Late Surfactant may not be effective, probably.

Posted on 29 October 2015 by Keith Barrington

A large multi-center trial (n=511) led by Roberta Ballard has just been published. (Ballard RA, et al. Randomized Trial of Late Surfactant Treatment in Ventilated Preterm Infants Receiving Inhaled Nitric Oxide. J Pediatr 2015.)

In this trial infants had similar enrollment characteristics to the NOCLD trial; babies were between 500 and 125o grams birthweight and less than 32 weeks gestation. They had to be receiving assisted ventilation. There were the following differences to the previous study I alluded to: in NOCLD infants were 7 to 21 days, in this trial 7 to 14 days; in NOCLD the smallest infants could be enrolled if they were on CPAP; not in this trial, everyone had to be intubated and ventilated.

The idea was, that infants with persistent respiratory distress after a week of age have evidence of surfactant dysfunction, so perhaps if we gave them more functional surfactant they would be able to overcome this, and then have reduced lung function abnormalities, would be able to breathe more efficiently and would end up with less lung injury. There are a couple of pilot studies showing short term improvements in pulmonary function and gas exchange in very preterm infants who were still getting respiratory support at a week of age, and who received surfactant. So the investigators thought that a big RCT to examine clinically relevant outcomes was warranted.

Which I think is fine. This was a reasonable question to ask, and a reasonable, clinically important, outcome to investigate (especially with a local treatment very unlikely to have systemic adverse effects). Given the previous data on inhaled NO in a very similar group of babies (in whom a secondary analysis suggested that the earlier part of the postnatal age group, i,e, 7 to 14 days, was more effective) you can’t fault the investigators for using iNO in all the babies. Even if the, as yet still unpublished, NewNO trial did not show a benefit.

All the babies were getting inhaled NO, according to the NOCLD protocol. The surfactant was randomly given to half of the babies.

But I can’t tell you how much surfactant was given, or with what frequency. A major problem with this report of the study is that I can’t figure out exactly what was the intervention. Which is a big problem. The investigators went to great (and probably unnecessary) lengths to mask the procedure, with a separate team, not otherwise involved in clinical care, who gave the surfactant (or didn’t) into the ETT behind screens. But they don’t actually say what dose was given.

Babies in the study got a dose of surfactant (or a sham procedure), as I said, the study report doesn’t even say how much they got (it was “standard clinical doses”) or how often they got it (it was every 24 to 72 hours if they remained intubated, starting at 48 hours after the first dose with a maximum of 5 doses; but 24 to 72 is a huge range…), they don’t say what were the criteria for retreatment, or for not retreating and extubating etc. There are several guidelines presented for steroids, for re-intubation etc, but not for surfactant/sham administration.

Table 3 of the results does show that about 80% in each group got 5 doses (of either surfactant or standing behind a curtain).

There was no benefit shown. Nothing, not even a whisper of a hint of a benefit. Which is disappointing, but at least seems at first look rather definitive. Or at least it would be definitive if we knew what the intervention group had received.

Even though surfactant dysfunction is a real problem in these babies, giving them additional Infasurf, according to this uncertain schedule, isn’t sufficiently effective to improve their outcomes.

This does, I think, help to improve care, (as there is no longer any stimulus to give surfactant to babies at this age) but it would have been much more useful, after what is probably several million dollars of investment, to know exactly what was done.

All we know is that, giving some dose of surfactant (Infasurf) and giving, mostly, 5 of those doses,  didn’t reduce BPD or death with a certain degree of confidence (see below).

To return to a comment I made above, why did I say that the sham procedure was unnecessary? Masking the intervention has become an essential feature of neonatal (and much clinical) research in order to get good funding; however, there is actually little empirical evidence that blinding/masking the intervention makes much difference to the size or direction of the effect of an intervention, particularly if objective outcomes are being studied. Diagnosis of BPD, if the ‘physiologic” definition is being used, is relatively objective, and is unlikely to be influenced by knowledge of an intervention performed several weeks earlier.

