More Hadfield

Posted on 14 May 2013 by Keith Barrington

One of the videos from Chris Hadfield that I really loved is this one, http://www.youtube.com/watch?v=AvAnfi8WpVE a duet with some of the Bare Naked Ladies (also Canadian!) and a choir of young people.

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A Space Oddity

Posted on 14 May 2013 by Keith Barrington

The Canadian astronaut Commander Chris Hadfield returned to Earth today. He was the first astronaut of the new internet age, in terms of the way he used his earthbound links. As someone born in the 1950’s (yes I know it is hard to believe) to me, the idea of someone circling the earth on a space station sending pictures and videos to his twitter followers is beyond belief. Yet it happened, His final video was a rendition of a David Bowie favourite, you may remember that David Bowie has already made an appearance on this blog, as Colm O’Donnell used a song title of his as the title of an article he wrote (Ch Ch Ch Changes…) http://www.guardian.co.uk/science/blog/2013/may/13/chris-hadfield-the-astronaut-s-best-tweets-photos-and-videos  During his months on the Space Station, Chris Hadfield sent many fabulous photos on his social media feeds, The Guardian page that the above link leads you to has many of his best.  This fragile Earth, seen from a new angle.

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SUPPORT: even better than originally thought

Posted on 14 May 2013 by Keith Barrington

Public Citizen are at it again, repeating and expanding their idiotic criticisms of the SUPPORT trial. And stating that the trial was ‘even worse than originally thought’. They are now focusing on the ‘problem’ that the NICUs used ‘intentionally inaccurate’ pulse oximeters.

The most disturbing finding from our review of the newly available information was the failure of half of the IRB-approved consent forms to disclose to the parents of the subjects the experimental procedure, under which the entire medical team caring for each premature baby in the study was intentionally given inaccurate information about the baby’s blood oxygen saturation levels by using pulse oximeters miscalibrated across the wide range of oxygen saturations between 85% and 95%. Of note, oxygen saturation measured by a pulse oximeter is a clinical parameter of such importance in monitoring critically ill patients that it is sometimes referred to as the “fifth vital sign.

Because of the inaccurately high oxygenation saturation values provided to the medical team by the pulse oximeters for babies in the low-oxygen experimental group, it is plausible that the medical team may have treated some critically ill babies with too little oxygen, potentially resulting in brain injury and death secondary to hypoxemia (deficient oxygen). In contrast, because of the inaccurately low oxygenation saturation values provided to the medical team by the pulse oximeters for babies in the high-oxygen experimental group, it is also plausible that the medical team may have treated those babies with more oxygen than they needed, resulting in severe retinopathy of prematurity, requiring surgery and possibly causing blindness. What we do not know because the study lacked a usual standard of care control group, but suspect, is that if the medical teams had been given the correct information about oxygen saturation levels and these babies had been treated based on their individual needs as per current routine standard of practice, some deaths might have been prevented in the low-oxygen group, and some cases of severe retinopathy might have been prevented in the high-oxygen group.

This is the core of the new ‘concerns’ raised by Public Citizen, and all they really show is the ignorance of the authors about how neonatology works.

For any readers who are also unaware, we choose saturation limits based on NICU protocols not on individual prescribed values. We have no data from which to prescribe individual limits, that is why we did these studies. Yes the saturations were offset by 3%, the only way to make this a masked study. And no this did not make being in the study more dangerous, in fact being in the study was less dangerous than being in the NICU and not in the trial. So in contrast to what they state, that there was no ‘usual standard of care control group’, there were many babies in the NICUs who were not enrolled in the trial, and were treated according to usual NICU practice, who had a higher mortality than the babies in SUPPORT. Let me also explain that in our unit at the time we allowed saturations to be between 84 and 95%. That is including both of the ranges of saturation that were tested in SUPPORT, we thought that that entire range was safe, and that being in the lower part was probably safer, we now know, only as a result of SUPPORT, BOOST2 AusNZ, BOOST2 UK, and COT, that we were wrong. That babies who were not in the trial were at higher risk, that the lower part of that range, which is where most NICUs were heading before these trials, is associated with increased mortality.

