Diamox Results in Urine: General and Specific Lessons from the DIABOLO Acetazolamide Trial

The trial of acetazolamide to reduce duration of mechanical ventilation in COPD patients was published in JAMA this week.  I will use this trial to discuss some general principles about RCTs and make some comments specific to this trial.

My arguable but strong prior belief, before I even read the trial, is that Diamox (acetazolamide) is ineffectual in acute and chronic respiratory failure, or that it is harmful.  Its use is predicated on a "normalization fallacy" which guides practitioners to try attempt to achieve euboxia (normal numbers).  In chronic respiratory acidosis, the kidneys conserve bicarbonate to maintain normal pH.  There was a patient we saw at OSU in about 2008 who had severe COPD with a PaCO2 in the 70s and chronic renal failure with a bicarbonate under 20.  A well-intentioned but misguided resident checked an ABG and the patient's pH was on the order of 7.1.  We (the pulmonary service) were called to evaluate the patient for MICU transfer and intubation, and when we arrived we found him sitting at the bedside comfortably eating breakfast.  So it would appear that if the kidneys can't conserve enough bicarbonate to maintain normal pH, patients can get along with acidosis, but obviously evolution has created systems to maintain normal pH.  Why you would think that interfering with this highly conserved system to increase minute ventilation in a COPD patient you are trying to wean is beyond the reach of my imagination.  It just makes no sense.

This brings us to a major problem with a sizable proportion of RCTs that I read:  the background/introduction provides woefully insufficient justification for the hypothesis that the RCT seeks to test.  In the background of this paper, we are sent to references 4-14.  Here is a summary of each:

4.)  A review of metabolic alkalosis in a general population of critically ill patients
5.)  An RCT of acetazolamide for weaning COPD patients showing that it doesn't work
6.)  Incidence of alkalosis in hospitalized patients in 1980
7.)  A 1983 translational study to delineate the effect of acetazolamide on acid base parameters in 10 paitnets
8.)  A 1982 study of hemodynamic parameters after acetazolamide administration in 12 patients
9.)  A study of metabolic and acid base parameters in 14 patients with cystic fibrosis 

10.) A retrospective epidemiological descriptive study of serum bicarbonate in a large cohort of critically ill patients

11.)  A study of acetazolamide in anesthetized cats

12 - 14).  Commentary and pharmacodynamic studies of acetazolamide by the authors of the current study

Sepsis Bungles: The Lessons of Early Goal Directed Therapy

On March 18th, the NEJM published early online three original trials of therapies for the critically ill that will serve as fodder for several posts.  Here, I focus on the ProCESS trial of protocol guided therapy for early septic shock.  This trial is in essence a multicenter version of the landmark 2001 trial of Early Goal Directed Therapy (EGDT) for severe sepsis by Rivers et al.  That trial showed a stunning 16% absolute reduction in mortality in sepsis attributed to the use of a protocol based on physiological goals for hemodynamic management.  That absolute reduction in mortality is perhaps the largest for any therapy in critical care medicine.  If such a reduction were confirmed, it would make EGDT the single most important therapy in the field.  If such reduction cannot be confirmed, there are several reasons why the Rivers results may have been misleading:

• As I have blogged in the case of intensive insulin therapy, Single center studies inflate treatment effects when compared to multicenter studies for reasons that are unclear, but which may be related to bias especially in unblinded studies.  (The revelation that Rivers was an investor in one of the devices used in the trial raised additional concerns about bias.)
• Regression to the mean may lead to reduced effect sizes when trials are repeated, especially when the index trial has a very large effect size.  In a similar vein, since large absolute mortality reductions are statistically unlikely in critical care medicine, Bayesian inference means that trials reporting large reductions are likely to represent type I statistical errors.

There were other concerns about the Rivers study and how it was later incorporated into practice, but I won't belabor them here.  The ProCESS trial randomized about 1350 patients among three groups, one simulating the original Rivers protocol, one to a modified Rivers protocol, and one representing "standard care" that is, care directed by the treating physician without a protocol.  The study had 80% power to demonstrate a mortality reduction of 6-7%.  Before you read further, please wager, will the trial show any statistically significant differences in outcome that favor EGDT or protocolized care?