I think, if it is relatively easy, and relatively inexpensive, to mask an intervention (such as an orally administered drug, for example) then go for it, there is often no good reason to not do so. But having an on-call surfactant or sham administration team, who will go through the ritual of masking used in this study, will have enormously increased the cost. They could have studied twice as many babies (I guess) for the same cost, and have a much better estimate of the size of the effect, or of the confidence with which we can eliminate a benefit or risk. Many of the original surfactant trials for treatment of HMD were masked, in a similar fashion, but not all. There is no clear difference in the estimates of efficacy between those that were masked and those that were not.

Which brings me neatly to the final comment, the study was stopped by the DSMB, because “based on a determination that the study treatment is very unlikely to demonstrate efficacy” they didn’t think they should continue. They actually made this determination when they had the outcome data of 301 infants. There is a lot of debate about stopping trials early for futility, one paper in Critical Care (freely available on-line) is actually a real debate. But I am a bit mystified in this case, when the decision to stop the trial was taken they had actually randomized 511, of the planned 524 babies. One of the justifications for early stopping for futility is that it saves wasting money. That clearly isn’t an issue in this case. But even with all the data from 511 babies available there is still major uncertainty about whether this intervention is actually futile; the 95% CI for death or BPD include a 25% increase or decrease in that outcome. Which is huge, and clinically important. A 25% reduction (or increase) in death or BPD is something I would be interested in.

When the DSMB recommended stopping the trial they only had data from 300 babies, which means the confidence for saying there is no benefit (or harm) was extremely lacking in, er, confidence. Depending on how you calculate it, (assuming that the groups both had a 40% incidence of death or BPD at that point) when they stopped the trial showed that the likely real difference in that outcome was between about a 35% increase or decrease in risk of death or BPD. The sample size for the study was based on a hypothesized 13% change in the incidence of “death or BPD”, so why would the trial be stopped early when the confidence intervals included the hypothesized difference?

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When should we treat hyperbilirubinemia in preterm infants?

Posted on 28 October 2015 by Keith Barrington

I missed this when it was first published, but it came up on one of my regular searches at the weekend. Hulzebos CV, et al. The bilirubin albumin ratio in the management of hyperbilirubinemia in preterm infants to improve neurodevelopmental outcome: a randomized controlled trial–BARTrial. PLoS One. 2014;9(6):e99466. The multi-centered Dutch group of authors randomized 615 preterms of less than 32 weeks gestation. Babies had their bilirubin treated according to some arbitrary nomograms for total serum bilirubin. They had to be arbitrary of course, because there are few good data to inform an evidence-based nomogram. The thresholds for treatment seem reasonable, and are all available on the free access web page where the article is published. The group randomized to have the bilirubin-albumin ratio taken into account were in addition treated if their B/A ratio exceeded a line on another nomogram, also somewhat arbitrary. The 2 nomograms were different for different strata of birthweight, and differed over the first couple of days of life.

The idea being that if you start treatment earlier for those babies with a low albumin, and a bilirubin/albumin ratio which is over the threshold, then they might have less bilirubin induced brain injury (often evident as motor disturbance later in life, they thought).

What this meant in the end was that the group with the B/A ratio included had an average of only 6 more hours of phototherapy (which was not statistically significant) and 2 exchange transfusions vs none in the TSB alone group. There were fewer deaths in the B/A group, 5.2% vs 8,1%, p=0.2, i.e. a difference which could easily be due to chance. The primary outcome was the composite motor score at 18 to 24 months corrected age.

There was no difference between the groups in the primary outcome. Or any indices of development at 2 years of age.

The only intervention which occurred as a result of this change in screening policy was a minor increase in the duration of phototherapy; I don’t think you can postulate that this was the cause of a minor reduction in mortality. The study was not designed, or powered, to show a difference in mortality. I think even doing the subgroup analysis that they present is really questionable, a subgroup analysis of an unexpected non-significant difference in a secondary outcome is something you should think twice about, and then think another three times, before presenting. It could easily mislead people into thinking that there was a real difference to worry about.

So either the B/A ratio is not of any value for directing therapy and improving motor outcomes in preterm infants, or the thresholds they created were not right. I guess its possible that a much stricter threshold for intervention would have shown some differences in outcome, which if it just led to more phototherapy might be a benign intervention. But on the other hand phototherapy is not entirely benign, it interferes with mother infant interactions, and affects developmentally sensitive care. Exchange transfusions are certainly not benign.