Later in the public citizen document they state

Understanding the clinical importance of oxygen saturation levels in the routine management of premature babies is essential for recognizing the serious risks of providing protocol-specified misinformation to the NICU medical teams that cared for the infants in the SUPPORT study

This is almost humorously ironic, as the authors of this document clearly don’t understand the importance of saturation monitoring, and how we had no idea which saturations to target prior to the trial.

The  authors of this report, one of which appears to be an adult nephrologist who does some lab research, another a Bioethicist, the 3rd another MD but I am unsure what he does, go on to pontificate about how we look after extremely preterm infants. A subject on which they are unqualified, and misinformed. They don’t even seem to know how pulse oximeters work!

Given the complexities of routine medical management of extremely premature infants and the interaction between the different complex experimental interventions of the SUPPORT study, the minimization of the risks to babies enrolled in the study would have required a detailed plan for unblinding the NICU medical teams when the masking procedure using intentionally miscalibrated pulse oximeters posed a threat to the health of the babies.

If, in the course of any study, the physician feels that the study procedures are putting a patient at risk, or course the patient needs to be taken out of the study. In some circumstances it is important to know what treatment the patient has been receiving, and to unmask the study. In this particular study all you needed to do was to use an ordinary pulse oximeter. Indeed, that was done a few times, a doctor thought that a baby with pulmonary hypertension, for example, and treated the baby with higher saturation targets, using an unadulterated oximeter, unmasking would not be necessary.

The reason that happened very rarely is that we do not fix individual saturation targets in the NICU. They are set by protocol.

Protocols which were arbitrary, based on guesses, and many of those guesses were wrong.

I guess the authors of this document think that all of the investigators in SUPPORT, all of the investigators in the other trials around the world are unethical, and don’t really care about preterm babies. Maybe if they stopped to consider that they are maligning hundreds of people who have dedicated their lives to looking after small newborn babies it would make them reconsider their ill-conceived and slanderous attacks.

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Does NIDCAP work?

Posted on 13 May 2013 by Keith Barrington

I guess that depends on what you mean ‘work’.  Does developmentally sensitive care lead to more responsive, humane, and less disturbing care, improving the environment for our preterm infants, I think the answer is clearly yes.

If you mean does NIDCAP improve commonly used objective outcome measures in preterm infants, the answer has to be ‘not proven’. Arne Ohlsson (who is supposed to be retired but you wouldn’t guess it) and Sue Jacobs have just published a systematic review. They found no good evidence of benefit for short term medical complications of prematurity, nor for long term neuro-developmental outcomes. The babies may go home a few days earlier (about 0.5 weeks), But apart from that there is little evidence of benefit.

A few provisos, NIDCAP is a basketful of interventions, some of which may be beneficial and others not so much. There are other models of developmentally sensitive and appropriate care which may be more effective, or less, and also need to be well tested. Don’t throw away all your developmental care interventions, lets try testing them (like cycled lighting for example) and find things that work best.

There is indeed some evidence that cycled lighting might be preferable to persistent darkness, even for the very preterm infant who ‘should’ still be in a low light environment. (See here and here and here). It may also be that some noise, especially the human voice, is better than being very quiet, some very preliminary data from Terrie Inder, presented at PAS suggests that maybe being too quiet isn’t good.

I think the time has come for objective evaluation of the different parts of ‘developmental care’ to ascertain those that are essential, and those that may be useless of harmful.

One thing that has always intrigued me is that Dr H Als, who invented the form of developmentally sensitive care that we call NIDCAP, based on a theory of neurodevelopment that she made up called the ‘synactive theory’, always finds in her studies that  all of the outcomes are better with NIDCAP, even in tiny underpowered studies. The latest included only 13 infants in the NIDCAP group, (with 17 controls) and supposedly found that brain structure and brain function were better on all of the measures that were performed. Now I don’t know about you, but the phrase ‘to good to be true’ springs to mind.

According to the manuscript this was a study registered as NCT00914108; but that study, which was only registered in 2009, recruited patients between 1996 and 2002 according to the entry on clinicaltrials.gov.

