Just do it! Who should go home on oxygen?

A new guideline from the ATS has been published, which gives guidelines for home oxygen therapy for children, one large group of which is, of course, babies with bronchopulmonmary dysplasia. Hayes D, Jr., et al. Home Oxygen Therapy for Children. An Official American Thoracic Society Clinical Practice Guideline. Am J Respir Crit Care Med. 2019;199(3):e5-e23.

The overall recommendation is that children with chronic hypoxemia should receive home oxygen therapy.

It is hard to argue with a recommendation like that! The big question of course is, how to define chronic hypoxemia? It should, I would think, be defined by a a level of oxygenation which has been shown to have an adverse clinical impact on the child, on their growth or development or chronic illness.

You can only really determine that by performing controlled trials where children with various levels of oxygenation receive either home oxygen or no O2. You would have to start with relatively higher levels of saturation to ensure safety, and then test lower levels until you find a clinical impact.

Of course, we don’t have good sequential data like that, but what do we have?

The guidelines authors reviewed the literature and found 11 observational studies comparing outcomes of BPD kids who had home oxygen therapy (which they abbreviate as HOT). Ten of them were eliminated as being biased, so the only evidence they have to support their recommendations is from a 1996 study. (Moyer-Mileur LJ, et al. Eliminating sleep-associated hypoxemia improves growth in infants with bronchopulmonary dysplasia. Pediatrics. 1996;98(4 Pt 1):779-83).

In that study infants who were already home on oxygen were admitted overnight to a clinical research unit and taken off oxygen for at least 8 hours. They were then divided into 3 groups depending on their saturations.

Group 1 consisted of 11 infants whose Sao2 decreased to between 88% and 91 % for more than 1 hour of sleep. Group 2 consisted of 34 infants whose sustained minimum Sao2 was 92% or greater for the entire recording. Group 3 consisted of 18 infants whose sustained minimum Sao2 was less than 88% for more than 1 hour of sleep. [HOT] for infants in groups I and 2 was stopped, but it was continued for infants in group 3. After a subsequent prolonged slep Sao2 evaluation, all but 6 infants in group 3 graduated to groups I and 2, and [HOT] was stopped.

Which sound like a reasonable design for a prospective observational study, my main question being what was done about intermittent desaturations? Certainly at discharge many of our babies have baseline saturations in room air above 92%, but have multiple brief, or not so brief, desaturations to below 88%. This report only refers to sustained desaturations which make up 12.5% of the 8 hour sleep study.

The age at which the trial of stopping HOT was done varied between 4 months average in group 1, 6 months in group 2, and 9 months in the infants who were initially in group 3. The major outcome reported for the infants is their growth, although hospitalisations were recorded, they don’t appear to be reported.

The study showed that group 1 infants, those with sustained saturations for more than an hour below 92% when O2 was stopped during an overnight study, had a fairly dramatic falling off of their growth after HOT was discontinued by the time of their next clinical visit, 6 to 8 weeks later. Their energy intake was the same, but their weight gain dropped from 16 g/kg/d to 4 g/kg/d. There were a total of 14 babies in that group.

So I guess a reasonable recommendation, based only on this one study including 14 relevant babies, could be that, with not much confidence, after a few months of HOT, oxygen could be stopped if a prolonged sleep saturation recording did not have a sustained period of more than 1 hour of desaturation to below 92%, and that infants with lower sustained saturations (to between 88 and 92%) risk a short term period of reduced growth if HOT is stopped, but it should state that there is no information about how prolonged that growth reduction might be or any other health effects.


This is the recommendation:

For patients with BPD complicated by chronic hypoxemia, we recommend that HOT be prescribed (strong recommendation, very low-quality evidence). Chronic hypoxemia is defined as either 1) greater than or equal to 5% of recording time spent with an SpO2 less than or equal to 93% if measurements are obtained by continuous recording or 2) at least three separate findings of an SpO2 less than or equal to 93% if measurements are obtained intermittently.

The ATS guideline also gives an instructive interpretation of what they mean by a strong recommendation:

Table 1. Meanings of the Strength of the Recommendations
A Strong Recommendation Conveys . . . A Conditional Recommendation Conveys . . .
It is the right course of action for >95% of patients. It is the right course of action for >50% of patients but may not be right for a sizable minority.
“Just do it. Don’t waste your time thinking about it, just do it.” “Slow down, think about it, discuss it with the patient.”
You would be willing to tell a colleague that he or she did the wrong thing if he or she did not follow the recommendation. You would NOT be willing to tell a colleague that he or she did the wrong thing if he or she did not follow the recommendation because there is clinical equipoise.
The recommended course of action may make a good performance metric. The recommended course of action would NOT make a good performance metric.

I find that table incredible!!

Based on very near to no data whatsoever, the ATS tell you that you should be like sheep and not even think about their recommendation, (“Just do it”: was this sponspored by NIKE?) and you should criticise your colleagues if they did something different. You are not supposed to even discuss starting O2 with the parents!! (Shared decision-making anyone?)