I think it is hard to believe that there will be another investigation of this issue, certainly not of this high quality. The difference in interventions would have to be greater that this to be able to show an effect. Perhaps another trial of prophylactic early phototherapy is warranted, as the large NICHD trial did show a reduction in “neurodevelopmental impairment”.

For now I think the thresholds for treatment suggested by Jeff Maisels and his pals are about as good as we can get.

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A new book, with great chapters!

Posted on 27 October 2015 by Keith Barrington

A new book about neonatal clinical ethics has just been released. Eduard Verhagen and Annie Janvier are the editors.

Here is the blurb:

Ethical Dilemmas for Critically Ill Babies

Editors: Verhagen, Eduard, Janvier, Annie.

Series: International Library of Ethics, Law, and the New Medicine, Vol. 65

20151027_145544

Addresses important ethical questions about human life and medical interventions

Only volume which covers the important issues related to ethical, legal and medical aspects of neonatology intensive care

Contains contributions from the leading experts in the field of neonatology, bioethics and health law. Most neonates who now survive intensive care would have died 50 years ago, and “nature” would have decided the outcomes, making ethical discussions about initiating or withholding resuscitation irrelevant. Medical developments in neonatology have changed the way we respond to diseases of neonates, to their illness, and to their parents. Not only as physicians, but also as a society. Decisions on when to start, withhold, or withdraw life-saving interventions in critically ill neonates are among the most difficult decisions in pediatric practice. These decisions are fraught with ethical dilemmas, for example deciding whether withholding intensive care –leading to death- is superior to uncertain survival with a risk of disability and the additional burden of intensive care. This book covers important ethical questions that arise in neonatal intensive care units. Questions such as, whether to intervene medically and whether we are good at predicting the outcome of fragile neonates; whether a medical intervention should be withheld or withdrawn, and who should be primarily responsible for these decisions and how?

____________________________________________________

The book is derived from presentations that were given at a conference near Geneva that was sponsored by the Brocher Foundation.   There are 2 chapters written by yours truly:

Predicting Outcomes in the Very Preterm Infant.

Keith J Barrington (page 51).

A perceptive and disturbing evaluation of why we do so many imperfect tests in the NICU to try and predict the future life of newborn babies.

(that’s not the publisher’s blurb, I wrote that)

and

Neonates are Devalued Compared to Older Patients

Annie Janvier, Carlo Bellieni, and Keith Barrington (page 25).

A perceptive and disturbing evaluation of the way newborn infants are treated differently, and negatively compared to older children.

(Guess who wrote that).

You can buy it here, as an ebook it’s a steal at $99.

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A step forward in neonatal resuscitation. And Oh So Simple.

Posted on 27 October 2015 by Keith Barrington

When you are resuscitating a baby, and you ask, how is the heart rate? What kind of answer do you get? “It’s good” “pulse is a bit slow” “I think its around 80”?

As Lou Halamek and his team recount (Yamada NK, et al. Impact of Standardized Communication Techniques on Errors during Simulated Neonatal Resuscitation. American journal of perinatology. 2015), such kinds of communication in an Air Traffic Control tower would see you booted out. In air traffic control, they realized that imprecise, or even just variable, ways of recounting what was going on, were leading to errors; so now, when there is a communication, it has to follow a strict format. Yamada et al have followed that lead and developed a standard lexicon of information transfer for neonatal resuscitation, including a closed-loop communication system for completing orders for medication or volume resuscitation.

In answer to the question above, the responses have to be one of the following “heart rate above 100″; ‘heart rate below 100”; “heart rate below 60”; or “we’re in deep shit’ (I made that last one up, it should be “heart rate zero”).

You can see how that would be better than “I can’t hear a heart rate” which might mean, “I have a middle ear infection”, or “my stethoscope just dropped on the floor”, or “the baby is asystolic”!

Similar structured phrases are presented for other issues during resuscitation.

