Does inhaling Nitric Oxide cause cancer?

How would you answer the question posed in this title? Given the relative rarity of infant cancers, I guess you would have to follow thousands of babies treated with iNO, and compare with thousands of babies who were equally sick but not treated with iNO. You could only do that with national databases I would guess. Here is a new study that has done exactly that: (Dixon F, et al. Treatment with nitric oxide in the neonatal intensive care unit is associated with increased risk of childhood cancer. Acta Paediatr. 2018). There are previous studies showing an increase in hepatoblastomas amongst very preterm babies, and apparently there are also some studies showing an increase in malignancies among larger than average babies.

This new publication suggests that, as a new potential risk factor, or marker of risk, inhaled nitric oxide use in the neonatal period is associated with an increased risk of neonatal cancers, and specifically liver tumours.

The birth database that the authors used included just over 1 million births between 2000 and 2011, with the outcome of interest being malignant disease diagnosed at any time, so the average follow up was about 6.5 years. There were just over 1000 cancers diagnosed, so about 0.1% of live born babies.

2.2% of the total birth cohort of babies were in the NICU database, whereas nearly 6% of the cancers were among NICU patients (or ex-NICU patients). They looked at demographics, especially gestational age and birth weight. And found 2 associations, being preterm or being high birthweight, between the occurrence of any cancer and the characteristic. Being born before 37 weeks gave an increased Odds Ratio of cancer of 1.3 (95% CI 1.0-1.6) and, for being over 4 kg the OR was 1.4 (1.2-1.6).

The authors then examined the various subgroups of cancers, for the preterm group, the risk appears to only be increased for hepatic tumours. The OR being over 12 for the babies between 23 and 31 weeks and 2.0 for the 32 to 36 week group. Although the impact of being very preterm was “statistically significant” this group only included 3 babies with liver tumours, similarly in the 32 to 36 week group there were another 3 babies, compared to 20 in the full term group.

The authors don’t identify the type of liver cancers in their study, but the majority of pediatric liver cancers are hepatoblastomas, those are embryonal tumours that are thought to often have their origin in the prenatal period. I have seen 3 or 4 hepatoblastomas diagnosed in the late fetal, or neonatal period. The association with preterm birth has been postulated to be due to exposure to numerous oncogenic or potentially oncogenic phenomena, such as x-rays, phthalates and other drugs.

In this study the authors excluded babies with a diagnosis in the first 4 weeks of life, so one of my first thoughts, which was that maybe the babies were sick because they already had complications of their cancer (although rare that could happen often enough to change the imbalance by a couple of kids or so).

Among the neonatal therapies they examined, from the NICU database were surfactant, indomethacin, postnatal steroids, and inhaled nitric oxide. There were 8 babies who received nitric oxide who developed a cancer, of a total of nearly 800 NO treated patients. In the abstract they note that the 8 who developed cancer 4 months to 5 years after inhaled NO treatment were between 30 and 41 weeks gestation. That information doesn’t seem to be anywhere else in the manuscript.

All observational studies are at risk of residual confounding, even when you do your best to correct for everything that you can think of. That is why RCTs are so powerful! So what are the risks for confounding in these data? Infants who receive inhaled NO are often acutely sick, have multiple infusions of multiple different drugs, may have TPN for prolonged periods, have multiple x-rays.

Is it biologically feasible that inhaled NO could increase the risk of hepatic tumours? There is some evidence, that the authors quote, of involvement of nitric oxide in oncogenesis, but the articles that the authors quote are all about intra and intercellular signalling by endogenously produced NO. That is very different to potential roles of inhaled NO, which has largely been degraded to nitrates and nitrites before it gets anywhere else in the body than the lung. Nitric oxide has oxidant and anti-oxidant and nitrosylating actions in the lungs of treated animals, but it might be a stretch to suggest that the same effects might occur in the liver or the brain.

If you take hepatic tumours out of the equation, is there any other signal in these data? That is hard to say as the numbers start to get too small, I would guess, if you break down different tumours by intervention type. But I would also guess that if all the 8 NO treated babies had the same kind of weird tumour (or the same kind of less weird tumour like Hodgkins Lymphoma for example) they would have said so.

