathematics learning disabilities in the VLBW infants, and more executive function difficulties. Many more required special assistance at school. Hack M, et al. Self-Reported Adolescent Health Status of Extremely Low Birth Weight Children Born 1992-1995. Pediatrics. 2012. The overall self-reported health status of the ELBW adolescents was very similar to the controls. There was less risk-taking behaviour, and less physical activity, but overall they were doing well.

Finally (and I could do this for a while, but I am just picking out a few of what I think are highlights, there are many others that someone else might choose instead): Wilson-Costello D, et al. Improved Neurodevelopmental Outcomes for Extremely Low Birth Weight Infants in 2000-2002. Pediatrics. 2007;119(1):37-45. This study compared the 20 month outcomes of ELBW infants during 3 different time intervals, the 80’s, the 90’s, and 2000-2002. The survival improves progressively reaching 71% in the 3rd period. Neurodevelopmental outcomes improved also, the “neurodevelopmental impairment” was lowest in the latest cohort.

I have decided that from now I on refuse to use that term. I will call it neurological impairment and developmental delay, NIDD.

In this publication, the rate of NIDD fell from 35% to 23%, developmental delay did not change much, the MDI scores were similar, but there was less cerebral palsy and less deafness and blindness. The study didn’t use the GMFCS system, but states that they only included moderate and severe CP. I think using the term impairment for CP, deafness and blindness is appropriate, (although including hypertonia and hypotonia might inflate the numbers a bit) they tend to persist, although the diagnosis of CP might occasionally change, and they satisfy WHO definitions of “impairment”. Low Bayley scores are not an impairment, overall 2/3 of the infants will not be impaired on later cognitive testing, as Maureen showed.

The largest component of the NIDD is low Bayley scores, 21 of the 36 infants with NIDD in this study met the definition because of a low MDI. We can therefore estimate how many will still be considered impaired at 8 years of age. As I noted above, infants with a low Bayley score who did not have a neurological impairment were more likely to have higher scores on the 8 year MPC. Only 9 of the 45 infants  with a Bayley2 MDI less than 70 but who did not have a neurological abnormality had an MPC of under 70 in the 2005 article from Pediatrics at the top of this post, and could be considered to have a cognitive impairment.   If that still holds true (and there is other evidence that it does) then the total frequency of neurological or cognitive impairment of this group at 8 years will be about 12%.

How can we further reduce this proportion? Maureen also studied the impacts of sepsis, of necrotizing enterocolitis, of postnatal steroids, and of bronchopulmonary dysplasia, and confirmed their negative impacts on outcomes. Reducing the incidence of those complications, and improving postnatal nutrition and growth will reduce their negative effects on NIDD, and eventually on NCI.

Thank you Maureen, farewell.


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Death In Simulation

Our group at Sainte Justine has just published an article, now available on-line in Pediatrics. (Lizotte M-H, Latraverse V, Moussa A, Lachance C, Barrington K, Janvier A. Trainee Perspectives on Manikin Death During Mock Codes. Pediatrics. 2015) We had originally called the article “Should the manikin die during mock codes?” but the editors didn’t like the question in the title.

The basic idea was to try and deal with one of the unrealistic characteristics of mock codes, which is that usually, during a simulated resuscitation scenario, if you follow guidelines and act correctly, the patient gets better. So if you follow NRP standards, the heart rate will come back, the patient will improve and you send them on to the NICU.

In real life, not always.

We are teaching trainees to have unrealistic expectations of the responses to their interventions. This has been addressed theoretically before, but I don’t think anyone has doe what the team here did, which is to evaluate how caregivers respond when the manikin dies, even after they have done everything correctly, and what they thought of the experience. A simulated baby was born pulseless, and residents were randomized to either have a baby that responded to NRP interventions, or one that did not, and remained pulseless. They were then exposed to the other scenario.

Firstly, we found it was difficult for people to stop, NRP teaches that after 10 minutes of asystole, once you have performed the appropriate steps, you should stop resuscitation, as survival is extremely uncommon. Many of our participants were still trying to resuscitate after 20 minutes (at which time the scenario was shut down).

Our participants were surprised that the manikin died, after they had done things well. They thought they must have made a mistake or missed something. They also appreciated the experience and thought they had learned something valuable, and did not want to have a “death disclosure” warning them before the simulation that the manikin might die. Even though they found the death of the manikin to be more stressful on a subjective stress scale.

