Another swing at the windmill of VAP

Sorry, folks, but I have been so swamped with work that I have been unable to produce anything cogent here. I see today as a gift day, as my plans to travel to SHEA were foiled by mother nature's sense of humor. So, here I am trying to catch up on some reading and writing before the next big thing. To be sure, I have not been wasting time, but have completed some rather interesting analyses and ruminations, which, if I am lucky, I will be able to share with you in a few weeks.

Anyhow, I am finally taking a very close look at the much touted Keystone VAP prevention study. I have written quite a bit about VAP prevention here, and my diatribes about the value proposition of "evidence" in this area are well known and tiresome to my reader by now. Yet, I must dissect the most recent installment in this fallacy-laden field, where random chance occurrences and willful reclassifications are deemed causal of dramatic performance improvements.

So, the paper. Here is the link to the abstract, and if you subscribe to the journal, you can read the whole study. But fear not, I will describe it to you in detail.

In its design it was quite similar to the central line-associated blood stream infection prevention study published in the New England Journal in 2006, and similarly the sample frame included Keystone ICUs in Michigan. Now, recall that the reason this demonstration project happened in Michigan is because of their astronomical healthcare-associated infection (HAI) rates. Just to digress briefly, I am sure you have all heard of MRSA; but have you heard of VRSA? VRSA stands for vancomycin-resistant Staphylococcus aureus, MRSA's even more troubling cousin, vancomycin being a drug that MRSA is susceptible to. Now, thankfully, VRSA has not yet emerged as an endemic phenomenon, but of the handful of cases of this virtually untreatable scourge that has been reported, Michigan has had plurality of them. So, you get the picture: Michigan is an outlier (and not in the desirable direction) when it comes to HAIs.

Why is it important to remember Michigan's outlier status? Because of the deceptively simple yet devilishly confounding concept of regression to the mean. The idea is that in an outlier situation, at least some of the effect is due to random luck. Therefore, if the performance of an extreme outlier is measured twice, the second time it will be closer to the population mean just by pure luck alone. But I do not want to get too deeply into this somewhat muddy concept right now -- I will reserve a longer discussion of it for another post. For now I would like to focus on some of the more tangible aspects of the study. As usual, two or three features of the study design reduce substantially the likelihood that the causal inference is correct.

First feature is the training period. Prior to the implementation of the protocol, which by the way consisted of the famous VAP bundle, which we have discussed on this blog ad nauseam, there was intensive educational training of the personnel on a "culture of change", as well as the proper definitions of the interventions and outcomes. It is at this time that the "trained hospital infection prevention personnel" were intimately focused on the definition of VAP that they were using. And even though the protocol states that the surveillance definition of VAP would not change throughout the study period, what are the chances that this intensified education and emphasis did not alter at least some of the classification practices?

Skeptical? Good. Here is another piece of evidence supporting my stance. A study from Michael Klompas from Harvard examined inte-rater variability in the assessment of VAP looking at the same surveillance definition applied in the Keystone (and many other) study. Here is what he wrote:

Three infection control personnel assessing 50 patients for VAP disagreed on 38% of patients and reported an almost 2-fold variation in the total number of patients with VAP. Agreement was similarly limited for component criteria of the CDC VAP definition (radiographic infiltrates, fever, abnormal leukocyte count, purulent sputum, and worsening gas exchange) as well as on final determination of whether VAP was present or absent.

And here is his conclusion:

High interobserver variability in the determination of VAP renders meaningful comparison of VAP rates between institutions and within a single institution with multiple observers questionable. More objective measures of ventilator-associated complication rates are needed to facilitate benchmarking and quality improvement efforts. 

Yet, the Keystone team writes this in their Methods section:

Using infection preventionists minimized the potential for diagnosis bias because they are trained to conduct surveillance for VAP and other healthcare-associated infections by using standardized definitions and methods provided by the CDC in its National Healthcare Safety Network (NHSN).

Really? Am I cynical to invoke circular reasoning here? Have I convinced you yet that CAP diagnosis is a moving target? And as such it can be moved by cognitive biases, such as the one introduced by the pre-implementation training of study personnel? No? OK, consider this additional piece from the Keystone study. The investigators state that "teams were instructed to submit at least 3 months of baseline VAP data." What they do not state is whether this was a retrospective collection or a prospective one, and this matters a little. First, retrospective reporting in this case would be a lot more representative of what has been, since these rates of VAP are already recorded for posterity and cannot presumably be altered. On the other hand, if the reporting is prospective, I can still conceive of ways to introduce a bias into this baseline measure. Imagine, if you will, that you are employed by a hospital that is under scrutiny for a particular transgression, and that you know the hospital will look bad if you do not demonstrate improvement following a very popular and "common-sense" intervention. Might you be a tad more liberal with identifying these transgressive episodes in your baseline period that after the intervention has been instituted? This is a subtle, yet all too real conflict of interest, which, as we know so well, can introduce a substantial bias into any study. Still don's believe me? OK, come to my office after school and we will discuss. In the meantime, let's move on.

