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Sporadic analyses of published research

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I met the author of this article at a CPS meeting a few years ago, she immediately impressed me with her unique perspective. Paige is a developmental pediatrician who does long-term follow-up of preterms, and is involved in developmental evaluation and intervention of children with other challenges, including Spina Bifida.

Church P. A personal perspective on disability: Between the words. JAMA Pediatrics. 2017.

As you will see if you read the article, Paige has a form of Spina Bifida herself, a Lipomyelomeningocele, with a neurogenic bladder and neurogenic bowel, requiring life-long interventions. She discusses the poor tolerance many medical people have of disability, and such how things are often discussed as black or white, whereas having a profound personal experience of disability has made her much more nuanced.

She recounts being involved in a discussion regarding a "selective reduction" of a twin pregnancy where the twin being considered for "reduction", i.e. abortion, had a similar lesion to her own.

That is an experience that I can barely understand: how would I react if a family was considering terminating  a pregnancy because of a condition that I had? Paige recounts the episode with tact and humanity.

I can imagine, as I have heard them many times, the words of the other physicians involved in such a decision, I am sure they talked about handicaps and limitations, poor quality of life, pain, and restrictions on family life. Most of which is said with good intentions but with no real knowledge of the literature, or of the range of experiences of families living with the challenges.

Just as with similar discussions regarding extreme preterm infants, a list of complications, interventions, disabilities, and long-term problems is often presented, but with no similar list of benefits, achievements, abilities, long-term adaptation, and happiness.

Near the end of her moving piece Paige writes:

Like most things in life, and medicine, disability is sharp, painful, humbling, as well as tremendous, giving, awe-inspiring. It is human. It is not easily distilled to an all or none discussion. Medicine sets the tone for this discussion and, to date, has done a miserable job. More is needed to appreciate the incredible opportunities that disability poses. More education is needed to provide the counselling families deserve: balanced, sensitive, thoughtful, and individualized rather than “objective.”

I sincerely hope that this piece by Paige will be part of a new discussion about these issues.

(Of note, even though the article is behind a paywall, JAMA lets you see the first page of the article before buying, in this case there is only one page, so you can read the whole thing for free!)


The PREMILOC trial was a multi-center RCT of hydrocortisone, 0.5mg/kg twice per
day for 7 days followed by 0.5 mg/kg per day for 3 days, given starting within 24 hours of age to infants of 24 to less than 28 weeks gestation.

Neurological and developmental follow-up has just been published (Baud O, et al. Association between early low-dose hydrocortisone therapy in extremely preterm neonates and neurodevelopmental outcomes at 2 years of age. JAMA. 2017;317(13):1329-37.)
There were 523 infants initially enrolled and 406 who survived to 2 years of age, 93% of those were seen at between 21 and 23 months corrected age, for examination and evaluation with standardized instruments.

You probably remember that the primary outcome of the trial was survival without BPD, which was somewhat reduced by the intervention (51% compared to 60% in controls). This was as a result of fewer deaths (18% compared to 23%) and less BPD (22% compared to 26%) neither of which component of the primary outcome was individually significant. In this follow-up study the authors not that after the 36 week end of the main data collection there were a further 8 deaths, 7 in the control group and 1 in the hydrocortisone group, 5 of which were from severe BPD (4 vs 1). (These deaths were also reported as the deaths before discharge in the initial publication, but I don't think the causes were noted).

All of the babies followed had a standardized neurologic evaluation, but unfortunately only 80% of them had the revised Brunet-Lézine evaluation of developmental progress, which gives a developmental quotient, standardized, as usual, with a population mean of 100 and SD of 15.

Basically there were no differences between the groups on neurological signs of impairment, or developmental scores. For example there were 6% of the hydrocortisone and 5% of the control group who developed cerebral palsy. Mean Global Development score was 91.7 in the hydrocortisone group and 91.4 in the control group.

I guess one could say that if there is less BPD and no increase in neuro or developmental adverse effects, we should think of using this as routine therapy?

But the group also report clinically important respiratory outcomes up to 2 years of age :


You can see from their table 2 that there is no sign of better respiratory health (or incidentally any effect on growth outcomes) among the survivors, with some of the minor differences being in one direction, some in the other direction.

Which calls into question again the use of oxygen at 36 weeks, as an outcome for RCTs even when combined with an oxygen reduction test, as in this trial. If kids are more likely to be out of oxygen at 36 weeks, but no more likely to go home on oxygen (14 babies in each group) and not more likely to have respiratory problems in follow-up, then the significance of getting extubated earlier, or needing oxygen for fewer days is questionable, at least the significance to families.

I think those outcomes are indeed benefits to families, its much better to see your baby with CPAP or non-invasive ventilation than intubated, but if there is on clear long-term benefit then we should be pretty certain that there is no harm before instituting this as routine therapy.

Currently, is there any other evidence of harm from this approach?

In the initial data from this trial, late onset sepsis was higher (31% vs 25% had at least one episode), NEC was higher (7% vs 5%) GI perforation was higher (5% vs 4%) use of insulin for hyperglycemia was higher (38% vs 34%) and severe RoP was higher (2% vs 1%) all of which could be due to chance effects, but the study was not powered to detect such small, but potentially important, differences; indeed in one subgroup, the most immature infants, the impact of steroids on late onset sepsis was, indeed quite different, 40% vs 23%, and their analysis showed this was unlikely due to chance. Its interesting in the on-line supplementary appendix that the major difference in late onset sepsis arose after the end of the treatment period.

It is also interesting that this dose of hydrocortisone had no evident impact on blood pressures, nor on the use of dopamine.

I think that all of these worrying differences between the groups, favoring control, with no evidence of long-term benefit, and the only evidence of short-term benefit being shorter intubation and shorter duration of oxygen therapy, that we should not introduce this regime as a routine in our patients.

There is a minor difference in survival with the hydrocortisone treatment though, with 19% mortality before discharge (and before 2 years) compared to 25% in the control group. I calculate the 95% confidence intervals of this 6% difference as being between 13% fewer deaths and 1% more deaths, using early low dose hydrocortisone in similar babies.

Unfortunately, I think I have to say that this therefore warrants further study. A larger trial with enough power to detect a 5% difference in mortality, perhaps in a region where the survival at 24 and 25 weeks is above 65% (as in this French multi-center trial; compared to for example 78% in the CNN database from 2015) should be performed.

I think a future trial should not use this as a definition of bronchopulmonary dysplasia, other definitions have been suggested, such as this recent publication from the CNN (Isayama T, et al. Revisiting the Definition of Bronchopulmonary Dysplasia: Effect of Changing Panoply of Respiratory Support for Preterm Neonates. JAMA Pediatr. 2017;171(3):271-9.) In this study the best discrimination between those who had serious respiratory morbidity after discharge (when seen at 18 month follow up) from data collected during the neonatal period, was the need for oxygen or respiratory support (anything that gave positive pressure including high-flow cannulae at more than 1.5 litres per minute) at 40 weeks post-menstrual age.

Serious respiratory morbidity was defined as either (1) 3 or more rehospitalizations after NICU discharge owing to respiratory problems (infectious or noninfectious); (2) having a tracheostomy; (3) using respiratory monitoring or support devices at home such as an apnea monitor or pulse oximeter; and (4) being on home oxygen or continuous positive airway pressure at the time of assessment between 18 and 21 months corrected age.

Just as important, a recognition that lung injury in the newborn is a continuous spectrum, and that artificially dividing that into 2 categories, with and without lung injury is an artificial distinction designed to aid research design, not to help babies, or their families. A description of long term respiratory morbidity between groups is essential, rather than a label based on an intermediate outcoem. Mortality, in contrast, is truly a dichotomous outcome, and if it can possibly be improved by low dose early hydrocortisone, than we should pursue that possibility with more studies.


In this rather weird, but interesting study from Italy, 10 mothers of preterm babies (less than 32 weeks or less than 1500 grams) without ultrasound brain injury or severe retinopathy, and 11 mothers of full term babies were shown photos of their own baby or photos of an unknown baby (from one of the other mothers) while they had their head in an MRI magnet. (Montirosso R, et al. Greater brain response to emotional expressions of their own children in mothers of preterm infants: an fMRI study. J Perinatol. 2017). The photos were of their baby's face while happy, neutral, or crying. Using functional MRI the researchers determined the activation of several different brain areas, at 3 months corrected age.

All the mothers had more activation in several areas when looking at their own baby's face than when looking at the unknown baby.

When they compared the responses between the groups, the preterm mothers had greater activation in several areas both when looking at their own baby's face, and also when looking at the unknown baby's face, than the term mothers, and when viewing their own infant's face they showed increased activation in an emotion processing area (i.e., inferior frontal gyrus) and areas for social cognition (i.e., supramarginal gyrus) and affiliative behavior (i.e., insula). The mothers were reasonably well matched, and not suffering from postnatal depression or anxiety.

The weeks of stress in an NICU watching their baby and being able to do little to protect them look like they change a mother's brain function.

Now what about the dads?

Another article (Paules C, et al. Threatened preterm labor is a risk factor for impaired cognitive development in early childhood. Am J Obstet Gynecol. 2017;216(2):157 e1- e7). and a very interesting editorial, compared 3 groups of children at 2 years corrected age. Babies born late preterm  and infants who had been  born at term, after an episode of preterm labour. And a group born at term, without a history of preterm labour. The groups were fairly small, (22, 23 and 42 respectively). The episode of threatened preterm labour occurred between 25 and 36 weeks gestation, and isn't described in this paper, in terms of actual gestational age or other complications associated, except that the membranes were not ruptured. Some of the mothers received steroids, and that was different between the late preterm born babies (55%) and the term delivering babies (100%).

The babies born after threatened preterm labour, whether they delivered at term or late preterm had scores on the developmental/cognitive/motor function screening test which were very similar to each other in almost all domains, and also lower in almost all domains than the controls. Overall, the Odds Ratio for what they call "mild delays in development" (more than 1 standard deviation below the mean, which is really in the lower part of the normal distribution), at 2 years was about 2.0, after an episode of preterm labour.

A very interesting editorial confirms that this is probably the first study to have published such outcomes, although previous studies have shown an increase in SGA after threatened preterm labour. In this new study, also, the threatened preterm labour babies born at term weighed 200 grams on average less than the controls despite being born only 1 day earlier. If this finding is true (and in such a small study we should be careful about relying on it too much) then the big question is: why? Why should an episode of threatened preterm labour, which resolves with eventual delivery at term have an effect on cerebral development? Is it an antenatal influence of perhaps increased intra-amniotic inflammation? Does such an episode affect the home environment? Is it related to the somewhat higher educational level of the control mothers? (Although this was included in the logistic regression model, the differences are quite large, 30% of term delivering babies after preterm labour only had primary education, compared to 14% of controls).

If this finding is confirmed it might lead the way to further research studying the mechanisms, and help us get a handle on the impacts of preterm birth after preterm labour also.



I have never been convinced that fluid restriction is a good thing for kids with BPD. I think the common practice came about because of the short-term improvements in lung function that sometimes follow if you start diuretics. The idea being that if diuretics improve lung function, then giving less fluid will also.

But this is a false equivalency, diuretics cause sodium depletion, and therefore decrease total body water, and probably lung water content also. Fluid restriction in contrast leads to a reduction in urine output, and, within clinically reasonable limits, will not have an impact on total body water, and there is no reason to believe that they will reduce lung water content either.