I think occasional death of a manikin during resuscitation scenarios should be the norm. Residents and other trainees could learn that good interventions don’t always lead to good outcomes, about how to deal with stopping an unsuccessful resuscitation, and most importantly, how to deal with the family. Although it would make the simulation much more difficult and expensive than just an “NRP drill”, having a simulated mother and/or father could be a very valuable learning experience.

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Re-re-re-visited (delayed cord clamping of course)

I received 2 comments about the last posting re: DCC. The way I set up this blog the comments aren’t necessarily very obvious, especially if you visit the home page rather than following a link to the individual posting. So I will sometimes copy parts of a comment into a new post. I will certainly never do that to criticize or embarrass anyone, just to try and further a discussion.

First a comment from Wally Carlo, who noted that Judith Mercer had an abstract at the PAS meeting reporting outcomes from a moderately large RCT of DCC. I didn’t put any data from that study in my analysis, because I don’t have the actual numbers, so I only put published articles in the Forest plots. But to clarify: Mercer’s study enrolled 208 babies under 32 weeks and basically showed no short term differences. The abstract doesn’t mention mortality, which makes me think that wasn’t significant either, but there were specifically no differences in IVH, or sepsis.

The other comment was from Michael Hewson, and I quote some of it here

It could be getting difficult to continue with the APTS trial enrollment after explaining to parents that in the data available so far delayed cord clamping reduced mortality and NEC by at least 50% (admittedly there is a 2.5% chance of obtaining such dramatic benefits by chance alone). It’s true that more data would be great, that we don’t have enough long term outcome data, and that APTS could theoretically swing the pendulum in the other direction (like INIS or BOOST) but still how to look past the existing delayed cord clamping data, including the physiological evidence?

There seems to be a tricky no mans land that is reached after the point of equipoise has been passed but before widespread acceptance of a new intervention… therapeutic hypothermia also springs to mind.

I think those are important points, both the specific point about this issue, and a general point about how much evidence is enough.

The summary statistics of the data that I selected for my Forest plots (I must emphasize that this is not an ‘updated systematic review and meta-analysis’ it is me trying to summarize what I think are the relevant data), show a difference in mortality which is actually between 6.8% in controls and 4.3 % with DCC. That makes the risk difference 0.025, with an NNT of 40, 95% CI of 20 to infinity. The p-value for the mortality difference is 0.11, which is not a 2.5% likelihood of being due to chance.

For trainees and others everywhere, what this p-value means is that random selection of 2 groups of patients from the population of very preterm infants would show differences as great, or more extreme, 11 times out of 100.

Now I don’t think that’s enough to be sure that this procedure is safe, let alone advantageous. I think it is probably safe, the likelihood of significant harm seems quite low from the data that have been collected so far.

The difference in NEC is 7.4% in the controls, and 3.8% with DCC, among the studies that reported the outcome, there were many studies that did not report NEC, so there are only 30 events in total, among over 500 babies in the trials with this result. But if we assume that those that didn’t report NEC did not have any (which is a dangerous assumption, but many of those trials were larger babies who were at lower risk), then the difference is between, 3.9% and 2.0%, or a risk difference of 0.019, and an NNT of 52, 95% CI also include infinity!

The p value for the difference, using the trials that reported NEC which I put in the meta-analysis,  is 0.09, far from what we usually consider to be significant, and again not a 2.5% likelihood of being due to chance, but much more than that.

If someone was to do a Jesper Brok style sequential analysis (Brok J, et al. Apparently conclusive meta-analyses may be inconclusive—Trial sequential analysis adjustment of random error risk due to repetitive testing of accumulating data in apparently conclusive neonatal meta-analyses. International Journal of Epidemiology. 2009;38(1):287-98.
which I have neither the time, the expertise, nor the software to do), I can bet you that it would be far, far away from a significant result.
We’ve been here before, as is mentioned in this comment, based on multiple small studies, IVIG seemed to reduce mortality in septic newborns. INIS showed absolutely zilch. Fortunately there was no prior evidence of harm in the IVIG studies before INIS, and that trial also confirmed that there was no harm.