The recommendations are nothing like the only study that they use to support their recommendations! 5% of recording time at <94% is the recommendation based on a study which showed an impact (of questionable long term health significance) for children with a sustained saturation <92% for at least 1 hour, i.e. 12.5% of recording time.

This recommendation, if followed, will mandate thoughtless imposition of home oxygen therapy on tens of thousands of babies.

In addition (and of course I always find some additions) this is based on a single >20 year old observational study. By relying on this, if they followed their statement development guidelines, they imply that there are no randomized trials. But that is not the case, of course : Askie LM, et al. Oxygen-saturation targets and outcomes in extremely preterm infants. The New England journal of medicine. 2003;349(10):959-67.

In the first BOOST trial, 350 preterm babies with evolving lung disease born at less than 30 weeks were randomzied to higher or lower saturations if they still needed oxygen at 32 weeks. Saturations of either 95-98% or 91-94% were targeted, until the infant no longer needed oxygen. So this impacted on how many children went home on oxygen, what saturations they targeted at home, and how long they stayed on oxygen after discharge. 30% of the high sat target group went home on oxygen, compared to 17% of the low target group.

That study showed no health benefits of higher saturation targets, and no impact on growth. There was a hint of worse pulmonary outcomes with higher saturations. Of course, some babies in each group had acceptable saturations in no oxygen prior to discharge, but no clinical benefits were found in the overall study

In the STOP-ROP trial 650 very preterm babies with threshold retinopathy who needed oxygen were randomized to higher (96-99%) and lower (89-94%) saturation targets, which was continued until RoP was regressing, which was almost always by 3 months corrected age, by which time there were substantial numbers of babies still on oxygen, 47% vs 37%, mostly, but not all, at home (13% vs 7% remained hospitalized). During those 3 months there was no impact on growth.

Again in contrast to what is stated by the ATS guidelines, who claim that there are no adverse effects of home oxygen, infants in both of these trials note an increase in some adverse pulmonary outcomes. In BOOST there were more late pulmonary deaths, and in STOP-ROP there were more infants with “pneumonia/CLD events” in the group who had more prolonged oxygen and were more likely to go home of oxygen.

Proof of safety of the oxygen therapy thresholds mandated by the ATS (mandate is not too strong a word given their definition of what they mean by strong recommendation) does not exist. Lower thresholds might be safer, and would lead to fewer children needing home oxygen.

It is incoherent to have a strong recommendation which is supported by extremely low quality data, or indeed, as in this case, no data at all. A recommendation to discuss the possible pros and cons with parents, a clear outline of what those pros and cons might be, a more careful analysis of potential and proven impacts, positive and negative, and an outline of what data are needed to be able to provide evidence-based guidelines, and a commitment to fund such trials would serve our patients much better than this.

Of course some babies need and benefit from home oxygen, but providing HOT to many babies who might well not need it, and could potentially suffer adverse effects, is not the way to ensure that those who truly benefit will actually receive it.

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RCTs prevail: Antibiotic impregnation of central lines doesn’t reduce sepsis.

In older children and adults who need central venous access, using catheters impregnated with stuff that kills bugs decreases invasive sepsis rates. A multicentre trial in English PICUs showed a reduction in sepsis from 4% to 1% when antibiotic impregnated catheters were used. In that study only a minority of the culture-positive sepsis was for coagulase negative staph (CoNS); given the differences in bacteriology, immune function, microbiome, and frequency of prolonged central line use, compared to older children, an RCT in the NICU was essential.

The PREVAIL trial was a multicentre RCT in 18 English NICUs, (Gilbert R, et al. Antimicrobial-impregnated central venous catheters for prevention of neonatal bloodstream infection (PREVAIL): an open-label, parallel-group, pragmatic, randomised controlled trial. Lancet Child Adolesc Health. 2019) newborn infants in the NICU who needed a peripherally inserted central catheter (picc) were randomized to either a regular 1Fr catheter or a catheter impregnated with rifampicin and miconazole. Allocation was masked, but the catheters were easily distinguished as the antibiotic ones were brown, therefore the intervention was unmasked.

The primary outcome was time to first bacterial infection, bloodstream or meningeal. I’m not sure why this was chosen as the primary outcome, the risk being that the catheters might delay the onset of infection by a couple of days, but not the overall incidence of infection. To me the clinically important question would be whether the total number of infections is reduced by using the special catheters, not how long it takes to get infected. I presume that this outcome was chosen to take account of the differing duration of catheter use.

In any case, the trial showed nothing.

Which is, in fact, not true. They showed the very important outcome that there was no appreciable difference in infection frequency between groups, no matter how they were analysed.

The same proportion of infants had infections during catheter placement, and the time to first infection was identical. About 11% in each group had an infection, there were actually slightly more babies in the antibiotic impregnated group with an infection than controls.

Infections per 1000 catheter days were also similar, and slightly higher in the antibiotic impregnated group (13 vs 11).

My main comment about this study is:


This is exactly the kind of study that we need to do in neonatology. A simple clinical question, with a clear, clinically important, outcome, a simple irreprochable research design, performed rapidly with immediate open-access publication. Let’s have more of this!

