Travelling again

Posted on 7 September 2013 by Keith Barrington

I am, for the next few hours, in Sydney Australia, at the end of a productive trip. We had 2 workshops, 1 on the current status of probiotics, the other on the question of consent for perinatal trials, focusing on the SUPPORT trial.

Both were productive I believe. And we will try and produce a report of each, and also another document which will be our recommendations. One of the best parts of the workshops was the involvement of several parents. Their contributions were the most important, and the use of social media by Melinda Cruz, the CEO and founder of the Australian Miracle Babies foundation allowed others to be involved in the discussion who weren’t even there… the wave of the future, or maybe of the present!

After it was over I took a ferry ride across Sydney Harbor, and on the way back a cruise liner was pulling out of the harbor behind the Opera House. It was a long exposure on a moving boat, but this is the least blurry of the shots that I got.

20130906_183558_LLS

Posted in Neonatal Research | Leave a comment

Does gestational age matter?

Posted on 4 September 2013 by Keith Barrington

Taking a break from the SUPPORT brouhaha for a moment, here is a great systematic review from Greg Moore and colleagues in Ottawa. (Moore GP, Lemyre B, Barrowman N, Daboval T: Neurodevelopmental outcomes at 4 to 8 years of children born at 22 to 25 weeks’ gestational age: A meta-analysis. JAMA Pediatrics 2013,)

I have mentioned many times on this blog the problems with relying on the 18 month or 2 year Bayley score for determining if outcomes are seriously limited or not. Most ex-preterm infants with a Bayley MDI under 70 at 2 years do not have a cognitive impairment when you retest them at school age. Even infants with very low scores (under 50) will often be in the normal range if you test them later, at an age when they are old enough that you can really say something about intellectual ability. Testing later, say at 3 years, and using more extreme cutoffs makes the testing more predictive, but there is still a lot of uncertainty, once children approach school age then testing becomes better at discriminating between children with serious limitations and those without.

A lot of the previous research has shown very little effect of week by week changes in gestational age on outcomes. Epicure follow up at 6 years, for example, showed almost no gradient of outcomes between 23 and 25 weeks. Even large regional studies such as Epicure may, however, be suffering from a lack of power.

So Greg Moore and his co-authors did a systematic review of all the good quality studies that they could find that studied extremely preterm infants at early school age (4 to 8 years). They looked for cohort studies published after 2004, with follow up rates over 65% using standardized testing.

The results I want to concentrate on are the effects of increasing gestational age on the prevalence of impairment.

The authors divide impairment into moderate (more than 2SD below the mean on IQ testing, ambulant cerebral palsy, GMFCS 2 or 3, substantial visual impairment (worse than 20/40) or hearing restored with amplification) and severe impairment (IQ more than 3 SD below the mean, CP with GMFCS 4 or 5, no useful vision worse than 20/200 or profound hearing loss). There are nearly 900 babies in all in the 9 cohorts reported with gestational ages from 22 to 25 weeks.

When you have this large a number of patients, there is some reduction in rates of moderate impairment from 22 to 25 weeks, the frequency is around 24% for babies born at 25 weeks and increases by 6.5% for each week less, a statistically significant increase at p<0.01, but a smaller increase than you might think.

When you look at severe impairment, there was no significant effect of weeks of gestational age, being 14% at 25 weeks, up to 17% at 23 weeks, (the numbers at 22 weeks are really too small to say anything (n=12)).

So the majority of survivors are unimpaired or mildly impaired at any gestational age, and few (too many, but still few) are severely impaired.

This is very interesting data, which helps to clarify the outcomes of these patients. I think such a low frequency of severely abnormal outcomes, and the lack of an effect of gestational age are very important. If there is no substantial effect of the number of weeks of gestation, and the proportion who are severely impaired is small (and the individuals affected unpredictable before birth) then this should not be part of our considerations about whether or not we should start intensive care.

Interestingly, both this article and the editorial which goes with it, discuss the question of using long-term outcome data as an issue in the decisions of whether to initiate intensive care for the extreme preterm.

I am coming to the opinion that the incidence of profound disability is so low (and I am the first to recognize that 15% is way too high), so unpredictable before birth, and so poorly correlated with gestational age, that we should not include this as a consideration in our decision making.

My good friend and colleague Bill Meadow has an article shortly to be published in ‘Neoreviews’ I hope he won’t be upset with me if I steal his closing paragraph, but he expresses, much better than I can, an opinion which is so close to mine, and which indeed reflects my own personal experience as a parent of an extremely preterm baby. We were incredibly fortunate to have Sophie Nadeau, Gene Dempsey, and the rest of the team at the Royal Victoria Hospital in Montreal helping us through those very difficult times.

Perhaps antenatal consults oughtn’t really be about helping parents make life-and-death decisions at all.  Perhaps they should be about reassurance and human kindness.  We (the neonatology team) are here for you in your moment of unexpected and indescribable fear.  We may not be able to help you with your decision prior to delivery – the data are just too ambiguous.  But we’ll be with you every step of the way.  And if things turn bad during the NICU stay, we’ll be there – supporting your autonomy and helping you make the difficult decision of what is now in your baby’s ‘best interests’.  That may be the best we can do.

That sounds to me like a pretty good ‘best’.

Posted in Neonatal Research | Tagged , , | 6 Comments

Marche pour les prématurés

Posted on 3 September 2013 by Keith Barrington

Last Sunday was the annual ‘marche pour les prématurés’ in Montreal, and several other cities across Québec. Some other towns have their walks this coming Sunday (see the website of Préma-Québec, who organize them). This year the walk was covered by the RDI TV station, who put a short section on their evening news. You can see it here (in French). Apart from the introduction with its obligatory statements like ‘the happiness of a birth is replaced by anguish when the baby is premature, often the parents have to live with the sequelae of saving their little miracle’ (Eugh). The rest of the presentation was rather well done. Of note there is an interview with our nursing unit chief and her daughter, born at 29 weeks, which Roxanne handles very well. And just before the end a flash of Violette picking up her badge with 24 written on it.