In this current manuscript it is stated that the infants were recruited from 2005 to 2008. So it cannot be 00914108. That is just sloppy.

This appears to be the study registered as NCT00166660, a single center study of 30 preterm SGA infants, which would match the recruitment dates. But I am not sure, there are a few things that appear different, babies were supposed to be 28 to 33 weeks gestation at birth according to the registration record, but infants in this study were eligible if they were at least 26 4/7 according to the article (which is a weird cutoff), with a birth weight below the 5th %le.

From the publication it is impossible to figure out what was the primary outcome variable, from the registration record of 00166660 it appears that there were 3:

  • Assessment of Preterm Infants’ Behavior (APIB) [ Time Frame: 2 weeks corrected age (2w CA)
  • Quantified Electroencephalography (qEEG) [ Time Frame: 2 weeks Corrected Age (2w CA)
  • Magnetic Resonance Imaging(MRI) [ Time Frame: 2 weeks Corrected Age (2w CA)

Clearly there was no power at all for 3 primary outcome variables, the 2nd and 3rd being so ill-defined that you could do a hundred analyses and only report those that you thought were significant. Indeed there were apparently 40 coherence factors analyzed for the EEG, 5 of which are reported as being ‘significant’.

The statistics section of the study calculates the power of the study using the 30 enrolled infants, which is different to doing an a prior power analysis and calculating how many you need.

Dr Ohlsson and Jacobs review has received a large number of letters to the editor, most of which state something like, ‘we know it works, so we don’t believe this review’, often stated very forcefully. Many of the letters point out the statistically significant results that have been found, such as a Bayley 2 at 9 months of age, which is marginally better in NIDCAP babies to controls, but ignore the fact that this review addresses outcomes that are similar to those examined in the majority of neonatal intervention studies. If NIDCAP cannot be shown to improve these outcomes is it worth the investment?

The authors of the review submit a long response which addresses all of the substantive issues, if you are interested I suggest you read their response rather than sending me a comment!

Being sensitive to the developmental needs and the sensorial sensitivity of preterm infants makes great sense, and many nurses have helped to make the NICU a more humane, less overstimulating and less intrusive place. My own daughter benefited from such sensitivities; but that is not the same as claiming that NIDCAP improves brain structure!

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Slug Porn

Posted on 9 May 2013 by Keith Barrington

David Attenborough, who has ‘appeared’ on this blog previously, has a TV series about invertebrates. He is a sprightly 87 years old (Annie is hoping I am as sprightly in 45 years time… !). The program is as usual, amazing, with some incredible filming of invertebrate behaviour. Some clips can be seen on youtube, including a video of leopard slugs doing what comes naturally (at least to them).

http://www.youtube.com/watch?v=FhVi4Z6CjZk

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How much oxygen?

Posted on 9 May 2013 by Keith Barrington

At the PAS meeting in Washington DC, that has just finished, the COT trial results were presented, as well as the short term outcomes of the BOOST trials.

These are a series of clinical trials which have compared higher saturations 91 to 95% to lower saturations 85 to 89%. As I mentioned before when discussing the SUPPORT trial, which had the same target ranges, and the same technique of using masked pulse oximeters, these target ranges are within the ranges that were being used routinely in NICUs around the world, but we did not know if one target range was better or worse than the other, overall. There has been a remarkable international collaboration to get several similar trials performed at around the same time, so that we can then get even more power by putting the results together.

The COT trial showed no significant difference between the high and low sat target ranges. The BOOST trials (BOOST UK (and Ireland) BOOST Australia and BOOST NZ) showed the increased mortality, in the low saturation group, that we have already heard about, and the increased retinopathy in the high saturation group similar to the SUPPORT trial. Both of these studies have also just been published, COT here and the BOOSTs here

Now what?

Closer examination of the COT results shows that there were more deaths in the low saturation group, 16.6% vs 15.3%. Although this is not significant (at usual levels of statistical significance) it is not very different in magnitude to the increased mortality in the other trials results. Even more concerning, the difference in mortality between the groups occurred entirely after introducing the new software in the Masimo oximeters. After changing the software, the mortality in the 2 groups was 16.8% in the low saturation group, and 14.1% in the high saturation group.