You could ask why this might be so different to older children, part of the reason might be the different bacteriology, 2/3 of the infections in this study were CoNS, 66 of a total of 94 organisms were CoNS, compared to a minority in older children.

Also I think the importance of CLABSI, (Catheter-Linked Acute Blood Stream Infections) as they are now called, has been overstated in the NICU. It is the overall frequency of late-onset sepsis which is important, some units have been very succesful at reducing CLABSI, but without much impact on overall LOS (Late-Onset Sepsis) rates. Many nosocomial sepsis events in the preterm are with gram negative, intestinal organisms, CoNS sepsis rates are inflated by contaminated cultures, and are much less important for long term outcomes.

Before this study we could all have been (mis)-led into using antibiotiic impregnated catheters in the newborn.  This is exactly why RCTs PREVAIL.

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Putting steroids in the lungs? Still unclear if it is safe or effective.

Systematic reviews, and meta-analyses should help us make a clinical decision, by accumulating all the evidence, determining its quality, and synthesizing impacts, we can then decide which therapeutic option to pursue. This latest review answers the following question “should I give intrapulmonary steroids to this preterm baby, who is somewhere between 0 and 14 days of age, and has either just been intubated for surfactant or is maybe still intubated because of early chronic pulmonary dysfunction”, In other words a question no-one has ever asked. (Delara M, et al. Efficacy and safety of pulmonary application of corticosteroids in preterm infants with respiratory distress syndrome: a systematic review and meta-analysis. Archives of disease in childhood Fetal and neonatal edition. 2019;104(2):F137-F44).

This SR therefore fails Barrington’s test, which is based on Barrington’s rule, “if an individual baby could not be eligible for the 2 or more trials which are included in an SR, don’t meta-analyze them”. The results are meaningless. Worse they are misleading, as this SR implies that pulmonary administration of steroids safely reduces BPD frequency, no matter how or when they are given.

(This isn’t the first time, I have written about this issue : https://neonatalresearch.org/2016/02/24/steroids-directly-in-the-lungs-version-2/)

This is also another publication with poor editing and galley proof revision. The rather humorous result being that 2 studies apparently administered influenza to their babies!

(I presume some junior copy editor was very pleased with themselves when they replaced FLU by influenza, without realizing that it was actually an abbreviation for fluticasone!)

They have also completely misrepresented the dose of inhaled dexamethasone in the trial by Pappagallo et al, they don’t seem to have realized that the two phases of the trial were performed on different patients. But, as there are no results presented from that trial anywhere in the review (reported outcomes are pulmonary function tests), I guess it is not that important.

What would be worthwhile is a systematic review that divided these interventions into groups with fairly similar eligbility criteria, such as babies recently intubated for HMD support, babies who do not drop to 21% oxygen after their surfactant treatment, or babies still ventilated at a 7 to 10 days of age.

Meta-analysis of multiple small studies is already problematic; multiple small studies, 3 medium sized studies and 1 large multicenter trial, which include completely different groups of babies, should not be analyzed together.

Let us also not forget that the NEUROSIS trial, referred to as Bassler et al in this systematic review, showed an increase in mortality. 82/413 inhaled budesonide babies died, compared to 58/400 placebo infants.  Bassler D, et al. Long-Term Effects of Inhaled Budesonide for Bronchopulmonary Dysplasia. The New England journal of medicine. 2018;378(2):148-57.

Delara et al wrongly state that the longest follow up for mortality was 35 days, whereas Bassler et al report death to discharge and then to 18 to 22 months when follow up examinations were performed.

Just as important is that this review, as many others, supposes that having fewer babies on oxygen at 36 weeks is an important goal in itself. BPD, by this definition, has very little correlation with long term pulmonary health. Indeed, steroids impair lung growth and development, so having lower oxygen requirements at 36 weeks may not translate to better pulmonary outcomes. Decreased early inflammation could be associated with impaired lung growth and alveolarization, so clinically important pulmonary outcomes must be studied before we universally start routinely putting steroids into the lungs of preterm babies.

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Insulin like growth factor: does it prevent BPD, or does it increase RoP and mortality?

In the March print edition of the Journal of Pediatrics, the report of the Insulin-like growth factor 1/IGF binding protein 3 trial, as a preventive for retinopathy. Ley D, et al. rhIGF-1/rhIGFBP-3 in Preterm Infants: A Phase 2 Randomized Controlled Trial. J Ped. 2019;206:56-65 e8.

Many years of fascinating work out of Sweden, by Dr Hellstrom in particular, have suggested a rôle for IGF in the development of retinopathy of prematurity. The evidence trail goes like this: extreme preterm babies with intra-uterine growth restriction are at increased risk of retinopathy, impaired early postnatal growth is also associated with more retinopathy. Babies with IUGR have lower IGF concentrations, as do babies with poor postnatal growth, and IGF levels correlate negatively with RoP risk. New vessel formation in the retina is important in the vasoproliferative phase (which is just saying the same thing twice!), and such new vessel formation is dependent on VEGF. Insulin-like Growth Factor 1 plays a rôle in retinal vascular development, it seems to be required for VEGF to have an effect. IGF1 concentrations decrease after preterm birth,  and then slowly increase. The low initial IGF1 concentration is thought to participate in poorer retinal development initially, but then, later on when the IGF1 levels increase, it permits VEGF to act, promoting neo-vascular proliferation. Earlier better nutrition leads to an increase in early IGF concentrations and a decrease in later concentrations, and is associated with less RoP.