Posted in Neonatal Research | 1 Comment

Blurring the line between patients and research subjects

Posted on 30 August 2013 by Keith Barrington

The US Department of Health and Human Services held a public meeting about consent issues for research on August the 28th, largely as a result of the controversy surrounding SUPPORT. It was called ‘Matters Related to Protection of Human Subjects and Research Considering Standard of Care Interventions’.

It was streamed live on the internet, but I only got to watch an hour or so, I suppose that much of it will be available in various forms in the future, hopefully all in one place on the HHS website.

Some of the presentations are already available elsewhere, for example the presentation by 2 people who call themselves ‘historians of medicine and human subjects’ research’. They are Alice Dreger, PhD, Professor of Medial Humanities and Bioethics, Northwestern University, Chicago, IL and Susan M.  Reverby, PhD  Professor in the History of Ideas and Professor of Women’s and Gender Studies at Wellesley College, MA.

The document is apparently a written version of their testimony to the panel set up by the HHS. It is a great example of the false dichotomy between clinical care and research; a lack of understanding of standard of care; a series of pontifications about acute care neonatology which only show they haven’t got a clue; and a misunderstanding of risk.

Drs Dreger and Reverby commence by claiming that doctors are being pushed into performing unethical research because of the pressure to publish, by the emphasis placed on academic productivity, and, even though they pay lip service to the idea that we may be motivated by a beneficent desire to do good, apparently that is being perverted by today’s academic climate. They of course give no data to support these offensive claims. There is of course also no acknowledgement that professional ethicists wholly supported by university salaries have academic pressure effectively coercing them into making scurrilous accusations about medical ethical lapses, nor that their livelihoods are threatened by physicians who have re-appropriated clinical ethics, so it is really good for their career prospects if they can claim that doctors are unethical and can’t be allowed to police themselves. (And in fact we don’t, IRBs all have non-medical and lay members, and more and more granting agencies require participation from families).

I will quote several illuminating passages:

As the OHRP found, parents should have been told that  randomization into restricted trial arms in this study could potentially increase (or  decrease) the odds that their babies would suffer death and particular impairments.  The protocol and publications show that the study was designed to determine just those risks. Consent was so poorly handled in this trial, OHRP should have required—and should still require—that the involved institutions now inform parents what they should have been told before enrollment—that being in the SUPPORT study was likely to have changed how their baby was treated in the neonatal intensive care unit (NICU) and might have increased the risk of death and disability.

Of course, most of that is not true, parents were informed that this was study to examine different oxygen saturation targets, and being in the study did not increase risks of death or disability. There was, I re-iterate, no difference in disability between the groups, although a potential difference was one of the reasons the study was done, there was no reason to believe that the 1300 babies enrolled in the trial would have more deaths or disability than 1300 similar babies treated outside of the trial. There still is no reason to believe that mortality was higher for the group as a whole, it is likely that as a group they benefited.

Parents were of course told that being in the trial might change how their baby was treated, that is what the consent process is all about, that is what clinical trials such as this one are all about; not continuing to do something when we are unsure what to do, but randomly comparing alternatives, which might not have been what the doctor would otherwise have done, but would have been acceptable alternatives.

Dreger and Reverby are very agitated about the use of the term Standard of Care. They believe that the use of this term is ‘most egregious’, seemingly being ‘designed to reassure parents who might enroll their very premature babies that it would have made no real difference whether or not they enrolled’. It was of course a statement of fact. Oxygen saturation targets differed greatly according to different hospital protocols, none of which were based on good evidence regarding clinical outcomes, and therefore were within usual acceptable standards of care. The ranges tested in SUPPORT were less extreme than some in active use at the time.

Standard of Care is sometimes used as a legalistic term (the Standard of Care for a ruptured appendix is immediate surgery, so you are negligent if you didn’t follow the Standard) but often in medicine there is no such Standard, and a wide range of approaches are within current acceptable limits, and can be considered to be standard of care. That is how the term was used here, and it is accurate, both oxygen saturation ranges were within the limits of acceptable contemporary practice, they were all within ‘standard of care’.

If  the  best  clinical  judgment  in  NICUs  was  not  evidence-based  because  we  lacked  the  data  the  SUPPORT  study  was  designed  to  generate,  then  the  parents  needed  to  be  told  that.

But they were told that! They were told: we don’t know which saturation range is best, that is why we are doing this study. In fact parents going into the trial were better informed than those who were not asked for consent. How many parents outside of the trial were told that the use of oxygen was extremely variable around the world, that the limits chosen in the unit where their baby would be treated were entirely arbitrary, and the saturation target limits chosen by their hospital might increase the risk of retinopathy or of disability?

Even if the same range of risks existed in ordinary NICU care, parents needed to understand their baby might be subject to a different subset of risk odds, and ultimately a different set of harms, via enrollment into this randomized clinical trial (RCT). The consent forms for the SUPPORT trial should have explained what care outside the trial would look like, and what risks were associated with that care.

I think you might expect that I don’t agree with this. at all.

The purpose of consent is to ensure that reasonably foreseeable risks of the research are explained. If the same range of risks exists in ordinary NICU care then to exaggerate the risks of being in the study by pretending that those risks are due to the research is untruthful. To try to guess what ‘subset of risk odds’ and what ‘different set of harms’ that parents need to understand is usually impossible until after the research is done.

We are also alarmed that pregnant women and their partners were asked to consider enrollment of their babies in this study just at the moment when those women were facing the very premature birth of their child. It is not clear to us that any mother, or her partner, in such a situation could have the mental wherewithal to seriously consider enrollment of their extremely premature baby in a major trial, particularly one that might change risks of death or disability. We hasten to remind those here that, much as we would dearly love data on certain interventions, there  are sometimes trials that simply cannot be done ethically.

