Pulmonary JC 4.30.12

Azithromycin to Prevent Exacerbations of COPD 
Click here to listen to a recording of the presentation.

Dr. Kim Suh presented a randomized trial of azithromycin (250mg daily) for prevention of exacerbations in COPD.  The authors hypothesized that azithromycin should reduce the rate of exacerbations, while potentially increasing colonization with macrolide-resistant organisms and causing an increased incidence of hearing loss.

Major exclusion criteria were asthma, resting tachycardia, a prolonged QTc at baseline or use of drugs known to prolong the QT interval (except amiodarone), and pre-existing hearing impairment.

This well-designed study demonstrated a reduction in median time to first exacerbation and the overall incidence of exacerbations, while documenting a 5% absolute increase in the rate of hearing decrements and a 40% absolute increase in the rate of nasopharyngeal colonization with respiratory pathogens resistant to macrolide antibiotics.

In the discussion, Dr. Boesch pointed out that one would really like to see the results broken down according to a standardized rating of disease severity, such as the GOLD system of staging, in order to see where the most benefit might be expected.  Dr. Subramanian and Dr. Schub agreed that, while this study should not revolutionize practice, it does represent a potential rationale for deploying azithromycin in patients with particularly intractable disease.

From the point of view of EBM, it is worth pointing out that this article includes a misleading presentation of the number needed to treat (NNT). (Click here for a recording of some remarks on this at Journal Club).

Albert et al. report an impressive NNT of 2.86 “to prevent one acute exacerbation of COPD.”  Conventionally, the NNT is calculated as the reciprocal of the absolute difference in the risk of a dichotomized outcome (such as mortality) between the treatment and control groups of a clinical trial.  However, what Albert et al. present is the reciprocal of the absolute difference in the rate of a recurring event, i.e. COPD exacerbations.  This gives the “event-based” NNT, rather than the conventional NNT.

As Aaron and Ferguson have recently pointed out, the “event based” NNT (which was first described by Halpin in 2005) is a theoretically frought statistic with unclear clinical application.  Because it incorporates multiple instances of the same event happening to the same person, it is generally smaller than the conventionally calculated NNT and tends to obscure heterogeneities in risk.   

To illustrate the first point, calculate a conventional NNT for Albert’s study (using the data in Figure 2): we get a value of 9.1 to keep one patient exacerbation free for the entire study period, which is considerably less impressive than the one they present.  The second point is best illustrated by a simple thought-experiment: in a study with ten patients in each of the treatment and control groups, where 20 exacerbations occurred in one individual in the control group and 2 occurred in one individual in the treatment group, the “event-based” NNT would be 0.56.  This might lead one to believe that only half a patient needs to be treated to prevent one exacerbation, and that the benefit would apply to the entire group; however, the former is impossible and the latter clearly wrong.

This is the third time this year that we have discovered a major error either in calculation or interpretation of NNTs in a journal club article - the first being in ICU journal club, the second in Cardiology journal club.  Such a high prevalence in such a small sample should remind us that it's worth checking other people's work before making major treatment decisions based on their calculations.  For those who are interested, here is an excellent article from CMAJ on the limitations of the NNT.

A Tyrosine Kinase Inhibitor in Idiopathic Pulmonary Fibrosis
(Sorry, no recording).

Dr. Boesch presented a randomized trial examining the safety and efficacy of a tyrosine kinase inhibitor in the treatment of idiopathic pulmonary fibrosis (IPF).

Patients were allocated to one of four doses of the study drug, BIBF 1120, or placebo, and treated for 12 months.  The primary endpoint was the annual rate of decline in FVC.  There was no significant difference between any of the treatment groups and the placebo group.  A difference of 0.13 L/yr is reported between the high-dose treatment group and the placebo group, but the confidence intervals for the actual values overlap one another and, considering that the trial was appropriately powered to detect a difference of 0.1L/yr or greater, this strongly suggests that BIBF 1120 (as used in the trial) does not work.

Whatever its other notable features, this article serves as a cautionary reminder of just how intimate the relationship between academic medicine and the drug industry actually is.  (Click here for a recording of some comments on this at Journal Club).  This study was funded by Boehringer Ingelheim, and all the data analysis was carried out in their facilities by their house statisticians.  The manuscript was written by "medical writers" from Flesichman-Hillard, an international marketing company whose website promises to "identify and effectively target key members of the medical community, strategically position your products in the face of increased regulation, [and] create and build trust with increasingly knowledgeable consumers [emphasis added]." 

The authors try to attenuate the appearance of industry influence by noting that "the steering committee made the decision to submit the manuscript for publication," but, if one looks at Appendix G and then reviews the  disclosure forms submitted by the authors, one finds that all the members of the steering committee were paid for their services by Boehringer Ingelheim.  In fact, all of the authors were either paid by Boehringer Ingelheim, or, as in the case Brun, Gupta, Juhel and Kluglich, were full-time employees. 

So, what we have here is a negative trial paid for by a drug company for which all the math was done by drug company statisticians, and which was written by a marketing firm.  Given this, it may be more appropriate to regard this article as a paid advertisement  for BIBF 1120 rather than a piece of clinical research.

t-PA and/or DNA-ase in Pleural Infection
(Sorry, no recording).

Dr. Patel presented a trial of tissue plasminogen activator and DNA-ase in pleural infection which, among other things, stands in refreshing contrast to the paper by Richeldi et al..  The investigators note the receipt of an unrestricted educational grant from the pharmaceutical company Roche UK, but clearly document that the company had no involvement in the actual study.  Moreover, their disclosure forms are completely clean.

Rahman et al. randomized patients with pleural infection to treatment with either intrapleural t-PA, DNA-ase, both, or placebo.  They used chest X-rays taken at day 1 and day 7 (or the last available X-ray) to determine the primary endpoint, which was the change in area of pleural opacity. 

Given these limitations, they did demonstrate a 7.9% increase in the change in pleural opacity (with a rather wide confidence interval of 2.4% - 13.4%) associated with the combination of tPA and DNA-ase.  Neither agent alone was effective in reducing pleural opacity area relative to placebo.

This trial was well-conducted and very well-reported, but does have some limitations.  First, it seems odd to use this a surrogate endpoint instead of a clinically relevant one (e.g. length of stay) as the primary outcome, and their method of determination was also odd given that they quote an accuracy of only 71% for chest X-ray in determination of pleural effusion volume when compared to CT.