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.