I think that, as with all well-performed large observational studies, we are left with associations, that could potentially be causative, but might also be related to other risks that the babies have in common. It would be nice to see a case control study, or one using propensity score matching, comparing sick NICU babies who received NO and those who didn’t but who had a similar duration of intensive care treatment, assisted ventilation, exposure to phthalates, numbers of chest x-rays etc, to see if the risk remains when well matched for other interventions. Other studies to see if there is a dose-response relationship might confirm the possibility that the effect is causative.

Given that there is no good evidence that inhaled NO improves clinically important outcomes in preterm babies, this new data suggest that we should avoid iNO in the preterm patient unless you have a good reason for supposing it will be helpful. In full term babies inhaled NO may be life-saving, and the possibility of an absolute 1% risk increase in cancer risk should be taken into account, but would not often change my mind. On the other hand, less of most things is likely to be less toxic, so weaning nitric oxide as soon as it isn’t helping anymore is probably a good thing to do, and not only for the possible cancer risk.

We should now perform more epidemiologic studies in unrelated populations to see if we can confirm this worrying association, and that it is robust after correcting for other potential confounders.




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Oxygen for preterm infants, what dose of this toxic drug is the right dose? #NeoEBM

The NeoProm primary publication is the result of a prolonged gestation; I remember meetings over 15 years ago when Cynthia Cole from Boston was suggesting the idea, and although she was not, I think, finally an author on any of the major trials or the Prospective Meta-Analysis, she was quite persuasive and helped to get the ball rolling.

Askie LM, et al. Association Between Oxygen Saturation Targeting and Death or Disability in Extremely Preterm Infants in the Neonatal Oxygenation Prospective Meta-analysis Collaboration. JAMA. 2018;319(21):2190-201. I am actually a little surprised that the title of this article starts with the word “association”; surely prospective randomized controlled trials are designed to investigate causation, rather than association?

What is NeoProm, and what is a prospective meta-analysis (PMA)? The idea behind PMA is that, to prove small, but clinically important, differences in outcomes we need to perform very large trials. In neonatology we look after about 10% of all human beings, but only for the first few days, or occasionally weeks, of life. When we are looking at an even smaller proportion of those live births, around 1%, that is, those born extremely preterm, then large international collaborations become essential for many of the important questions in the NICU.

Costs for such very large trials can become prohibitive for a single funding agency, even if, like NIH (USA), CIHR (Canada), NHMRC (Australia), and the MRC (UK), many large national bodies are willing to fund participants in other countries, if you need to fund a trial in 5000 intensive care patients, requiring extensive data collection, it gets very expensive. One alternative is to perform a number of co-ordinated trials, funded by different agencies, with the intention of performing an Individual Patient Data meta-analysis. You facilitate the IPD, by agreeing beforehand on what data will be collected, and how, and what the definitions of certain outcomes will be. It is also important, of course, to pre-define the primary outcome and the important secondary outcomes. These restrictions on trial design are what makes a PMA different to a post-hoc IPD meta-analysis.

A PMA is not as powerful as an individual trial with the same number of participants, because you have to use some of the statistical power to account for possible differences between trials. You also have to be careful that all the originally planned trials are truly committed to the PMA, otherwise you might end up with fragmentary publications, which might artificially inflate the apparent “significance” of the results.

The NeoProm collaboration is, I think, the first PMA in neonatology. Bravo to all the PI’s, the steering committees, the local investigators (including me!) and in particular to Lisa Askie, who seems to still be sane (or at least as sane as she ever was) following the successful completion of this megaproject.

The Collaboration included SUPPORT, which was started and finished first with dates that overlapped the others, the BOOST-2 trials in Australia and in NZ, BOOST2-UK, and COT. In total there were indeed almost 5000 extremely preterm babies in the trials.

