Comparative Effectiveness Research: a parable

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.

About keithbarrington

I am a neonatologist and clinical researcher at Sainte Justine University Health Center in Montréal
This entry was posted in Neonatal Research and tagged , , . Bookmark the permalink.

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