Diuretics may have other direct effects on pulmonary function, that will not occur with fluid restriction. Inhaled furosemide, for example, improves pulmonary mechanics in BPD, presumably by acting on the same sort of ion pump that loop diuretics block in the kidney.

Even in adults with fluid overload (those with oedematous congestive heart failure) RCTs of fluid restricion show no effect, unless sodium intake is also severely restricted. Sodium restriction alone works as well, so the fluid restriction adds nothing.

Despite this, there are recommendations from usually reliable people that babies with BPD should have their fluid intake restricted, such recommendations are often accompanied by a reference, usually a reference to another recommendation or to a narrative-type review article.

I have been planning for years to do a systematic review for the Cochrane library, of fluid restriction as treatment for early or established BPD. We have finally finished the review and it has just appeared. (Barrington KJ, Fortin-Pellerin E, Pennaforte T. Fluid restriction for treatment of preterm infants with chronic lung disease. Cochrane Database of Systematic Reviews. 2017(2).)

Using the usual search procedures we could only find one relevant trial. In fact the initial search didn't find the article (Fewtrell MS, et al. Randomized trial of high nutrient density formula versus standard formula in chronic lung disease. Acta Paediatrica. 1997;86(6):577-82.) even though I knew it existed; the Pubmed key words did not mention fluid volumes or restriction, so we tweaked the search to ensure that we found the article, and to make sure that we would find any others that exist.

So the only RCT evidence addressing fluid restriction is a study of 60 preterm babies with early chronic lung disease (needing oxygen at 28 days of age) who were randomized to either get 180 mL/kg/day of a regular formula, or 145 mL/kg/d of a concentrated formula. Unfortunately they didn't report on one of our outcomes, oxygen requirement at 36 weeks, as it wasn't the standard outcome that it has since become.

That study showed no benefit of fluid restriction on any outcome. The fluid restricted group had more apneas, a finding unlikely to be due to chance, and also had more babies who needed more than 30% oxygen during the trial, a difference which may have been due to chance.

Fluid restriction risks nutritional restriction also; even though the idea may be to reduce the free water intake, babies often get fewer calories and less protein when fluid restricted, while babies with BPD actually need more calories. They will also produce more concentrated urine, which might increase the risk of nephroclacinosis as well.

The final message is that there is no evidence to support the practice of fluid restriction of babies with early or established BPD. There is no physiologic rationale either. There are potential risks to the practice.

We should stop doing it.


In 2007, when I was chair of the CPS Fetus and Newborn Committee, we published a guideline regarding the approach to term and late preterm infants with perinatal risk factors for sepsis. Obviously any infant with clinical signs consistent with sepsis needs immediate work up and antibiotics, but the management of infants with risk factors for sepsis and no clinical signs evident was the focus of that guideline.

This is what we said about chorioamnionitis, based on what we thought was the most reliable literature:

The risk of sepsis (which may be due to a variety of different organisms, including GBS, E coli and other Gram-negative organisms) in an infant whose mother had definite chorioamnionitis is approximately 8%, and is approximately 3% to 4% if ‘possible’ and ‘definite’ chorioamnionitis are considered together [31][32] (evidence level 2b); among all mothers with fever, the incidence is 2% to 6% depending on the height of the fever [31] (evidence level 2b). Infants who do not have signs at birth are unlikely to develop sepsis, the odds ratio for sepsis among infants who are well at birth is 0.26 (95% CI 0.11 to 0.63) [31]. The incidence of invasive infection in the present study in an initially well-appearing infant with a maternal history of fever or chorioamnionitis was less than 2%, and this is confirmed by other data [33] (evidence level 2b). Therefore, it seems reasonable to perform a CBC and closely observe such an infant, and to only perform a full diagnostic evaluation and treat with antibiotics if the CBC is strongly suggestive of infection (low total WBC count) or if clinical signs develop. A requirement for extensive resuscitation at birth should be considered a sign of possible infection in such infants [32][33].

At that time the CDC guidelines recommended cultures and empiric antibiotics for all such infants, the CDC guidelines were updated in 2010, and continue to recommend the same thing, with the clarification that you should talk to the obstetricians (always a good idea!)

Well-appearing newborns whose mothers had suspected chorioamnionitis should undergo a limited evaluation and receive antibiotic therapy pending culture results (AII). The evaluation should include a blood culture and a CBC including white blood cell differential and platelet count; no chest radiograph or lumbar puncture is needed. Consultation with obstetric providers to assess whether chorioamnionitis was suspected is important to determine neonatal management (CIII).

Is there anything new recently? I think you all know the answer to that question.

Braun D, et al. Low Rate of Perinatal Sepsis in Term Infants of Mothers with Chorioamnionitis. Amer J Perinatol. 2016;33(02):143-50. This database analysis from Kaiser Permanent Southern California found an incidence of maternal fever in labour (38 degrees or more) at or after 35 weeks to be 9% and chorioamnionitis (based on ICD-9 codes from discharge data) to be 4%, chorioamnionitis based on a fever of 38 degrees followed by antibiotic treatment was 5%. There were around 30,000 deliveries in this cohort and in total there were 19 babies with culture positive early onset sepsis, 14 were symptomatic and 5 had bacteremia without clinical signs. That gives an overall incidence of culture positive symptomatic sepsis of 0.45 per 1000, and of culture positive bacteremia without clinical signs of 0.16 per 1000. Among mothers without fever the rate of sepsis was 0.5 per 1000, if they had fever without chorioamnionitis it was 0.6 per 1000, and if they had chorioamnionitis it was 4 per 1000.

One interesting thing in this study is that many physicians do not follow the CDC guidelines, the rate of neonatal treatment with antibiotics after maternal chorio, which should be close to 100%, ranged from 7 to 76% in different hospitals.

The authors don't say how many of the babies without clinical signs were from the maternal chorio group, there were 5 babies who did not have clinical signs, if all of them were from mothers with chorioamnionitis (which I think is unlikely) then you would have to treat 250 clinically well infants after maternal chorioamnionitis with antibiotics to be sure to cover 1 baby with bacteremia. Of course if some of those babies were symptomatic, then you would have to treat many more without clinical signs for each baby infected, for example if the proportion of asymptomatic babies is the same as in the next study (about 1/3) then you would have to treat over 700 asymptomatic babies to cover that 1 with bacteremia.

The authors also calculated that if the CDC guidelines had been followed (for chorioamnionitis, but also for other indications for neonatal antibiotic treatment) then 8% of all the term and late preterm babies would have received 48 hours of antibiotics.

Another very large study Wortham JM, et al. Chorioamnionitis and Culture-Confirmed, Early-Onset Neonatal Infections. Pediatrics. 2016;137(1). instituted prospective surveillance for early onset sepsis among nearly 400,000 deliveries. In contrast to the other study they did not collect data from mothers whose babies did not get septic, so we don't know overall incidence of chorioamnionitis in this study, and you can't make some of the same calculations.
They found 389 cases of early onset, culture positive, infections, in the cohort which included both preterm and term babies. Eighty-one of those infections were in term babies (37 weeks and more; from 350,000 term deliveries) 58 of which had clinical signs at birth. Which leaves 23 term infants who had no signs at birth but had culture positive sepsis, from mothers with chorioamnionitis, and 6 preterm babies with the same combination. The authors include some babies, 1 at  term and 4 preterm, who only had histological evidence of chorioamnionitis, which doesn't help our decision-making as you don't know about those unless you did placental pathology and got the results back.

If the prevalence of chorioamnionitis is 4 to 5% (as in the first study), then there would have been about 16,000 cases of chorio among the term deliveries, which gives the incidence of early neonatal sepsis (81/16,000) of 5 per 1000 which is very similar to the Kaiser Permanent data. We know 23 were without signs at birth (but one of those would not have had a diagnosis of chorio) so to ensure that 22 those asymptomatic babies with sepsis received early treatment, you would have to screen, culture and treat 16,000 babies, which is a number needed to treat of over 700.

I think that is too many. NICE in the UK seems to have a similar opinion in their guideline from 2012, their guidance is a little more complicated, but goes like this (the links should work to take you to the tables):

Use the following framework based on risk factors and clinical indicators, including red flags (see tables 1 and 2), to direct antibiotic management decisions:

  • In babies with any red flags, or with two or more 'non-red flag' risk factors or clinical indicators (see tables 1 and 2), perform investigations (see recommendations– and start antibiotic treatment. Do not delay starting antibiotics pending the test results (see recommendations–
  • In babies without red flags and only one risk factor or one clinical indicator, using clinical judgement, consider:
    • whether it is safe to withhold antibiotics, and
    • whether it is necessary to monitor the baby's vital signs and clinical condition – if monitoring is required continue it for at least 12 hours (at 0, 1 and 2 hours and then 2-hourly for 10 hours).


In their scheme chorioamnionitis is a risk factor, but not a "red flag", so if the baby does not have any of the clinical indicators they would be observed, but not treated.

As I said I think that an NNT of over 700 is too many, but others may not agree, specifically the parents may not agree. Shouldn't they be involved in that decision? A decision aid may help them to decide, with the medical team, between one or multiple IV installations, antibiotics for 36 hours (you can stop them before the 48 hour dose if cultures are negative) and hospitalisation for at least that long. Depending on how your hospital is organized term newborns on antibiotics may also not be in the room with the mother. The contrasting choice is close observation with the option of starting antibiotics later if clinical signs appear (which happened in 18 of the 23 initially asymptomatic term babies with positive cultures). Also there is no difference in mortality (there was one death in the Wortham study, a baby who died soon after cultures and never had antibiotics, 2 deaths in the Braun study both of whom were symptomatic) shown in these recent studies.

Very frequent use of antibiotics of course affects colonization and resistance patterns in an environment, and will affect the development of the infant's microbiome, perhaps for many months or years.

I think in these days of shared decision-making and family centered care, when a term baby is born after maternal chorioamnionitis but is clinically well, we should inform the parents that the baby has a very small risk of having an infection, (1 in several hundreds) and that there are 2 options. We should also organize our care so that both close repeated observation, and/or antibiotic administration, can be performed in a mother and infant room, without interfering with breastfeeding and the evolution of the new family, and then give the parents a big place in that decision.



I hope this link stays active for ever as it is a great resource... Courtney Wusthoff from Stanford has developed a web-based educational tool, designed initially, I think, for medical (pediatric) residents. Their team has evaluated whether or not this works by showing pediatric residents videos of actual examinations of asphyxiated newborn infants, and asking them to identify whether the babies were normal or had encephalopathy that was either mild moderate or severe. They repeated the process after using the web-based tool described above.

They showed substantial improvements in the skills of residents in evaluation of such infants. Ivy AS, et al. Improving the Identification of Neonatal Encephalopathy: Utility of a Web-Based Video Tool. American journal of perinatology. 2016.

Hey, the internet works, sometimes!


When there is a threatened delivery in the periviable period, one of the decisions that have to be made is about the mode of delivery. In my opinion (IMHO, I think those young'uns say) we should consider the different parts of the decision-making to be linked but separate. A decision to give antenatal steroids, for example, does not mandate a cesarean delivery or intensive care of the baby. A decision to not perform a cesarean does not mean that fetal heart rate monitoring should not be performed, or that a live-born baby might not have active resuscitation.

