Sunday, April 5, 2009

Another [the final?] nail in the coffin of intensive insulin therapy (Leuven Protocol) - and redoubled scrutiny of single center studies

In the March 26th edition of the NEJM, the NICE-SUGAR study investigators publish the results of yet another study of intensive insulin therapy in critically ill patients: .

This article is of great interest to critical care practitioners because intensive insulin therapy (Leuven Protocol) or some diluted or half-hearted version of it has become a de facto standard of care in ICUs across the nation and indeed worldwide; and because it is an incredibly well-designed and well-conducted study. My own interest derives also from my own [prescient] letter to the editor of the NEJM after the second Van den Berghe study ( , the criticisms I levied against this therapy on this blog after another follow-up study recently showed negative results ( ), and in a recent paper railing against the "normalization heuristic" ( ). The results of this study also add to the growing evidence that intensive control of hyperglycemia in other settings may not be beneficial (see the ACCORD and ADVANCE studies.)

The current study was designed to largely mirror the enrollment criteria and outcome definitions of the previous studies, had excellent follow-up, had well described and simple statistical analyses with ample power, and is well reported. Key differences between it and the original Van den Berghe study were the lack of high-calorie parenteral glucose infusions, and its multicenter design. This latter characteristic may be pivotal in understanding why the initially promising Leuven Protocol results have not panned out on subsequent study.

The results of this study can be summarized simply by saying that it appears that this therapy is of NO benefit and actually probably kills patients, in addition to markedly increasing the rate of very very severe hypoglycemia (6.3% increase, P<0.001). In contrast to Van den Berghe's second study in medical patients, there were no favorable trends towards reduction in ICU length of stay, time on the ventilator, or reduced organ failures. In short, this therapy appears to be a complete flop.

So why the difference? Why did this therapy, which in 2001 appeared to have such promise that it enjoyed rapid and widespread [and premature] adoption fail to withstand the basic test of science, namely, repeatability? I think that medical history will judge two factors to be responsible. Firstly, the massive dextrose infusions in the first study markedly jeporadized the external validity of the first (positive) Van den Berghe study - it's not that intensive insulin saves you from your illness, it saves you from the harmful caloric infusions used in the surgical patients in the first study.

Secondly, and this is related to the first, single center studies also compromise external validity. In a single center, local practice patterns may be uniform and idiosyncratic, so that the benefit of any therapy tested in such a center may also be idiosyncratic. Moreover, and I dare say, investigators at a single center may have more decisional latitude and control or influence over enrollment, ascentainment of outcomes, and clinical care of enrolled patients. The so-called "trial effect" whereby patients enrolled in a trial receive superior care and have superior outcomes may be more likely in single center studies. Such effects are of increased concern in trials whre total blinding/masking or treatment assignment is not possible. (Recall that in the Van den Berghe study, kan endocrinologist was consulted for insulin adjustments; in the current trial, a computerized algorithm controlled the adjustments.) Moreover still, for single center studies, investigators and the instutution itself may have more "riding on" the outcome of the study, and collective equipoise may not exist. As an "analogy of extremes", just for illustrative purposes, if you wanted to design a trial where you could subversively influence outcomes in a way that would not be apparent from the outside, would you design a single center study (at your own institution where your cronies were) or a large multicenter, multinational study? Which design would allow you to have more influence?

I LOVE the authors' concluding statement that "a clinical trial targeting a perceived risk factor is a test of a complex strategy that may have profound effects beyond its effect on the risk factor." This resonates beautifully with our conceptualization of the "normalization heuristic" and harkens to Ben Franklin's sage old saw that "He is the best physician who knows the worthlessness of the most medicines." I think that we now have more than ample data to assure us that intensive insulin therapy (i.e., targeting a blood sugar of 80-108) is a worthless medicine, and should be largely if not wholly abandoned.

Addendum 4/7/09: Also note the scrutiny of the only other "positive" study (with mortality as the primary endpoint) in critical care in the last decade: Rivers et al; see: .


  1. While I agree with your conclusions....a couple of caveats
    1. The comparison arm in this study was not "no control of glucose." Prior to Leuven 1, many of us simply used sliding scale insulin when glucose levels topped 200. This strategy (that I am aware) has not been compared to less trict control with IV insulin.
    2. Why did the strict normoglycemia group die? What was the mechanism? There was no increase in new organ failures so did organ failure simply not resolve?

  2. I would like to echo what O'Brien said about the management ranges. I would also challenge your assessment of this being a very well designed study. We simply do not have the all the information from NS we need to make any type of conclusive decision (and most certainly can not call it foolproof). This is what always concerns me about these studies. We read headlines and do not analyze the contents before making changes (this happened with Leuven 1). Let me point out a couple of concerns with the NS study:
    1) Range control of the study arms. This is something that is routinely vetted by FDA prior to drug or device release, but for some studies including this one nobody seems to care. The mean BG level of the control arm was 145 and the time weighted BG was 144. That was the very bottom of the range as established in the protocol. That means that many of the results for these patients were much lower then 144 and this data is included in the control range results. Do we really know what the outcome was of a patient managed between 150-180?
    2. BG was supposed to be tightly managed in both groups. If this was the case, why so many hypos in the IIT group. There is no reason with adequate monitoring that hypo should ever be over 1% regardless of the target.
    3) Different feeding techniques. We need to remember that they do feed differently in Europe then we do here in the US, Canada, and Australia. We certainly should have some concern when we look at the calories intake of the patients in NS - certainly not optimal.
    4) the number of hypos was disproportionately high in the IIT group. Why with supposedly good glucose management? But more importantly, did this group contribute to the higher rate of mortality? If so, then the results strongly suggest a BG management issue not an improvement in outcome.

