Move Over Feckless Extubation, Make Room For Reckless Extubation

Following the theme of some recent posts on Status Iatrogenicus (here and here) about testing and treatment thresholds, one of our stellar fellows Meghan Cirulis MD and I wrote a letter to the editor of JAMA about the recent article by Subira et al comparing shorter duration Pressure Support Ventilation to longer duration T-piece trials.  Despite adhering to my well hewn formula for letters to the editor, it was not accepted, so as is my custom, I will publish it here.

Spoiler alert - when the patients you enroll in your weaning trial have a base rate of extubation success of 93%, you should not be doing an SBT - you should be extubating them all, and figuring out why your enrollment criteria are too stringent and how many extubatable patients your enrollment criteria are missing because of low sensitivity and high specificity.

Don't Get Soaked: The Practical Utility of Predicting Fluid Responsiveness

In this article in the September 27th issue of JAMA, the authors discuss the rationale and evidence for predicting fluid responsiveness in hemodynamically unstable patients.  While this is a popular academic topic, its practical importance is not as clear.  Some things, such as predicting performance on a SBT with a Yang-Tobin f/Vt,  don't make much sense - just do the SBT if that's the result you're really interested in.  The prediction of whether it will rain today is not very important if the difference in what I do is as small as tucking an umbrella into my bag or not.  Neither the inconvenience of getting a little wet walking from the parking garage nor that of carrying the umbrella is very great.  Similarly, a prediction of whether or not it will rain two months from now when I'm planning a trip to Cancun is not very valuable to me because the confidence intervals about the estimate are too wide to rely upon.  Better to just stick with the base rates:  how much rainfall is there in March in the Caribbean on an average year?

Our letter to the editor was not published in JAMA, so I will post it here:

To the Editor:  A couple of issues relating to the article about predicting responsiveness to fluid bolus¹ deserve attention.  First, the authors made a mathematical error that may cause confusion among readers attempting to duplicate the Bayesian calculations described in article.  The negative predictive value (NPV) of a test is the proportion of patients with a negative test who do not have the condition – the true negative rate.²  In each of the instances in which NPV is mentioned in the article, the authors mistakenly report the proportion of patients with a negative test who do have the condition.  This value, 1-NPV, is the false negative rate - the posterior probability of the condition in those with a negative test.

Second, in the examples that discuss NPV, the authors use a prior probability of fluid responsiveness of 50%.  A clinician who appropriately uses a threshold approach to decision making³ must determine a probability threshold above which treatment is warranted, considering the net utility of all possible outcomes with and without treatment given that treatment’s risks and benefits⁴.  Because the risk of fluid administration in judicious quantities is low⁵, the threshold for fluid administration is correspondingly low and fluid bolus may be warranted based on prior probability alone, thus obviating additional testing.  Even if additional testing is negative and suggests a posterior probability of fluid responsiveness of only 10% (with an upper 95% confidence limit of 18%), many clinicians would still judge a trial of fluids to be justified because fluids are considered to be largely benign and untreated hypovolemia is not⁴.  (The upper confidence limit will be higher still if the prior probability was underestimated.)  Finally, the posterior probabilities hinge critically on the estimates of prior probabilities, which are notoriously nebulous and subjective.  Clinicians are likely intuitively aware of these quandaries, which may explain why empiric fluid bolus is favored over passive leg raise testing outside of academic treatises⁶.

1.            Bentzer P, Griesdale DE, Boyd J, MacLean K, Sirounis D, Ayas NT. WIll this hemodynamically unstable patient respond to a bolus of intravenous fluids? JAMA. 2016;316(12):1298-1309.

2.            Fischer JE, Bachmann LM, Jaeschke R. A readers' guide to the interpretation of diagnostic test properties: clinical example of sepsis. Intensive Care Med. 2003;29(7):1043-1051.

3.            Pauker SG, Kassirer JP. The threshold approach to clinical decision making. N Engl J Med. 1980;302(20):1109-1117.

4.            Tsalatsanis A, Hozo I, Kumar A, Djulbegovic B. Dual Processing Model for Medical Decision-Making: An Extension to Diagnostic Testing. PLoS One. 2015;10(8):e0134800.

5.            Investigators TP. A Randomized Trial of Protocol-Based Care for Early Septic Shock. N Engl J Med. 2014;370(18):1683-1693.

6.            Marik PE, Monnet X, Teboul J-L. Hemodynamic parameters to guide fluid therapy. Annals of Intensive Care. 2011;1:1-1.

Scott K Aberegg, MD, MPH

Andrew M Hersh, MD

The University of Utah School of Medicine

Salt Lake City, Utah

Early Mobility in the ICU: The Trial That Should Not Be

I learned via twitter yesterday that momentum is building to conduct a trial of early mobility in critically ill patients.  While I greatly respect many of the investigators headed down this path, forthwith I will tell you why this trial should not be done, based on principles of rational decision making.