One might decide, for example, that a mother will receive betamethasone, with a goal of improving the chances of a good outcome, and we might then decide to plan on providing active intensive care for the baby, but then the decision may be that the risks and benefits, for this particular mother, of performing a cesarean are not consistent with her goals and values; in which case a cesarean for fetal indications will not be performed. We might still want to monitor the fetal heart rate, as knowledge of the heart rate during the last minutes prior to delivery could help in resuscitation decisions; if the fetus has been bradycardic for a prolonged period prior to delivery, and is then born asystolic, a decision to not attempt resuscitation could be quite reasonable, compared to a fetus with good heart rate patterns just before delivery.

One part of this decision-making matrix that has been somewhat lacking is good data about maternal complication rates in this time period. What are the risks to the mother of a classical cesarean, a lower segment cesarean, or a vaginal delivery before 26 weeks? What are the risks for this pregnancy, and for the next pregnancy?

Several recent articles, one still on-line only, help to clarify the risks (although the relative benefits of each mode of delivery need RCTs for reliable scientific data, which may well never be done).

These articles are all therefore observational studies, which describe the frequency of various maternal outcomes after preterm delivery.

The first article answers a question for which I last did a literature search a couple of years ago, at that time I wasn't able to find any good data, : "what is the risk of a classical, or an extremely preterm lower transverse, cesarean on uterine rupture in future pregnancies?" This risk is often stated by obstetricians to be a major part of their reluctance to perform a cesarean in the periviable period, and although the risks are clearly greater than for a vaginal delivery I was never sure what was the magnitude of that risk. In this publication the authors state that they also could find no good data, so my lit review was not inadequate, there just was no data. Their study, in contrast, gives very clear information about those risks.

Lannon SM, et al. Uterine rupture risk after periviable cesarean delivery. Obstetrics and gynecology. 2015;125(5):1095-100.

The authors used linked databases from Washington state to determine the risks of uterine rupture in a subsequent pregnancy after a cesarean delivery performed at 20-26 weeks gestation, and compared the risks to a cesarean performed at term.

Overall, the risks of future uterine rupture after a periviable cesarean were about 1.8% (2.4% if you restrict the analysis to classical scars) compared to 0.4% after a cesarean at term. The results are also presented as an Odds Ratio (which is 4.9, 95% CI 1.7-13.1); unfortunately few physicians understand what an Odds Ratio is (but when the risks are small there isn't much difference between the Odds Ratio and the Relative Risk). I think for individual mothers making a decision, that the absolute risks are more useful numbers; also a comparison to cesarean deliveries performed at term is an interesting and useful comparison to put the risks in context, but doesn't help in decision-making much as that isn't the option that would be on the table.

There is also a comparison of other maternal morbidities in the current (or "index") pregnancy; periviable cesarean deliveries are a little more morbid (14% of mothers have one or more of transfusion, bleeding, coagulopathy, chorioamnionitis, sepsis, maternal infection or hysterectomy as recorded in the hospital discharge diagnoses, which means that bleeding is not strictly defined) than term cesareans, which I was a bit surprised to see were also pretty morbid (10% had the same complications) but the difference was consistent with a chance finding.

Mothers who have a periviable cesarean are different in many ways from mothers having a term cesarean, so how much of the increase in maternal morbidity is due to the classical incision (almost all of the term cesareans are lower segment transverse incisions) and how much to their other demographic and clinical differences? Also important, does having a cesarean delivery at periviable gestation have other effects on subsequent pregnancies, other than the risk of uterine rupture?

The same group (Lannon S, et al. Mode of delivery at periviable gestational ages: impact on subsequent reproductive outcomes. Journal of perinatal medicine 2013. p. 691.)
has looked at the risks for a subsequent pregnancy,  and compared a vaginal birth in the periviable period to a cesarean delivery. Overall having a delivery in the periviable period led to the same outcomes in a subsequent pregnancy regardless of mode of delivery, the gestational age at birth of the subsequent pregnancy were almost identical; the only individual outcome which was affected was uterine rupture. There were some very small differences, which were statistically significant because of the large numbers of pregnancies being evaluated, for example after a periviable vaginal delivery the median gestational age of the subsequent pregnancy was 38 weeks, and after a cesarean it was 37 weeks. the authors interpret this difference as the wish to perform cesarean in the subsequent pregnancy prior to labour to avoid uterine rupture if possible.

The next study compared the maternal outcomes of classical cesarean to low transverse cesarean on maternal morbidity (for the index pregnancy only). Kawakita T, et al. Maternal Outcomes associated with early preterm cesarean delivery. Am J Obstet Gynecol. 2016. They looked at hospital records of mothers who delivered between 23 and 32 weeks gestation, and then looked at the stratum under 28 weeks. They showed that in the higher gestational age stratum (28 to 32 weeks) that classical cesareans had more morbidity, in particular more transfusion and more need for ICU admission. But in the lower GA group the risks were the same for both types of cesarean incision, for example about 10% needed a blood transfusion in each group.

Another paper from the NIH MFM network examined deliveries between 23 weeks and 34 weeks.  Reddy UM, et al. Serious maternal complications after early preterm delivery (24-33 weeks' gestation). Am J Obstet Gynecol. 2015;213(4):538 e1-9. Deliveries at 23 to 27 weeks gestation were more morbid, with 7% having hemorrhage, compared to 3% for the group at 31 to 33 weeks, in this study hemorrhage was clearly defined, as it was part of the prospective data collection, as blood loss ≥1500 mL, blood transfusion, or hysterectomy for hemorrhage.

The absolute risks associated with an extremely preterm cesarean delivery are not noted in this publication, but the adjusted relative risk of a cesarean delivery at 23 to 27 weeks compared to a vaginal delivery is presented. The combined relative risk of hemorrhage, postpartum infection, and ICU admission is 3.22 for a classical cesarean delivery and it is 2.8 for a low segment delivery, both compared to vaginal delivery at the same gestational age.

I can't tell you based on these data what are the absolute risks, but I guess-timate from these data (about half of the deliveries were vaginal) that about 6% of mothers delivering vaginally between 23 and 27 weeks will have a serious complication, (hemorrhage infection or ICU) and about 18% of mothers who had a cesarean in this time interval. That is a bit higher than Kawakita if I have estimated the absolute risks correctly, but not too much different, and of course definitions and data finding are different.

Another study from the Canadian Perinatal Network (Crane J, et al. Maternal and Perinatal Outcomes of Pregnancies Delivered at 23 Weeks’ Gestation. JOGC 2015;37(3):214-24.)  included only deliveries at 23 weeks, serious maternal outcomes were common (about 40% of mothers had at least one serious outcome), but the large majority of them were chorioamnionitis, about 38%; after that the next most common was blood transfusion which was required in about 4% of women. About 10% of the 230-ish mothers had a cesarean, and the authors don't compare the maternal outcomes between Cesarean and vaginal deliveries, but most of the data are from the vaginal deliveries.

To summarize, having babies is dangerous. Having a baby by cesarean section at term has risks, including a frequent need for transfusion. The overall risks of having a cesarean delivery in the periviable period for the current pregnancy are somewhat greater than at term, but the magnitude of the increase is probably less than 5%, most of those risks are short-term and treatable, with the most common being the need for a transfusion. A vaginal delivery in the periviable period has fewer risks for the mother  Uterine rupture in the next pregnancy, if there is one, occurs less than 3% of the time.

I want to emphasize here that uterine rupture is a big deal. I am not trying to minimize it, and we should find a way to explain to mothers the importance of uterine rupture in future pregnancies, but we should do that without exaggerating its incidence (perhaps a visual decision aid?), and ensuring that mothers understand the major impact of a uterine rupture, and that the risk of rupture persists even when the obstetrician tries to take steps to avoid it. Of course that is a risk which is important for a woman who will have a future pregnancy, and may be of little importance for a woman who has decided against that option.

I think that it is good for the neonatal team to have an understanding of the risks to the mother, so that we can be reasonable and well-informed as we participate in decision-making; but clearly the final decision about route of delivery should be made between the mother and her obstetrician.


Acupuncture is nonsense. There I have said it. I'll probably get at least a few comments for this post, but I'm not backing down. Acupuncture is based on pre-scientific ideas about how the body works, believing that some sort of vital energy flows along meridians in the body, and that sticking a needle into the skin at certain specific points can have distant effects, by letting out the Xi.

Xi is non-existent, meridians are non-existent and there are no acupuncture points, they just don't exist.

This is all ridiculous, and people with a medical education should know better. Trials of acupuncture in adults have shown that it doesn't matter where you put the needles, or even if you puncture the skin or not. The better controlled the trials are the less effect there is, and trials with really good sham procedures don't show a difference between the sham procedure controls and the actually needled groups.

Any effect is simply a placebo effect, and the whole procedure with its  insertion of needles and fake explanations has been characterized as a "theatrical placebo". For a sampling of deconstructions of acupuncture studies just search acupuncture on the blog "respectful insolence" which you can do by following this link .

Unfortunately there are many who have been taken in by the pseudoscience of this quackery, even in neonatology. A few trials have even been published, including those using electrical stimulators of non-existent acupuncture points, and a few where lights have been shone onto those same points.

The two most recent studies I glimpsed are examples of those 2 methods, Abbasoglu A, et al. Laser acupuncture before heel lancing for pain management in healthy term newborns: a randomised controlled trial. Acupuncture in medicine. 2015;33(6):445-50. 42 term babies having a heelstick were randomized to laser acupuncture or sucrose. The study found that sucrose was better than shining a light on the Yintang point (the non-existent acupuncture points, scattered along the non-existent meridians, all have names, this one is between the eyebrows and is also called EX2).

Mitchell AJ, et al. Does Noninvasive Electrical Stimulation of Acupuncture Points (NESAP) reduce heelstick pain in neonates? Acta Paediatrica. 2016. This study used different fake acupuncture points (ZuSanLi (ST36), SanYinJiao (SP6), KunLun(Bl60), and TaiXi (KI3) which are on the legs) and randomized babies undergoing heelstick to 4 groups, sucrose with "Sham NESAP", NESAP plus water, NESAP with sucrose, and sham NESAP with water. They randomized 142 term infants who were undergoing a heelstick procedure and analyzed the videos of their faces for PIPP scoring. In the Sham NESAP groups the electrodes were placed adjacent to these fantasy acupuncture points but the stimulator was not turned on, All babies at least had facilitated tucking and a soother, which are both effective at reducing pain from heelstick, which was shown by the relatively small mean increases in PIPP scores in all the groups. Sucrose limited the increases in PIPP compared to the groups which didn't get sucrose, and electrical stimulation of ZuSanLi etc didn't do anything. This study did at least have the potential for a measurable effect, because, unlike shining a light on the skin, there is at least a potential that the transcutaneous electrical stimulation could have an analgesic effect. As it appears to for, in particular, chronic pain.

Although the NESAP groups without sucrose didn't have a large mean increase in PIPP scores, the mean peak scores were up to 4.9 and 5 (compared to 4 or less for the sucrose groups), but the standard deviations of those scores were much larger than the sucrose groups, (4 compared to less than 2) which means that there were probably substantially larger numbers of babies who had pain scores of over 6, and had appreciable pain. Which means that yet again I can say that we shouldn't be performing heelsticks without using all the proven evidence-based methods for reducing pain prior to such procedures, of which sucrose is top of the list.