The next nugget is in the graph in Figure 1, where VAP trends over the pre-specified time periods are plotted (you can find the identical graph in this presentation on slide #20). Look at the mean, rather than the median line. (The reason I want you to look at the mean is that the median is zero, and therefore not credible. Additionally, if we want to assess the overall impact of the intervention, we need to be embracing the outliers, which the median ignores). What is tremendously interesting to me is that there is a precipitous drop in VAP during the period called "intervention", followed by much smaller fluctuations around the new mean across the subsequent time periods. This to me confirms the high probability of reclassification (and Hawthorne effect), rather than an actual improvement in VAP rates, as the cause of the drop.

Another piece of data makes me think that it was not the bundle that "did it." Figure 2 in the paper depicts the rates of compliance with all 5 of the bundle components in the corresponding time periods. Again, here as in the VAP rates graph, the greatest jump in adherence to all 5 strategies is observed in the intervention period. However, there is still a substantial linear increase in this metric between the intervention period and through to 25-27 months period. Yet, looking back at the VAP data, no such robust commensurate reduction is observed. While this is somewhat circumstantial, it makes me that much more wary of trusting this study.

So, does this study add anything to our understanding of what bundles do for VAP prevention? I would say not, and it actually muddies the waters. What would have been helpful to see is whether any of the downstream outcomes, such as antibiotics administration, time on the ventilator and length of stay were impacted. Without impacting these outcomes, our efforts are Quixotic, merely swinging at windmills, mistaking them for a real threat.

       

          

Intervention in ICU reduces hospital mortality, but by how much?

Addendum #2, 12:09 PM EST, 2/2/11:
So, here is the whole story. Stephanie Desmon, the author of the JH press release, e-mailed me back and pointed me to Peter Pronovost as the source for the 10% reduction information. I e-mailed Peter, and he got back to me, confirming that 

"The 10 percent is the rounded differences in differences in odds ratios"

Moral of the story: The devil is in the details.


And speaking of details, I must admit to an error of my own. If you look at the figure reproduced below, I called out the wrong points. For adjusted data, you need to look at the open circles (for the intervention group) and squares (for the control group). In fact, the adjusted mortality went from about 20% at baseline to 16% in the 13-22 months interval for the Keystone cohort, while for the control group it went from a little over 20% to a little under 18%. This makes the absolute reduction a tad more impressive, though there is still less than a 2% absolute difference between the reduction seen in the intervention vs. the control group, leaving all of my other points still in need of addressing. 


Addendum #1, 11:00 AM EST, 2/2/11:
I just found what I think is the origin of the 10% mortality reduction rumor in this press release from Johns Hopkins. I just e-mailed Stephanie Desmon, the author of the release, to see where the 10% came from. Will update again should I hear from either Maggie Fox or Stephanie Desmon.  

Remember the Keystone project? A number of years ago when we started to pay close attention to healthcare-associated infections (HAI), and hospitals started to take introspective looks at their records, it turned out the the ICUs in the state of Michigan for one reason or another had very high rates of HAIs. As this information percolated through our collective consciousness, the stars aligned in such a away as to release funding from the AHRQ in Washington, DC, for a group of ICU investigators at the Johns Hopkins University School of Medicine in Baltimore, MD, headed by Peter Pronovost, to design and implement a study employing IHI-style (Boston, MA) bundled interventions to prevent catheter-associated blood stream infections (CABSI) and ventilator-associated pneumonia (VAP) across the consortium of ICUs in MI. Whew! This poly-geographic collaboration resulted in a landmark paper in 2006 in the New England Journal of Medicine, wherein the authors showed that the bundled interventions directed by a checklist aimed at CABSI were indeed associated with a satisfying reduction of CABSI. Since 2006 the ICU community has been eagerly awaiting the results of the VAP intervention from Keystone, but none has come out. When there is a void of information, rumors fill this void, and plenty of rumors have circulated about the alleged failure of the VAP trial.

I do not want to belabor here what I have written before with regard to VAP and its prevention, and what makes the latter so difficult, and how little evidence there really is that the IHI bundle actually does anything. You can find at least some of my thoughts on that here. But why am I bringing up the Keystone project again anyway? Well, it is because Pronovost's group has just published a new paper in BMJ, and this time their aim was even more ambitious: to show the impact of this state-wide QI intervention on hospital mortality and length of stay. This is a really reasonable question, mind you, since, we could argue that, if the intervention reduces HAI, it should also do something to those important downstream events that are driven by the particular HAI, namely mortality and LOS. But here are a couple of issues that I found of great interest.