All of which information has led to the important question: if we supplement IGF early, can we decrease retinopathy?

That it turn led to the performance of studies to show that recombinant human IGF-1 can be given intravenously, that it increases measured IGF levels, and that we have some idea about dose requirements.

And then to an RCT to show whether or not IGF infusions decrease retinopathy. During the course of these investigations, a mixture of IGF and an IGF binding protein was developed. IGF-1 usually is transported in the circulation bound to an IGFBP, the most important of which appears to be number 3, IGFBP-3, and it is a mixture of recombinant IGF-1 and recombinant IGFBP-3 which was tested in this trial.

If you were to design such a study, you would include only babies at substantial risk of serious RoP, you would ensure that the sample size was large enough to demonstrate an impact, and you would determine whether or not there was an impact on mortality and other potential adverse consequences.

Unfortunately with studies designed, funded, and run, by pharma the justifications are different, they want to design studies with the highest likelihood of showing a positive effect, at the lowest cost, in order to ensure that profits are maximized. They also don’t want to have eligibility criteria too restrictive, otherwise the eventual licence is likely to be restrictive.

The best study of IGF prophylaxis against RoP would, therefore, be designed to include only babies of 24 weeks or less (in whom vision-threatening retinopathy is a serious issue) who were already on optimal nutritional protocols. They would evaluate serious RoP (and not particularly stage 1 disease) and have active surveillance for all potential and possible adverse impacts in this critical group of patients. Reductions in stage 1 disease might be important in terms of pathophysiology, but they are not very important clinically. Inclusion of babies born at 27 weeks gestation, for example would have little value, as they very rarely develop vision-threatening RoP, and so would massively increase the required sample size.

How about the current study? It was a randomized unmasked study which included :

Infants with gestational age at birth of 230/7-276/7 weeks … Exclusion criteria included monozygotic twins, detectable gross malformation, known/suspected chromosomal abnormality, genetic disorder/syndrome, a persistent blood glucose level of <2.5 mmol/L or >10 mmol/L on the day of birth, anticipated need for administration of rh erythropoietin during treatment, a history of maternal diabetes requiring insulin, and clinically significant neurologic disease (germinal matrix hemorrhage allowed)

Babies were randomized and started on protocol within 24 hours of birth; intervention group babies received IGF-1/IGFBP-3 infusion continuously up to the start of their 30th week PMA. Normal dose was 250 microg/kg/d of a 50 microg/mL solution, which they therefore received for between 2 to 7 weeks.

The primary outcome variable of this trial was maximum severity of RoP, expressed according to ICROP grading, and analyzed as an ordinal result (0,1,2,3,3+,4 and 5; in the text it states “ROP outcome stages in the current study were classified as 0, 1, 2, 3, and >3” but in the table the results are given for ≥ 3, the numbers are quite small in each group, however).

Results: there were more controls without RoP, 48%, compared to babies who received IGF, 29.8%. The absolute risk increase of 18% in all stages of RoP is most compatible with an absolute RoP difference between a 1.1% decrease and a 35% increase in all stages with the use of IGF.  There were also more IGF babies who developed ≥ stage 3 RoP, 25.5% compared to 18% among the controls (there were no retinal detachments (stage 4 or 5) in either group). This is exactly the opposite of what was expected, and calls into question the premise of the study.

There were also more deaths with IGF than among the controls, 20% vs 12%. It isn’t clear how many of those who died after their eye exam actually had RoP, or what the incidence of RoP was among survivors; but we do know that the majority of the deaths occurred before their first eye exam (11/12 IGF infant deaths, and 5/7 controls) so the other 3 babies won’t affect the results much.

The results, therefore, show an absolute increase in severe RoP, with the intervention, of 7.5%, which is most compatible with an absolute difference of between an 8% decrease and a 24% increase in severe RoP. In terms of relative risk that is an RR of 1.31, (compatibility intervals of 0.6 to 2.9) In other words the results show an increase in all stages of RoP and an increase in severe RoP, both of which are compatible with small decreases or major increases.

The authors of the study state that IGF use decreased the occurrence of severe BPD, but if we analyse the trial using standard methods, i.e. no BPD versus BPD (4/49 placebo cf 4/47 IGF with no BPD, using the newer definition), there is no difference between groups. If we just concentrate on those who were in oxygen at 36 weeks, i.e. previous definition of BPD, and what is called here moderate/severe BPD using the newer definition,  there were 27 of 49 evaluated surviving placebo babies vs 19 of 47 evaluated surviving IGF babies with moderate/severe BPD); p=0.22 using Chi-square with Yates’ correction, the 15% absolute decrease in BPD among survivors is compatible with a difference between an increase of 5% and a decrease of 33% with IGF. To express that as a relative risk, the RR for BPD with IGF compared to control was 0.84, most compatible with an RR between 0.54 and 1.3, among surviving babies.