Lets stop investigating this nonsense in neonatology, we should be using our time and efforts and resources to examine therapies that have some basis in reality and science. Whatever next, ear candling, or craniosacral therapy for newborns? OH NO!


There is a reason we don't perform pupillary reactions to light in preterm babies, and that is that they don't react. They also tend to be large. This post is in response to my trying to find out what had been published about this phenomenon, when a case in our NICU raised a teaching point. I decided to go back through the literature to find out what was actually documented in peer-reviewed publications, and found, for a change, some good quality data.

The first of these, chronologically, is from 1989 Isenberg SJ, et al. The pupils of term and preterm infants. Am J Ophthalmol. 1989;108(1):75-9. This group from UCLA studied prospectively pupils of 100 babies from 26 weeks through to 46 weeks, with a standardized methodology; pupils were larger in mm for more immature infants, even though their eyes are a bit smaller. Pupillary light responses were usually absent before 30 weeks PMA, and only reliable after 32 weeks.

Robinson J, Fielder AR. Pupillary diameter and reaction to light in preterm neonates. Arch Dis Child. 1990;65(1 Spec No):35-8. A similar study from Birmingham, England followed 50 babies, and found similar things, the few babies who responded before 31 weeks all had a slow reaction.

Isenberg SJ, et al. The fixed and dilated pupils of premature neonates. Am J Ophthalmol. 1990;110(2):168-71. The UCLA group again, this time with a cohort of 30 babies who were examined every week, they were all less than 31 weeks at the first examination and none of them reacted at that time. The proportion having a detectable response to light increased, and most were reacting by 32 weeks.

Isenberg SJ, Vazquez M. Are the pupils of premature infants affected by intraventricular hemorrhage? J Child Neurol. 1994;9(4):440-2. The answer to the question in the title is no. The pupils of babies with any grade of hemorrhage (1 to 4) are not larger and do not have different reactions to light than those without hemorrhage.

There are a couple of more recent publications, but they don't really add anything. Until the baby has passed 32 weeks post-menstrual age, there is no point looking for pupillary light reflexes, and the pupils will look fixed and dilated.


This publication appeared on-line a couple of months ago, and still isn't in print. Prentice T, et al. Moral distress within neonatal and paediatric intensive care units: a systematic review. Arch Dis Child. 2016. It is a systematic review from Melbourne, with the help of Annie Janvier, of the literature surrounding moral distress in health care workers in the NICU and the PICU. All of the studies included nurses, and some of them also studied other health care workers.

Moral Distress refers to subjective feelings of distress in response to the ethical challenges of health care work. It is a term which first appeared in the nursing literature, and, although other terms have been suggested, I think it fits. Moral residue is another term these authors refer to, which is the lingering feelings which persist after the "morally distressing" case has ended. As we deal with children and babies who are fragile, dependent, and may have life-long complications, the NICU and PICU are places where moral distress is likely to be frequent. How frequent it is, and what causes the situations most likely to lead to distress, where the questions that lay behind this systematic review.

They found 13 articles, of varying size and quality, (including one of ours); from the results of the systematic review article:

Common themes represented included disproportionate care, ‘aggressive’ use of technology, powerlessness, and communication around life and death issues. Interestingly, moral distress is generally reported as occurring because a provider feels she/he is ‘doing too much’..... The converse is rarely reported as causing moral distress, for example, deciding for palliative care in the face of uncertainty. Concepts of moral distress are expressed differently within nursing and medical literature.

One of their findings is the different ways in which moral distress is discussed in the articles, publications in the nursing literature frequently emphasize the subjective experience of the nurses, and the fact that they lack power and are having to provide interventions that they do not always agree with; they are sometimes portrayed as the victims of the aggressive care being perpetrated by the physicians. Whereas in the medical literature moral distress is described in terms of the objective situations that create confrontations or dilemmas. The reality is though, that physicians also experience moral distress (with about the same frequency as nurses), they also find themselves sometimes performing tasks and providing care which is against their own conception of what the best interest is for their patients.

What has been shown previously is that moral distress may lead to burnout, and decrease retention of staff. It is also probably unavoidable in intensive care, but we should, and could, work harder to minimize it, and minimize its impact.


In the UK an "intensive care" day for a newborn is defined as a day where the baby is intubated and ventilated, or is on non-invasive respiratory support (CPAP of non-invasive ventilation) AND parenteral nutrition, or on the day of surgery, or on the day of death, or a day when they have any of the following:

  • Presence of an umbilical arterial line
  • Presence of an umbilical venous line
  • Presence of a peripheral arterial line
  • Insulin infusion
  • Presence of a chest drain
  • Exchange transfusion
  • Therapeutic hypothermia
  • Prostaglandin infusion
  • Presence of replogle tube
  • Presence of epidural catheter
  • Presence of silo for gastroschisis
  • Presence of external ventricular drain
  • Dialysis (any type)

The next level of care is referred to as "high-dependency" and includes for example CPAP with full enteral feeds, or parenteral nutrition without positive pressure respiratory support.

The British Association of Perinatal Medicine standards state that on an intensive care day a baby should have a 1:1 nurse ratio, on a high-dependency day they should have 1 nurse per 2 babies.

A new publication from a group in the UK has found that in 2008 only 9% of intensive care days had 1:1 staffing, and in 2012 that had fallen to 6%, when examining data from 30 to 40 NICUs around the country. As you are all aware, the severity of illness of babies who would be classified as "intensive care" using the BAPM criteria varies hugely. In order to determine whether there is an impact of nursing ratios on outcomes, it is necessary to try to adjust for this severity. But just crudely, if the reduction of days of 1:1 ratio is because the babies are less sick (and someone thought they didn't really need 1:1) then mortality should have fallen. In fact it increased. Over the years where the proportion of days with less 1:1 nursing was falling mortality increased from 4 out of every 100 babies receiving intensive care to 4.5, passing a peak of 5.3 in 2010 and 2011.

Of course the authors have much more sophisticated analysis than that, and after doing all the adjustments that they could, they calculate that, from a median mortality rate of 4.5, every time you decrease the proportion of 1:1 days by 10% you increase mortality by 0.6, that is, to 5.1, then to 5.7... An accompanying editorial says it all:

..there is already a sufficient body of evidence to justify a renewed focus on working towards achieving the national standards set for one-to-one nurse staffing in neonatal intensive care. If not now, when?

The data may not be directly applicable to other health care systems, where some of the roles of NICU nurses in the UK are covered by other professionals, in the UK, for example they do not have respiratory therapists, and it is the nurses who do the tasks that RTs do in our NICU. Nevertheless I am convinced that the same principle applies in North American NICUs, when the workload is higher, and we can provide fewer 1:1 nurse assignments, then infection rates are higher, and probably, mortality also.

I also think that maybe the BAPM should rethink their criteria. Does every child with an Umbilical Venous Line really need 1:1 nursing? A full term baby with hypoglycemia who has a UVC placed for glucose administrator would be classified as "intensive care" and would be supposed to have 1:1. A nurse could probably safely look after 2 babies whose only criteria for "intensive care" was the presence of a chest tube. If you could rationalize the criteria you would probably be able to put more pressure on the system to provide 1:1 for those babies that really need it.

On the other hand a baby who no longer needs parenteral nutrition, but who has just been extubated to CPAP would not be "intensive care" but really needs expert dedicated nursing at a high ratio to prevent re-intubation, and should maybe be considered "intensive care" if they are under 28 weeks for the first 48 hours at least.

I have said many times that I think the most important factor in mortality and morbidity of the extremely immature babies is the quality of the nursing care they receive. In order to give care of good quality, as this study shows, you need adequate quantity.


Singh N, et al. Comparison of animal-derived surfactants for the prevention and treatment of respiratory distress syndrome in preterm infants. Cochrane database of systematic reviews (Online). 2015;12:CD010249.

This is the sort of systematic review that I find really helpful. Some (including some of my own) end up finding little good evidence, and summarizing the results of only one or 2 small trials. That may help to point out the lack of evidence, and to stimulate future trials, but doesn't often give enough information to really inform practice, and individual treatment decisions.

In contrast, this review includes a significant number of trials, some with respectable sample sizes, and ends up  finding significant differences between some of the surfactants that are available.

The review divides the surfactants into the following:

bovine lung lavage surfactant extract, which includes Infasurf, bLES (the Canadian one) and Alveofact

bovine minced lung surfactant extract, which includes Survanta and Surfacten (the old surfactant TA, the Japanese one)

porcine minced lung surfactant extract, which I  know as Curosurf,

porcine lung lavage surfactant, which is apparently called Surfacen.


The authors searched for all the comparisons that had been studied.

Most of the comparisons showed no difference in important clinical outcomes, (although some comparisons had relatively little power,) for example, bovine minced lung and bovine lung lavage surfactants were basically equivalent for all the outcomes. This was true both for prophylactic use and for rescue use.

The comparison that did show different effects was the comparison between minced bovine lung, and minced porcine lung (that is between Survanta and Curosurf), these were all rescue/treatment trials: The first outcome was mortality.

surf death

As you can see the studies are all fairly small, and individually do not show a difference, that is always a bit of a worry, as multiple small studies can inflate an effect. Nevertheless, the summary effect shows higher mortality with the bovine minced lung preparations than the porcine surfactants.

The next outcome is 'BPD' or oxygen requirement at 36 weeks.

surf bpd

Here there is no sign of a difference, when the outcome is expressed as a proportion of those who were enrolled into the study.

The authors of the review also present the outcome "death or BPD" which, as those of you who were at my talk in Baltimore know, I think is not an appropriate composite outcome, and those who were at the International Neonatal Collaboration INC meeting in Bethesda recently know that many of the leaders in the field are of the same opinion. The outcomes of death and BPD have different value for parents (and for society as a whole) and may not change in the same direction. I think the outcomes of Death as one outcome, and BPD as a separate outcome among surviving infants, make much more sense. Unfortunately you can't always tell from data as presented, but, in this case, if we make the probably unsafe, but probably not very wrong, assumption that all the deaths were before 36 weeks, then you can estimate the BPD among survivors. You come up with a relative risk of exactly 1.0, (95% CI 0.85, 1.18).

So overall it seems that porcine minced surfactant leads to more survivors, but the same proportion of BPD (that is O2 requirement at 36 weeks) among surviving infants.

As I mentioned, the confidence intervals are wide, and there are several small studies, but despite these concerns, there are relatively fewer deaths with porcine surfactant, with a risk difference of 0.05 and an NNT, for one fewer death, of 20. These data suggest therefore, that if you treat 20 babies with poractant rather than a minced bovine lung preparation, there would be one more survivor.

Also there are substantially fewer babies who need a second treatment.

surf dose

The NNT here is 7, which means that for every 7 babies you treat, one extra baby will need a second dose. (In the babies in the review, a second dose was required for about 40% of the bovine and about 25% of the porcine treated).

Pneumothoraces were a bit less frequent with porcine, maybe due to chance, and if all airleak syndromes were put together, there were fewer airleaks with porcine.

For the other comparison which is of specific interest to me, that is minced bovine lung to bovine lung lavage surfactants, almost all of the data comes from the trials of Bloom which compared calfactant (Infasurf) to beractant (Survanta). Neither the prophylactic nor rescue trials showed any differences.