Yes of course parents are stressed when their baby is in, or likely to be admitted to, intensive care, but we simply cannot accept the idea that there are some issues that cannot be investigated ethically as a result of their stress. As a group of people who talk to stressed parents every day of our professional lives (except when we are writing blogs) neonatologists are much more aware of this than most academic ethical thinkers. I have spoken to parents at 2 am who have just had a baby admitted to the NICU, and yes you can get a valid research consent in those circumstances. If the alternative is to give up, then I refuse that alternative.

we also must insist that discussing the  SUPPORT trial as a case of so-called “standard of care research” is just plain wrong. Several of the experimental interventions in the SUPPORT study did not represent commonly used clinical interventions. For example, we are unaware of any NICU that would carefully seek to maintain a very premature baby at an oxygen saturation level of 85-89% regardless of the baby’s clinical status, as happened to babies in one arm of the oxygen saturation intervention. We are unaware of any NICU that would regularly withhold surfactant from very premature babies.  Surfactant is a treatment widely believed to make an enormous difference in survivability of extreme prematurity. We are also unaware of NICUs where practitioners would, outside of research, be blinded as to the real oxygen saturation levels of children they are treating.

Unlike these authors, the SUPPORT investigators actually knew what goes on in an NICU.  And yes, before the SUPPORT trial was published there were (and maybe there still are) NICUs that maintained a babies saturation in that range for as long as they needed oxygen, regardless of other issues.

The statement about surfactant is perhaps the most revealing of the authors’ ignorance. In this trial surfactant was either given routinely after intubation in the delivery room or according to a different protocol which tried to avoid intubation until it was clear that the individual baby needed it. ‘Withholding life-saving surfactant’ sounds terrible doesn’t it, especially if you are totally uninformed; the babies in the restricted surfactant group DID BETTER. There was a 9% reduction in the rate of BPD which was almost significant. Infants who had their ‘life-saving surfactant’ withheld less frequently required intubation or postnatal corticosteroids for BPD (P<0.001), and required fewer days of mechanical ventilation (P = 0.03), so they were better off if they were in the ‘surfactant withholding’ arm of the trial. Babies benefit from surfactant if they need it, but exactly when you can be sure they need it still isn’t clear, even after SUPPORT. This landmark study showed that if you don’t intubate for surfactant until the baby reaches 50% oxygen, then they do better than giving them all ‘life-saving surfactant’.

As I said, I think this statement is very revealing, it really shows how little the authors know about neonatal care, but they still feel qualified to malign the doctors who performed this trial. ‘We are unaware of any NICU that would regularly withhold surfactant from very premature babies’. That could only have written by someone who has no conception of what the study was about, and never bothered to ask a neonatologist.

The statement about the masking of the saturation monitors is just bonkers. If the 2 approaches are clinically acceptable then to compare them in a masked fashion just makes the study more reliable. Of course you don’t do that outside of a trial, but it doesn’t make the trial non ‘standard of care’.

The authors object to the idea that health care should become

a so-called “learning health care system,” in which
essentially every patient becomes a subject (as this) requires a system where the line between patient and research subject necessarily becomes blurry. We strongly object to this idea.

Well sorry, the line is already blurry. We must continually learn about what we are doing. There are many ways in which evaluation of patient outcomes are used to try and improve the care that we give. Even the most unreliable reasons for changing how we deliver care (such as what happened to the last patient you treated) are based on data from other patients. The idea of building learning health care systems is to make that process reliable, and to benefit everybody, including current patients. If I analyze anonymized retrospective data to see if one hospital has better outcomes than another, then all of the patients whose data I look at are contributing to that process. A process which, in that situation, is without any risk to the individual, but which is limited, it can only give indications, and potential questions to answer.

Formally comparing current treatment approaches in randomized trials still treats all the patients as patients, who should, and in my experience do, receive compassionate thoughtful care. In fact, I would like to restate what I said above, there is no line, even a blurry one, between being a patient and a research subject, you can be both.

Posted in Neonatal Research | 4 Comments

Comparative Effectiveness Research: a parable

Posted on 29 August 2013 by Keith Barrington

Two neonatologists work in the same NICU. One of them routinely starts assisted ventilation of babies with volume ventilation, the other starts with pressure ventilation. There is controversy in the literature and in practice among currently active neonatologists; some preliminary data suggests that there might be advantages of the newer mode of ventilation. On the other hand a majority of neonatologists continue to use pressure ventilation. Observational data from the NICU where these two doctors work does not show any difference in outcomes of one doctor compared to the other.

The pair decide to participate in a large multi-center trial, comparing their two favorite approaches. Because any differences that arise are expected to be modest, the sample size is large, over 1000 extremely preterm infants will be studied. The 2 doctors realize that the data to support one approach over the other is weak, and the situation in their NICU is evidence that a definitive trial is needed.

The primary outcome of interest is lung injury. Because infants who die cannot develop lung injury, the primary outcome variable of death or bronchopulmonary dysplasia (BPD) is used, but the prior data show no difference in mortality; the only difference that people think may be found is BPD.

 I think some of the controversy regarding comparative effectiveness research comes down to a difference in the answers to what is, to some extent, a philosophical question is: what is the risk of being in such a study?

Is it the risks of all the things that can happen to sick extremely preterm infants: death, IVH, sepsis, NEC, PVL, Retinopathy as well as BPD in the two groups? Let us suppose that there is no prior reason to suppose any difference in the other outcomes, should the consent forms describe these outcomes as potential risks of the intervention? On the other hand the published systematic review does state that serious hemorrhage and PVL, when put together as a combined outcome, are more frequent in the volume group, but those data are really questionable, the pathophysiology of the 2 injuries are different, putting them together can be questioned, and the subset of studies which are most relevant for the design of this new trial do not confirm the increase, also observational data don’t show more brain injuries in hospitals that tend to use pressure rather than volume ventilation.