The analysis which is reported, and which is touted as being significant, ranks the severity of BPD; that analysis was not mentioned in the study registration (which is admittedly a bare-bones document), and gives a p-value of 0.04. (p-hacking, anyone?). But that analysis is only for BPD among surviving infants who were still in the study at 36 weeks for their evaluation.

I actually think that treating BPD as a spectrum, rather than as a dichotomous outcome, is a better idea than our traditional BPD/no BPD, but I don’t think this division into moderate and severe depending on whether you are over 30% oxygen is necessarily the way to go, It replaces one way of dichotomising the outcome with another. Does being in 35% oxygen at 36 weeks have a greater impact on respiratory outcomes of importance than requiring 27%? For an evaluation of outcomes at 36 weeks, I guess it is, however, justifiable, but should be supplemented with data of more clinical importance, such as respiratory disease during the first year of life. The other reason for being very concerned about the likely reproducibility of these results is the very high rate of severe BPD in the controls. I think likely as a random fluke, there were 4.5 times more severe BPD cases among controls than moderate BPD. Indeed a frequency of 45% severe BPD among infants less than 28 weeks gestation is enormously high, higher, for example, than any of the European regions that recently reported the variation in severe morbidity incidences across multiple European regions. (Edstedt Bonamy AK, et al. Wide variation in severe neonatal morbidity among very preterm infants in European regions, (Archives of disease in childhood Fetal and neonatal edition. 2019;104(1):F36-F45).

In contrast to the apparent decrease in BPD severity, mortality was higher with IGF treatment (12% placebo vs 20% IGF) by chi-square with Yates’ correction p=0.33, this gives a relative risk of death with IGF treatment of 1.68, most compatible with a relative risk of death with IGF of between 0.71 and 4.0.

If the outcome were to be the more frequently used “death or BPD”, that occurred in 34/56 controls and 31/59 intervention babies: p-value from Yates’ corrected chi-square = 0.75. Or for “death or severe BPD” 29/56 vs 22/59, p=0.4237. The authors state that they did a supplementary analysis putting the deaths in the severe BPD group, and note that a “trend for a decrease in severe BPD among treated infants remained (37.3% in rhIGF-1/rhIGFBP-3 group vs 51.8% in the standard of care group)” but no statistic is provided. I re-ran the analysis as a Mann-Whitney U test, putting deaths as a separate, worse group than severe BPD (i,e, coding them as 0 for no BPD, 1 for mild, 2 for moderate, 3 for severe, and 4 for dead), the p-value was 0.49.

I find these results, especially the increase in retinopathy, somewhat surprising, but I guess that is why we have to do prospective randomized trials. The increase in mortality is also concerning, is at least as striking, and, I would suggest, much more important, than the possible shift in severity of BPD.

Why might this be so? There are numerous explanations possible, firstly the compatibility intervals are wide and it is possible that another study might find a decrease in RoP; but the best estimate of a potential positive impact is a small reduction.  It is also possible that the association of early lower IGF-1 concentrations among preterm infants who later develop RoP is just an association and not causative, and that the increase in RoP shown by this study is evidence of the permissive impact of IGF-1 on VEGF activity in the retina, later on during the proliferative phase

When I searched the registration documents for the trial to try to find what analyses had been planned for the primary outcome variable, I was surprised to find the large number of revisions (25), many of which were just procedural (addition of centers and so on), but analyzing the documents, almost everything about this trial has changed between initial registration and final publication. The sponsor changed, the intervention changed (it started as a trial of IGF-1, and then IGFBP-3 was added later), the duration of the intervention (originally up to 31 weeks 6 days, changed to 29 weeks and 6 days), the sample size and the exclusion criteria have all changed.

I think this makes a mockery of trial registration, they basically studied a different medication in a different group of babies, with a different sample size, for a different duration than the original registration.

As far as I can see most of those changes were made with the revision in May 2014, which is prior to the actual start of the phase of the study that is reported in this manuscript, which started enrolling in September 2014. So why not just register this as a different trial? That would leave the original documents untouched, and would make it easier for everyone to find what is going on. Changing trial registration documents this extensively means that it will remain difficult to find what studies have been planned, or performed, and never published. Which is one of the important functions of registration.

In summary, this trial seems to show that a prolonged infusion of IGF-1/IGFBP-3 among very preterm infants leads to an increase in retinopathy, an increase in mortality, and a possible decrease in BPD severity, but only compared to a control group with an unusual very high incidence of severe BPD.

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Measure gastric residuals? Safe to stop?

A new RCT published in JAMA pediatrics compared growth and other clinical outcomes between infants <33 weeks gestation and <1250g who were managed with routine gastric residual measurements or without. (Parker LA, et al. Effect of Gastric Residual Evaluation on Enteral Intake in Extremely Preterm Infants: A Randomized Clinical Trial. JAMA Pediatr. 2019) I was quite interested to read this when I saw the title, unfortunately the way it was analyzed, and the way it is presented make it nearly impossible to interpret. In addition there is at least one major error in the data presented.