    The biggest challenge with this study is that as I have spoken to colleagues around the US and they are routinely saying that they will change their current ranges to <180. This is ludicrous!! We have absolutely no data that supports that better outcome is achieved with any patient above 150 (145 to be exact) until some study analysis is completed.

    The final point and the one that disappoints me most in our reaction to this study is the lack of clearly trying to achieve best in class medicine. I do not know what the best range for BG is in our critically ill patients, but it does seems to make sense that somewhere near normal, if not normal, would be best. We know that Leuven has shown three times (2001, 2004, 2009) that normal glucose improves outcomes in their environment. We also know that Furnary in Portland and the folks at UCLA (among others)have demonstrated that normal BG also improves outcome, decreases stay. Yes these are all single centers, but different centers.

    It seems that because we as a whole have not been able to meet the challenge (constant monitoring of BG and best in class insulin management) that we would rather take the NS results and say I told you so.

    This is just the opening chapters in this book and I hope that other physicians across the US do not just read the headlines. They need to think about what makes sense, what the totality of the evidence suggest, and continue to push themselves and their staffs to best in practice BG management and a level lower then 150 until more data proves otherwise.

  3. Jim -

    Yes, you can always say that the dose (target) was wrong, and that a different dose (target) would work, but do you really really think that's likely here? I mean, if these date were available 10 years ago, would anybody be studying IIT today? I doubt it. This thing is like steroids in critical illness, and like acinetobacter, they just won't die. If you can't even get separation (of effect) with this drastic approach, you think you're going to get it with a less drastic approach? Oh, please don't say yes and refer me to Eichacker and Natonson's U-shaped curve article (even though they may have a point).

    There's just no consistent signal here. This stuff just doesn't work. We're wasting our time. In fact, my suggestion for a study is insulin (you choose the target, just don't make it 80-110) versus NOTHING. Just do NOTHING. Let the BS ride as it may. That's a study I'd like to see. Like Voltaire said, "The art of medicine is amusing the patient while nature cures the disease."

    To answer your second question, I'd say that unrecognized severe hypoglycemia led to excess cardiovascular deaths - that's just a hypothesis. I hope nobody tests it prospectively. They could test for an interaction, but I don't see it reported.

  4. Jonathan -

    Thanks for your comments. I will reply to a few of your points.

    1.) You appear to disagree with the inclusion criteria. There's not too much to say about that, it is what it is. However, it is always convenient and perhaps too easy to retrospectively say "yeah, but if....". Generally, these enrollment criteria are fiercely debated by experts in the field when the study is designed and they generally are well appraised of the available data that would suggest the most likely groups to benefit. In any case, if the effect of a therapy is robust, it should not be terribly sensitive to small changes in enrollment cut-offs like the BS levels you mention.

    2.) One of the things this study shows is that it is just not possible to totally control the BS level. Hubris leads us all too often to believe that we can control physiology as an ex-vivo homeostat of sorts. Alas, we cannot.

    3.) Nobody knows the optimal caloric intake of these patients. The reporting of the data are different from the Van den Berghe and Brunkhorst articles which do not average over all 14 days - if you do that like the NS investigators did, you drag down the average because of days 0-2 when you're ramping up. I highly doubt that this factor wiped out any robust treatment effect. To say so would imply that you think there's an interaction between treatment effect and caloric intake, and things get complex and Sir William of Ockham turns over in his grave.

    4.) The number of hypos is always higher in the IIT group and this re-emphasizes that this therapy is not without risk. I know offhand that it was higher in VdB2 and Brunkhorst, and it's higher here. I have no uncertainty about whether IIT causes excess hypoglycemia and there is a high pre-test probability for this biologically plausible finding.
    I totally agree with you however that we need to see if there was an interaction between hypo and mortality as I commented above with Jim.

    I'm not sure why you think, given the available data, that "somewhere near normal, if not normal, would be best". There just dont' seem to be data to support that contention.

    I am willing to wager and I'll give you 2:1 odds that in the next 10 years we are not going to consistently find any BS target that improves mortality in this population. We can debate till the cows come home but only time will tell. But I will wager in the meantime that this just doesn't work.

    Thanks again for your many thoughtful comments. And let me know if you're willing to make a gentleman's wager at 2:1 odds.

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  7. In following up Johnathon's comments, I suspect the glucose levels in the higher range group were at the lower end of the range due to some patients being less than 144 despite no insulin. There was no protocol effort to RAISE these glucose levels (nor do I think anyone would argue for doing so) to the "goal range." The "goal range" was, in fact, a target once intervention was indicated. However, it was a one-way effort - lowering to that range - not intervening to raise back into that range.

    I agree with Scott completely about the hypoglycemia. Critically ill patients can't complain about symptoms (or we don't recognize it) of hypoglycemia the way ambulatory patients can. So we rely on lab testing, which currently is intermittent. Perhaps closed-loop technology with continuous monitoring will correct this - but not yet.

    I also am interested by the belief that there is a well-established caloric goal in critically ill adults. Is our desire to provide the full "daily caloric needs" simply driven by our tendency to normalize? Last time I was sick (and not as sick as my average ICU patient) I had no appetite. Perhaps this is an adaptive phenomenon intended to prevent the supply of fule to dysfucntional mitochondria - a hibernation of sorts. Perhaps we should NOT be feeding our critically ill patients - enteral or parenteral? EDEN-OMEGA may provide some information - at least in ALI patients.