Also, in COT, retinopathy of prematurity (RoP) was not different between the groups, this is harder for me to understand, there was really no difference at all between the saturation groups. If COT had been published first, then I would have thought that maybe the increase in RoP with oxygen mostly occurs with higher sats, and is not different between the high 80s and the low 90s, but the other trials now all show more RoP between these target ranges.

So probably, and this question was asked by Richard Martin in the meeting, a meta-analysis will show that the confidence limits of the COT mortality difference have a wide overlap with the other oxygen trials, and most likely the overall analysis will still show a significant increase in mortality with lower saturations, and, I would guess, with very little heterogeneity.

One of the strengths of these oxygen trials, as I mentioned above, was that even from before they started there was a plan to perform a prospective meta-analysis, whereby the individual patient data are entered into a database, but with variables defined a priori, and the data to be collected agreed from the start. All of the oxygen trials (SUPPORT, COT, the BOOSTs) agreed to participate in this NeoProm collaboration, one of the reasons that many of us were very happy to participate in COT , was the participation in NeoProm (I actually initiated COT in two hospitals, the Royal Victoria Hospital in Montreal, where it was ably taken over by Nabeel Ali when I left, and then at Sainte Justine).

I think it is vitally important that we all continue this collaboration, to be able to answer the important questions, that were raised several years ago, with the greatest confidence.

Lisa Askie, the expert in this kind of analysis in the perinatal field, has written a review of the current situation (already a bit out of date with these new presentations, and publications). She notes the preliminary data regarding increased mortality, and describes the NeoProm collaboration in some detail. As she notes, the BOOST trials were stopped early as a combined preliminary analysis showed the increase in mortality that I am describing, COT did not contribute to this preliminary analysis, and an article published in Trials (open access) recently by the BOOST steering committee describes the history of what happened as the steering committees were struggling to decide what to do with the data showing increased mortality with lower saturations.

I think the time has come for complete openness with trial data. Iain Chalmers notes that the enrollment in the BOOSTs was stopped after the interim analysis, a process which would have been easier and done with more confidence if the COT data had been available, such a decision has major consequences whichever way it goes, reducing sample size and reducing power, exposing subjects to risks, or truncating a trial which did not truly have differential risks. These are all potentially of great importance. The only way to make a good decision is to have all the available relevant information.

NeoProm will help us to finally answer the question posed in the title of this post: each of the 2 new publications is accompanied by an editorial, (here and here) both of them state that we should now target 90 to 95% saturation, which should avoid the increased risk of death with the lower saturations, and although there will probably be some more retinopathy, the risk of serious visual problems in the long term is not increased because of the high quality ophthalmological screening and treatment we currently have.

The data from clinical trials do not belong to the PIs and the steering committees of the trials. They should be considered to be the property of the whole community: the babies and families who participated, the funding agencies and the societies that support them, and the investigators and health care workers who facilitate the trials.

Chalmers paper mentioned above includes the following sentence ‘If the academic community wishes to be seen to be putting the interests of patients and science above individual agendas, concerns and benefits, the issue of sharing interim analyses needs to be given more attention’ they give examples of 2 situations in which similar on-going trials have agreed to share data during the performance of those trials. Only by doing this will we be able to avoid situations where continuing trials, or stopping them too early, causes unnecessary harm.

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Smaller plates please

Posted on 2 May 2013 by Keith Barrington

In this study, first grade children were randomly given either adult sized plates or smaller kiddie plates. (DiSantis KI, Birch LL, Davey A, Serrano EL, Zhang J, Bruton Y, Fisher JO: Plate Size and Children’s Appetite: Effects of Larger Dishware on Self-Served Portions and Intake. Pediatrics 2013, 131(5):e1451-e1458). The kids took more food when given the bigger plates, and ate most of the extra food that they took. The answer to the obesity epidemic!