The primary outcome, agreed before the collaboration proceeded, was a composite of either death or “major disability” at 18 to 24 months corrected age: major disability was any of the following: Bayley Scales Development version 3 cognitive or language score of less than 85; severe visual loss (cannot fixate or is legally blind with visual acuity <6/60 in both eyes); cerebral palsy with the GMFCS 2 or higher; or deafness requiring hearing aids.

Basically there was no impact of the different saturation targets (high 80’s vs low 90’s) on the primary outcome.

I guess I could stop there, but you know me!

I have serious concerns about how this result might be interpreted, and about the relevance of this primary outcome.

A Bayley-3 score of under 85 at 2 years of age is NOT A DISABILITY. The Bayley test is a somewhat useful, over-sensitive, screening test (over-sensitive as most screening tests should be) for developmental delay, the MAJORITY of infants with a Bayley under 85 at 24 months do not have any long-term impairment. Very few of them have a disability, and even fewer have a handicap. It is certainly not equivalent to being dead.

The major part of the “disability” outcome was a low Bayley score, of the 1429 babies with “major disability” 1319 had a low Bayley score, 213 had cerebral palsy, 120 were deaf and 48 had serious visual problems; and there were 896 deaths in total by 2 years of age. (In the supplemental information you can find that the Bayley-3 language or cognitive composite scores were under 70 for 443 of the infants).

I understand the problem of competing outcomes, that a baby who is dead cannot have a developmental delay at 24 months, but there are other ways of dealing with competing outcomes that do not imply equivalence. Including: hierarchical outcome evaluations, for example, which evaluate the most important first.

What should the primary outcome be for large neonatal studies? Almost all of our survivors have acceptable quality of life, so I think that survival should be the primary outcome of any of these studies. There might be some reasonable disagreement, however, about the place of very profound disability with inability to communicate, although rare, there are reasonable people, and parents of extremely preterm babies, who find such an outcome to be equivalent to death, in terms of the value to them and the infant. Perhaps the first outcome to evaluate could be a composite of death and very profound impairment (inability to communicate). I also think that the decision regarding primary, and other, outcomes should be made in collaboration with parent partners, and former preterm infants.

Following this, evaluation of other aspects of longer term outcomes could follow.

As profound impairment with inability to communicate is so rare among our extreme preterm babies, the primary outcome of this PMA would likely be unchanged if death or profound disability was used as the primary outcome, compared to death alone. The PMA shows an absolute decrease in mortality before discharge of 2.4%, and a relative decrease of 17% when the higher saturation targets are used, compared to lower targets. The 95% confidence intervals for that outcome do not include ‘no difference’, so the difference is unlikely to be due to chance alone. As the article in JAMA is (too) ready to point out, that is a secondary outcome; the components of a primary outcome are strictly always secondary outcomes, but I think they have a different status to other outcomes, which are not directly related to the primary, such as, for this study, bronchopulmonary dysplasia for example. Many years ago when we started on this adventure I thought that BPD would probably be less frequent in the low saturation group, as you would need less oxygen and lower mean airway pressures during ventilation, and less non-invasive ventilation afterwards; but there really is no signal at all for BPD. There are of course more babies in the high saturation target group receiving oxygen at 36 weeks gestation, but other indicators of lung injury severity, such as the proportoin going home on oxygen (supplemental appendix), when home oxygen babies came out of their oxygen, and hospital readmissions in the first years of life, were the same between groups. One think I hadn’t particularly been expecting was that the lower saturation group would have more severe Necrotising Enterocolitis (that is needing surgery or dying), but that does seem to be the case, with 9% in the low saturation group, and 7% in the high saturation group.

The implication of this for clinical practice is that NeoProm confirms that the only target SpO2 range which is evidence-based is between 90 and 95%. Anything else (such as 88 to 92% for example) is speculative and would require other studies of many thousands of babies. I don’t think that is likely to happen in the near future.

The main adverse outcome of higher saturations is worse retinopathy, leading to an increase in the need for treatment, from 11% to 15%. As noted in the individual trials, even though treatment was more frequent, visual outcomes at 2 years of age were not different. We need to find other ways of decreasing retinopathy, in particular improving nutritional standards and growth outcomes.