Public Citizen would probably argue that pressure ventilation has the risk that there may be more hypocapnia, which can lead to more brain injury, they would argue that, on average, intra-thoracic pressures are higher with pressure ventilation, which might affect cardiac output, etc. They would probably say that there are more breaths with excessive volume delivered during pressure ventilation which might lead to pneumothorax.

They would also argue that with volume ventilation there may be ETT leaks which lead to underestimation of the delivered tidal volume and consequent delivery of excessive pressure which might lead to pneumothorax.

They would state that all these potential  problems in the 2 groups must be described in detail in the consent form, supposing that they are risks of the research project.

They would also include in their objection letter the following bizarre statement ‘The random assignment of the premature infants to one of the different modes of ventilation that are currently used — independent of certain clinical factors that would normally be taken into account in making ventilation decisions as part of routine care of an individual infant — clearly has the potential to alter the care that the premature infants would otherwise receive as part of usual care if they are not enrolled in the trial.’

(The adolescent response comes to mind ‘Well, Duuuuh’.)

Well of course, that is the whole point of doing the study, instead of babies haphazardly getting one treatment or another depending on who is on call, which NICU they are in, the time of night, the availability of equipment and how opinionated the respiratory therapist is, they will be randomly assigned, so that all those other characteristics are balanced; which means that some babies that would have had pressure will get volume, some who would have had volume will get pressure.

It must also be emphasized that in no study are all eligible babies enrolled. This occurs for several reasons, but one of the reasons is that, if a doctor thinks, for an individual baby, that it is clear that one of the study interventions is preferable; in such a case they have a moral obligation to treat the baby with that particular treatment. Hopefully such decisions will have an evidence-based reasoning. So the ethical requirement for equipoise must be understood to include equipoise for the individual patient. In other words, there must be no rational objection to this particular baby receiving either volume or pressure ventilation in order for them to be enrolled.

Furthermore, if during the study it becomes clear that the randomly assigned form of ventilation is not working for your patient then you must stop the study intervention and do what you think is best. This is not a theoretical concern, it happens all the time. Study protocols are designed to minimize such violations, by allowing other therapies in defined circumstances, for which the data are collected. All studies have some protocol violations, sometimes they are just mistakes, but sometimes it is because the clinical situation makes the doctor use treatment which is contrary to the protocol, which is as it should be if they have a good reason for supposing that their patient will be better off.

The consent forms for this hypothetical trial (actually a trial that really, really needs to be done! See my previous post) state that there are no additional risks of being in this trial in excess of routine care.

The consent forms state that ‘we don’t know if there is a difference in BPD, but that is why we are doing the study to find out, so we will count how many babies survive without BPD in each group.’

I think that would be appropriate.

The implications of the SUPPORT controversy are that some people think however that the consent forms should state that the babies in one group are more likely to have BPD and that the babies in the other more likely to have brain injury, that pneumothoraces are a risk of participation in the trial, and that babies managed outside of the trial will have individualized therapy designed by their doctors to give them the best outcome. Such a consent form would be much more misleading than stating that there are no additional risks to being in the trial.

 Let us hypothesize a possible outcome of the trial.

At the end of the study there is a difference in BPD, 25% in the volume group and 35% in the pressure group, which is statistically significant.

The babies enrolled in the study have a 45% incidence of that list of serious complications above, slightly less than the 50% incidence in contemporary babies not in the trial.

So overall 30% of the babies in the study developed BPD. The same 1000 babies treated outside of the study, would probably have had the same overall incidence of BPD, (or more likely they would have had more, as just being in a trial has benefits).

The babies who were started on volume ventilation end up having the lower rate of BPD; if they had received volume ventilation outside of the trial, which would have been true for half of them, they would have had that same rate of BPD. But the other half, who would have been pressure ventilated, have, as individuals, benefitted from the trial.

The babies in the pressure group end up having a higher rate of BPD, but those who would have been treated with pressure ventilation outside of the trial, would have had that higher rate of BPD in any case. The individual babies who ‘would have’ been treated with volume ventilation, but get randomized to pressure ventilation, are more likely to have BPD than would have been their ‘fate’ if they had not been in the study.

Of course, we did not know before the study that there was going to be a difference, and there is no way to know for an individual baby which group they ‘would’ have been in outside of the trial. That is starting to get a but metaphysical.

So can we say post hoc, that there was no additional risk of being in the trial? I would say yes.

One pressure group will criticize the study, because there was not a 3rd arm of the trial where the doctor decides, based on his gut feeling, which mode of ventilation to use. Another states that the consent forms do not mention that there might have been a difference in mortality, which should be revealed to the parents.

The pressure group states that babies in the trial may receive a treatment which is different to what they would have had if they were not in the trial. The investigators reply ‘exactly, that is the whole point’.

The need for comparative effectiveness research is because we have many situations where the variations in practice are large, the variations in outcomes are great, and it is not clear which variations in practice are related to which variations in outcomes. Does randomly comparing 2 different modes of therapy in routine use pose risks? No more than (and arguably, less than) the risks of haphazard variations in care leading to different modes of therapy being used.

If you are admitted to an NICU which is not in the trial you might get volume or pressure ventilation. If you are admitted to an NICU participating in the trial you will be asked to join, and if you consent you might get volume or pressure ventilation.

So it all comes down to where you think the risks lie. If you calculate risk based on the overall outcomes of the participants there is no increase in risk. If you calculate risk after the study is over, when you know the results, and you compare the outcomes of the group who had the worse outcome with their potential outcomes had they not been in the trial, then their incidence of the adverse outcome was higher (and the other group  was lower). But that is not ‘risk’. That would be like saying that driving at 100 kph through a built up area is not risky if, after you get home, it turns out you didn’t actually hit anyone. Or that giving up smoking doesn’t decrease your risk if you end up with lung cancer anyway.