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Neonatal Updates #31

Posted on 2 May 2013 by Keith Barrington

Yoder BA, Stoddard RA, Li M, King J, Dirnberger DR, Abbasi S: Heated, Humidified High-Flow Nasal Cannula Versus Nasal CPAP for Respiratory Support in Neonates. Pediatrics 2013. A multi-center RCT among just over 400 infants who were at least 1 kg and at least 28 weeks gestation. Infants who would otherwise receive CPAP were randomized to either CPAP (at 5 or 6 cm H2O) or high flow cannulae at between 3 and 5 liters per minute depending on their body weight. Babies were eligible either in the first 24 hours or after extubation. The outcomes were very similar in the two groups, with some minor evidence of benefit with CPAP (fewer days of positive pressure in total).

Azzopardi D, Robertson NJ, Kapetanakis A, Griffiths J, Rennie JM, Mathieson SR, Edwards AD: Anticonvulsant effect of xenon on neonatal asphyxial seizures. Archives of Disease in Childhood – Fetal and Neonatal Edition 2013. Of 14 infants receiving xenon gas in addition to cooling, 5 had seizure. The seizures stopped during xenon therapy, started again when xenon was withdrawn, and stopped again when xenon was restarted.

Bohnhorst B: Usefulness of abdominal ultrasound in diagnosing necrotising enterocolitis. Archives of Disease in Childhood – Fetal and Neonatal Edition 2013. A good quality review, appropriately cautious about the place of ultrasound. I have certainly had radiologists tell me that a baby had penumatosis on an abdominal ultrasound performed for other reasons entirely, I do think that portal venous gas is probably a reliable sign of NEC, and ultrasound is probably much more sensitive than x-ray for this finding.

Bremer DL, Rogers DL, Good WV, Tung B, Hardy RJ, Fellows R: Glaucoma in the Early Treatment for Retinopathy of Prematurity (ETROP) study. Journal of American Association for Pediatric Ophthalmology and Strabismus 2012, 16(5):449-452. It is not common, but I was unaware that babies with high risk prethreshold RoP are at risk of glaucoma, about 2% before 6 years of age, regardless of whether they had early laser treatment or not.

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Music has charms to soothe a savage breast

Posted on 1 May 2013 by Keith Barrington

William Congreve, The Mourning Bride, 1697: (from Act 1 Scene 1)

Musick has Charms to sooth a savage Breast,
To soften Rocks, or bend a knotted Oak.
I’ve read, that things inanimate have mov’d,
And, as with living Souls, have been inform’d,
By Magick Numbers and persuasive Sound.
What then am I? Am I more senseless grown
Than Trees, or Flint? O force of constant Woe!
‘Tis not in Harmony to calm my Griefs.
Anselmo sleeps, and is at Peace; last Night
The silent Tomb receiv’d the good Old King;
He and his Sorrows now are safely lodg’d
Within its cold, but hospitable Bosom.
Why am not I at Peace?

Our preterm babies in general do not have savage breasts, they are cool, and rarely savage at all.  But it may be anyway that music helps them to be soothed. (Loewy J, Stewart K, Dassler A-M, Telsey A, Homel P: The Effects of Music Therapy on Vital Signs, Feeding, and Sleep in Premature Infants. Pediatrics 2013.)

The infants in this multicenter trial were randomly put in one of 4 experimental conditions, control, parents favourite lullaby, a noise maker that sounds a bit like breathing (Remo ocean disk) and a gato box which produces two gentle tones that can be timed to the babies rhythms.

I think this is a reasonable thing to think about, lullabies are known in all cultures, they seem to have similar characteristics in different cultures, and they do calm down babies.

Unfortunately there are some flaws in the paper, the authors list 4 different primary outcomes, which they say were ‘included’ in the primary outcomes. So how many they analyzed isn’t clear; it looks like they did a repeated measures test for each individual intervention, with each outcome variable, making about 20 tests for the short term physiologic responses. They also say in the methods ‘The study was powered to detect any outcome that was measured along a continuum that had a small ES’ (Effect Size). I have no idea what that means, I don’t think it means anything. They also present data about sleep without giving any indication how different sleep stages were diagnosed, and then talk about ‘good sleep’ while the graph they show is ‘for % active sleep’

This is a randomized controlled trial but the report does not follow CONSORT guidelines. as the journal website says that it must.