The first problem is that although the “standard care” group has residuals measured, there is no indication of how they were interpreted. In the protocol which is provided as a supplemental file, the only mention of the feeding standards is as follows :

In addition, the nurse assesses the infant for any signs or  symptoms of feeding  intolerance or NEC (i.e., abdominal  distension and/or tenderness, increased abdominal girth, visible bowel loops, presence of emesis, and visible blood in the stool). It is standard protocol to  aspirate RGC prior to each feeding. However, for this study, this will only occur in infants randomized to Group 1.

What was done with any of this information is not described. Was the volume considered important? The colour? Presumably they didn’t aspirate prior to each feed in order to ignore the findings.

The next big problem is the primary outcome: “weekly enteral nutrition measured in mL/kg for 6 weeks after birth”, I am not sure what that means. Did they add all the intake over 6 weeks and compare between groups? Did they compare after each week, and so do 6 comparisons? Apparently, from the protocol, the plan was to do a t-test, designed for groups with unequal variance (“Welch adjusted” they call it). But the analysis which is presented is a Generalized Linear Mixed Model, which is a term that doesn’t tell me anything, but it seems to have been some sort of repeated measures test, which therefore should account for the multiple comparisons.

So what did they find? What were the primary outcome data for the two groups? I don’t know. Nowhere in the manuscript are the primary outcome results given. They do give a p-value however! In table 2 the first group of numbers are for weekly feedings in mL/kg/d and the p-value for Treatment is 0.048, but the actual numbers are written as NA. The next group of numbers are for the “simple main effect” and give some numbers which are not consistent with anything else they have written, i.e. for week 6 the numbers are “128.4 (119.9 to 136.9)” and “141.6 (133.2 to 150.0)”, according to the methods this should be the weekly feeding volume  which seems quite unlikely. I presume this is either the daily volume on the last day of week 6, or the averaged daily volume over the 6th week. And I have to guess that the figures in parentheses are mean plus or minus 1 standard deviation, but that is never specified.

As far as I can tell then, by week 6 the babies were receiving inadequate feeds if they didn’t measure gastric residuals, and even more inadequate feeds if they did! To only achieve 140 mL/kg/d after 6 weeks of feeds in a group of babies with a mean of about 27 weeks and 900 grams seems to be well below what we should be achieving. As a result the growth outcomes are very poor, a 27 week baby weighing 900 grams, should by 6 weeks of age be weighing about 1400g, but, from one of the few results that are presented as interpretable data, both groups weighed just over 1100g (which I think are means adjusted for covariates)

Many of the results are presented as “least square means” which is an SAS (that is a particular stats software package) jargon for means, adjusted for covariates. Which again makes them difficult to interpret. Some of them are presented as the “mean estimated log weights” in the abstract, and sometimes in the abstract they are completely unexplained: “the no residual group were discharged 8 days earlier (4.21 [95% CI, 4.14-4.28] vs 4.28 [95% CI, 4.19-4.36]; P = .01)” 4.21 what? (I could have written WTF? but I am too polite).

It is not really surprising that not measuring aspirates would accelerate feed progression, even though here the weekly increase is from a desperately slow 18 mL/kg/d to an extremely slow 21 mL/kg/d. The big question is, is it safe?

Here again there are problems, in the abstract and in the text it is stated that the Odds for developing NEC in the intervention vs control group are 0.58 [95% CI, 0.18-0.19] vs 0.026 [95% CI, 0.006-0.109]). Which would be a 22-fold increase in the Odds of NEC, or an Odds Ratio of 22. But of course an Odds of NEC in the intervention group of 0.58 would mean that there were 25 cases of NEC and 44 without NEC, so that isn’t likely either, especially as the odds doesn’t lie between its 95% confidence intervals, which is impossible.

There is some potential clarification from the body of the article, in table 5 it is noted that the “odds” of NEC was 0.058 (0.018, 0.19) and in the results at the end of the section describing the subjects it is noted that 4 patients in the intervention group were withdrawn for NEC. Four out of the 69 intervention patients makes an incidence, a rate, or a frequency of 5.8% or 0.058. But it does not make an Odds of 0.58, the Odds of NEC is 4/65 (NEC/no NEC) which is 0.061. It looks like there were probably 2 cases of NEC among the 74 standard care group, for an incidence of 2.7%, and an odds of 0.0278.

After slogging my way through all these results it appeared that there were about twice as many cases of NEC in the intervention group as in the controls. I thought I was getting this all clear when I looked at the flow chart, the CONSORT figure, which states that there were 7 cases of NEC in the intervention group, and 4 cases in the controls. Which completely messes up all my attempts to understand this article. If there were 7 cases of NEC, then the incidence of NEC among the intervention babies is actually 10.1%, and the odds is 0.012, compared to 4 controls. with a frequency of 5.4% and an odds of 0.057.

In the discussion the authors state “we found no differences in incidence of NEC” which is clearly untrue, the incidence of NEC was quite different between groups. A true statement would have been “the difference in incidence of NEC that we found has very wide compatability limits, which include a possibility of a large reduction or a major increase in NEC”.

