"Prophylactic" NIPPV for Extubation in Obese Patients? The De Jong study, Lancet Resp Med, 2023

I got interested in this topic after seeing a pulmccm.org post on 4 studies of the matter this morning. "They" are trying to convince me that I should be applying NIPPV to obese patients to prevent....well, to prevent what?

We begin with the French study by De Jong et al, Lancet Resp Med, 2023. The primary outcome was a composite of: 1. reintubation; 2. switch to the other therapy (HFNC); 3. "premature discontinuation of study treatment", basically meaning you dropped out of the trial, refusing to continue to participate. 

Which three of those outcomes mean anything? Only reintubation. I actually went into the weeds of the trial because I wanted to know what were the criteria for reintubation. If you have some harebrained protocol for reintubation that is triggered by blood gas values or even physiological variables (respiratory rate), it could be that NIPPV just protects you from hitting one of the triggers for reintubation. You didn't "need" to be reintubated, your PaCO2 which changed almost imperceptibly (3mmHg) triggered a reintubation. These triggers for intubation are witless - they don't consider the pre-test probability of recrudescent respiratory failure, and this kind of mindless approach to intubation gets countless hapless patients unnecessarily intubated every day. Alas, the authors don't even report how the decision to reintubate was made in these patients.

But it doesn't matter. Prophylactic NIPPV doesn't prevent reintubation:

As you can see in this table, the entire difference in the composite outcome is driven by more people being "switched to the other study treatment". Why were they "switched?" We're left to guess. And being a non-blinded study, there is a severe risk that treating physicians knew the study hypothesis, believed in NIPPV, and were on a hair trigger to do "the switch". 

But it doesn't matter. This table shows you that you can start off on HFNC, if you look at the doctors cross-eyed and tachypneic, they can switch you from HFNC to NIPPV and voile! You needn't worry about being reintubated at a higher rate than had you received NIPPV from the first.

Look also at the reintubation rates: ~10%. They're not extubating people fast enough! Threshold is too high.

So we have yet another study where doing something to everyone now saves them from the situation where a fraction of them would have had it done to them later. Like the 2002 Konstantinidis study of early TPA for what we now call intermediate risk PE. In that study, you can give 100 people TPA up front, or just give it to the 3% that crumps - no difference in mortality.

I won't do it. Because people are relieved to be extubated and it's a buzz kill to immediately strap a tight-fitting mask to them. 

Regarding the Thille studies (this one and this one): I'm already familiar with the original study of NIPPV plus HFNC vs HFNC alone directly after extubation in patients at "high risk" of reintubation. The results were statistically significant in favor of NPPV with 18% reintubated vs 12%. And, they did a pretty good job of defining the reasons for reintubation - as well as anybody could. But these patients were all over 65 and had heart and/or lung diseases of the variety that are already primary indications for NIPPV. And the post-hoc subgroup analysis (second study linked above, a reanalysis of the first) focusing on obese patients shows the same effect as the entire cohort in the original study, with perhaps a bigger effect in overweight and obese patients. But recall, these patients have known indications for NIPPV, and we've known for 20 years that if you extubate everybody "high risk" to NIPPV, you have fewer reintubations. (The De Jong study, to their credit, excluded people with other indications for NIPPV in that study, e.g., OHS.) The question is whether you want an ICU full of people on NIPPV for 48 hours (or more) post-extubation with routine adoption of this method, or whether you wanna use it selectively. 

Now would be a good time to mention the caveat I've obeyed for over 20 years. That's the Esteban 2004 NEJM study showing if you're trying to use NIPPV as "rescue therapy" for somebody already in post-extubation respiratory failure, they are more likely to die, probably because of delay of necessary reintubation and higher complication rates stemming therefrom.

Now, whenever I can get access to the Hernandez 2025 AJRCCM study, which is firewalled by ATS for this university professor (who is no longer an ATS member, having rejected the political ideology that suffused the society), I will do a new post or add to this one.

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.

You Have No Idea of the Predictive Value of Weaning Parameters for Extubation Success, and You Probably Never Will

As Dr. O'brien eloquently described in this post, many people misunderstand the Yang-Tobin (f/Vt) index as being a "weaning parameter" that is predictive of extubation success.  Far from that, it's sensitivity and specificity and resultant ROC curve relate to the ability of f/Vt after one minute of spontaneous ventilation to predict the success of a prolonged (~ one hour) spontaneous breathing trial.  But why would I want to predict the result of a test (the SBT), and introduce error, when I can just do the test and get the result an hour later?  It makes absolutely no sense.  What we want is a parameter that predicts extubation success.  But we don't have that, and we probably will never have that.