Dead in the Water: Colloids versus Crystalloids for Fluid Resuscitation in the ICU

It is a valid question:  at what point has a concept been tested ad infinitum such that further testing is not worthwhile?  There are at least three reasons why additional study of a concept may not be justified:

1. Because the prior probability of success is so low (based on extant trials) that a subsequent trial is unlikely to influence the posterior probability that any success represents the truth.  (This is a Bayesian or meta-analytic worldview.)
2. Because the low probability of success does not justify the expense of additional trials
3. Because the low probability of success violates bioethical precepts mandating that trials must have added value for patients and society

And so we have, in the November 6th edition of JAMA, the CRISTAL trial of colloids versus crystalloids for resuscitation in the ICU.  As is customary, I will leave it to interested readers to peruse the manuscript for details.  My task here is to provide some background and nuance.

Prophylactic Cranial Irradiation: a matter of blinding, ascertainment, side effects, and preferences

Slotman et al (August 16 issue of NEJM: http://content.nejm.org/cgi/content/short/357/7/664) report a multicenter RCT of prophylactic cranial irradiation for extensive small cell carcinoma of the lung and conclude that it not only reduces symptomatic brain metastases, but also prolongs progression-free and overall survival. This is a well designed and conducted non-industry-sponsored RCT, but several aspects of the trial warrant scrutiny and temper my enthusiasm for this therapy. Among them:

The trial is not blinded (masked is a more sensitive term) from a patient perspective and no effort was made to create a sham irradiation procedure. While unintentional unmasking due to side effects may have limited the effectiveness of a sham procedure, it may not have rendered it entirely ineffective. This issue is of importance because meeting the primary endpoint was contingent on patient symptoms, and a placebo effect may have impacted participants’ reporting of symptoms. Some investigators have gone to great lengths to tease out placebo effects using sham procedures, and the results have been surprising (e.g., knee arthroscopy; see: https://content.nejm.org/cgi/content/abstract/347/2/81?ck=nck).


We are not told if investigators, the patient’s other physicians, radiologists, and statisticians were masked to the treatment assignment. Lack of masking may have led to other differences in patient management, or to differences in the threshold for ordering CT/MRI scans. We are not told about the number of CT/MRI scans in each group. In a nutshell: possible ascertainment bias (see http://www.consort-statement.org/?o=1123).

There are several apparently strong trends in QOL assessments, but we are not told what direction they are in. Significant differences in these scores were unlikely to be found as the deck was stacked when the trial was designed: p<0.01 was required for significance of QOL assessments. While this is justified because of multiple comparisons, it seems unfair to make the significance level for side effects more conservative than that for the primary outcome of interest (think Vioxx here). The significance level required for secondary endpoints (progression-free and overall survival) was not lowered to account for multiple comparisons. Moreover, more than half of QOL assessments were missing by 9 months, so this study is underpowered to detect differences in QOL. It is therefore all the more important to know the direction of the trends that are reported.

The authors appear to “gloss over” the significant side effects associated with this therapy. It made some subjects ill.

If we are willing to accept that overall survival is improved by this therapy (I’m personally circumspect about this for the above reasons) the bottom line for patients will be whether they would prefer on average 5 additional weeks of life with nausea, vomiting weight loss, fatigue, anorexia, and leg weakness to 5 fewer weeks of life without these symptoms. I think I know what choice many will make, and our projection bias may lead us to make inaccurate predictions of their choices (see Lowenstein, Medical Decision Making, Jan/Feb 2005: http://mdm.sagepub.com/cgi/content/citation/25/1/96).

The authors state in the concluding paragraph:

“Prophylactic cranial irradiation should be part of standard care for all patients with small-cell lung cancer who have a response to initial chemotherapy, and it should be part of the standard treatment in future studies involving these patients.”

I think the decision to use this therapy is one that only patients are justified making. At least now we have reasonably good data to help them inform their choice.