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Even more thoughts on breast milk fortification

I thought I would discuss the new study by O’Connor and colleagues in a little more detail (O’Connor DL, et al. Nutrient enrichment of human milk with human and bovine milk-based fortifiers for infants born weighing <1250 g: a randomized clinical trial. The American journal of clinical nutrition. 2018). They randomized babies who were under 1250 g birth weight whose mothers were planning to breast feed. There were about 250 eligible babies, and about half of them (127) were enrolled and randomized. The primary outcome variable of this new study from the OptiMom program was feeding intolerance, defined as having feeds stopped for more than 12 hours, or having a >50% reduction in feed volume. That might not be the best outcome, in terms of clinical significance, but choosing most aspects of trial design requires compromise, between what is important, what is essential, and what is possible.

The authors note in the introduction that a trial with NEC as the primary outcome would have needed nearly 1200 babies. I think that is a study that now really needs to be done. But, Prolacta supplied the human milk based fortifier for the study at the cost of manufacturing, the trial was otherwise funded by the CIHR.

I think trying to finance a trial similar to this new one, but much bigger at 1200 babies, might be impossible. According to a study of the cost effectiveness of an “exclusive human milk diet” (compared to a diet using bovine milk supplements and mother’s milk with a bovine fortifier) by Ganapathy et al in 2011, the fortifier cost about $10,000 per baby. Just the cost of the fortifier for a 1200 patient study would be 6 million dollars, if the 600 human milk fortifier babies received about the same amount of fortifier as in that analysis, and it was supplied at market rates. Even if it was supplied at cost it might be prohibitive. I think the next best thing we can do is to perform epidemiologic studies, preferably with propensity score matching, to see, in babies who all receive mothers milk supplemented with pasteurized donor milk, if human milk based fortifier really does lead to less NEC than bovine protein based milk fortifier.

In the absence of any such data I certainly can’t see my health care system funding the human milk based fortifier! I think that the O’Connor study might lead to some insurers in the USA wanting to stop re-imbursing this cost also, if there are many that do so.

The 95% confidence intervals for the difference in stage 2 NEC between the 2 groups in O’Connor’s study was about -8% to +8%. In the Ganapathy analysis that I just mentioned they calculated the cost-effectiveness of a mother’s milk with human milk based fortifier diet based on a reduction from 16% to 6% in NEC. With such a reduction in NEC the hospital costs of the fortifier were calculated to be less than the hospital costs of medical and surgical NEC.

In the two studies from the OptiMom project that I have discussed here recently (the study above and the comparison between artificial formula and donor human milk as supplements), the frequency of NEC in the groups that received mother’s milk, with a donor human milk supplement as necessary, and bovine fortifier, was very similar at just under 5%.

If we calculate the cost-effectiveness of an exclusive human milk based diet by assuming that the human milk diet completely eliminated NEC (which isn’t likely to be true, see below), then we can redo the analysis of Ganapathy.

Using a 5% frequency of NEC you can use the same calculations as Ganapathy did, to calculate the additional costs of NEC, basically, at an incidence of 16%, the costs of NEC per baby were about $24,000, so at 5% the additional costs per baby average somewhere around $8000. Human milk based fortifier is then not quite cost-effective even if you completely eliminated NEC! Of course cost-effectiveness is not the only concern: if you can truly prevent NEC then that is worth something! It certainly seems highly unlikely that a new large trial will show NEC to be completely eliminated by human-milk based fortifier, decreasing from 5% to 0%.

In the new study babies randomized to the human-milk based fortifier had an incidence of NEC of 5%; in the older study Sullivan S, et al. An Exclusively Human Milk-Based Diet Is Associated with a Lower Rate of Necrotizing Enterocolitis than a Diet of Human Milk and Bovine Milk-Based Products. The Journal of pediatrics. 2010;156(4):562-7.e1. The exclusive human milk group had an incidence of NEC of 6%.