First, as we have discussed before, whether or not VAP itself causes death in the ICU population (that is patients die from VAP), or whether VAP tends to attack those who are sicker and therefore more likely to die anyway (patients die with VAP) remains unclear in our literature. There is some evidence that late VAP may be associated with an attributable increase in mortality, but not early, and these data need to be confirmed. Why is this important? Because if VAP does not impart an increase in mortality, then trying to decrease mortality by reducing VAP is just swinging at windmills.

So, let's talk about the study and what it showed as reported in the BMJ paper. You will be pleased that I will not here go through the traditional list of potential threats to validity, but take the data at face value (well, almost). The authors took an interesting approach of comparing the performance of all eligible ICUs regardless of whether they actually chose to take part in the project. Of all the admissions examined in the intervention group, 88% came from Keystone participants. This is a really sound way to define the intervention cohort, and it actually biases the data away from showing an effect. So, kudos to the investigators. The comparator cohort came from ICUs in the hospitals surrounding Michigan, those that were not eligible for Keystone participation. One point about these institutions also requires clarification: I did not see in the paper whether the authors actually looked at the control hospitals' QI initiatives. Why is this important? Well, if many of the comparator hospitals had successful QI initiatives, then one could expect to see even less difference between the Keystone intervention and the control group. So, again, good on them that they biased the data against themselves.

This is the line of thinking that brings me to my second point. Reuters' Maggie Fox covered this paper in an article a couple of days ago, an article whose byline lede (thanks for the correction, @ivanoransky) floored me:

(Reuters) - A U.S. program to help make sure hospital staff maintain strict hygiene standards lowered death rates in intensive care units by 10 percent, U.S. researchers reported on Monday.

Mind you, I read the article before delving into the peer-reviewed paper, so my surprise came out of just knowing how supremely difficult it is to reduce ICU mortality by 10% with any intervention. In the ICU we celebrate when we see even a 2% absolute mortality reduction. So, it became obvious to me that something got lost in translation here. And indeed, it did. Here is how I read the data.

There are multiple places to look for the mortality data. One is found in this figure:

Now, look at the top panel and focus on the solid circles -- these depict the adjusted mortality in the Keystone intervention group. What do you see? I see mortality going from about 14% at the baseline to about 13.5% at implementation phase to about 13% at 13-22 months post implementation. I do not see a 10% reduction, but at best about a 1% mortality advantage. What is also of interest is that the adjusted mortality in the control group (solid squares) also went down, albeit not by as much. But almost at every point of measurement it was lower already than in the intervention group.

Then there is this table, where the adjusted odds ratios of death are given for the two groups at various time points:

And this is where things get interesting. If you look at the last line of the table, the adjusted odds ratios indeed look impressive, and, furthermore, the AOR for the intervention group is lower than that for the control group. And this is pleasing to any investigator. But what does it mean? Well it means that the odds of death in the intervention group went down roughly by 24% (give-or-take the 95% confidence interval) and by 16% in the control group,each compared to itself at baseline. This is impressive, no?

Well, yes, it is. But not as impressive as it sounds. A relative reduction of 24% with the baseline mortality of 14% means an absolute reduction in mortality of 14% x 24% = 3.4%. But, you notice that we did not actually observe even this magnitude of mortality reduction in the graph. What gives? There is an excellent explanation for this. It is a little known fact to the the reader (and only slightly more so to the average researcher and peer reviewer) that the odds ratio, while a fairly solid way to express risk when the absolute risk is small (say, under 10%), tends to overestimate the effect when the risk is higher than 10%. I know we have not yet covered the ins and the outs of odds ratios, relative risks and the like in the "reviewing literature" series, but let me explain briefly. The difference between odds and risk is in the denominator. While the denominator for the latter is the entire cohort at risk for the event (here all patients at risk for dying in the hospital), that for the former is that part of the cohort that did not experience the event. See the difference? By definition, the denominator for the odds ratio is smaller than for the relative risk calculation, thus yielding a more impressive, yet inaccurate, reduction in mortality. 

Bottom line? Interesting results. Not clear if the actual intervention is what produced the 1% mortality reduction -- could have been secular trends, regression to the mean or Hawthorne effect, to name just a few alternatives. But regardless, preventing death is good. The question is were these improvements in mortality sustained after hospital discharge, or were these patients merely kept alive so that they could die elsewhere? Also, what is the value balance here in terms of resources expended on the intervention versus the results that may not even be due to the particular intervention in question?

All of this is to say that I am really not sure what the data are showing. What I am sure of is that I did not find any evidence of a 10% reduction in mortality reported by Reuters (I did e-mail Maggie Fox and at this time still awaiting a reply; will update if and when I get it). In this time of aggressive efforts to bend the healthcare expenditures curve we need to pay attention to what we invest in and the return on this investment, even if the intervention is all "motherhood and apple pie."