I think this paper is a complete failure of the review and editorial process of JAMA pediatrics (and of galley editing), how this could have been published in this form I don’t understand. It could have been  a nice little RCT adding a bit more data to the question of measuring residuals, and should most clearly have stated that there was inadequate power to determine safety, and that the confidence intervals for the incidence of NEC are extremely wide. (If we assume that there were 4 cases of NEC in the intervention/no residuals group, and 2 in the controls, then the relative risk of NEC is 2.15 with 95% compatibility limits of 0.4 and 11. If there were 7 cases vs 4 cases, the RR is 1.99, 95% CL 0.6-6.5).  We should also note that there were 6 deaths in the standard/measured residual group, and only 1 in the intervention/no residual group; which gives an RR of 0.19, 95% CL 0.02 to 1.5).

As it is we still are not clearly any the wiser, after a trial where it is not clear what was done or what was found.

I don’t take note of residual volumes, I have worked at one place which had not measured them for 15 years, and in 2 other places we stopped routinely measuring residuals completely while I was there. All that observational data suggests no benefit, and potential nutritional harms from measuring gastric residuals, but some stronger data, to convince other units to stop the practice if it is indeed safe, would have been helpful to improve nutritional outcomes of our very preterm babies.

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Do transfusions trigger NEC? or does anemia?

I am still unconvinced that transfusion associated NEC is a real thing, I think it is possibly a real phenomenon, but I am not sure how to know for sure.

Some of the best evidence I think comes from the PINT trial, a randomized trial of transfusion thresholds. The preterm infants in the high threshold group received many more transfusions, but did not have more NEC, in fact they had less NEC 5.3% vs 8.5% (RR with restrictive transfusion 1.62 (95% CI 0.8, 3.26). The other 2 RCTs included in the Cochrane systematic review that reported NEC were much smaller and did not contribute much to the meta-analysis which thus gives the same overall RR of 1.62).

In the RCTs of later use of erythropoietin, babies in control groups had many more transfusions, but the Cochrane systematic review does not show a major difference in NEC, RR 0.88 with epo, (95% CI 0.45, 1.7).

In contrast, the Cochrane systematic review of early use of erythropoietin does show less NEC with epo, and, of course, the epo babies also had fewer transfusions.

An observational study from 2016 might explain some of the confusion, They suggest that severe anemia might be associated with NEC, rather than red cell transfusion. (Patel RM, et al. Association of Red Blood Cell Transfusion, Anemia, and Necrotizing Enterocolitis in Very Low-Birth-Weight Infants. JAMA. 2016;315(9):889-97). They used the data from a prospective cohort study of transfusion related CMV in preterm infants; because of variations in practice, as indications for transfusions were not standard, they could attempt to analyze the separate impacts of transfusion and anemia, with a hemoglobin less than 80g/100mL. They included 600 VLBW infants, who had 42 episodes of at least stage 2 NEC. About half of the babies were transfused, and they were smaller, less mature and sicker than non-transfused infants, and 18% had at least one hemoglobin under 80.

The rate of NEC was increased in VLBW infants who received RBC transfusions compared with infants who did not (cause-specific HR, 2.33 [95% CI, 1.18-4.60]; P = .01)….

In multivariable analysis, including adjustment for birth weight, duration of breastfeeding, illness severity, severity of anemia, duration of antibiotic treatment, and center, any RBC transfusion in a given week was not independently associated with an increased rate of NEC (cause-specific HR, 0.44 [95% CI, 0.17-1.12]; P = .09) or mortality (cause-specific HR, 1.36 [95% CI, 0.27-6.82]; P = .71)…. In a given week, VLBW infants with severe anemia had a higher estimated rate of NEC compared with VLBW infants without severe anemia (adjusted cause-specific HR, 5.99 [95% CI, 2.00-18.0]; P = .001).

Of course because transfusion is used to treat anemia, and babies with more severe anemia are more likely to be transfused, these are things that are difficult to separate, but these data  do at least suggest that it is severe anemia, rather than transfusion which increases NEC.

I think this all might add together, with early epo there is less severe anemia, and thus, if the association is actually causative, there should be somewhat less NEC; in the PINT trial the high transfusion threshold group were unlikely to develop severe anemia, and so were less likely to develop NEC. In normal clinical practice we are more likely to transfuse the most anemic babies, and thus there is an apparent association between transfusion and NEC. Confirmation of this from another database, and analysis of the TOP trial when completed (I think enrolment has finished and outcome assessment should finish this year) will be important to answer these questions.

The study that I am blogging about is fairly old news, for my blog, from 2016, but I was reminded of it as we have been working on developing standardized transfusion criteria, and by a couple of recent publications:

Does severe anemia really affect the gut? A prospective study from Turkey measured fatty acid binding proteins in very anemic babies before and after transfusion (Ozcan B, et al. Severe Anemia Is Associated with Intestinal Injury in Preterm Neonates. American journal of perinatology. 2019). Intestinal FABP and liver FABP are apparently good markers of intestinal injury, and previously liver FABP has been shown to increase with NEC of all grades, and I-FABP only with very severe NEC. In this new study I-FABP was only slightly higher among anaemic babies than among controls, but liver-FABP was appreciably higher, and remained high 48 hours after transfusion.