The manufacturers will I am sure moan that not all the surfactants within each of these groups are identical, and indeed there are some differences in the details. Calfactant, for example has around twice as much Surfactant Protein B and C compared to bLES. But there is almost no comparative data available for bLES.

Why is the porcine preparation better, that is it works faster, leads to fewer airleaks and has lower mortality?

The studies generally used the manufacturers recommended dose, which is higher for poractant than for the bovine preparations. That may be the only reason, I am not sure about that, but in any case poractant alpha is concentrated enough that the higher initial dose is easily tolerated, whereas it would mean quite large fluid volumes for the other preparations.

In Canada we are still waiting for Curosurf. It has been approved, over a year ago, but is still not being marketed. Come on Chiesi! We are waiting...


The trial this time is from Japan, Nakamura T, et al. Early inhaled steroid use in extremely low birthweight infants: a randomised controlled trial. Archives of Disease in Childhood - Fetal and Neonatal Edition. 2016. 211 babies with a birth weight less than 1000 grams were randomized between June 2006 and Dec 2009; if they were still intubated at 24 hours they received a metered-dose inhaler with either fluticasone or placebo, from which they had 2 'puffs' (total dose of 100 microgams) per day for as long as they were intubated (maximum 6 weeks). The initial plan was to randomize about twice as many babies, but they ran out of money.

The primary outcome variable was going home on oxygen, which I think is a more important outcome than oxygen need at 36 weeks, needing oxygen at home has much more impact on the family than O2 at 36 weeks. However, even in a blinded trial, criteria for needing home oxygen should be clear, so that the external validity of the result can be assessed. I don't know if the criteria for home oxygen in Japan are the same as for my babies, for example. I can't find any criteria for home oxygen in the trial report.

The babies were followed until 3 years of age with a very high rate of retention of the subjects, almost all of the survivors were evaluated.

Basically there was no effect. No improvement in discharge without oxygen, and no impact on neurological or developmental progress.

There were a couple of subgroups that had a difference in the primary outcome, the middle stratum of gestational ages, 24 to 26 weeks, had a different (possible positive effect of the steroids) effect to the other 2 strata, but I don't see a statistical evaluation of the interaction, so even though the result is different to the other strata we don't know if that difference is itself statistically significant.

Babies who had a history of chorioamnionitis also might have had more of an effect, and babies with evidence of RDS might also have had more of an effect, again, for neither of these sub-group comparisons is there a test of the significance of the interaction term.

One surprising aspect of this study is how few of the babies received antenatal steroids; less than 43% in each group. Why? I think its questionable ethically to perform studies when a simple, safe, proven, intervention is not being applied. Similar studies in other populations will usually have over 80% antenatal steroid use, and most of the missed patients are those that deliver too quickly to get a benefit. (80% of the babies were delivered by cesarean section, in contrast, so they were getting active perinatal care). To give the authors the benefit of some doubt, the trial entry criteria may have partially selected babies without antenatal steroid coverage, as they are the ones more likely to be still intubated at 24 hours of age. But I don't think this can be the entire reason for this very low coverage with antenatal steroids, the recent Neurosis trial for example had 90% antenatal steroid use for a similar group of babies.

What this study shows is that in babies with a totally inadequate level of coverage with antenatal steroids, postnatal inhaled steroids don't have much detectable effect on long term oxygen requirements, or on longer term development.

So where do we stand now, with these recent early pulmonary steroid studies? I think there is still room for a well-powered trial; I'm not sure if budesonide mixed with surfactant and given a few times, with each dose of surfactant for example, would be preferable, or an inhalation (of budesonide of even fluticasone) given over the first days and weeks of assisted ventilation make most sense. This new trial and the modest benefits in the Neurosis trial make me wonder if an inhaled aerosol is likely to give much benefit.

Needing oxygen at hospital discharge, and other effects which are of consequence for the life of the family (such as re-admission for respiratory indications during the first year of life) and developmental and neurological progress of the infants should be the outcomes of interest, I think, but a wide consultation of parents to ask them what is most important as an outcome for such a trial would be even better.


TPN toxic?

Humans, after they are born, are supposed to receive their nutrition via the gut. Before that of course, they receive a continuous infusion of nutrition via the umbilical vein. We are far from having an intravenous nutrition mixture for sick preterm infants which closely reflects what the fetus receives from the placenta, but it is clear that we can affect the usual catabolic state of an unfed newly born preterm infant by initiating intravenous nutrition immediately. Whether this is safe and whether it improves clinical outcomes has not been proven in a strictly scientific sense, but immediately starting amino acid solutions for small preterm infants has become the "norm" in the NICU.

Once we leave the immediate neonatal period of course, there is no similar analogy; parenteral nutrition is abnormal, and could well have a different balance of risks and benefits. Which is not to say that we should ignore data from older patients such as these from this new publication.

A high quality new large 3 center RCT (Fivez T, et al. Early versus Late Parenteral Nutrition in Critically Ill Children. The New England journal of medicine. 2016), the PEPaNIC trial, challenges the benefits of early intravenous nutrition in critically ill children, and is consistent with other data in adults. In studies from the adult ICU, early initiation of parenteral nutrition (I will call it PN) may increase infections, had no clear benefits, and, even among those who are extremely high risk of malnutrition, has not been shown to have benefit. This seems to be particularly true in adults who can receive early oral or enteral nutrition, adding early PN may be detrimental.

The new RCT is in  children admitted to the PICU with an expectation that they would have to stay for at least 24 hours. They were randomized to have early PN, or late PN. The protocol for early PN varied among the units, which is both a strength and a weakness of this study, all children received enteral nutrition as soon as it was thought to be safe; in one center the early PN was started on day 1 with an amino acid mixture, the other two centers started with a glucose infusion alone. All 3 centers added lipids on day 2, one of the centers started amino acids on day 2, the third added the amino acids on day 3.

The late-PN group had no intravenous nutrition until day 8.

The main finding of the study was that early PN led to an increase in the proportion of patients who developed a new infection during hospitalisation. The biggest increase was in respiratory infections, which brings me to one question I have about this study; there is no definition of the primary outcome in the paper, nor in the study protocols, which are available from the FPNEJM (formerly prestigious new england journal of medicine). In the supplemental appendix it is noted that the diagnosis of infection was made by "infectious disease specialists" blinded as to treatment allocation, who reviewed the hospital charts of every patient who had more than 48 hours of antibiotics, started after arriving in the PICU. They give a reference at that point, (Horan TC, et al. CDC/NHSN surveillance definition of health care-associated infection and criteria for specific types of infections in the acute care setting. American journal of infection control 2008;36:309-32) which does contain widely used definitions of infections, but the manuscript, and the appendix, don't explicitly say if those were the definitions that had to be followed in each case. If we assume that to be so, then the blood stream infections are easy-ish, diagnosing respiratory infections is much more difficult, especially in the newborn were there are no validated definitions of ventilator associated pneumonia. If the infectious disease specialists were indeed effectively masked to treatment allocation, this may not produce a bias, but might add some random noise.

I am going into some detail about this study, as, even though it was in a PICU population, 209 of the 1440 patients were newborns who had been born at full term, that is they were less than 28 days old on admission to the study. Subgroup analysis revealed no statistically significant differential effect between the newborns and the remaining patients. By which I mean to say that early PN was just as harmful in the newborns as it was in the older children.

The overall study outcomes were: an increase in new infections from 10.7% with delayed PN to 18.5% with early PN, airway infections increased from 4.2% to 8.2%, and bloodstream infections from 1.4% to 3.2%. Other infections were rarer and not affected. So the Odds ratio for developing a new infection was 0.48. It was 0.47 among the newborn subgroup, (95% CI for the adjusted OR for the overall analysis, 0.35, 0.66).

The other primary outcome was length of PICU stay, which was substantially  longer with early PN, from an average of 6.5 days to an average of 9.2 days. The newborns also had a longer PICU stay if they had early PN.

Among the secondary outcomes, the duration of mechanical ventilation was longer with early PN, 6.4 days on average compared to 4.4 days.

Mortality was almost unchanged in the study, 6.1% with early PN  and 5.3% with late. there was more hypoglycemia with the late PN, but that was the only potential advantage of early PN.

As I mentioned above, the results are similar to other studies in adults, in particular a study of over 4000 adult ICU patients run by the same group from Leuven. In that study adults who were mostly able to tolerate some oral or enteral nutrition were randomized to a similar comparison to the PEPaNIC trial. That study also showed an increase in infections and increased duration of ICU stay with early PN, and no difference in mortality. In contrast another study in 1372 adults with contraindications to enteral nutrition showed no difference in infections and shorter duration of assisted ventilation when they were randomized to early PN, compared to delayed PN. In yet another, much smaller study among 300 adults randomized after 3 days in the ICU if they were receiving less than 60% of their nutritional needs enterally. In that study the group that did better was the early PN group, who actually had fewer nosocomial infections.

Which is all a bit confusing, but in general, I would suggest the following interpretation: it seems to me that if you can get very little or none of your nutrition by the enteral route, that early PN has benefits, with maybe a reduction in ventilator days, and an uncertain effect on infections. If there is no contra-indication to increasing nutrition by the enteral route as quickly as possible, then adding early PN, just to try and get the numbers right in terms of calorie and protein administration, may have a balance of negative effects with an increase in infections.

What are we neonatology folks going to do about this? I don't know, is the simple answer. I don't routinely start PN on admission for full-term babies in the NICU, but many of them get started very quickly afterward, often ordered the next morning, unless enteral nutrition can be increased quickly. Some full term  babies with gastrointestinal anomalies who we can't feed get PN very quickly, and get it increased rapidly

So the question is relevant to our babies, if we delayed PN for a few days while increasing enteral nutrition, might they do better?

How are our babies different to those in PEPaNIC?

In my NICU, most of our full term babies are admitted on day 1 or 2, with a few others through to the end of the first week, thereafter they are admitted to the PICU. Very few of the babies in the PEPaNIC study would have been admitted on day 1, if admission patterns in Belgium (and the 3rd site in Edmonton Alberta) are like ours. How much difference might that make? We worry that a period of low calorie intake after birth leads to a catabolic state, which can be reversed by good PN. But, many acutely sick older children are also catabolic on admission to the PICU. So it may not be that much different a situation.

As for the diagnostic mix, The authors state that diagnostic group did not interact with the benefits of delaying PN.

The frequency of new infections among these children seems high compared to what I can find from NICU publications. In the latest CNN annual report for example, the incidence of blood stream infections more than 48 hours after birth was 1% (The definition is "after birth" not "after admission" so this definition leaves the possibility that there might be a few babies admitted with a diagnosis of sepsis at 3 days of age who would be included in the CNN definition, but not in PEPaNIC) , 64 babies among 6,200 babies of 37 weeks gestation or more admitted to the NICU and surviving more than 2 days. Some of these babies will likely be of lower risk than the babies in the PEPaNIC trial, but I think most term admissions to the NICU have a predicted length of stay of at least 48 hours, and many are critically ill. Having been attending staff in both NICU and PICU, I don't think PICU very young infants have an overall systematically different severity of illness than the NICU term babies.

Overall, I would guess that I have to say that the newborn stratum of the PEPaNIC trial are potentially relevant to NICU term babies. The differences with preterm infants are much greater, but even there the relevance is not so far-fetched.