A trial is a diagnostic test of a hypothesis, a complicated and costly test of a hypothesis, and one that entails risk.  Diagnostic tests should not be used indiscriminately.  That the RCT is a "Gold Standard" in the hierarchy of testing hypotheses does not mean that we should hold it sacrosanct, nor does it follow that we need a gold standard in all cases.  Just like in clinical medicine, we should be judicious in our ordering of diagnostic tests.

The first reason that we should not do a trial of early mobility (or any mobility) in the ICU is because in the opinion of this author, experts in critical care, and many others, early mobility works.  We have a strong prior probability that this is a beneficial thing to be doing (which is why prominent centers have been doing it for years, sans RCT evidence).  When the prior probability is high enough, additional testing has decreasing yield and risks false negative results if people are not attuned to the prior.  Here's my analogy - a 35 year old woman with polycystic kidney disease who is taking birth control presents to the ED after collapsing with syncope.  She had shortness of breath and chest pain for 12 hours prior to syncope.  Her chest x-ray is clear and bedside ultrasound shows a dilated right ventricle.  The prior probability of pulmonary embolism is high enough that we don't really need further testing, we give anticoagulants right away.  Even if a V/Q scan (creatnine precludes CT) is "low probability" for pulmonary embolism, we still think she has it because the prior probability is so high.  Indeed, the prior probability is so high that we're willing to make decisions without further testing, hence we gave heparin.  This process follows the very rational Threshold Approach to Decision Making approach proposed by Pauker and Kasirrer in the NEJM in 1980, which is basically a reformulation of VonNeumann and Morganstern's Expected Utility Theory to adapt it to medical decisions.  Distilled it states in essence, "when you get to a threshold probability of disease where the benefits of treatment exceed the risks, you treat."  And so let it be with early mobility.  We already think the benefits exceed the risks, which is why we're doing it.  We don't need a RCT.  As I used to ask the housestaff over and over until I was cyanotic: "How will the results of that test influence what you're going to do?"

Notice that this logical approach to clinical decision making shines a blinding light upon "evidence based medicine" and the entire enterprise of testing hypotheses with frequentist methods that are deaf to prior probabilities.  Can you imagine using V/Q scanning to test for PE without prior probabilities?  Can you imagine what a mess you would find yourself in with regard to false negatives and false positives?  You would be the neophyte medical student who thinks "test positive, disease present; test negative, disease absent."  So why do we continue ad nauseum in critical care medicine to dismiss prior probabilities and decision thresholds and blindly test hypotheses in a purist vacuum?

The next reasons this trial should not be conducted flow from the first.  The trial will not have a high enough likelihood ratio to sway the high prior below the decision threshold; if the trial is "positive" we will have spent millions of dollars to "prove" something we already knew at a threshold above our treatment threshold; if the trial is positive, some will squawk "It wasn't blinded" yada yada yada in an attempt to dismiss the results as false positives; if the trial is negative, some will, like the tyro medical student, declare that "there is no evidence for early mobility" and similar hoopla and poppycock; or the worst case:  the trial shows harm from early mobility, which will get the naysayers of early mobility very agitated.  But of course, our prior probability that early mobility is harmful is hopelessly low, making such a result highly likely to be spurious.  When we clamor about "evidence" we are in essence clamoring about "testing hypotheses with RCTs" and eschewing our responsibility to use clinical judgment, recognize the limits of testing, and practice in the face of uncertainty using our "untested" prior probabilities.

Consider a trial of exercise on cardiovascular outcomes in community dwelling adults - what good can possibly come of such a trial?  Don't we already know that exercise is good for you?  If so, a positive trial reinforces what we already know (but does little to convince sedentary folks to exercise, as they too already know they should exercise), but a negative trial risks sending the message to people that exercise is of no use to you, or that the number needed to treat is too small for you to worry about.

Or consider the recent trials of EGDT which "refuted" the Rivers trial from 14 years ago.  Now, everybody is saying, "Well, we know it works, maybe not the catheters and the ScVO2 and all those minutaie , but in general, rapid early resuscitation works.  And the trials show that we've already incorporated what works into general practice!"

I don't know the solutions to these difficult quandries that we repeatedly find ourselves in trial after trial in critical care medicine.  I'm confused too.  That's why I'm thinking very hard and very critically about the limits of our methods and our models and our routines.  But if we can anticipate not only the results of the trials, but also the community reaction to them, then we have guidance about how to proceed in the future.  Because what value does a mega-trial have, if not to guide care after its completion?  And even if that is not its goal, (maybe its goal is just to inform the science), can we turn a blind eye to the fact that it will guide practice after its completion, even if that guidance is premature?

It is my worry that, given the high prior probability that a trial in critical care medicine will be "negative", the most likely result is a negative trial which will embolden those who wish to dismiss the probable benefits of early mobility and give them an excuse to not do it.

Diagnostic tests have risks.  A false negative test is one such risk.