That means that in total there are about 29+138+64 (=231) babies from the randomized trials who have received an exclusive human milk based diet, and in those 3 groups there were 12 cases of NEC stage 2 or more. For an incidence of just under 5%, and 95% confidence intervals of just under 3% to just over 9%, 99% confidence intervals are 2.2% to 10%

So it seems unlikely that a larger study would show a complete elimination of NEC, and cost-efficacy will depend on whether NEC really is decreased by replacing bovine-protein based fortification with human-milk based fortification.

It seems from the available studies that supplementing mother’s own milk with a pasteurized donor milk when there is not enough mother’s milk, decreases NEC, even when the milk is fortified with bovine milk products. In contrast there are no reliable data that going the next step and replacing the fortifier with a human-milk based product has any influence on the primary outcome of O’Connor, which was major feeding interruptions, or any of the other indicators of tolerance, which were very similar between the groups. It may be that diluting the bovine proteins in human milk, rather than giving a full feed of bovine-based milk, has very different impacts on gut inflammation. If there is an impact on NEC it is probably quite small. Growth variables were also no different between groups, partly because, probably, the human milk based group were immediately fortified to a higher assumed calorie density than the bovine based fortification group. With this difference in feeding approach, the weight, length, and head circumference remained very similar.

Late onset sepsis was numerically lower in the human milk based group, but may have been due to random error, Intriguingly though, severe retinopathy was much lower in the human milk based group (RoP needing intervention or stage 4 or 5) 6 cases (bovine fortifier) vs 1 case (human fortifier). Retinopathy of all grades was very similar in Sullivan’s study, and Cristofalo’s by diet group; so this might just be a chance, finding, but needs to be pursued in other epidemiologic work.

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More on breast milk fortification

The trial that I mentioned in my previous post on this topic, that I said had not been published, has now been published! O’Connor DL, et al. Nutrient enrichment of human milk with human and bovine milk-based fortifiers for infants born weighing <1250 g: a randomized clinical trial. The American journal of clinical nutrition. 2018.

Thanks to Cindy Ulrich from Toronto who gave me the heads up. The new publication reports a trial that  (in both groups) supplemented mothers milk with pasteurized banked human milk when necessary, and compared fortification of the milk with either a human milk based fortifier or a bovine-protein based fortifier.

Unfortunately there were only 127 babies randomized, which limits the power of the trial for clinically important outcomes. Nevertheless, they showed no difference in any outcome. All of the outcomes were very similar between human milk based fortification, and cows’ milk based fortification.

In specific terms there were just under 5% of cases of NEC stage 2o or more in the 2 groups. That is 3 babies in each group.

For now the implication of this trial is that, when a mother of a very preterm baby wants to breast feed, if there is not enough milk and the baby needs a supplement, then pasteurized donated human milk is the optimal source.  Once the TPN is being withdrawn, and the baby needs fortification of their feeds, there is no clear advantage of either a human-milk based fortifier, or a bovine based fortifier, on clinically important outcomes.

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Don’t push so hard! Diaphragmatic hernia babies have fragile lungs that can easily be overdistended.

Neonatology ‘grew up’ treating babies with surfactant deficiency. We all learnt about recruiting lungs with PEEP, and that increasing mean airway pressure improved oxygenation.

It is generally true that babies with acute pulmonary disease of low-volume such as HMD, pneumonia, and some babies with meconium aspiration, increasing mean airway pressure improves oxygenation. I remember an old paper from my mentor Neil Finer, that showed that all ways of increasing MAP were not equivalent. For the same increase in mean airway pressure, increasing PEEP was more effective, in terms of increasing oxygenation, than increasing the peak inspiratory pressure or changing the Inspiration:Expiration ratio. Increasing lung recruitment by maintaining a higher pressure in the lungs during expiration, thus improving end-expiratory lung volume, improves V/Q matching.

Unfortunately this has led to the tendency to always increase PEEP, and/or mean airway pressure, when oxygenation is a problem.

But some lungs are not recruited by increasing PEEP. Specifically, babies with pulmonary hypoplasia do not benefit from increased PEEP, (unless they also have HMD).