I think the way forward is to consult parents. I think we need to find situations in which parents would agree that a waiver of consent is reasonable. If parents don’t find that to be a reasonable option for a study, then they should be involved in improving the consent process. By which I mean not making the forms longer, the SUPPORT forms were already almost unreadable, not in the reading level, but conveying the complexity of the issues, in the detail that is already required, led to forms which were 9 pages long or more. It is entirely appropriate to state that a study such as this does not increase risk, but, how do we talk to parents about the implications of the fact that we might actually find an important difference between the groups once it is over?

Should we always include something like ‘when the study is completed it may be that one group has better outcomes than the other, for example there may be more babies with BPD in one group than in the other’. I think that is implicit in the consent process for such a trial, but perhaps that would be preferred by parents. We should ask them.

Posted in Neonatal Research | Tagged , , | Leave a comment

Is volume ventilation really better?

Posted on 29 August 2013 by Keith Barrington

A systematic review published in 2011 of the studies comparing pressure to volume ventilation stated that there was ‘reduced death/BPD, duration of ventilation, pneumothoraces, hypocarbia and periventricular leukomalacia/severe intraventricular hemorrhage’ using volume targeted ventilation.’

I think it may be true that volume ventilation is preferable, but I also really don’t think there are adequate data in published trials to state that with any confidence.

Lets quickly review the data in that systematic review.

There are 9 trials, almost all with tiny sample sizes. between 34 and 57, one was 109, and the largest was 213. The studies used different ventilators, made different comparisons, some used different triggering techniques in the two arms of the study, and in many the actual comparisons were unclear. 3 of the trials, including the largest, used the Servo300, pressure regulated volume control mode, which is completely inappropriate for volume ventilation in the small infant.

Let me explain.

The Servo 300 measures the volumes at each end of the ventilator circuit, so the actual infant tidal volumes are always different to the measured volumes, by an amount equivalent to the pressure differential between PEEP and pip multiplied by the compliance of the circuit. In other words, the volume you have to set depends on the relative compliance of the babies lungs and the ventilator circuit. That makes it very difficult to set up appropriately in clinical practice, and means you need to change the volume if the babies compliance changes. Which rather defeats the purpose of volume ventilation.

I’ll give you an example: the compliance of the circuits we used to use with the Servo300 was about 1  ml/cmH2O. So if you put a 1 kg baby on the Servo, before giving him surfactant you might set the ventilator to give a volume of 20 mL, that would give a pressure of 22 /6. The 16 cmH2O pressure difference between inspiration and expiration leads to a volume difference in the circuit of about 16 mL between inspiration and expiration and the baby gets a tidal volume of 4 mL, which is about right, the dynamic lung compliance is about 0.25 mL/cmH2O.

But then you give surfactant, the babies compliance improves dramatically within a few minutes, the tidal volume is still set to 20 mL, but the babies lungs are better (dynamic compliance increases to 1 mL/cmH2O), the peak pressure falls to 16, the ventilator ‘tidal volume’ is now going to be 11, and the infant tidal volume is now 10 mL. The infant is set up for volutrauma, which is what volume ventilation is supposed to prevent!

The only way you can use this ventilator safely is to constantly adjust the delivered Vt, depending on the measured pressures, to give the calculated, infant, Vt that you want: that is not exactly what volume ventilation is supposed to be all about. It is why we now have ventilators which measure the volume actually delivered to the infant, at the patient ‘Y’. It is also why the publication of the largest trial did not state what volume they used, the ventilators were set up as follows

Target PaO2 values were 45 to 60 torr for infants born at 24 to 26 weeks’ gestation, 50 to 70 torr for infants born at 27 to 28 weeks’ gestation, and 60 to 80 torr for infants born at more than 28 weeks’ gestation. Target PaCO2 values were 45 to 55 torr regardless of gestational age at birth. Specific ventilator settings to achieve these targets were determined by the clinical team’

So there was no particular tidal volume in the protocol, it was frequently changed in order to get the blood gases that they wanted, and the tidal volumes needed on PRVC were 16 mL/kg with a standard deviation of 5, that is mostly between 6 and 26 mL/kg! (those are the Vt’s measured by the ventilator, the Vt of the baby and of the circuit)

Not surprisingly the authors of that study found no difference in any clinical outcome between PRVC and SIMV, also mostly using the Servo300 ventilator.

The much smaller 1st Polish study that also used the Servo300 started the babies on a tidal volume of 5 to 6 mL/kg. and added 4 to 5 mL for the ‘compressible volume of the circuit’ which doesn’t make much sense, given that the circuit tidal volume varies depending on the pressures, that study was also a comparison with non-synchronized IMV using the Bearcub or Sechrist ventilators. The 2nd Polish study using the Servo300 I haven’t read as it is in Polish, but I don’t think I’ll bother given my comments above.)

So basically we can discount the studies using the Servo300 as being studies of volume ventilation compared to pressure (D’Angio’s study is more really a study of assist/control vs SIMV). we are left then with 6 RCTs including a total of 304 randomized babies.

None of those individual trials found a significant difference in any one of the outcomes listed as being benefits of volume ventilation. Some of those outcomes, hypocarbia for example, are based on vanishingly small subgroups of babies. For hypocarbia the n is 58!

The Cochrane review does something that the version published in neonatology (by the same authors, including the same trials) does not, that is, it divides the trials into those that were really just a comparison of volume versus pressure ventilation, and those where there were other differences in ventilator management between the groups (which they called ‘hybrid’ studies). The 3 Servo300 trials are in the hybrid subgroup. The outcome death or BPD actually therefore depends on the data from less than 200 babies, from 3 trials, none of which individually had a difference, and with an upper limit of the 95% confidence interval of 0.96. None of the other dichotomous outcomes were different in the group of studies that only investigated volume compared to pressure ventilation.

That is pretty weak stuff to make a decision on ventilator management that will affect millions of babies.