For medications or volume, the order must include the name of medication, dose, concentration and route AND it must be repeated by the person taking the order and include all the same information.

They studied this in an RCT, with nurses trained in the lexicon. A cross-over design was used, so the trained nurses either used the lexicon or did not, and 13 people with some experience in NRP were enrolled as the study subjects.

This is a weakness in design of this study,  I think, the trained nurses were told for the control group to “follow the general pattern of imprecise communication that is typical of nonstandardized speech”. It is certainly possible that the nurse participants, who were probably invested in showing that this works, might have used even more imprecise phrases than usual. I don’t remember ever hearing “wow he’s crackly” (one of their examples) when asking about air entry, but I guess the point is that it could happen. I think it would have been better to use non-trained nurses as the controls, but I can see that would introduce other biases also.

The other problem is that although this seems like a major, and very obvious, improvement (although I didn’t think about it), the sample size was so small that most of the changes seen were not that significant. There were fewer errors of omission (failure to perform an intervention that was clinically indicated), cardiac compressions were started earlier, by about 8 seconds, PPV was started earlier by about 2 seconds. Communication techniques were used much more frequently; that comparison was statistically significant.

This is another place where I am not sure we need another trial; we should probably all start doing this, making sure communication is clear, by using standard phrases. I can’t see any down side, it wouldn’t cost anything, and the only thing a larger study is likely to find is that sometimes communication errors lead to screw ups.

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Also, still no parents!

Posted on 27 October 2015 by Keith Barrington

My previous post was long enough without addressing another serious deficiency in these guidelines. It is worth its own post.

The guidelines are written by doctors. And only doctors (actually only Obstetricians). There is no input mentioned from any other stakeholders.

Most importantly no parents.

Surely the time has come to stop doing this, to stop physicians gathering in closed rooms and deciding what is best for the rest of the population. This is not a new idea, it has been strongly recommended for many years. The Institute of Medicine published guidance 4 years ago (to my mind their guidance leaves the patient/parent out of the process until too late) about involving patients/parents in the guideline development process. There are very high profile editorials in leading journals. There are even blog posts about it!

So why are bodies like ACOG and the SMFM not doing this? Is it because they may not like what they would hear? Is it easier to meet around a table with other physicians and not be challenged by a patient? Is it even easier if you limit the physicians to just your Obstetrical colleagues?

One of the reasons identified for why clinical practice guidelines have little effect on practice is the lack of involvement of the people most affected by them.

Because that is the whole point. The Obstetrician will leave work at the end of the day to go home, the families are marked forever by these decisions. Whichever way they go.

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Another extremely flawed guideline on periviable deliveries

Posted on 26 October 2015 by Keith Barrington

Oh Dear, here we go again…

This is a joint statement from ACOG and the SMFM. There is some good in here, but you’d think they could at least get the facts right.

“Delivery before 23 weeks of gestation typically leads to neonatal death irrespective of newborn resuscitation (5-6% survival)”.

This is just nonsense. What does this mean, that if you don’t resuscitate you will get the same survival as if you do? Survival is 0% without resuscitation and between 21 and 40% if you do. What is the point of mixing figures from patients with active treatment, and those without? So that you can say to an expectant mother, “in a mixed group of infants, some of whom received active care and others did not, (but we aren’t going to tell you how many) 5 to 6% survived”?

The references they give for that percentage show what can happen if you provide active treatment. Survival in Stoll BJ, 2010 at 22 weeks was 21%, in Rysavy et al it was 23%, among actively treated infants. Other figures show similar things in even more detail. The EXPRESS group in Sweden have been leaders in this, their article in JAMA in 2009 shows that in 51 infants of 22 weeks (there were 2 babies of slightly less than 22 weeks included) there were 19 who were admitted to the NICU for active care, 5 survived, or 26%. Including the infants who were born alive but not resuscitated decreases the survival to 9%, but telling a mother that the risk of survival is 9% makes no sense at all.

You can only give informed consent if you have not been misinformed! The chance of survival is either 0 or 26% from those figures.