I appreciate the comment about the importance of making sure parents are well informed of the current state of the literature when getting consent to enroll them, that is of course essential, and these things can be difficult to explain, but I would insist that it is by no means clear that the differences in mortality or NEC are really due to the DCC. Hopefully enough parents will agree that this is an important question to answer, and will consent to randomization. I think if a parent, presented with this information, requested DCC (or requested immediate clamping) there would be no good reason for denying it. If you are set up to do the study then presumably you have equipoise, so organising a DCC should be no problem.

As there is no “trend” towards harm in any of the outcomes presented, and babies who have DCC need less blood in most of the studies (but interestingly not in that study by Judith Mercer, the hematocrits, at least, were no different between groups) I think it is unlikely that we are harming babies with DCC, but there really isn’t yet any reliable evidence of any benefit other than a possible reduction in blood transfusion. Most of that data of course comes from more mature preterm babies; for us to ensure that this is really safe, and that there are real benefits for small preterm infants, requires us to finish large studies if we at all can.

I think the example of the hypothermia studies is not a clear parallel. It became difficult to randomize after the publication of two large high quality multicenter trials, after the 3rd was published I was of the opinion that the other studies should stop, and that it was no longer appropriate to continue to randomize patients. We are far from that situation with DCC in the very preterm baby.  Even one well done, large multicenter trial, if it showed no harm, and clarified what the real benefits might be, could be enough to appropriately change practice everywhere.

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Very Sad News

Maureen Hack has died.

Apparently she died earlier today. Although several years past a usual person’s retirement age, Maureen was still a towering, (metaphorically) and very active figure in neonatology, her follow up research, and her insights were very valuable for all of us.

I remember her as someone who was easy to talk too, interested and interesting, who made contributions to neonatology which will be quoted for a very long time, and who was humble enough to be open to new interpretations of her results as her subjects aged.

Maureen showed that extremely low birth weight babies mostly functioned very well as they entered adolescence and adulthood. She showed the importance of having a good control group from similar backgrounds to the preterm subjects. She showed more clearly than anyone else at the time how much test scores improve over time for the majority of preterm babies who have developmental evaluations in the first couple of years.

She will be sorely missed.

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Keep people like this away from the NICU

After my novel-length post earlier, a quick rant.

In the few weeks since the NICHD ‘before 24′ paper came out there have been a number of newspaper articles reporting the results, and responses to them. A report in the National Post included some comments made by an “ethicist” by the name of Arthur Schafer who for a long time apparently was an advisor to the Winnipeg neonatal group** UPDATE** see the comment from Molly Seshia after the post**. I can only say I feel sorry for them. His comments show a lack of understanding of the issues and a deep misunderstanding/mistrust of modern medicine, not a good combination for a bioethicist:

“Relying on gestational age to judge the viability of a preemie may be inexact and arbitrary – like setting a speed limit or legal drinking age – but it does provide some useful guidance”, argues Arthur Schafer, head of the University of Manitoba’s Centre for Professional Applied Ethics.

What a ridiculous analogy. Keeping to the speed limit won’t kill you, waiting until you reach legal drinking age won’t kill you either. And you can tell pretty accurately how fast you are going, most of us know how old we are.

“Some of the time I had to struggle to suppress the thought ‘How unlucky for these families that their child was born with access to an NICU,'” he says.

“Wouldn’t they have been more fortunate if they had been living in a remote area … where the baby would have died instead of being put through days and weeks of intensive, high-tech medicine, with virtually no chance of surviving, or surviving without overwhelming impairments.”

What a disgusting thing to say. Would he dare say that to parents of a child with leukemia? Or a child who has just been badly burned or hit by a bus? I wonder if he might be more fortunate to be living in a remote area when he gets his stroke.

How unlucky for the babies in Winnipeg that they were born with access to a bioethicist like this.

He clearly has no idea what the actual results of NICU care are. “virtually no chance of surviving, or surviving without overwhelming impairments”? What on earth is he talking about?

Even more unfortunate, we sometimes hear neonatologists say similar things, and they have said them again since that article was published. Seriously, if you think your patients would be better off being born without access to an NICU, you should get a new career. We need neonatologists who will advocate FOR their patients, and not against them.

Posted in The CPS antenatal counselling statement | Tagged , , | 4 Comments

Delayed Cord Clamping re-re-visited

I have been trying to develop some sort of protocol for babies in our center, so I have been reading in some detail the studies about very preterm births and cord clamping that are in the literature. It seems from the PAS meeting that everyone is jumping on the bandwagon, hence my detailed inspection of the trials (and the Cochrane and other systematic reviews), because we are thinking of jumping on too, to make sure that we are going to do the right thing.

