Even the lay public and popular press (see: http://www.nytimes.com/2011/01/11/science/11esp.html?_r=1&scp=1&sq=ESP&st=cse) caught on to the subversive battle between frequentist and Bayesian statistics when it was announced (ahead of print) that a prominent psychologist was to publish a report purporting to establish the presence of Extra Sensory Perception (ESP) in the Journal of Personal and Social Psychology (I don't think it's even published yet, but here's the link to the journal: http://www.apa.org/pubs/journals/psp). So we're back to my Orange Juice (OJ) analogy - if I published the results of a study showing that the enteral administration of OJ reduced severe sepsis mortality by a [marginally] statistically significant 20%, would you believe it? As Carl Sagan was fond of saying, "extraordinary claims require extraordinary evidence" - which to me means, among other things, an unbelievably small P-value produced by a study with scant evidence of bias.
And I remain utterly incredulous that the administration of a paralytic agent for 48 hours in ARDS (see Papazian et al: http://www.nejm.org/doi/full/10.1056/NEJMoa1005372#t=abstrac) is capable of reducing mortality. Indeed, FEW THERAPIES IN CRITICAL CARE MEDICINE REDUCE MORTALITY (see Figure 1 in our article on Delta Inflation: http://www.ncbi.nlm.nih.gov/pubmed/20429873). So what was the P-value of the Cox regression (read: ADJUSTED) analysis in the Papazian article? It was 0.04. This is hardly the kind of P-value that Car Sagan would have accepted as Extraordinary Evidence.
The correspondence regarding this article in the December 23rd NEJM (see: http://www.nejm.org/doi/full/10.1056/NEJMc1011677) got me to thinking again about this article. It emphasized the striking sedation practices used in this trial: patients were sedated to a Ramsay score of 6 (no response to glabellar tap) prior to randomization - the highest score on the Ramsay scale. Then they received Cis-at or placebo. Thus the Cis-at group could not, for 48 hours, "fight the vent," while the placebo group could, thereby inducing practitioners to administer more sedation. Could it be that Cis-at simply saves you from oversedation, much as intensive insulin therapy (IIT) a la 2001 Leuven protocol saved you from the deleterious effects of massive dextrose infusion after cardiac surgery?
To explore this possibility further, one needs to refer to Table 9 in the supplementary appendix of the Papazian article (see: http://www.nejm.org/doi/suppl/10.1056/NEJMoa1005372/suppl_file/nejmoa1005372_appendix.pdf ) which tabluates the total sedative doses used in the Cis-at and placebo groups DURING THE FIRST SEVEN (7) DAYS OF THE STUDY. Now, why 7 days was chosen, when the KM curves separate at 14 days (as my former colleagues O'Brien and Prescott pointed out here: http://f1000.com/5240957 ), when the study reported data on other outcomes at 28 and 90 days, remains a mystery to me. I have e-mailed the corresponding author to see if he can/will provide data on sedative doses further out. I will post any updates as further data become available. Suffice it to say, that I'm not going to be satisfied unless sedative doses further out are equivalent.
Scrutiny of Table 9 in the SA leads to some other interesting discoveries, such as the massive doses of ketamine used in this study - a practice that does not exist in the United States, as well as strong trends toward increased midazolam use in the placebo group. And if you believe Wes Ely's and others' data on benzodiazepine use, and its association with delirium and mortality, one of your eyebrows might involuntarily rise. Especially when you consider that the TOTAL sedative dose administered between groups is an elusive sum, because equivalent doses of all the various sedatives are unknown and the total sedative dose calculation is insoluble.