If you decide that there were no advantages to pressure ventilation, so you might as well start with volume, just in case it is true that it is better, then what tidal volume should you choose? Sinha used 5 to 8  mL/kg (I am not clear why the range) Lista and Keszler used 5 mL, Singh used 4 to 6 mL/kg, and Cheena used 4 mL/kg. In most of those studies control groups were pressure ventilated babies in whom the clinical staff adjusted the pressures to try and give an average tidal volume that was the same as the volume ventilated group. So it looks like 5 mL/kg is the most studied, but that was chosen rather arbitrarily, and it may not be optimal, we just don’t know. But lets assume for the moment that we are going to use 5 mL/kg, should that be with SIMV or A/C? If with A/C is that a PSV mode or one with constant Ti? If SIMV should we have pressure support between assisted breaths or not? These are not questions that are exclusive to volume ventilation, but they are potentially important variables that could easily affect outcomes of very preterm babies.

There are also other unanswered questions, such as: what is the maximum leak that was allowed before switching to pressure? If the ETT leak is too great there is a risk that the ventilator will increase pressures right up to the limit to try to achieve the measured volume that you want, so at some point the clinicians should say, this is not working, we have to ventilate by pressure (or switch to High Frequency Ventilation or something).

My overall verdict on this is that the advantages of volume ventilation in terms of improving clinical outcomes are ‘not proven’. Many other physicians agree, as a result there are still substantial numbers who continue to use pressure ventilation.

So what we need is more ‘clinical effectiveness research’. Research which compares current protocols of care, to produce robust data on which future practice can rely. Ohhh dear, back to the SUPPORT controversy!

In fact, the reason I started writing this post was for just that reason, to write some more about comparative effectiveness research, and the ethical implications. See next post.

Posted in Neonatal Research | Tagged , , | 1 Comment

Commenting on Nature

Posted on 28 August 2013 by Keith Barrington

The editorial in Nature about the SUPPORT controversy has now been opened for comments. It wasn’t when I first mentioned it.

I just left a comment, which may not be available until they have read it to make sure I haven’t abused anyone ( I didn’t state that the editorial writer was ‘full of shit’ so it might make it through). In the meantime, John Lantos has written a comment, which is worth reading (as is everything he writes) he talks about his own experience as a grandpa of extremely preterm twins, and his insights are very valuable.

Posted in Neonatal Research | Tagged , , | Leave a comment

Is cows milk just for cows?

Posted on 26 August 2013 by Keith Barrington

A new publication from the trial funded by Prolacta looking at possible benefits of their donor-human-milk derived preparations. This time it is the other comparison from the registered trial. That is; mothers who did not plan to breast feed were approached to randomize their infants, birth weights 500 to 1250 g.

(Cristofalo EA, Schanler RJ, Blanco CL, Sullivan S, Trawoeger R, Kiechl-Kohlendorfer U, Dudell G, Rechtman DJ, Lee ML, Lucas A et al: Randomized trial of exclusive human milk versus preterm formula diets in extremely premature infants. The Journal of pediatrics 2013)

The 2 groups received either processed, standardized donor human milk, with human milk based fortifier; or a preterm formula (which one is not stated). It is not clear what calorie density was given at what stage during the feeding regimes, although both seem to have started at 20 kcal/oz, and increased later on to 24 kcal/oz.
The primary outcome variable, as in the other part of this study, was the duration of parenteral nutrition, compared using a Kaplan Meier analysis. The sample sizes were tiny. Only 26 babies per group were planned, which was based on a very hopeful 50% reduction in the duration of PN which they thought would average 35 days in the formula group (SD 22 days).

This study was masked, which, as mentioned in the previous post, is rather important when many of the outcomes are based on subjective factors.

The enteral nutrition regime was supposed to start with 1 to 4 days npo, followed by up to 5 days of trophic feeding, followed by progression at 10 to 20 mL/kg/d up to 150 mL/kg/d.

Before getting to the clinical outcomes, it is interesting to note that the actual timing of introduction of the first feed was actually 6.5 days on average for the cow’s milk group and 4.0 days for the human. So most of the babies were started on feeds after the upper limit of the planned duration of being npo; it then took 25 days for the human milk fed babies to reach full feeds, and 29 days for the cow’s milk. I think we can do better than that. I think most very preterm babies can start feeds on day 1, and there is no good justification for not immediately starting to increase feeds, aiming for 30 mL/kg/d.  The data show that having trophic feeds is better than no feeds, but there is no data to show that trophic feeds are better than immediately increasing feed volume. There is no data that different rates of feed advancement affect NEC.

In this study the parenteral nutrition duration was longer with cow’s milk, (p=0.4). There was a lot of NEC in the bovine group, 5 cases, 21%, and 1 case in the human milk group, which was not statistically significant. 4 of the NEC cases in the cow’s milk group went for surgery, but not the human milk baby (p=0.036).

That is an awful lot of NEC, and an awfully high proportion needing surgery. I don’t think I have ever seen that in a publication, and I also used to work in a center where there was very little breast milk when I arrived, and we didn’t have anywhere near that incidence (even though it was too high).

I think we do need to be a little skeptical about this result, it is, again a secondary outcome, in a very small trial which was seriously underpowered, with a very small number of total events, but it is suggestive that this approach may be a big advance, if it can be confirmed in further, larger trials.

One thing also worth noting is that the incidence of late onset sepsis was not affected in either of the  Prolacta trials. In this new publication a whopping 79% of the bovine and 55% of the human milk babies got at least one late onset infection (difference not significant). In the previous study it was between 19 and 28% (highest in one of the human milk fortifier groups). Clearly human milk is not the answer to infection prevention, we need other approaches.

Posted in Neonatal Research | Tagged , , , , | Leave a comment

We didn’t find what we wanted to find, so we thought we’d re-analyze the data until we found it.

Posted on 26 August 2013 by Keith Barrington

…oh and by the way, we are the manufacturers making the product in question, so we had objective scientific reasons for doing this, no conflict of interest whatever.