I created a couple of tables with some of the details of the studies that have been done, both those in the Cochrane review, and some done since the review. These are the studies of delayed clamping (further down are the studies of cord milking):

Nom N GA Delay (s) Position
Hofmeyr 38 <35 60
Hofmeyr 1993 86 expected to be <2 kg 60-120 At level of uterus
Ibrahim 32 24 to 28 20 At level of introitus
Baenziger 39 24 to 32 60-90 As low as possible
Chu 36 24 to 32 30-45
Kinmond 36 >27 to <33 30 20cm below introitus
Kugelman 65 >24 to<35 60-90 20-30 below introitus
Mcdonnell 46 26 to 33 30 Between mother’s legs
Mercer 32 <32 30 to 45 10 to 15 inches lower than placenta
Mercer 72 24 to 32 30 to 45 10 to 15 inches lower than placenta
Nelle 19 <1.5 kg, c/s only 30 30 cms lower than placenta
Oh 33 24 à 28 30 à 45 10 cm below introitus
Rabe 40 <33 45 Below the placenta
Elimian 200 24 to 34 30 + cord milking, x 3 to 4 “not below the introitus or on thetable”
Gokmen 42 24 to 32 30 to 45

As I was analyzing the studies, I found a number of disturbing issues, for example the study by Aladangady states that they did not report any clinical outcomes, the study by Baenziger also reported none, they both appear to have been part of a large multicenter trial of delayed clamping in the preterm, which has never been published. Which is outrageous. How can anyone morally perform a randomized intervention trial in a high risk population (or any population), and then not report ANY clinical outcomes, not even whether the “subjects” survived or not? Where are those data? These studies were from before registration of RCTs, so I haven’t been able to find out who has the data of these high-risk babies, who were randomized in an international RCT, and never published. Please, if anyone knows, the trial publication amnesty would make it easy to publish these extremely important data.

There were 2 studies in the Cochrane review that I think we can disregard: the study by Strauss et al was a study for babies under 36 weeks, but those under 30 weeks were not randomized to DCC nor to cord milking; the intervention group <30 wk was an attempt to obtain placental blood by needle puncture of the placental vein, after immediate clamping and place in a transfusion bag for later infusion. They weren’t actually able to do this in any of the babies in that group except 1. So I think we can reasonably leave their data out of a very preterm baby review. Ultee et al only randomized late preterm babies 34 to 36 weeks, and the controls had a 30 s delay anyway, so it was really a comparison of DCC and very DCC. Heike Rabe’s study was also a comparison between 20 and 45 seconds of delayed clamping, although it included babies <33 weeks, with no stated lower limit, so it is a comparison of moderately DCC to DCC.

We are therefore left with the other studies and can add two other, newer, RCTs not in the Cochrane review, Elimian and Gokmen, which add a total of 242 babies.

In almost all the studies the average gestational age of the babies was between 29 and 32 weeks. So there are few very preterm babies in these trials.

One of the studies included in the Cochrane review was not clearly randomized (Nelle et al is only reported as an abstract from the ESPR, and does not mention randomization). Others had outcomes which I think the Cochrane has tabulated incorrectly. For example the NEC outcomes reported from the Oh trial are for stage 2 or 3; but the numbers from the 2 Mercer trials and included in the Cochrane review, were actually the numbers for “suspected NEC” meaning, basically, any baby who had an abdominal x-ray. The numbers for actual NEC are in the publications, but harder to find, and not so clearly defined, also the numbers of NEC cases in the second Mercer trial are not consistent, the number in the DCC group is 1 in their Table 3, but 2 in Table 5. I have put the numbers for stage 2 NEC or worse, and used the figure of 2 cases from Mercer’s 2nd study. Also I am not clear of the numbers from the McDonnell trial, the paper states that 43 “cases” were randomized, which might have been mothers or babies (it is one of the few trials that includes twins, and there were 4 sets of twins, but data are very scanty in the publication).

Other systematic reviews don’t come out of this scrutiny any better, The review by Backes includes data from the NICHD pilot trial twice, including the IVH rates from the abstract as well as from the final publication, they also use the same numbers from that abstract for total IVH and for severe IVH, and use an incorrect denominator for the late onset sepsis rates from that study. The meta-analysis by Ghavam et al, which is restricted to extremely low birth weight infants presents the “number of blood transfusion” (sic) which is reported as 79 vs 70 with a weighted mean difference of 2.22. What on earth does that mean? That review noted the paucity of data from the ELBW, and the consequent lack of power for any important outcome. They found extremely limited data regarding neurological/developmental outcomes, which showed no difference.

