Showing posts sorted by relevance for query tobin. Sort by date Show all posts
Showing posts sorted by relevance for query tobin. Sort by date Show all posts

Monday, December 31, 2007

Is there any place for the f/Vt (the Yang-Tobin index) in today's ICU?

Recently, Tobin and Jubran performed an eloquent re-analysis of the value of “weaning predictor tests” (Crit Care Med 2008; 36: 1). In an accompanying editorial, Dr. MacIntyre does an admirable job of disputing some of the authors’ contentions (Crit Care Med 2008; 36: 329). However, I suspect space limited his ability to defend the recommendations of the guidelines for weaning and discontinuation of ventilatory support.

Tobin and Jubran provide a whirlwind tour of the limitations of meta-analyses. These are important considerations when interpreting the reported results. However, lost in this critique of the presumed approach used by the McMaster group and the joint tack force are the limitations of the studies on which the meta-analysis was based. Tobin and Jubran provide excellent points about systematic error limiting the internal validity of the study but, interestingly, do not apply such criticism to studies of f/Vt.

For the sake of simplicity, I will limit my discussion to the original report by Yang and Tobin (New Eng J Med 1991; 324: 1445). As a reminder, this was a single center study which included 36 subjects in a “training set” and 64 subjects in a “prospective-validation set.” Patients were selected if “clinically stable and whose primary physicians considered them ready to undergo a weaning trial.” The authors then looked a variety of measures to determine predictors of those “able to sustain spontaneous breathing for ≥24 hours after extubation” versus those “in whom mechanical ventilation was reinstituted at the end of a weaning trial or who required reintubation within 24 hours.” While not explicitly stated, it looks as if all the patients who failed a weaning trial had mechanical ventilation reinstituted, rather than failing extubation.

In determining the internal validity of a diagnostic test, one important consideration is that all subjects have the “gold standard” test performed. In the case of “weaning predictor tests,” what is the condition we are trying to diagnose? I would argue that it is the presence of respiratory failure requiring continued ventilatory support. Alternatively, it is the absence of respiratory failure requiring continued ventilatory support. I would also argue that the gold standard test for this condition is the ability to sustain spontaneous breathing. Therefore, to determine the test performance of “weaning predictor tests,” all subjects should undergo a trial of spontaneous breathing regardless of the results of the predictor tests. Now, some may argue that the self-breathing trial (or spontaneous breathing trial) is, indeed, this gold standard. I would agree if SBTs were perfectly accurate in predicting removal of the endotracheal tube and spontaneous breathing without a ventilator in the room. This is, however, not the case. So, truly, what Yang and Tobin are assessing is the ability of these tests to predict the performance on a subsequent SBT.

Dr. MacIntyre argues that “since the outcome of an SBT is the outcome of interest, why waste time and effort trying to predict it?” I would agree with this within limits. Existing literature supports the use of very basic parameters (e.g., hemodynamic stability, low levels of FiO2 and PEEP, etc.) as screens for identifying patients for whom an SBT is appropriate. Uncertain is the value of daily SBTs in all patients, regardless of passing this screen or not. One might hypothesize that simplifying this step even further might provide incremental benefit. Yang and Tobin, however, must consider a failure on an SBT to have deleterious effects. They consider “weaning trials undertaken either prematurely or after an unnecessary delay…equally deleterious to a patient’s health.” There is no reference supporting this assertion. Recent data suggest that inclusion of “weaning predictor tests” do not save patients from harm due to avoiding SBTs destined to fail (Tanios et al. Crit Care Med, 2006; 34: 2530). On the contrary, inclusion of the f/Vt as the first in Tobin’s and Jubran’s “three diagnostic tests in sequence” resulted in prolonged weaning time.