I was recently “accused” in a public meeting of wanting to resuscitate 100% of live born babies. Which is untrue. But I do want 100% of mothers to be able to make decisions based on accurate information, based on sensitive personalized counselling. To make decisions that are best for them and their family, which they cannot make unless they really know what the options are. Which means good data.

Lets return to the statement, and another inaccurate piece of information:

“Among rare survivors significant morbidity is universal (98-100%)”.

Although morbidity is not defined here, I presume this is referring to adverse long-term outcomes, as they are the only things discussed in this statement. If so it is a gross exaggeration, the 2 references given show no such thing. Rysavy et al showed 61.1% ‘significant morbidity among survivors’ and Stoll et al contains no data on long term outcomes. It does show that all infants born at 22 weeks are sick, which should be no surprise, and surely should not be confused with data about long term neurological and developmental prognosis.

In fact Rysavy et al’s paper is grossly misquoted in Figure 2. The percentages shown are completely wrong.

Also it is ridiculous to mix together, in Figure 2 the following :

Greg Moore’s systematic review of outcomes at 4 to 8 years which defined moderate and severe impairment as an IQ less than 70 and Cerebral Palsy with a GMFCS of 2 or worse.

Rysavy et al’s data which examined babies at 18 to 22 months and defined moderate and severe impairment as a Bayley3 less than 85 and CP with a GMFCS of 2 or worse

Two publications with data from different tests at 2 different ages from the original EpiCure dataset. Marlow 2006, for example, defined severe disability as a cognitive score less than 70 and non-ambulatory CP, at 6 years of age.

Ishii from Japan, who at 3 years defined profound impairment as cognitive score less than 50 or “profound CP”

What possible use is a figure that mixes all those together, and then completely misses the mark with one study (Rysavy) by showing outcomes among all babies delivered, including those who were not offered intensive care.

This is another statement that should be junked. At least get your literature review right first. Then you can start on the value-laden judgements about when to intervene.

And if the whole point is to make an individual decision, based on the families values and interests (which is the message being given by tables 1 and 2), then why on earth do you need the completely inconsistent table 3? Table 3 which then goes back to the standard old-fashioned approach making decisions according to completed weeks of gestation. So for example antenatal corticosteroids are “Not recommended” up to 22 weeks and 6 days, but you can consider them at 23 weeks and 0 days, up to 23 weeks and 6 days, when one day later they become recommended.

How “Not recommended” was graded as a recommendation 1A which means, according to their system “strong recommendation, high-quality evidence”, is completely beyond me. What evidence is there of harm? Which is what you need according to their own framework to make that statement. Their own brief review shows no harm, although there is no proof of major benefit at 22 weeks, and suddenly at 23 weeks and 0 days there is a reduction in death, severe IVH, NEC and PVL.

It should be “strong recommendation, entrenched prejudice”.

The best you can really say is that whether or not steroids help at 22 weeks is uncertain, and there is currently no evidence of harm. An honest evaluation of the literature should lead to a recommendation of “we don’t know”. Which would mean discuss this with the mother.

Which is really what a statement regarding counselling should be all about. How to understand the evidence, the limitations of the evidence, how to explore the values, hopes and desires of a woman in distress, and her partner if there is one. How to come to a decision that is within the bounds of what is reasonable, and to take into account the interests of the baby.

I started off this post by saying that there is some good here. I think that many of the issues addressed in those first 2 tables are spot on. There is a recognition of the poor accuracy of gestational age assessment, a brief note regarding the limitations of survival figures, an acknowledgement that there is no good evidence that antenatal risk calculators affect decision-making or improve satisfaction. There are some general recommendations about how where and by whom counselling should be done, and about taking into account other factors than gestational age which alter outcomes. They then seem to ignore most of their own advice in table 3.

My main issue is that to make a blanket recommendation for all women at 23 weeks and 4 days, or at 22 weeks and 3.24 days, is inconsistent with good medical practice, and is inconsistent with the initial paragraphs and the first 2 tables. After recognizing the limitations in the evidence, the limitations in gestational age assessment, the uncertainty of other risks, and the variations in individual values and preferences, then steroids may or many not be a reasonable intervention for a particular mother (for example).  To say that would be much more useful, I think than, at 24 weeks and 0 days do X (or consider X, or don’t do X). It might not make things cut and dried and easy for the Obstetrician, or MFM specialist, but it ain’t supposed to be easy. Oh and next time talk to a neonatologist, someone who understands a bit about perinatal epidemiology, and someone who understands about long term follow-up.