One neat feature of the study was that when the parents did not identify a particular lullaby, they all got ‘twinkle twinkle’. They were then able to show that the specific lullaby of the family was more effective than the generic ‘twinkle’. The lullabies where mostly sung by the parents, after some hints from the music therapists, but sometimes it was other caregivers.

Despite the limitations of this report, I think it looks like it is safe to have parents sing to their preterm babies (!) and indeed lullabies may well soothe the babies breasts.

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What the… #2

Posted on 1 May 2013 by Keith Barrington

Some of you may remember my rant about the article that was supposedly about in-hospital developmental care recently published in Early Human Development. Well I sent a note to the editor through the web page telling him about my concerns. I received a reply, not from the editor, but from someone at Elsevier asking me to submit a letter to the editor. I found this a little strange, as I did not write to Elsevier and it is the editors responsibility what is published in the journal, but nevertheless I went to the website to submit the letter. The journal website now has instructions for authors available on the appropriate page, which was blank when I visited previously, maybe it was just a glitch, but the instructions to authors clearly state that all RCT reports should comply with CONSORT. Which this one did not.

The text of my letter is reproduced below. I will keep you posted.

To the editor:

Re: Chen L-C, Wu Y-C, Hsieh W-S, Hsu C-H, Leng C-H, Chen WJ, Chiu N-C, Lee W-T, Yang MC, Fang L-J et al: The effect of in-hospital developmental care on neonatal morbidity, growth and development of preterm Taiwanese infants: A randomized controlled trial. Early Human Development 2013, 89(5):301-306.

This recent publication is an embarrassment to the medical community. The authors have been allowed to publish an article in which the infants were enrolled before they were eligible, where some of the outcome variables are used as exclusion criteria, where other outcome variables could not possibly have been affected by the intervention, where the number of outcome variables and statistical analyses is so great that one can have no confidence whatsoever in the results. In addition the interventions are so poorly described that it is impossible to know what they were investigating.

Unfortunately the investigators have used substantial resources, enrolled large numbers of infants, and I am sure had the best of intentions.

Even the title of the article is profoundly misleading, as the intervention started at 34.7 weeks, and continued after discharge (apparently, even though even this is not clear), and we are informed that all groups received ‘in-hospital developmental care’ including the controls. The different interventions, which started on enrollment into the study, commenced at 34.7 weeks PMA as noted in table 2.

Eligibility criteria: the authors state in the eligibility criteria that these include being ‘physiologically stable, i.e., no ventilator use, absence of apnea, bradycardia, or desaturation with or without oxygen use at post-menstrual age (PMA) of 36 weeks; [6] hospital discharge prior to PMA of 44 weeks’ so the infants were not eligible until 44 weeks PMA, but they were enrolled and had intervention started by 34 .7 weeks, i.e. 10 weeks before they were eligible, if the authors did not have access to a time machine this is clearly impossible.

Outcome variables: the outcome variables used include BPD, as infants were not eligible until after 36 weeks the authors would already know if they had BPD when enrolled. RoP is also used as an outcome variable, when it is also an exclusion criterion, and again would have been diagnosed by the time the infants were eligible. Feeding desaturation; as noted above infants were ineligible for the study if they had desaturation, so to include feeding desaturation as an outcome variable is incomprehensible.

Significance of statistics. The authors never state which outcomes were primary or secondary, they have therefor performed 18 t tests (having decided to ignore the fact that there were 2 different intervention protocols). There is no adjustment for multiple testing which means that there was over a 60% chance of a type 1 error. The 2 outcomes which are supposed to be different between groups are outcomes which could not have been different between groups, as RoP occurred before the children were eligible and feeding desaturation made the infants ineligible.

It is inconceivable that an intervention which commences at 34.7 weeks could have any effect on BPD or on RoP.

Your instructions to authors page clearly states in detail that all RCT reports should comply with CONSORT. This publication did not. There is no flow sheet, it does not specify primary and secondary outcomes, and there are many other failings.

The publication of this trial in your journal makes clear that the editorial standards and refereeing of ‘Early Human Development’ are inadequate. It makes it impossible to have any confidence in any of the articles published in your journal. This article should be retracted.

Sincerely

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