Tobin and Jubran also note the importance of prior probabilities in determining the performance of a diagnostic test. In the original study, Yang and Tobin selected patients who “were considered ready to undergo a weaning trial” by their primary physicians. Other studies have reported that such clinician assessments are very unreliable with predictive values marginally better than a coin-flip (Stroetz et al, Am J Resp Crit Care Med, 1995; 152: 1034). Perhaps, the clinicians whose patients were in this study are better than this. However, we are not provided with strict clinical rules which define this candidacy for weaning but can probably presume that “readiness” is at least a 50% prior probability of success. Using Yang and Tobin’s sensitivity of 0.97 and specificity of 0.64 for f/Vt, we can generate a range of posterior probabilities of success on a weaning trial:


As one can see, the results of the f/Vt assessment have a dramatic effect on the posterior probabilities of successful SBTs. However, is there a threshold below which one would advocate not performing an SBT if one’s prior probability is 50% or higher? I doubt it. Even with a pre-test probability of successful SBT of 50% and a failed f/Vt, 1 in 25 patients would actually do well on an SBT. I am not willing to forego an SBT with such data since, in my mind, SBTs are not as dangerous as continued, unneeded mechanical ventilation. I would consider low f/Vt values as completely non-informative since they do not instruct me at all regarding the success of extubation – the outcome for which I am most interested.

Other studies have used f/Vt to predict extubation failure (rather than SBT failure) and these are nicely outlined in a recent summary by Tobin and Jubran (Intensive Care Medicine 2006; 32: 2002). Even if we ignore different cut-points of f/Vt and provide the most optimistic specificities (96% for f/Vt <100, Uusaro et al, Crit Care Med 2000; 28: 2313) and sensitivities (79% for f/VT <88, Zeggwagh et al., Intens Care Med 1999; 25:1077), the f/Vt may not help much. As with the prior table, using prior probabilities and the results of the f/Vt testing, we can generate posterior probabilities of successful extubation:


As with the predictions of SBT failure, a high f/Vt lowers the posterior probability of successful extubation greatly. However, one must consider the cut off for posterior probabilities in which one would not even attempt an SBT. Even with a 1% posterior probability, 1 in 100 patients will be successfully extubated. This is the rate when the prior probability of successful extubation is only 20% AND the patient has a high f/Vt! What rate of failed extubation is acceptable or, even, preferable? Five percent? Ten percent? If one never reintubates a patient, it is more likely that he is waiting “too long” to extubate rather than possessing perfect discrimination. Furthermore, what is the likelihood that patients with poor performance on an f/Vt will do well on an SBT? I suspect this failure will prohibit extubation and the high f/Vt values will only spare the effort of performing the SBT. Is the incremental effort of performing SBTs on those who are destined to fail such that it requires more time than the added complexity of using the f/Vt to determine if a patient should receive an SBT at all? Presuming that we require an SBT prior to extubation, low f/Vt values remain non-informative. One could argue that with a posterior probability of >95%, we should simply extubate the patient, but I doubt many would take this approach, except in those intubated for reasons not related to respiratory problems (e.g. mechanical ventilation for surgery or drug overdose).

Drs. Tobin, Jubran and Marini (who writes an additional, accompanying editorial, Crit Care Med 2008; 36: 328) are master clinicians and physiologists. When they are at the bedside, I do not doubt that their “clinical experience and firm grasp of pathophysiology” (as Dr. Marini mentions), can match or even exceed the performance of protocolized care. Indeed, expert clinicians at Johns Hopkins have demonstrated that protocolized care did not improve the performance of the clinical team (Krishnan et al., Am J Resp Crit Care Med 2004; 169: 673). I have heard Dr. Tobin argue that this indicates that protocols do not provide benefit for assessment of liberation (American Thoracic Society, 2007). I doubt that the authors would strictly agree with his interpretation of their data since several of the authors note in a separate publication that “the regularity of steps enforced by a protocol as executed by nurses or therapists trumps the rarefied individual decisions made sporadically by busy physicians” (Fessler and Brower, Crit Care Med 2005; 33: S224). What happens to the first patient who is admitted after Dr. Tobin leaves service? What if the physician assuming the care of his patients is more interested in sepsis than ventilatory physiology? What about the patient admitted to a small hospital in suburban Chicago rather than one of the Loyola hospitals? Protocols do not intend to set the ceiling on clinical decision-making and performance, but they can raise the floor.