In contrast, increasing PEEP in such babies has a number of potential adverse effects. These have been very nicely demonstrated by a recent article reporting a cross-over study in 17 patients with congenital diaphragmatic hernia (CDH) and pulmonary hypertension. (Lower Distending Pressure Improves Respiratory Mechanics in Congenital Diaphragmatic Hernia Complicated by Persistent Pulmonary Hypertension, Guevorkian D et, J Pediat 2018)  In the postoperative period infants were randomly placed on a PEEP of 2 or 5 cmH2O for an hour, and then switched to the other pressure. Lung mechanics and hemodynamics were measured at the end of each hour. The peak pressure was adjusted by 3 cmH2O also, in order to keep the ‘delta-P’ unchanged.

Lower PEEP led to substantially higher compliance, higher tidal volume, and much lower PCO2. Left pulmonary artery blood flow velocities, diastolic left ventricle diameter, and the left atrium to aorta diameter ratio were greater at 2 cmH2O of PEEP compared with 5 cmH2O. Here is the compliance figure:

Of note, at 2 cmH2O oxygenation was much better, oxygen requirement dropped from 35% at a PEEP of 5 cmH2O, to 25% at 2 cmH2O, with a preductal saturation that was higher, and a post-ductal saturation that was much higher at the lower PEEP (Mean 91% compared to 81%).

In other words, increasing PEEP from 2 to 5 cmH2O led to overdistension of the lungs, pushing them to a higher, flatter part of the pressure volume curves (decreasing compliance and minute ventilation), and led to compression of the pulmonary vasculature which increased shunting, and worsened ventilation and oxygenation.

There is little previous data to compare this to, but a study in 2000 from Dresden measured FRC directly in 5 patients with CDH both before surgery and after, and also measured lung mechanics. They used varying PEEP levels, between 1 and 4 cmH2O, for the postop measurements. They showed that after surgery, at a PEEP of 4, there was a reduction in compliance compared to pre-op, and that with reductions in PEEP to 1 cmH2O compliance progressively improved, FRC was about 20% higher at a PEEP of 4 than at 1 cmH2O, confirming the obvious interpretation that the adverse effects of PEEP were caused by an increase in lung volume, and overdistension. They also studied the effects of suction on the chest tube, and showed similar effects, with increasing FRC and decreasing lung compliance as suction increased from 0 to -10 cmH2O.

Although both of these studies show the effect in the postoperative period, I can’t see any good reason that the effects would be different pre-operatively, or indeed in other patients with pulmonary hypoplasia.

You can see similar effects in babies with HMD who have had a good response to surfactant. There are a few articles that have measured mechanics and lung volumes at different levels of PEEP after surfactant treatment. They show that over-distension of the lungs at relatively low levels of PEEP is frequent, Eduardo Bancalari’s group compared PEEP of 2, 4 and 6 cmH2O, Anne Greenough studied 0, 3 and 6 cmH2O, Dinger et al from Dresden compared 0.2, 0.3 and 0.4 kPa (which is almost exactly 2, 3, and 4 cmH2O, I believe) .  All the studies in preterm babies after surfactant show, as you would expect, that if you use higher pressure during expiration the lung volume will be higher, they usually also show a decrease in compliance as the PEEP increases.

These findings explain a paradox that often baffles fellows when they start neonatology. Dynamic respiratory compliance, in several studies, does not improve after surfactant therapy if you leave the ventilator settings unchanged. FRC increases substantially however, and if you reduce PEEP after the surfactant, then you will see an improvement in compliance, this is evident with volume guarantee ventilation, peak pressures don’t change after surfactant until you drop the PEEP a little, then you will see much greater decreases in the peak inspiratory pressure than the change you made to the PEEP.

Overdistension of lungs in babies with diaphragmatic hernia is common and easy to achieve even with relatively modest levels of PEEP.

In preterm babies, after surfactant, also.