Another relevant recent publication is from a mouse model (Arthur CM, et al. Anemia induces gut inflammation and injury in an animal model of preterm infants. Transfusion. 2019;59(4):1233-45).  In this study they correlated cytokine concentrations in preterm infants with their hemoglobin levels, more anemic samples had higher Interferon alpha levels. They then performed a mouse study gradually bleeding the mice to anemia (PIA ia phlebotomy-induced anemia) and performing a number of fascinating analyses of their intestines.

Gradual induction of PIA in a pre‐clinical model resulted in significant hypoxia throughout the intestinal mucosa, including areas where intestinal macrophages reside. PIA‐induced hypoxia significantly increased macrophage pro‐inflammatory cytokine levels, while reducing tight junction protein ZO‐1 expression and increasing intestinal barrier permeability.

Preventing severe anemia with a combined approach of delayed cord clamping and erythropoietin should lead to less NEC if these findings are real; a systematic review of delayed cord clamping did show a bit less NEC RR=0.88 [95% CI 0.65–1.18], although they marked the quality of this evidence as low. (Fogarty M, et al. Delayed Versus Early Umbilical Cord Clamping for Preterm Infants: A Systematic Review and Meta-Analysis. Am J Obstet Gynecol. 2017), I am not sure how effective delayed clamping is in preventing late severe anemia, I don’t think that has been reported often in the studies, but early hemoglobin is, of course, higher. But a few weeks later, after being in the ICU for a while, with multiple blood sampling and intercurrent illnesses, the effects of delayed clamping on late severe anemia might well be dissipated. On-going trials of erythropoietin for brain-protection in preterm infants may also be able to answer questions about anemia and NEC, depending on doses and duration.

Thinking about it, I am not sure why many of us went of the routine use of erythropoietin, I guess we were all focused on trying to reduce donor exposure, which is generally unaffected with current transfusion practices. I think avoiding blood transfusions and reducing severe anemia are probably valuable goals in themselves. Maybe we should rethink erythropoietin/darbepoietin routine use.

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Platelet transfusions don’t close the PDA, but they may increase IVH

I would never have actually thought to ask the question whether platelet transfusion might close the PDA, although early thrombocytopenia is associated with persistent PDA, and platelet plugs seem to be part of the mechanism of closure. A group in India have just published an RCT in preterm infants with a PDA (hemodynamically significant, whatever that means) who had a platelet count under 100,000. Kumar J, et al. Platelet Transfusion for PDA Closure in Preterm Infants: A Randomized Controlled Trial. Pediatrics. 2019. Gestational age averaged 30 weeks, and they were enrolled at a mean of 3 days of age. Median time to PDA closure was identical in the group randomized to receive transfusion (10, 15 or 20 mL/kg depending on the count) and the control group, at 72 hours in each group, data based on repeated echo every 24 hours until closed. All babies received ibuprofen or acetaminophen also. 44 babies were enrolled, and of the 22 in the transfusion group there were 9 new IVH (4 severe, grade 3 or 4) after enrolment, compared to 2 new IVH among the controls, (both severe).

In the much older study by Maureen Andrew and colleagues, (Andrew M, et al. A randomized, controlled trial of platelet transfusions in thrombocytopenic premature infants. The Journal of pediatrics. 1993;123(2):285-91). Preterm infants with a platelet count less than 150,000 were randomized to be transfused or not. 12/78 transfused babies developed a serious grade 3 or 4 IVH, and 9/79 controls. The 33% increase in IVH was “not statistically significant” they said, but as you all know that doesn’t mean that it isn’t real!

In the recent PLANET2 trial there were more serious bleeding episodes in the transfused babies than in the controls, and apparently most of them were IVH, I don’t have access to those numbers, but whatever they are, the effect appears to be in the same direction.

I would like to see a meta-analysis, which would have some limitations given the 3 different thresholds in those 3 trials (which are as far as I know the only RCTs of platelet transfusion at different thresholds), but if the PLANET2 data are indeed consistent, and with a much greater power than the 2 other small trials, that would be very powerful data. It would confirm that not only are platelet transfusions in general ineffective in preventing bleeding at these 3 threshold levels, but they likely increase the risk of IVH.

Why would that be the case? It may be that transfusing adult platelets to babies with newborn plasma, which is already hypercoagulable, causes the effect, either by capillary damage, or by causing infarctions which then become hemorrhagic, or some other mechanism. It could just be the effect of volume expansion, which can certainly cause lesions in newborn beagle puppies (see Laura Ment’s studies from the 80’s and 90’s), and many observational studies that have correlated volume expansion with IVH. Platelets are often given somewhat faster than red cell transfusions, (it does not appear to have been specified inPLANET2, the dose was 15 mL/kg, but the duration isn’t mentioned in the protocol) often over 1 hour. Volume expansion is also probably more effective than with saline, much of which rapidly leaks out of the circulation.  I think either some impact on overall coagulation/anticoagulation balance or hemodynamic changes, or both, may be responsible for the apparent increase in IVH.

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