The commercial sponsors of a negative trial decided that they didn’t like the results, so they have re-analyzed it. Two of the 3 authors of the new publication, including the corresponding author, are employees of the company that makes the product tested in the original trial. The original trial found no effect on the duration of intravenous feeding (TPN) in preterm babies randomized to receive a human milk based breast milk fortifier, compared to standard fortifier. So they analyzed the same data in a different way, and lo and behold, found that they were significantly different after all!!

So let’s have a look at the original trial.

The original trial was a multi-center RCT of 3 different regimes of enteral nutrition in infants 500 to 1250 g birth weight, whose mothers wanted to give breast milk. One group received a standard cows-milk-based breast milk fortifier, the other two groups received a new fortifier derived from donor human milk, one of which started the fortifier earlier than the other.  There were 207 babies in total, planned to be 69 per group. The primary outcome variable was duration of TPN (intravenous nutrition). The study was negative, there was no difference in duration of TPN between the groups.

On first reading the trial appears to have been well designed, and well performed (but way too small). I do have problems with the way it was presented. Even the title was misleading (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).

It would have been more accurate to use a title such as ‘An Exclusively Human Milk-Based Diet has no effect on TPN duration, but Secondary Outcomes show Possible Marginally Significant Reduction in Necrotizing Enterocolitis compared to a Diet of Human Milk and Bovine Milk-Based Products’.

That would be  a more accurate, but less sexy title.

The original study showed a possibly significant (more of that later) difference in the frequency of one of a large number of secondary outcomes: namely Necrotising Enterocolitis. So the title of the publication, and the abstract, and the discussion,  focused on this outcome. You can’t help but wonder if that focus had something to do with the fact that the study was funded by, and several of the authors were employees of, the company that makes the human milk based fortifier.

I once was co-author of a study where the first draft of the publication emphasized the interesting secondary outcome; it did not mention in the title the primary outcome, and concentrated in the abstract on the secondary outcome before describing the negative primary. I understand the desire to do this but it should be resisted by authors and by reviewers. We changed our title, abstract, and presentation to concentrate on the primary outcome, while still describing and discussing the secondary outcome. in the text.

Studies are designed to have power to detect a difference in the primary outcome. They are very rarely powered to be able to study 2 outcomes. So a positive secondary outcome must always be considered suspect. Especially if you examine multiple secondary outcomes. Important secondary outcomes do need to be measured and reported, but they must be considered exploratory and preliminary, needing confirmation.

The original publication of the Sullivan et al study found that the frequency of NEC in one HM (human milk based fortifier) group was 3/67, in the 2nd HM group it was 5/71, and with breast-milk receiving infants who got a cow’s, bovine, milk based fortifier (BOM) the incidence was 11/69. Firstly, that is a very high rate of stage 2 NEC in the breast-milk fed BOM controls (a 17% rate of NEC in preterm babies of this gestation receiving breast milk is highly unusual), so it may just be a quirk. Secondly, I have put these numbers in my software, and if you put them in as 3 groups, they actually are not significant. If you compare the 2 combined HM groups to the BOM group then the p value is 0.03, which is what was reported in the paper. That may be an appropriate way to analyze the data, as long as you planned it that way from the start. The study is way underpowered to compare 3 groups for any of their outcomes.

The trial registration documents state that the sample size was supposed to be 260; and although I don’t find the documents very clear, there were supposed to be 5 groups, the 3 mentioned here and 2 other groups which were of babies who do not receive mothers milk, randomized to either donor human milk preparation plus HM fortifier or premie formula.

NEC was not listed as a secondary outcome variable in the registration page of the website. This may be evidence of one of the limitations of trial registration, and of trial reporting. Maybe the website just doesn’t include all of the pre-specified secondary outcomes. I think CONSORT should require that registration documents are supplied with the final manuscript and any discrepancies be clearly described in the manuscript.

To be honest, I think this is a real shame, I think a human milk based fortifier is a good idea, and if we could really show that it was preferable I would be all in favour. But this study does not prove benefit, just a potential signal that needs to be appropriately investigated, with adequately powered studies, which would have to be much larger than this to have enough power to show a difference in NEC.

Also studies of NEC should be blinded. Diagnosis of NEC is quite subjective, and differentiating stage 1 from stage 2 requires identification of pneumatosis. There are at least 2 publications (here and here) which show that the inter-rater variability for diagnosing pneumatosis gives a Kappa score of between 0.2 and 0.3, which, to interpret for you, is lousy! There is a serious risk of bias in unmasked studies when the important outcome is so subjective. I can’t see any good reason why this study could not have been blinded.

If it were done correctly, and still proved that human milk based fortification reduced NEC then I would be first in line to get my hospital to pay for it. Until then I think we can still accept  the previous evidence from systematic review of 7 trials including 640 preterm infants, that cows-milk protein based fortifiers have no effect on the incidence of NEC.

__________

Update August 29th. Mike Hewson wrote a comment that I have decided to put here as he is completely correct.

Hi Keith – the previous evidence (the Cochrane review) does not show that cows milk protein based fortifiers have no effect on NEC. What it shows is a trend towards more NEC (and more death) in the fortification groups. The effect size is quite large but the numbers are too small so there is a very real risk of Type 2 error here. The Cochrane review phrases it as “insufficient evidence to be reassured that there are no deleterious effects”. We need a large study of cows milk fortifier versus control adequately powered for real long term outcomes to assess risks and benefits.

I replied to him:

I agree, your wording is preferable to what I put in the post, there is no strong evidence of adverse effects with the use of cow’s milk based fortifiers, but not enough evidence of safety. We certainly need better studies of fortification which include enough babies who are at risk of adverse outcomes to have the power to say whether they are safe or not.

Posted in Neonatal Research | Tagged , , , , , | 2 Comments

Public Citizen are a public danger: part 2

Posted on 24 August 2013 by Keith Barrington

The other part of the criticisms of Public Citizen, included in their letter to the secretary of the HSS in the USA, in which they call for the TOP (transfusion of preterms) trial to be stopped immediately, are regarding the consent forms.