Once the fetal lung fluid has been resorbed in the first few minutes of life, most babies with CDH should be managed with very low PEEP. The same applies to babies after surfactant who fall to 21% oxygen or near to it, the most immature babies, and those with CDH have very fragile lungs and improving their outcomes requires that those lungs be protected.


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When should we fortify feeds in extremely preterm babies?

This post is not based on a new publication, but is stimulated by the introduction of an update to our nutritional protocol in our NICU. Since the previous update of the protocol we have been fortifying breast milk early. We order the fortification (or rather the protocol orders it) when a baby is receiving 25 mL total of breast milk per day. We do this because the packets of fortifier that we use are designed to be added 1 mL to each 25 mL of milk, and we prepare feeds for 24 hours at a time. This is done by dietetic technicians in a “milk kitchen” which is part of our new NICU. We don’t want to throw milk away, so we decided to start fortification when the babies get 25 mL total per day, which is at feeds of 2mL q2h for the smaller babies or 3 mL q3H for the larger ones. For a 500g baby in that case they will be receiving 50 mL/kg/day of feeds, and obviously for larger babies it is started sooner on a mL/kg/day basis.

Many people that we present our protocol to are surprised by the early introduction of fortifier, which, in our observational study of the impact of our feeding protocol, was well tolerated, and the new protocol was associated with a small reduction in necrotizing enterocolitis, but with better nutritional outcomes. We are maintaining the same timing of introduction in the new version of the protocol, but in preparation we reviewed the literature to make sure that what we were already doing was evidence based, and to direct any changes in the protocol.

What data exist about the effects of adding fortifier (bovine milk protein based) to human milk on clinical outcomes? And specifically data about the timing.

There is a Cochrane review of the impact overall of bovine, multicomponent, milk fortifiers, when added to maternal milk, that shows no adverse impact on clinically important outcomes, in particular in necrotising enterocolitis. The latest version of that review dates from 2016.

More recently there has been much interest in human milk only diets, which use human milk based fortifiers added to maternal or donor milk. The evidence to support their impact is currently weak.

The 2 randomized trials using Prolacta products made the following comparisons:

1 Cristofalo et al. Donor milk with human milk based fortifier was compared to preterm formula. This was a small study with an extremely high frequency of NEC among the formula babies (21%), and a lower frequency in the donor milk arm.

2 Sullivan et al. Mother’s milk with supplements of donor milk as required and fortification with human milk based fortifier starting at 40 mL/kg/d, compared to the same regime but with fortifier introduced at 100 mL/kg/d. The 3rd randomized group was mothers milk with supplements of artifical formula as required with the maternal milk fortified with bovine fortifier introduced at 100 mL/kg/d. That study showed a higher frequency of NEC in the formula supplements/bovine fortifier group, who received on average 20% of their milk as artificial formula.

The lower incidence of NEC in these 2 trials may have nothing to do with the nature of the fortifier, as it was not the only difference between the  groups.

What I think does not yet exist in the published literature is a trial using mothers milk with donor milk as required in both arms, with one arm getting a human milk based fortifier and the other arm getting a bovine milk based fortifier. There has been such a trial, from the group based in Toronto, part of their OptiMom program of research. It was presented at last years PAS, but has not been published yet. As I remember the results from the presentation last year, there was no difference in NEC between the groups. But, as the abstracts from last year are no longer available I can’t check on that.

I actually just found another trial which is probably relevant, but I don’t have the full text yet, Adhisivam B, et al. Does fortification of pasteurized donor human milk increase the incidence of necrotizing enterocolitis among preterm neonates? A randomized controlled trial. The journal of maternal-fetal & neonatal medicine: 2018:1-6. It seems to be an RCT with both groups receiving donor milk, and only one group being fortifed, it looks like there were 40 babies per group, with 1 NEC in the fortified group, and 3 in the non-fortified. I will update this post when I get the full text and get more details.