As these authors note, prior observational studies showed associations of early nutritional support with improved outcomes. Which shows again the importance of randomized controlled trials.

Which means (drum roll) I think we need a large enough trial in the NICU term population to investigate the risks of early PN. It should be stratified according to whether enteral nutrition is extremely limited or nil, in one stratum, compared to rapidly advancing in the other, and should compare very early PN to PN delayed until.... when? Perhaps for our population, a good date for late starting of PN would be when the nutritional deficits are accumulating, rather a strict number of days; but the size of the potential effects seems quite large, and certainly worth investigating.

If a term NICU trial shows the same adverse effects if early PN as PEPaNIC, then a further preterm trial might be warranted even though, at present, all the data we have supports giving PN immediately in the very preterm; as science-based medicine advocates, we have to always be ready to admit, "I might be wrong".


An important high quality trial has just been published, it has taken me a bit longer than usual to process the new info. Among other reasons a nice review was posted on the "other neonatal blog", but I wanted to try and put this in context of the other similar published trials. The new trial is Baud O, et al. Effect of early low-dose hydrocortisone on survival without bronchopulmonary dysplasia in extremely preterm infants (PREMILOC): a double-blind, placebo-controlled, multicentre, randomised trial. The Lancet. 2016.

523 babies of less than 28 weeks, and at least 24 weeks, were enrolled and randomized (23 week gestation infants are not generally actively treated in France, so they weren't included) in the first 24 hours of life. Infants who were severely growth restricted or asphyxiated were not included. They didn't have to be on a ventilator or even requiring oxygen, so it was a true trial of prophylaxis. Babies received 1 mg/kg/d of hydrocortisone (divided in 2 doses) for 7 days followed by 0.5 mg/kg/d for 3 days, or placebo. The primary outcome was survival without bronchopulmonary dysplasia at 36 weeks. The study had a sequential analysis design, so sample size is not specified strictly in advance, an interim analysis was done every time an additional 100 patients reached the primary outcome. The maximum sample size that they were aiming for was 786 infants, but the study was stopped prior to that, not because they crossed the analysis lines showing efficacy or futility, but because they were running out of money and resources, so in March 2013 they decided they would have to stop in January 2014.

They found an improvement in the primary outcome, that was just "statistically significant", that is, the estimated probability that such a difference would occur due to chance alone is 0.04, or 1 in 25. Neither of the 2 components of the primary outcome were individually statistically significant, but both were improved in the hydrocortisone group compared to control.

This study has something in common with  several other prior trials. I have summarized the previous trials that randomized all very preterm infants, or all very preterm infants on ventilators to low dose hydrocortisone starting before 48 hours. As you can see they all used relatively similar doses of hydrocortisone, and all except the latest study required babies to be intubated. Some of the babies were a bit larger than Baud's subjects.

Publication Patient characteristics Dose per kg per day used.
Watterberg 1999 N=40, MV, 500-999g, <48h 1 mg x 9d, 0.5 x 3d
Biswas 2003 N=253, MV, <30 wk, <9h 1 mg x 5d, 0.5 x 2d (plus T3)
Watterberg 2004 N=360, MV, 500-999g, 12-48h 1 mg x 12d, 0.5 x 2d
Peltoniemi 2005 N=51, MV, 500-1250g, <36h 2 mg x 2d, 1.5 x 2d, 0.75 x 6d
Bonsante 2007 N=50, MV, <1250g (24-30wk), <48h 1 mg x 9d, 0.5 x 3d
Baud 2016 N=523, 24-<28 wk, <24h 1mg x 7d, 0.5 x 3d

The Biswas study also treated the experimental group with tri-iodothyronine, but T3 is not effective in improving survival or BPD so it could be left in a review for now.

I haven't found any other trial data so far, if anyone knows of any, please let me know.

I did my usual thing and put the data in Revman to see what the Forest plots now look like.

The first is the meta-analysis of the effects on Death, which doesn't look very impressive

Forest plot death

The next is the impact of hydrocortisone prophylaxis on BPD, which is similarly not "statistically significant"

Forest plot BPD

Finally the combined outcome of "death or BPD", which is an outcome that should perhaps be junked, suggests a possible 11% reduction, but with an upper 95% confidence interval that is very close to 1.0

Forest plot death or BPD

These trials were all of reasonably good quality, with some heterogeneity in the 3rd of these analyses, if you do some sensitivity analyses, taking out the Biswas trial because it also used T3, the results are almost identical.

I think at this point we have to say the benefits of early low-dose universal hydrocortisone prophylaxis are "Not Proven", either among all very preterm babies or among those who are ventilated. If there is a real effect it is probably not huge, but there is a potential for as much as a 32% reduction in mortality if you look at the confidence intervals for death. Unfortunately you will all guess what comes next, we need another bigger trial. Before designing such a trial however, the long term follow up of these trials should be collated, there have been some indications of adverse effects of adverse long term effects from the small Peltoniemi trial, but the data from the follow-up of Watterberg's 2004 trial were reassuring. Long term outcomes of the new PREMILOC trial will be essential before either instituting this therapy, or performing another larger trial.


Ohls RK, et al. Preschool Assessment of Preterm Infants Treated With Darbepoetin and Erythropoietin. Pediatrics. 2016;137(3):1-9.

Robin Ohls has been working on Erythropoietin, and its longer acting analogue darbepoietin, for many years now. As well as demonstrating that it stimulates the bone marrow in preterm babies, it now is clear that erythropoietin in some models is neuro-protective. In 2014 she reported the developmental follow up of a randomized trial in infants of 500 to 1250 g birthweight, about 100 infants were randomized to either placebo, erythropoietin or darbepoietin and then followed to discharge and again at 18 months of age with a Bayley assessment of development. During the initial hospitalization the infants in the 2 intervention groups received half as many blood transfusions, and there were no significant complications (in particular no effect on retinopathy). At follow up the 2 "poietin" groups had better scores on the Bayley 3 cognitive composite and on the language composite. It must be said, though, that there are only 24 placebo babies in the follow up, and they had relatively poor scores on the Bayleys, 83 mean for language and 88 for cognitive. Although the differences were significant, these are lower scores than you would normally expect from an unselected group of babies under 1250 g, so it may be that by chance the outcomes of the followed-up babies in the placebo group were worse, the "poietin" groups results were in contrast 91 and 97 on those two scales.

The new data published in the last few weeks are from continued follow-up of the babies to 3.5 to 4 years of age. Unfortunately there has been a lot of drop off, so only 14 placebo and 39 "poietin" babies were examined with IQ tests, and tests of executive function. The previously shown differences persisted, but again it has to be noted that the 14 placebo babies had extremely adverse results, with a full-scale IQ mean of 79, and a performance IQ of 79 whereas the active treatment groups, taken together had means of 93 and 91.

If you were to compare this, for example, to the 5 year follow up of the babies in the caffeine trial, the mean IQ of the control group of babies, who were also of birth weight between 500 and 1250 g, was 97 for the full-scale IQ and 99 for the performance score. The CAP babies may have been lower risk (to be eligible, they had to be considered for caffeine treatment at less than 10 days of age, whereas Ohls' study took any baby expected to survive for at least 48 hours) but those differences are enormous. The babies in Robin Ohls study were not all that sick either, judging from a mortality of 7% in the group after enrollment (it was just over 5% for the infants in the CAP trial). So the very poor scores in the controls can't be easily understood.

Although these data for erythro- or darbe- poietin are hopeful, I think we definitely need to get more data from a much larger trial with high rates of long term follow up before we can be sure that this difference is really an effect of the medications. As darbepoietin seems effective, and there is no evidence of  a differential benefit of one bone-marrow stimulator over another, then darbepoietin, which can be given once a week instead of 3 injections a week would probably be the most appropriate to study in a trial.


Two recent randomized trials, one from our group, and another one from Melbourne have evaluate the role of the videolaryngoscope (VL) in teaching trainees in neonatology to perform endotracheal intubations. The two trials are structured differently and tell us different things about the use of the VL in teaching.

The first, from the Melbourne group, (O'Shea JE, et al. Videolaryngoscopy to Teach Neonatal Intubation: A Randomized Trial. Pediatrics. 2015;136(5):912-9) used the VL for all intubations, but covered the screen in a randomly selected half of the intubations. Just over 200 intubations were randomized, and there were 36 residents with less than 6 months NICU experience who performed them. During the intubation the residents were supervised, therefore during the study many of the residents were accumulating some experience, however there were 42 intubations performed by residents with no previous successful intubations, (so residents who failed an intubation were counted in that group each time they attempted until they got one) most of the residents therefore had very little experience in intubation. Residents had simulation training before attempting intubation of a real baby, and intubations in the delivery room or in the NICU were eligible.

Intubations were supervised using a fairly standardized script by a group of more senior people who could guide the intubation, and identify the structures for the residents during the procedure when the screen was uncovered, or just give tips about technique when it was covered. Each intubation was individually randomized, so a resident could potentially have several covered (or uncovered) intubations in a row.

The primary outcome was success during the first attempt at intubation. (I'm not sure what happened for subsequent attempts when the first failed, if the resident might try again or if someone else then took over.)

Intubations with the screen visible were much more likely to be successful on the first attempt than those with the screen covered (66% vs 41%), this was particularly so for premedicated intubations in the NICU, (72% vs 44%). In the delivery room the subgroup analysis was no longer statistically significant, but remained better for the uncovered group, 50% vs 30%. The duration of the intubations was the same and the number of babies desaturating was similar. Interestingly the first attempt at intubation averaged over 50 seconds duration, but was no different between groups. As the residents gained experience in intubating there was no improvement in success rate for the intubations with covered screen, but the uncovered, screen visible intubations became more and more likely to be successful at the first attempt.

In the other study, from our expert in pedagogical research, Ahmed Moussa and a group of colleagues at our institution (Moussa A, et al. Videolaryngoscope for Teaching Neonatal Endotracheal Intubation: A Randomized Controlled Trial. Pediatrics. 2016;137(3):1-8.) it was the residents who were randomized, not the intubations. So a resident with little prior experience of intubation was randomized, after the initial simulation training in the simulation center, to intubate either with the videolaryngoscope (this group had some extra training in the use of the VL, but no extra training in how to intubate) or a standard laryngoscope. Most of the residents had not previously intubated a neonate, although some of them did have a few prior attempts, and only intubations in the NICU were included. All of the resident were supervised by an attending or a fellow, many of the intubations were nasotracheal, about 70% (especially for the larger babies, that remains our standard in the NICU, if the tube cannot be passed easily through the nose then orotracheal intubation is performed) and 100% of the intubations were premedicated with atropine, fentanyl and succinylcholine.

The study was performed before we introduced our tiny baby intubation team, which I have mentioned here previously, so some of the babies being intubated were very immature, the median gestation was 29 weeks. The overall success of the intubation attempt was significantly higher with the VL than with a conventional laryngoscope, 75% compared to 63%, and the majority of the intubations were successful on the first attempt. Residents were allowed up to 3 attempts, if the baby is tolerating the procedure well, and the intubation was considered a success if the resident was able to insert the tube in those 3 attempts.  By the 7th intubation the residents randomized to the VL were successful over 90% of the time.