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Life in a hospital…

Posted on 26 October 2015 by Keith Barrington

My nephew Charles has a youtube channel that I directed readers to previously, I really like his funny recent video `life in a hospital‘ but I hesitated to publish a link here. There are some stereotypical nurse images that might be misinterpreted by some of my esteemed nursing colleagues.

I truly understand that response, but on the other hand, maybe, in his current situation (he is practically living in the hospital) we can cut him some slack. Maybe this most recent video ‘how to tell someone that you have CF‘ will help us all to understand a bit.

 

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Another confirmation of the excellent quality of life of very preterm infants

Posted on 22 October 2015 by Keith Barrington

Huhtala M, et al. Health-related quality of life in very low birth weight children at nearly eight years of age. Acta Paediatrica. 2015

This study from Finland showed an excellent quality of life of former VLBW infants at “nearly 8 years of age”. The QoL scores were no different to full term babies. VLBW infants with major morbidities did however have lower scores in some domains, specifically, “eating, speaking clearly, going to the toilet, learning and concentrating at school and dissatisfaction with the subjects appearance”. As they appropriately state, this means that we need to work harder to avoid those morbidities. Which are: cerebral palsy, visual impairment and “obstructive airways disease”.

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Can we stop worrying about neonatal hypoglycaemia?

Posted on 21 October 2015 by Keith Barrington

In the same, neonatal, issue of the Formerly Prestigious New England Journal of Medicine as my recent post about inhaled steroids, is a fascinating cohort study of serial blood glucose monitoring in 404 at-risk term infants (the CHYLD study). The infants were initially enrolled in two studies, one of them examining the effects of hypoglycemia on the EEG and the other being the “sugar babies” study, an RCT looking at the use of oral glucose gel as treatment for hypoglycemia. About 75% of them had continuous subcutaneous glucose monitoring started at a median of 4 hours of age. The definition of hypoglycemia used for the primary analysis was a glucose less than 2.6 mmol/L (multiply by 18 for old-fashioned folks= 47 mg/dl).

In both of the initial studies, the protocol was designed to monitor the blood glucose at 1 hour of age then before feeds every 3 to 4 hours. In both studies the protocols were designed to intervene and attempt to maintain a blood sugar above 2.6. Babies from both of those other studies were enrolled in a follow-up program which examined them at 2 years of age with Bayley scales (version 3) and tests of executive function.

They defined 2 major outcomes,

Neurosensory impairment was defined as any of the following findings: developmental delay (BSID-III cognitive or language composite score of <85), motor impairment (BSID-III motor composite score of <85), cerebral palsy, hearing impairment (requiring hearing aids), or blindness (≥1.4 logMAR [log10 of the minimal angle of resolution] in both eyes).

Processing difficulty was defined as either a motion coherence threshold or an executive-function score that was more than 1.5 SD from the mean, indicating performance in the worst 7% of the cohort.

The investigators found no evidence of an adverse effect of low blood sugars at 2.6 mmol/L threshold, (nor at lower thresholds, of 2.3, 2.0 or 1.7, at least as far as I can see from the figures provided in the supplementary appendix). When they looked at the data from the continuous subcutaneous monitoring, there was also no convincing evidence of an adverse effect of low blood sugars, even though a quarter of the babies with low blood sugar actually had hypoglycemia that lasted for 5 hours of more when they examined the data from the continuous monitoring (which they call interstitial glucose in the article).

In fact there was some evidence that babies who had an early blood sugar above 3.0 mmol/L actually had worse outcomes.

This makes me feel good, (when I first typed that it came out “this makes me feel god”, I hope that isn’t a Freudian mis-type!) because the statement that the Fetus and Newborn Committee of the CPS came out with, while I was chair, suggested that a first blood glucose of 1.8 (at 2 hours of age) was acceptable (although it needed following). And that eventually blood sugars should be maintained over 2.6. This was based on relatively limited data, which suggested that the lower limit (or rather the 5th percentile) of blood glucose in healthy full-term breast fed infants with no other risk factors was about 1.8 at 2 hours of age. Of course basing a recommendation on a statistical norm in a healthy population, and then applying them to an at-risk population as a goal of therapy is not necessarily correct.