You will remember that the OptiMom trials are from the same group in Toronto that performed the Domino randomized controlled trial, in that study mother’s milk was supplemented when required with either donor human milk or with artificial formula. The results showed an important reduction in NEC, from 11% down to 4% with donor human milk supplementation. About 17% of the babies in each group never received a supplement at all, as they only ever got their mother’s milk, among those who did get a supplement, on average they received about 40% of their feeds as a supplement. Those in the donor human milk group had a bovine-protein-based fortifier used for all their feeds when they reached 125 mL/kg/d of enteral feeds. The formula supplementation group had their mother’s own milk fortified with the same fortifier.

Avoiding formula as a supplement for at-risk babies seems therefore to reduce NEC, and that could be the reason for the results in the two “Prolacta” trials that I mentioned above. There is no clear evidence that bovine protein based fortifiers increase NEC, in a recent study with many small babies and using modern neonatal care, but donor milk appears to prevent NEC. This is similar of course to the older data from the Cambridge studies of Alan Lucas which did not use a breast milk fortifier, those trials were first published in the early 1980’s.

A systematic review published last year examined all the evidence they could find for the timing of the introduction of fortifiers, one of the trials they included was the trial of human milk fortification using human-milk-based fortifier (Sullivan) above. The other prospective trial was this one Shah SD, et al: Early versus Delayed Human Milk Fortification in Very Low Birth Weight Infants-A Randomized Controlled Trial. The Journal of pediatrics 2016;174:126-131 e121. of 100 VLBW babies comparing the introduction of fortifier at 20 mL/kg/day to 100 mL/kg/day, that found no adverse effect of earlier fortification, but an increase in protein intake with earlier fortification. The other studies they found in the systematic review were observational and were reassuring also. There has been since then another RCT of 80 LBW babies comparing starting fortification with the first feed to waiting until 75 mL/kg/d, which was not included in the systematic review, Alizadeh Taheri P, et al. Is early breast milk fortification more effective in preterm infants?: a clinical trial. Journal of perinatal medicine. 2016, the babies were of 28 to 34 weeks gestation. They showed no adverse effects of earlier supplementation.

The ADEPT trial from the UK compared starting feeds early (24-48h) to starting them late (after 5 days npo) in preterm babies (<35 weeks) with growth restriction and abnormal antenatal umbilical artery dopplers. Fortification of the breast milk was suggested in both groups once the babies were on full feeds (150 mL/kg/day) although I can’t find in the results what proportion of babies had fortifier or when it was exactly added. The early feeding group reached full feeds 3 days earlier. There was no difference in NEC (stage 2 or 3: 8%). In the subgroup of 83 babies 83 under 29 weeks gestation, the incidence of stage 2 or 3 NEC was 18%. and was also not different between the groups. The early feeding group presumably had their fortification started earlier in terms of the day of life when it was started, but what the difference was is not reported. The differences between the outcomes of the 2 groups were that the early group reached full feeds sooner, had less TPN and less cholestasis and had their central lines taken out sooner, had less postnatal growth restriction and had less culture positive late-onset sepsis (28% vs 35%, not conventionally “statistically significant”, RR 0.8, 95%CI 0.6 to 1.08).

Being critical then, I guess you could say there are no robust data to determine at what point breast milk supplementation with currently available cow’s milk protein based fortifiers should be introduced, but the limited data available shows no evidence of an adverse effect of introducing them earlier. Earlier introduction does allow for greater calorie and protein intakes during the transition from intravenous to enteral nutrition. With earlier fortification it is possible to reach the desired 4 to 4.5 g/kg/d of protein intake sooner; there are conflicting data about the benefits of increasing to that level, but I think that overall higher protein intakes in that range seem to improve fat-free mass, and probably body length by the time of discharge.

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The PAS-meeting App, revisited

I received a comment on my previous post about this issue about the 2018 PAS meeting from the executive director of the meeting, Eileen Fenton. She told me that the permanent record of the abstracts is an issue they are dealing with, and they realize is important. She also said that if there are suggestions for improvement of the Apps or the website, send an email with your suggestions, and/or comments to

Please send your comments and suggestions for improvement. You have already seen my complaints, so constructive suggestions will be helpful, I hope .

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