In order to determine the sensitivity and specificity of a test for extubation success, we will need to ascertain the outcome in all patients regardless of their performance on the test of interest.  That means we would have to extubate patients that failed the weaning parameter test.  In the original Yang & Tobin article, their cohort consisted of 100 patients.  60(%) of the 100 were said to have passed the weaning test and were extubated, and 40(%) failed and were not extubated.  (There is some over-simplification here based on how Yang & Tobin classified and reported events - its not at all transparent in their article - the data to resolve the issues are not reported and the differences are likely to be small.  Suffice it to say that about 60% of their patients were successfully weaned and the remainder were not.)  Let's try to construct a 2x2 table to determine the sensitivity and specificity of a weaning parameter using a population like theirs.  The top row of the 2x2 table would look something like this, assuming an 85% extubation success rate - that is, of the 60 patients with a positive or "passing" SBT score (based on whatever parameter), all were extubated and the positive predictive value of the test is 85% (the actual rate of reintubation in patients with a passing weaning test is not reported, so this is a guess):

Once Bitten, Twice Try: Failed Trials of Extubation

“When a distinguished but elderly scientist states that something is possible, he is almost certainly right. When he states that something is impossible, he is very probably wrong.”                                                                                   – Clark’s First Law

It is only fair to follow up my provocative post about a “trial of extubation” by chronicling a case or two that didn’t go as I had hoped.  Reader comments from the prior post described very low re-intubation rates.  As I alluded in that post, decisions regarding extubation represent the classic trade-off between sensitivity and specificity.  If your test for “can breathe spontaneously” has high specificity, you will almost never re-intubate a patient.  But unless the criteria used have correspondingly high sensitivity, patients who can breathe spontaneously will be left on the vent for an extra day or two.  Which you (and your patients) favor, high sensitivity or high specificity (assuming you can’t have both) depends upon the values you ascribe to the various outcomes.  Though these are many, it really comes down to this:  what do you think is worse (or more fearsome), prolonged mechanical ventilation, or reintubation?

What we fear today we may not seem so fearsome in the future.  Surgeons classically struggled with the sensitivity and specificity trade-off in the decision to operate for suspected appendicitis.  “If you never have a negative laparotomy, you’re not operating enough” was the heuristic.  But this was based on the notion that failure to operate on a true appendicitis would lead to serious untoward outcomes.  More recent data suggest that this may not be so, and many of those inflamed appendices could have been treated with antibiotics in lieu of surgery.  This is what I’m suggesting with reintubation.  I don’t think the Epstein odds ratio (~4) of mortality for reintubation from 1996 applies today, at least not in my practice.

Trial of Extubation: An Informed Empiricist’s Approach to Ventilator Weaning

“The only way of discovering the limits of the possible is to venture a little way past them into the impossible.”    –Clark’s Second Law

In the first blog post, Dr. Manthous invited Drs. Ely, Brochard, and Esteban to respond to a simple vignette about a patient undergoing weaning from mechanical ventilation.  Each responded with his own variation of a cogent, evidence based, and well-referenced/supported approach.  I trained with experts of similar ilk using the same developing evidence base, but my current approach has evolved to be something of a different animal altogether.  It could best be described as a “trial of extubation”.  This approach recently allowed me to successfully extubate a patient 15 minutes into a trial of spontaneous breathing, not following commands, on CPAP 5, PS 5, FiO2 0.5 with the vital parameters in the image accompanying this post (respiratory rate 38, tidal volume 350, heart rate 129, SpO2 88%, temperature 100.8).  I think that any account of the “best” approach to extubation should offer an explanation as to how I can routinely extubate patients similar to this one, who would fail most or all of the conventional prediction tests, with a very high success rate.

A large part of the problem lies in shortcomings of the data upon which conventional prediction tests rely.  For example, in the landmark Yang and Tobin report and many reports that followed, sensitivity and specificity were calculated considering physicians’ “failure to extubate” a patient as equivalent to an “extubation failure”.  This conflation of two very different endpoints makes estimates of sensitivity and specificity unreliable.  Unless every patient with a prediction test is extubated, the sensitivity of a test for successful extubation is going to be an overestimate, as suggested by Epstein in 1995.   Furthermore, all studies have exclusion criteria for entry, with the implicit assumption that excluded patients would not be extubatable with the same effect of increasing the apparent sensitivity of the tests.

Even if we had reliable estimates of sensitivity and specificity of prediction tests, the utility calculus has traditionally been skewed towards favoring specificity for extubation success, largely on the basis of a single 20-year old observational study suggesting that patients who fail extubation have a higher odds of mortality.  I do not doubt that if patients are allowed to “flail” after it becomes clear that they will not sustain unassisted ventilation, untoward outcomes are likely.  However, in my experience and estimation, this concern can be obviated by bedside vigilance by nurses and physicians in the several hours immediately following extubation (with the caveat that a highly skilled airway manager is present or available to reintubate if necessary).  Furthermore, this period of observation provides invaluable information about the cause of failure in the event failure ensues.  There need be no further guesswork about whether the patient can protect her airway, clear her secretions, maintain her saturations, or handle the work of breathing.  With the tube removed, what would otherwise be a prediction about these abilities becomes an observation, a datapoint that can be applied directly to the management plan for any subsequent attempt at extubation should she fail – that is, the true weak link in the system can be pinpointed after extubation.