One final problem with the data, the Hofmeyr study was published in the “online journal of Current Clinical Trials” which was one of the first on-line journals, set up by the American Association for the Advancement of Science. It lasted about 2 years, and then disappeared, in about 1995, with no arrangements being made to have an archive available. Which is also outrageous. Published data from RCTs which included sick patients are no longer available. Surely the AAAS could deposit them in Pubmed Central? Surely they have a moral responsibility to do so.

For cord milking, the studies are outlined in the next table:

Nom N GA Méthode
March 75 24 – 28 Milking x 3 before clamping
Alan 44 <32 Milking x 3 before clamping
Hosono 40 24 – 28 Milking x 2-3 before clamping
Katheria 60 <32 Milking x 2 before clamping

As you can see, 2 of these studies were restricted to very preterm babies, with average gestational ages around 26 weeks, the others with average GA around 29-30.

For each of these studies the cord milking required some delay in clamping also, as the cord was milked 2 to 3 times, often with a description in the papers of how fast to milk, meaning that cord clamping was delayed for probably around 10 to 20 seconds in many of these studies. There is therefore some overlap, especially with the study of Elimian, 30 seconds of delay with 3 to 4 “milking’s”.

Finally to construct the figures that I am including here, I included the data from Ibrahim et al, that the Cochrane review excluded because the delay in clamping was only 20 seconds, and it therefore didn’t meet their criteria. The hematocrit and transfusion results do suggest that those babies got a significant transfusion, so I decided to put them in here. I couldn’t find any numbers for grade 2 NEC or severe IVH, only for mortality; it is also the only delayed clamping study restricted to very preterm babies, other than Oh et al, and their mean GA was 26.5 wks in the 2 groups.

This is the Forest plot for mortality

Forest plot mortality

So 1000 babies randomized, all in very small studies, one which is slightly larger.  The babies were largely at low risk of mortality, so the number of actual events, is tiny, and the difference between the groups could easily be due to chance, especially when you add the potential for an inflation of type 1 error with multiple small studies.

Severe IVH:

Forest plot severe IVH

The differences are in the direction of fewer hemorrhages with DCC, but a substantial chance that they are due to random effects.

Stage 2 or 3 NEC :

Forest plot NEC

So again, tiny numbers of events, and differences which could be due to chance.

So why all this rush to delay cord clamping in the very preterm infant? I really don’t understand the ACOG opinion. They have it entirely the wrong way round. They state that the benefits in term infants are not clear,

insufficient evidence exists to support or to refute the benefits from delayed umbilical cord clamping for term infants that are born in settings with rich resources. Although a delay in umbilical cord clamping for up to 60 seconds may increase total body iron stores and blood volume, which may be particularly beneficial in populations in which iron deficiency is prevalent, these potential benefits must be weighed against the increased risk for neonatal phototherapy.

But Iron Deficiency is prevalent everywhere, the exact incidence depends on your definition and the population. But, in the US it is between 7 and 21% in toddlers according to a recent review. With our current more restrictive phototherapy use, I can’t see any downside really for doing this as a routine in term infants. One of the best term studies, by Ola Andersson and colleagues was performed in Sweden in the recent era, and had about a 1% rate of phototherapy, not different between groups. He has also just published 4 year follow up of the infants in the study, showing some developmental advantages in the DCC group.

In contrast, given the weakness of the evidence, their committee opinion for preterm babies is wrong in the other direction.

However, evidence supports delayed umbilical cord clamping in preterm infants. As with term infants, delaying umbilical cord clamping to 30–60 seconds after birth with the infant at a level below the placenta is associated with neonatal benefits, including improved transitional circulation, better establishment of red blood cell volume, and decreased need for blood transfusion. The single most important clinical benefit for preterm infants is the possibility for a nearly 50% reduction in intraventricular hemorrhage.

I think the evidence of benefits of cord clamping for any clinical outcomes is highly questionable in the very preterm, and given the fragility of these patients we really need good quality large studies, powered for clinical outcomes. Which are fortunately being performed, the APTS trial is planned to include 1600 babies under 30 weeks gestation.