Thursday, May 24, 2018

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):



Tuesday, December 4, 2012

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?

Wednesday, January 11, 2017

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 benefits4Because 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


Tuesday, May 31, 2016

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.

Tuesday, April 19, 2011

ECMO and logic: Absence of Evidence is not Evidence of Absence

I have been interested in ECMO for adults with cardiorespiratory failure since the late 1990s during the Hantavirus cardiopulmonary syndrome endemic in New Mexico, when I was a house officer at the University of New Mexico. Nobody knows for sure if our use of AV ECMO there saved any lives, but we all certainly suspected that it did. There were simply too many patients too close to death who survived. It made an impression.

I have since practiced in other centers where ECMO was occasionally used, and I had the privilege of writing a book chapter on ECMO for adult respiratory failure in the interim.

But alas, I now live in the Salt Lake Valley where, for reasons as cultural as they are scientific, ECMO is taboo. The main reason for this is, I think, an over-reliance on outdated data, along with too much confidence in and loyalty to, locally generated data.

And this is sad, because this valley was hit with another epidemic two years ago - the H1N1 epidemic, which caused the most severe ARDS I have seen since the Hanta days in New Mexico. To my knowledge, no patients in the Salt Lake Valley received ECMO for refractory hypoxemia in H1N1 disease.


Thus I read with interest the Pro Con debate in Chest a few months back, and revisited in the correspondence of the current issue of Chest, which was led by some of the local thought leaders (and those who believe that, short of incontrovertible evidence, ECMO should remain taboo and outright disparaged) - See: http://chestjournal.chestpubs.org/content/139/4/965.1.citation and associated content.

It was an entertaining and incisive exchange between a gentleman in Singapore with recent ECMO experience in H1N1 disease, and our local thought leaders, themselves led by Dr. Alan Morris. I leave it to interested readers to read the actual exchange, as it is too short to merit a summary here. My only comment is that I am particularly fond of the Popper quote, taken from The Logic of Scientific Discovery: "If you insist on strict proof (or disproof) in the empirical sciences, you will never benefit from experience and never learn from it how wrong you are." Poignant.

I will add my own perhaps Petty insight into the illogical and dare I say hypocritical local taboo on ECMO. ECMO detractors would be well-advised to peruse the first Chapter in Martin Tobin's Principles and Practice of Mechanical Ventilation called "HISTORICAL PERSPECTIVE ON THE DEVELOPMENT OF MECHANICAL VENTILATION". As it turns out, mechanical ventilation for most diseases, and particularly for ARDS, was developed empirically and iteratively during the better part of the last century, and none of that process was guided, until the last 20 years or so, by the kind of evidence that Morris considers both sacrosanct and compulsory. Indeed, Morris, each time he uses mechanical ventilation for ARDS, is using a therapy which is unproved to the standard that he himself requires. And indeed, the decision to initiate mechanical ventilation for a patient with respiratory failure remains one of the most opaque areas in our specialty. There is no standard. Nobody knows who should be intubated and ventilated, and exactly when - it is totally based on gestalt, is difficult to learn or to teach, and is not even addressed in studies of ARDS. Patients must be intubated and mechanically ventilated for entry to an ARDS trial, but there are no criteria which must be met on how, when, and why they were intubated. It's just as big a quagmire as the one Morris describes for ECMO.

And much as he, and all of us, will not stand by idly and allow a spontaneously breathing patient with ARDS to remain hypoxemic with unacceptable gas exchange, those of us with experience with ECMO, an open mind, equipoise, and freedom from rigid dogma will not stand by idly and watch a ventilated patient remain hypoxemic with unacceptable gas exchange for lack of ECMO.

It is the same thing. Exactly the same thing.