The specificity-heavy utility calculus, as I have opined before, will fail patients if I am correct that an expeditious reintubation is not harmful, but each additional day spent on the ventilator confers incremental harm.  Why don’t I think reintubations are harmful?  Because when my patients fail, I am diligent about rapid recognition, I reintubate without observing complications, and often I can extubate successfully the next day, as I did a few months ago in a patient with severe ARDS.  She had marginal performance (i.e., she failed all prediction tests) and was extubated, failed, was reintubated, then successfully extubated the next day.  (I admit that it was psychologically agonizing to extubate her the next day.  They say that a cat that walks across a hot stove will never do so again.  It also will not walk on a cold stove again.  This psychology deserves a post of its own.)

When I tweeted the image attached to this post announcing that the patient (and many like her) had been successfully extubated, there was less incredulity than I expected, but an astute follower asked – “Well, then, how do you decide whom and when to extubate?”  I admit that I do not have an algorithmic answer to this question.  Experts in opposing camps of decision psychology such as Kahneman and his adherents in the heuristics and biases camp and Gary Klein, Gird Gigerenzer and others in the expert intuition camp could have a heyday here, and perhaps some investigation is in order.  I can summarize by saying that it has been an evolution over the past 10 or so years.  I use everything I learned from the conventional, physiologic, algorithmic, protocolized, data-driven, evidence-based approach to evaluate a patient.  But I have gravitated to being more sensitive, to capture those patients that the predictors say should fail, and I give them a chance – a “trial of extubation.”  If they fail, I reintubate quickly.  I pay careful attention to respiratory parameters, mental status, and especially neuromuscular weakness, but I integrate this information into my mental map of the natural history of the disease and the specific patient’s position along that course to judge whether they have even a reasonable modicum of a chance of success.  If they do, I “bite the bullet and pull it.”

I do not eschew data, I love data.  But I am quick to recognize their limitations.  Data are generated for many reasons and have different values to different people with different prerogatives.  From the clinician’s and the patient’s perspective, the data are valuable if they reduce the burden of illness.  I worry that the current data and the protocols predicated on them are failing to capture many patients who are able to breathe spontaneously but are not being given the chance.  Hard core evidence based medicine proponents and investigators need not worry though, because I have outlined a testable hypothesis:  that a “trial of extubation” in the face of uncertainty is superior to the use of prediction tests and protocols.  The difficult part will be determining the inclusion and exclusion criteria, and no matter what compromise is made uncertainty will remain, reminding us that science is an iterative, evolving enterprise, with conclusions that are always tentative.

Does Investigating Delirium Make You Delirious? A Sober Look at Sedation and Analgesia in the ICU

Michael's Milk

I rarely use the Medical Evidence Blog to discuss review articles, but today's NEJM has one that I can't pass up about Sedation and Delirium in the Intensive Care Unit.  It is my opinion that we have gotten carried away by the torrent of articles, many in prominent journals, about delirium in the ICU and that while this is an important topic for research, it is extremely premature to try to translate the findings into practice, and moreover, that the approach to sedation suggested by the article is lacking in common sense.

As chronicled in the accompanying perspective article by D.S. Jones, delirium has been around as long as ICUs have, and the longer you're there, the more likely you will become delirious.  It's an exposure thing.  Thus, until somebody reports the results of a trial of delirium treatment or prevention that has important and undeniable effects on clinically relevant outcomes, I will continue to approach delirium as I always have - by going to great lengths to get patients out of bed, off the vent, and out of the ICU as fast as I possibly can - because these things benefit all patients regardless of whether they have an impact on delirium.

Bite the Bullet and Pull It: The NIKE approach to extubation.

I was very pleased to see McConville and Kress' Review article in the NEJM this week (December 6, 2012 issue) regarding weaning patients from the ventilator. I have long been a fan of the University of Chicago crew as well as their textbook and their pioneering study of sedation interruption a decade ago.

In their article, they provide a useful review of the evidence relating to the discontinuation of mechanical ventilation (aka weaning , liberation, and various other buzz words used to describe this process.) Yet at the end of the article, in describing their approach to discontinuation of mechanical ventilation, they provide a look into the crystal ball that I think and hope shows what the future may hold in this area. In a nutshell, they push the envelope and try to extubate patients as quickly as they can, ignoring inconvenient conventional parameters that may impede this approach in select instances.

Much of the research in this field has been dedicated to trying to predict the result of extubating a patient. (In the case of the most widely cited study, by Yang and Tobin, the research involves predicting the result of a predictor of the ultimate result of interest. This reminds me of Cervantes' Quijote - a story within a story within a story....but I digress.) And this is a curious state of affairs. What other endeavor do we undertake in critical care medicine where we wring our hands and so helplessly and wantonly try to predict what is going to happen? Don't we usually just do something and see what happens, making corrections along the way, in silent acknowledgment that predicting the future is often a fool's errand? What makes extubation so different? Why the preoccupation with prediction when it comes to extubation? Why not "Just Do It" and see what happens?