In the meantime, what to do while waiting for the results of adequately powered trials? The one benefit of delayed clamping or milking, which I think is clear, is that the babies have a greater red cell mass after either procedure. Which leads to fewer transfusions. The transfusion outcome has not always been reported in the same way, so its not easy to do a meta-analysis, but I think it’s fairly consistent, almost all of the trials have shown a reduced need for transfusion, either the total volume required, or the proportion of babies transfused, and so on. That, in addition to the lack of harm shown in the studies, and the physiologic rationale suggests to me that it is reasonable to institute DCC (or milking) while waiting for the large RCT results. I think we need to continue surveillance of adverse outcomes after instituting DCC, including a watch on admission temperatures, especially for the most immature babies, but those have not been adversely affected to date.

Figuring out how to resuscitate babies during DCC is an interesting idea, but given that the  evidence of benefits of DCC could only be considered marginal as yet, I am not rushing to buy a special table.

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Should we resuscitate children?

I am going to be deliberately provocative today… for a change.

A very interesting study from Japan has reported the results of out-of-hospital cardiac arrest in children. Goto Y, et al. Decision tree model for predicting long-term outcomes in children with out-of-hospital cardiac arrest: a nationwide, population-based observational study. Critical Care. 2014;18(3):R133. (open access). They have a national database which records the phenomenon, and the outcomes. The authors report the survival and the survival with a good cerebral outcome at one month using the following scale

Cerebral Performance Category (CPC) scale: category 1, good cerebral performance; category 2, moderate cerebral disability; category 3, severe cerebral disability; category 4, coma or vegetative state; and category 5, death

I think it is a very well done study, with a large cohort of patients that they used to make a prediction model, and another large cohort used to validate the model, which showed that the model gave consistent results. The meat of the initial results are in this figure.


1 month survival with reasonable cerebral outcome was between 3.5% and 4.5%.

You probably can guess what is going to come next: that is far worse than the survival with reasonable cerebral outcome of 22 week gestation babies. So if we were to apply the same logic to children that is invoked for extremely preterm infants by many perinatal societies, you should never offer resuscitation to children experiencing a cardiac arrest out of the hospital.

Which would mean of course that survival would go down to zero, which would prove that we were right.

Rather than say that, the authors examined predictive factors to see which were associated with a higher likelihood of a good outcome. cc13951-3

As you can see, if a child has an unwitnessed cardiac arrest, it extremely unlikely that they will have a good outcome, whereas,  after a witnessed arrest, a return of circulation before arriving in the ER has a relatively good outcome. The authors of the article discuss what they refer to as TOR (termination of resuscitation) and note how tricky the decision is in children. In the discussion they note the following:

If a child with unwitnessed OHCA is transported to the hospital before ROSC, even an adult-oriented physician can immediately understand that the child will have a very poor outcome and can counsel the family on whether to terminate the futile resuscitation. On the contrary, if a child has prehospital ROSC together with an initial shockable rhythm, the physician can immediately expect survival with a favorable neurological outcome and should perform resuscitation with advanced life support according to accepted guidelines.

Which sounds entirely reasonable to me, and I think is analogous to what we should do with extremely immature babies: we should gather all the useful prognostic features (not just the gestational age in completed weeks!) and use that to counsel parents about whether to institute or limit resuscitation. In cases where outcomes are more likely to be positive, the default should be to institute active care and re-evaluate. In situations where the expectation of a good outcome is very poor, there should be an evaluation of the parents values and desires and a shared decision.

I don’t know of any situation in neonatology which approaches the level of futility shown in this study for children with an unwitnessed arrest, it is possible that a best guess gestational age under 22 weeks in a boy who weighs under 400 grams might have a survival with good outcomes of less than 0.7%, but we don’t have enough numbers to know.

I don’t think we can actually calculate prognosis accurately enough to have precise thresholds for “futility”, nor do I think we should have externally imposed limits of predicted good outcomes that should be applied to all families. So I would be very wary of trying to define the terms I just used, “outcomes are more likely to be positive” and “expectation of a good outcome is very poor”. Trying to put a numerical limits to those phrases risks replacing one simplistic rule with another: less simplistic, more rational perhaps, but also with the risk imposing the values of one group on another family.

I’m sorry folks, but there are no simple rules. Or at least, there should be no simple rules. Life is hard, life and death decisions for others are even harder.

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