The letter reviews the two previous trials as I have presented them in part one, and repeatedly states that there were:

‘less favorable outcomes seen in the IOWA and PINT studies for subjects in the restrictive transfusion group’

Public Citizen are willfully misrepresenting the results of those two trials: they did not show less favorable outcomes, as I have explained in part 1.

That being the case, what are the additional risks of being in the TOP trial, compared to being in an NICU and not participating in the trial?

Most babies under 1kg get transfused during their hospital stay. They may be transfused according to thresholds which are similar to the high TOP thresholds or the low TOP thresholds, or some other number, based on whatever the doctor is feeling like that day. So there are great variations around the world, and the procedures to be studied in TOP are well within the range of current clinical practice. There is therefore a very good justification for saying that the research poses no additional risks. It is dangerous to be an extremely preterm baby, transfusions on the other hand are really rather safe (safer than being ventilated, or having an arterial line). Studies in adults in ICU showed unexpectedly that lower transfusion thresholds were preferable, except maybe if you have unstable coronary artery disease. In the PICU transfusing at lower thresholds was not different from higher thresholds. The prior studies in the preterm baby have shown no difference, but are under-powered for the long term outcomes.

By the way, according to the Public Citizen standards those two previous trials were unethical; neither the TRICC trial, nor the TRIPICU trial had a ‘carry-on-doing-whatever-it-is-you-already-do,-and-transfuse-when-you-feel-like-it’ group (thankfully).

Public Citizen seem to think that the TOP IRBs were all misled or weren’t doing their job, and that they should have required the consent forms to list all possible complications associated with transfusions and/or prematurity as things that might possibly be different between the groups.

Their specific issues with the consent forms are as follows:

(1) As previously discussed, as part of routine care outside the research context, the hemoglobin level at which a particular premature infant would be transfused is routinely based on consideration of many individual patient factors, only some of which are taken into consideration in the experimental algorithms for the liberal and restrictive transfusion groups. Note also that an experimental  algorithm based in part on a poll of hemoglobin thresholds that would be acceptable to neonatologists in the context of a randomized clinical trial is not the same as what the hemoglobin thresholds for blood transfusion would be in usual care outside of a clinical trial. None of the consent forms clearly describe how the research interventions deviate from the usual individualization of transfusion care in extremely premature infants not enrolled in the study.

This is just evidence that they don’t know how we decide to transfuse patients.

It is also an egregious misunderstanding of clinical research. It is actually essential that the thresholds being tested are thresholds which would be used outside of a trial. If not the trial is a waste of time. If they were to compare transfusion at 20 to transfusing at 2, then that would be useless, as we won’t ever do that. If the thresholds being tested would be unacceptable in clinical care that really would be unethical, and you should just save your money and go home.

(2) Only two of the 17 IRB approved consent forms identified the restrictive group as being the usual approach for infants not enrolled in the research at that institution.  None of the other consent forms explained how the thresholds used for the two experimental groups compared to those used at the institution where the infant would be hospitalized if not enrolled in the research.

Not everyone would agree that the restrictive group is the usual approach, I would certainly say that both the restricted and the liberal approach are within usual care. Like many hospitals practice in my NICU is very variable, and you could find babies in my unit today who have received transfusions at the upper or lower limit, so to make such a statement would be misleading.

(3) Seven consent forms included the following misleading statement or one very similar to it:

This study does not alter the routine care of your baby.

The protocol changes nothing about routine care, other than obviously the transfusion threshold. That is what that statement means.

(4) Sixteen consent forms included the following uninformative and misleading statement that blurred the distinction between the two research interventions being tested and the individualized transfusion decisions that would occur for infants not enrolled in the research:

Both of these [hemoglobin threshold] levels [for determining when to transfuse blood] are in the usual range used by doctors in the NICU.

That is neither misleading nor uninformative, it is an accurate statement.

Public Citizen go on to state:

Finally, it seems unlikely that any parent who fully understands the results of the prior clinical trials, as well as the true risks, purpose, and nature of the experiment, would be willing to enroll their premature infant in this study.

Well I would. I am a parent of a premie, who understands these issues much better than Public Citizen, and I would certainly have been willing to enroll my baby.

They are also inconsistent, they note that the restricted transfusion thresholds are described, in the protocol, as being closer to the current practice of more neonatologists than the higher thresholds, then repeatedly claim that the lower thresholds are already known to be more dangerous (which is not true). Don’t they understand that would be really good evidence that we need to do this trial? And surely they can’t think that their own cursory perusal of the published evidence is so much more perceptive than the world experts on transfusion of the preterm who have got together to do this study?

Unfortunately Public Citizen get media attention. The NPR website for example has a news item ‘Another Study Of Preemies Blasted Over Ethical Concerns‘ which is not too unbalanced but does quote some of the dangerous misconceptions of Public Citizen. It seems that trying to destroy the confidence of parents in the ethical oversight of research in the preterm is one of their goals, if they succeed, they will seriously harm many thousands of babies, whose treatment will be improved by this kind of trial.

The last word again to Dr Lantos

What a topsy-turvy world! Today, neonatologists around the world want to carefully and collaboratively study the risks and benefits of common therapies. They publically announce their intentions and seek feedback from research review boards. Their study designs are rigorously scrutinised, and their consent forms are reviewed for accuracy and understandability. Parents are accurately informed of the reasonably foreseeable risks and benefits of the research. The studies are carefully monitored. Babies in the studies are protected from the risks of research and the risks of treatment with non-validated therapies. Their outcomes are better than those of babies not in the studies.

But then these neonatologists are criticised by advocacy groups and by the federal agencies whose mandate is to ensure the responsible conduct of research. These groups suggest that babies would be better off if doctors would misrepresent the risks of the studies, frighten parents away, prevent responsible research and continue to treat babies based on their non-validated beliefs about what is best.

We cannot let that happen.

Posted in Neonatal Research | Tagged , , | Leave a comment