What Ahmed had thought when designing the study is that most of our residents, after graduation, will be covering delivery rooms, and neonatal nurseries in level 2 centers, where they won't necessarily have access to a VL, so he wanted to ensure that if you learnt how to intubate with the VL, you could still intubate with a conventional device; The second phase of the study was that all residents intubated with a standard laryngoscope, the success rate of the VL residents dropped a little, but was not statistically different from the conventional group who continued to do their intubations with the standard device. He didn't get as many intubations in phase 2 as he wanted, because the residents graduated from the program, which was very ungrateful of them. Therefore the power of the 2nd phase of the study was not as good as he had wanted.

Of note the intubations were initially a bit longer with the VL, frequently the supervisor was able to redirect the resident to the cords and get the tube in, but that took up a few extra seconds. The median duration of the attempt (from insertion to removal of the blade from the mouth) ended up about 50 to 60 seconds after the first few trials.

The VL used in the 2 studies was not the same. In our hospital the Storz device was used, in Melbourne they chose the Laryflex. In the study from Montreal there were a few of the VL babies where the blade was felt to be too big, which wasn't mentioned by the Melbourne group. The minor differences in blade design might be important for the tiniest babies.

It certainly looks like this is a great way to teach people how to intubate, I think it should become the standard for teaching, based on these data. If we can train residents to intubate with simulations, followed by more stable babies at lower risk of complications using the VL, then when they have proven they are competent they can proceed to intubation of more high-risk infants. It is a skill that many of them will need when they are out in practice, for those who need to be competent for future babies, ensuring that they are capable of intubating by the time they leave residency is an on-going struggle.


A couple of weeks ago I discussed a new multicenter RCT which examined the effects of multiple repeated doses of steroids, given by inhalation starting on the first day of life, and continuing, at least until the infants reached 14 days of age. That study showed an improvement in the primary outcome of survival without BPD with the inhaled steroids.

A newly published trial Yeh TF, et al. Intratracheal Administration of Budesonide/Surfactant to Prevent Bronchopulmonary Dysplasia. Am J Respir Crit Care Med. 2016;193(1):86-95. examines a similar question, but with a somewhat different intervention, and eligibility. The subjects of the trial were very low birth weight infants who were intubated and requiring more than 50% oxygen within the first 4 hours of life. Infants then received either surfactant alone (4 mL/kg of Survanta) or 4 mL/kg of surfactant and 1 ml/kg of budesonide suspension, mixed in a syringe with a label placed to hide the volume. Thy had 858 VLBW infants intubated in the NICU at less than 4 hours of age, of whom 287 had severe enough lung disease to qualify.

Babies received repeat dosing, every 8 hours, if they needed more than 30% oxygen, up to 6(!) doses. The budesonide dose was 0.25 mg/kg/dose. They note that 65% of the budesonide infants only received one dose, compared to 37% of the controls, presumably because of an acute clinical response; indeed the FiO2 over the first few hours after intervention was lower in the budesonide treated babies.

The primary outcome of survival without BPD was improved in the intervention group (death or BPD was 42% with budesonide and 66% in controls). Both components of the primary outcome were improved with budesonide, (death 13%vs 16%, BPD 29% vs 50%).

The paper also includes some summary long-term outcome data from 172 of the survivors. I have no idea why this important data is stuck on as, what seems like an afterthought, when it is not yet complete, (as they note in the discussion). I presume some incompetent peer-reviewer asked them to throw whatever data they have into this publication, when it really needs a separate appropriately presented publication. There aren't enough details about the methodology or the results to say a lot. For example the authors state the follow up was done at 2 to 3 years of age, but they don't say whether they corrected for prematurity (presumably they did, but it would be nice to have the details). The scores on the Bayley version2 Mental development and Motor scales were very similar, with a similar proportion under 70.

They also did a lot of other surveillance for safety, such as presenting blood sugars, and electrolytes, blood pressure and growth data, all of which were unaffected by the intervention.

The online supplement also has some pretty pictures of rats under a PET scan getting budesonide mixed with surfactant, showing it getting rapidly distributed, and staying in the lungs.

I find this very interesting, and worthy of a confirmation trial. Other things I would like to know are : can you safely give prophylactic indomethacin when you have had intra-tracheal budesonide? Are the results still positive if you give surfactant sooner, at 30% oxygen (which is when most of us would give surfactant, rather than waiting to get to 50%)? Are there other respiratory practices which might affect the efficacy of budesonide? Does it work as well if you limit to 2, or 3 doses? Is there any improvement in long-term respiratory health?

It is interesting that the long-term differences are minimal between groups, so, although there is less "BPD", there is no major long term benefit to the babies. There are very few details as I said, but the authors note no health advantage to early budesonide use, in terms of respiratory or overall health.

I think, before starting to do this more widely, we need at least one more large multi-center RCT, powered for the long term follow-up. Outcomes should include respiratory health, to prove a real benefit, rather than just the reduction in a diagnostic label, and neurological and developmental outcomes, to ensure safety.


The long-running epic of the oxygen saturation targeting trials is nearing completion. This publication of the joint results of the Australia and UK trials now includes the primary outcome for the trials, the combined rate of death or "disability". Australia Boost-II and United Kingdom Collaborative Group. Outcomes of Two Trials of Oxygen-Saturation Targets in Preterm Infants. The New England journal of medicine. 2016. Disability is defined as being a cognitive or language score on the Bayley-3 of less than 85, severe visual loss, or disabling CP (GNFCS of 2 or more). I will avoid (for a change) ranting about the inappropriateness of referring to a Bayley cognitive or language score of less than 85 as a "disability".

Because of what happened during the trials the analysis can seem quite complex. But the overall message is that the adverse outcome was increased in the low saturation group when the two trials are combined, however you slice the data.

In case there are any readers who don't know, a calibration artefact was discovered during the trials, which was corrected, leading to each of these trials, and the COT trial, to have babies with oximeters from a before-correction group and an after-correction group. In the two trials, the difference in mortality only occurred after the change in oximeter algorithm, whereas the smaller NZ trial used only the original algorithm and didn't find an effect on mortality (or on long term outcome) and SUPPORT, with somewhat different entry criteria, did show a difference in mortality despite using only the original oximeters. The Canadian Oxygen Trial also showed a higher mortality in the low saturation group after the oximeter adjustment, but it didn't reach statistical significance.

The new publication shows no effect of the trial on "disability", but the analysis of the primary outcome "death or disability" was significant for the pooled data. What gets complicated is that the UK group changed their primary outcome during the trial to be the rate of death or disability with the revised oximeters, whereas the Australians kept this as the whole group. In the UK the oximeters were changed after roughly ¼ of the babes were enrolled, while in Australia 3/5 of the babies were studied with the original devices.

So the primary outcome analysis of the original trials presented doesn't include some of the randomized babies (in the UK trial), which bothers me a bit, but their data are presented and analyzed. And then there is quite a lot of detail in one of the tables. The combined outcome of death or disability was significant for the pooled data which included all of the randomized babies (48% vs 43%) and not far from significant for the revised oximeters (49% vs 44%, RR 1.12, 95% CI 0.99-1.27). As I mentioned above, there isn't any sign of an effect on disability, the difference is all in mortality, now updated to mortality before 2 years of age, most dramatically when the analysis is restricted to the revised oximeters. For the revised oximeters alone the relative risk of death in the low saturation target group was 1.45, (95% CI 1.16 to 1.82).

As everyone now who has Masimo oximeters, they use the new algorithm, and other oximeters were never affected, this is the part of the results which is now most relevant, and I think needs to be taken very seriously.

One comment I would like to make is that the primary analysis for the trials is described as "pre-specified". But how can the analysis by oximeter algorithm be pre-specified if the problem was discovered during the trial? Pre-specified is supposed to mean, "determined before the trial started". I think the analysis is just fine, the dilemma about what to do when this was discovered part way through a trial is not easily resolved, and the different choices of the 2 trials can both be justified. It is the use of the word "pre-specified" that I think is incorrect. Also the definition of disability was changed after the study commenced as they (quite appropriately) changed from the Bayley version 2 to the Bayley version 3. The authors describe these events quite clearly in the text, but as they were changed after the trial started they shouldn't be referred to as pre-specified. the authors are using the term to mean specified before the analysis was started, which  is of course essential and very important, to avoid picking data that look interesting after they have been collected.

To end the saga that I mentioned at the beginning now only needs the NeoPROM collaborative to analyze the individual patient data. It's hard to think that this will give any result other than an increase in mortality with the lower oxygen target.

One other outcome of interest is that in this trial, as in all the others, there was no increase in blindness. This despite an increase in retinopathy requiring treatment. This was also seen in the SUPPORT trial, but there was no increase in retinopathy in COT. I think this means we can be a bit re-assured that the use of carefully targeted saturations in the low 90's will not lead to a new epidemic in blindness; but should not be sanguine about the risks of targeting the higher saturation group, treatment of retinopathy is not, by any means, without consequences, even if we can usually prevent blindness, very severe myopia, loss of peripheral vision, and poor cosmetic results are common.


Azzopardi D, et al. Moderate hypothermia within 6 h of birth plus inhaled xenon versus moderate hypothermia alone after birth asphyxia (TOBY-Xe): a proof-of-concept, open-label, randomised controlled trial. The Lancet Neurology. 2016;15(2):145-53.  Babies who undergo therapeutic hypothermia for perinatal encephalopathy are still at high risk of significant long term impairments. Other therapies to add to hypothermia are being sought and tested, one of them being Xenon. Inhaled xenon gas has neuroprotective effects in many models; but it is expensive and difficult to use, in order to make it affordable for use over several hours you need to recirculate the exhaled xenon, so you need a special ventilator, which has been developed for this trial. In this "pilot' RCT, eligible babies were typical of infants who are cooled, and had to have started on hypothermia within 6 hours after birth. As is usual, most of the 92 enrolled babies (2/3) were born in peripheral hospitals and transported in, many babies were cooled quite quickly, 93% before 4 hours of age. Xenon or standard care was started after randomization which was after arrival in the study centre, so the assigned treatment didn't start until an average of 10 hours of age.  Xenon (or no xenon) was then continued for exactly 24 hours of age.

The primary outcomes of the study were MR findings; using spectroscopy they calculated the ration of lactate to N-acetyl aspartate in the thalamus, and using diffusion tensor imaging they calculated the fractional inosotropy of the posterior limb of the internal capsule. Scans were performed after the end of cooling at about 6 days of age. Because of deaths and a small number of scans not done in survivors, they ended up with around 75 babies with data for each of the two primary outcomes, data from the MRI were analyzed by a masked individual (images of the lone ranger... radiologist) . Basically the study showed no effect of Xenon.

Which is a bummer. (that is colloquial English for "a real shame")

Why didn't it work? I think first off we have to be careful in saying it didn't work, there was no effect on the primary outcomes, but the primary outcomes are surrogates. Surrogates should always be mistrusted, even when they are called "biomarkers". Is the surrogate an accurate enough predictor of good or adverse clinically important outcomes? I think that is questionable here, mostly because I don't know the data well enough to answer the question, but is it possible that a clinically significant benefit of xenon will be shown if (hopefully when) these babies are followed up? My guess is that such an outcome is quite unlikely, but possible. In fact I think this study is a good opportunity to prove the value of the MR surrogates. If the authors are right (and usually Dennis Azzopardi, Dave Edwards and the many associated luminaries who wrote this article are indeed right) then using similar surrogates in future trials will help to screen for effective adjunctive therapies in cooled babies, and more quickly than waiting 2 years or so for follow up.