So maybe we haven’t done any harm with those recommendations, at least, and we might have reduced some over-interpretation and over-treatment of a usually benign phenomenon, which looks like it may be benign even in at-risk babies.

But:

The real problem with all this comes from another very recent publication which suggests that transient hypoglycemia might be harmful. Kaiser JR, et al. Association between transient newborn hypoglycemia and fourth-grade achievement test proficiency: A population-based study. JAMA Pediatrics. 2015;169(10):913-21. It is a study with a different design, different analysis, and different conclusions. In this study from a hospital in Arkansas they had a universal glucose screening policy. The first screen was done at 1 to 3 hours of age, and the “usual practice” was to treat if the glucose was <2 mmol/L. In this study they compared school outcomes between children who had 1 blood glucose <2, <2.25 or <2.5. Children whose neonatal blood sugar was still below the particular threshold on the second blood sugar were eliminated.

They started out with nearly 2000 babies (of 23 to 42 weeks gestation) who had blood sugar results, and were able to confidently match about 1400 of them with school achievement scores.

The babies who were hypoglycemic, below each of the thresholds, were more premature, lower birth weight, and more likely to be twins and more likely to be SGA. their mothers were more likely to be diabetic, have pregnancy complications, and a cesarean delivery, they were also more likely to have not completed high school. All of these variables were then put in a logistic regression, which finally showed an association between having a single blood sugar below each of the thresholds and having lower proficiency on the math or literacy tests.

I’m really not sure about these data, the hypoglycemic babies had so many different characteristics than the non-hypoglycemic, that I am uncertain if logistic regression can really correct for all of them.

What to do with all this, I don’t know if we will ever have an RCT to answer the questions surrounding early hypoglycemia in the newborn. The CHYLD study suggests that at-risk babies, if treated in a protocol designed to try and get the blood sugar over 2.6 mmol/L (47 mg/dl) don’t have any adverse effects of blood sugars getting as low as 1.7 mmol/L. The Kaiser et al paper suggests that in a heterogenous and unselected group of newborns, with a usual practice of trying to get the blood sugar above 2, there is an adverse association of having just one blood sugar under 2.5.

My take on this is that we could continue to follow the CPS statement recommendations for now. I think there is too much risk of residual bias in the Kaiser data to change practice and aim for higher blood sugars, but I must say I am not certain about that, and I don’t know how we will even answer the question. We need more data, it is easy to always say. I think more cohort study data as high quality as the CHYLD study might be able to give us clearer answers. Although the sample size of CHYLD was good, more data with larger samples, and including some lower-risk babies would help. I guess I could dare to suggest an RCT? If we randomly compared at-risk babies at one hour after birth, with 2 different thresholds for intervention, and an effective but non-invasive intervention, and followed them for long enough to see a clinically significant effect, then we could get the answers we need. Any takers?

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A couple of excellent articles

Posted on 20 October 2015 by Keith Barrington

The first of these 2 articles is a general tale of evidence-based medicine. One of the best articles (or blog posts) that I have read in a long time, from the excellent David Gorski of Science-based Medicine, who is also known as Orac (whose blog is ‘respectful insolence’). It is a discussion of why campaigns such as choosing wisely may fail unless we put different structures in place to support the initiatives.  www.sciencebasedmedicine.org/choosing-wisely-changing-medical-practice-is-hard/ he discusses, among other important issues, the place and the importance of comparative effectiveness research.

Another article, this time from Mother Jones, not a science publication; the writer shows a better understanding of the science surrounding breast cancer screening than many supposedly science based journals, or “scientific physicians” such as Dr Daniel Kopans from Harvard, a radiologist who can always be counted on to criticize studies which call into question the value of universal mammography.  www.motherjones.com/politics/2015/10/faulty-research-behind-mammograms-breast-cancer

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