Maybe starting xenon at 10 hours of age is just too late? As the authors point out, they performed a trial in a real world environment, it would be possible, if you had the ventilator always ready and available, to start Xenon the moment a baby enters the referral NICU, but that would still lead to significant delays of evaluation and transport. Maybe 24 hours is too short? It was based on the best previously available literature, and again technically feasible, before doing another study with longer Xenon administration I think we would need some very good rationale.

In the end, this real-life application of xenon in cooled babies didn't show any sign of being effective. We should look elsewhere I guess, something that could be given very quickly when a baby is cooled, such as melatonin, or erythropoietin look like they are the most worthy of further investigation. A review of the literature from 3 to 4 years ago concluded that, and I haven't seen much to change the situation since then. Robertson NJ, et al. Which Neuroprotective Agents are Ready for Bench to Bedside Translation in the Newborn Infant? The Journal of pediatrics. 2012;160(4):544-52.e4.


I have often wondered why my obstetrical colleagues would often induce labour once a woman with ruptured membranes reached 34 weeks. I wasn't aware of any data to support doing this, or, on the other hand, any good data to say that you shouldn't.

It turns out that I was well-informed, there just wasn't any good data, until now. Morris JM, et al. Immediate delivery compared with expectant management after preterm pre-labour rupture of the membranes close to term (PPROMT trial): a randomised controlled trial. Lancet. 2015;387(10017):444-52. In this study over 1800 women with singleton pregnancies and ruptured membranes without labour, who were between 34 and 37 weeks gestation, were randomized to either immediate delivery (induction or cesarean) or expectant management, in which case the woman and her obstetrician waited for spontaneous labour or another indication to deliver. Women whose membranes ruptured before 34 weeks became eligible when they hit that mark.

This remarkable study took 10 years to recruit their subjects. It was run out of Sydney, and funded by the NHMRC of Australia and enrolled mothers from 11 different countries.

What did they find? Well, neonatal sepsis occurred in 23 (2%) of the babies in the immediate delivery group, 29 (3%) of the expectant group, a difference which could easily be due to chance. There were 3 neonatal deaths in each group. On the other hand, expectantly managed pregnancies ended up with a significantly higher gestational age and birthweight, not surprisingly, and as a result less NICU admission, less respiratory distress, less assisted ventilation,  and fewer days in hospital, all of which were highly statistically significant. For the mothers there were some downsides, there was a slight increase in  antepartum or intrapartum haemorrhage from 3% to 5% and they had one day more of hospital stay with expectant management, but they had many fewer cesarean deliveries. 19% in the expectant group compared to 26%.

This is very high quality evidence that we should not be doing what ACOG currently states, which is to deliver immediately because of the risk of neonatal sepsis. If things are going well, and there is no sign of infection, pre-labour preterm rupture of membranes can be followed closely, with delivery for other obstetric indications.


The oxygen saturation targeting trials showed more retinopathy with higher oxygen saturation targets. Will this translate into more retinopathy in actual practice? Many units have increased their saturation targets as a result of those studies. This may indeed lead to more RoP, and the expected result seems to have happened, in Melbourne at least. A before and after study showed that there was an increase in retinopathy, both overall and of stage 2 or more. They evaluated the outcomes in babies under 30 weeks or under 1250 g who survived to get retinal screening, about 150 before they changed and nearly 200 afterward. They saw more total RoP. There were very few babies who needed laser, 1 before and 3 after, which may have been due to chance, with such small numbers, but it certainly didn't go down. Among infants of less than 28 weeks, the stage 2 disease incidence went from 16% to 34%.

What can we do to counter this? Which is likely to be repeated in many different units who have raised their saturation limits. What interventions are there that can reduce retinopathy? Well, we know that poor early neonatal growth is associated with an increased risk of retinopathy. So optimizing neonatal nutrition in at-risk infants should help, although that hasn't been proven in randomized trials, as far as I am aware.

An RCT from Poland (with the collaboration of Michael Sherman) suggests that a mixed lipid source, including some fish oil/omega-3 fatty acids may reduce RoP in very preterm infants. They randomized infants <1250g and less than 32 weeks. The 70 control infants received a mixture of soy and olive oil lipids (Clinoleic, which is used in Europe, but I don't think is licensed in North America). The 60 babies in the intervention group received half Clinoleic, and half Omegaven (the fish oil emulsion with lots of omega-3 goodies) by volume, but the Clinoleic is a 20% emulsion, the Omegaven is a 10% emulsion. So they had about 1/3 omegaven, 2/3 the other stuff.

It was an unblinded study, apart from the ophthalmologist who was apparently… uuh…blinded. (Sorry about that). The primary study outcome was "an assessment of ROP severity and whether laser photocoagulation was required to save vision" which isn't a primary study outcome, of course, you can't have a study outcome which is an "assessment of" something. The sample size was calculated based on an extremely high frequency of retinal ablation in the controls, of 27%, and a massive reduction to 7.5% in the fish oil group. so we will call that the primary outcome variable.

The babies in the study were on average just under 1000g birth weight, and were 28 weeks gestational age. Those in the new-lipid group got much more DHA (docosahexaenoic acid, an omega-3 FA) which they incorporated into red cell membranes. They defined cholestasis as more than 20% of the bilirubin being conjugated; which was very frequent in the controls, 20/70 vs 3/60 in the group with the fish oil. Treated retinopathy was extremely frequent in the controls, 22/70 and decreased to become very frequent in the fish oil group, 9/60.

The proportions of fish oil are not the same with their mixture as with SMOFLipid, a mixture of Soy, Medium chain triglycerides, Olive oil, and Fish Lipids, which is commercially available. In SMOF about 15% of the lipids are fish oil derived.

This looks hopeful, but we will need to be sure that the results are the same with an approved lipid in Canada (SMOFLipid is approved, but not specifically for newborns in Canada), or wherever you are in the world. Also that it is effective in NICUs with a much lower rate of retinopathy needing treatment, then providing enough omega-3 FAs from early life in the very preterm infant might help to counter the effects of keeping the saturations a little higher. 


Which is no surprise, I hope, to any of us.

Neil Finer has been a leader in the field of recognizing and quantifying the adverse physiologic effects of endotracheal intubation, and of finding ways to reduce those effects using premedication.

It was largely as a result of his work that professional societies now recommend using medications prior to intubation; medications that reduce pain, help to stabilize the babies physiology and facilitate the intubation.

We have recently, in our NICU, restricted the performance of endotracheal intubation in our most fragile patients to only those professionals who have already demonstrated their competence with larger, more stable babies. Infants under 29 weeks gestation are now only intubated by physicians, NNPs, or respiratory therapists who have shown that they can intubate larger infants. Babies with diaphragmatic hernia are also only intubated by a restricted list of people. I think that the sickest babies are not the place where a first-timer (or a second-timer) should be learning what is a difficult skill. Although junior residents who may in the future become the physician covering a delivery service in a peripheral hospital, and may well become the NRP team leader, do need to learn how to perform this skill well, our first priority has to be the babies, and making sure the most at-risk, tiniest, babies have the most skillful person performing procedures. It would be better, I think, to also have restrictions for the sickest larger babies with very stiff lungs who often desaturate severely and very quickly during intubation, but we have to find ways to ensure that residents leaving the training program have enough exposure to become competent.

We have submitted an abstract with our data to the next PAS meeting, and I will reveal our results at a later date, except to say that more experienced intubators are much more likely to intubate on the first attempt.

Does this matter? Well a new observational study from Hatch and co-workers in Vanderbilt studied 273 intubations in 162 patients. Adverse events occurred in 107 (39%) intubations with nonsevere and severe events in 96 (35%) and 24 (8.8%) intubations, respectively.

Nonsevere events included : Esophageal intubation with immediate recognition, Mainstem bronchial intubation (confirmed by chest radiograph), Oral/airway bleeding, Difficult bag-mask ventilation, Emesis, Chest wall rigidity

Severe complications included: Hypotension receiving treatment, An urgent or elective intubation becoming an emergency, Chest compressions, Code medications (presumably this means needing an epinephrine bolus), or Pneumothorax.

Adverse events were much more frequent for emergency, rather than elective or urgent intubations, and the odds of having an adverse event were doubled if there was more than one attempt at intubation. Infants who needed 3 or 4 attempts had about a 75% chance of an adverse event. Novice intubators had 22% success on the first try while for experienced intubators that was up to 57%.

Hypoxia and bradycardia were not counted as adverse events, as the authors wanted to be able to compare their data to studies looking at intubation for older children. But those two "secondary" outcomes were very common. 44% of the babies desaturated to below 60% saturation, and 24% had a bradycardia to less than 60 per minute.

We continue, in our NICU, to allow less experienced intubators to be the first to attempt intubation on larger babies as we think that the consequences, in the  long term, for the larger baby are probably less important, but are there long term consequences of all these adverse events in very immature babies?

A study from Stanford by Wallenstein and colleagues suggests that there are serious consequences. They compared the outcomes of babies under 1000g who needed intubation in the delivery room between those who were successfully intubated on their first attempt to those who required more than 1 attempt.

There were 88 babies over a 6 year period who were in their cohort.  40% were intubated on the first attempt and 60% required multiple attempts. Babies who were not intubated the first time were more likely to need chest compressions after the first attempt, were more likely to develop a grade 3 or 4 IVH, were more likely to develop NEC, a pneumothorax or PVL. Differences which remained after adjusting for other risk factors, and each of which individually was not "statistically significant".

Death or neurodevelopmental impairment occurred in 29% of infants intubated on the first attempt, compared with 53% of infants that required multiple attempts, adjusted odds ratio 0.4 (95% confidence interval 0.1 to 1.0), P<0.05. Which was due to a more than doubling in the odds of dying (from 11 to 25%), and nearly a doubling in the odds of "neurodevelopmental impairment".

What should we do about this?

Firstly, I think that our approach, of restricting intubation attempts by inexperienced personnel to only the more stable babies, is the way to go. More experienced personnel have a much higher rate of success on the first attempt, and fewer attempts means much fewer complications.

Secondly, we should all have strict protocols for premedication for elective intubations. The evidence of benefit, and the reduction of adverse events during premedicated intubations is very clear. One criticism of the data from Vanderbilt is that almost none of the intubations were preceded by muscle relaxation, and those that were pre-medicated used an opiate and a benzodiazepine. This despite the good evidence that muscle relaxation facilitates and shortens intubation, improves intubation conditions, and improves success on the first attempt; and the complete lack of evidence for a benefit of benzodiazepines.

Thirdly we need to find ways of training junior staff in this skill that do not include exposing critically ill babies to inexperienced intubators with a low success rate, including much more extensive use of simulation, simulations which are much more realistic, video-laryngoscopy, improved video-laryngoscopes, and so on.

Fourthly, we need to continue to investigate ways to make intubation less traumatic, less painful, less frequently unsuccessful, and faster.

Finally whenever we are about to intubate a baby, we should ask ourselves if we are in the best place to do it (can we wait till we get the baby to the NICU, place an IV and pre-medicate?) with the best personnel (do we have rules that there is always an experienced person present for every birth of an extremely preterm infant?) the best environment, the best equipment, and the best monitoring.


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.


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 ****' (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.