To the Editor: We’ve read the editorial comment1 made by Dr. Turi on our study “Percutaneous Mitral Valvotomy: Six Year Follow-up”.2 Although we thank Dr. Turi for his insights, we disagree profoundly with the core of his criticism concerning lack of follow-up for 46 patients. We clearly stated that this was an analysis of patients with more than 6 months of follow-up. The rest of the population that he claims we didn’t follow is explained because we didn’t have the data regarding restenosis at 6 months, simply by the fact that they haven’t yet reached that time point. Nevertheless, we do have data concerning the clinical status of all of those patients, which we intend to communicate in future reports. Another aspect that we considered for the analysis was the availability of the echocardiographic score before and after the procedure. Some patients, especially the earlier cases in our series, didn’t meet this criterion. Unfortunately, Dr. Turi misinterpreted the information, adding to his analysis and theorizing over patients in whom we can’t make valid conclusions. A more careful reading by Dr. Turi would have surely answered his doubts on this crucial point, as all of the above was clearly stated. Dr. Turi is also wrong in criticizing our statistical method. The use of decimal points to express results is perfectly valid when working with medians since all variables were quantitative and not ordinal. A multivariate analysis was used to establish the relationship between variables, so the association between pulmonary hypertension and restenosis was obtained in the presence of all the other variables. It is true, however, that we didn’t calculate a type II error, but generally this is insignificant in a multivariate model like the one used in our study. Concerning the deaths in our series, none were attributed directly to the procedure in the immediate post-procedure period (in-hospital mortality). We only had 1 death of a patient who developed severe mitral regurgitation after PMV but who refused surgery and died months later due to heart failure. If this patient had accepted surgery, his outcome would have probably been different. The other deaths (3 patients) were also during late follow-up, expressing cardiovascular mortality — a pre-defined endpoint. In our paper, we focus the discussion only on patients who developed mitral regurgitation after the procedure because that could directly affect the outcome. Nevertheless, we did have 3 other complications related to the PMV: a non-disabling embolic stroke, a femoral artery pseudoaneurysm at the puncture site that required surgery and an acute limb ischemia successfully treated with heparin therapy. We do agree with Dr. Turi that the definition of success was not mentioned in the paper, but we used the same definition accepted in the literature.3,4 By differentiating optimal and suboptimal results, we only intended to see if those patients who developed mitral regurgitation after the procedure would still gain some clinical amelioration of their symptoms. In fact, only 3 of the 7 patients who developed mitral regurgitation deteriorated their ventricular function and NYHA class. Another omission in our paper was the definition of pulmonary hypertension; once again, we used the widely accepted value of >= 35 mmHg. We thank Dr. Turi for noting these pitfalls in our paper. With all the limitations that this study might have, we still think that 48% follow-up between 2–4 years and some of them (23%) reaching up to 6 years doesn’t invalidate the title “…Six Year Follow-up”; therefore, we don’t consider it to be “hyperbole”. We hope to complete the follow-up of our later patients to expand our sample and complement our report. As Dr. Turi states, the Wilkin’s score is flawed but it is nevertheless an essential tool to compare populations. We hope to complete the follow-up of our newer patients, to expand our sample and to complement our report to contribute in the understanding of the late clinical evolution of patients with percutaneous mitral valvotomy. Yours sincerely, Humberto Dighero, MD and Pablo Sepúlveda, MD The Pabellón de Hemodinamia y Cineangiografia, Departamento de Cardiologia, Hospital San Juan de Dios, Santiago, Chile References 1. Turi Z. Letting the air out of the follow-up balloon. J Invas Cardiol 2001;13:800–801. 2. Dighero H, Zepeda F, Sepúlveda P, et al. Percutaneous mitral balloon valvotomy: Six-year follow-up. J Invas Cardiol 2001;13:795–799. 3. Desideri A, Vanderperren O, Serra A, et al. Long term (9–33 months) echocardiographic follow-up alter successful percutaneous mitral commissurotomy. Am J Cardiol 1992;69:1602–1606. 4. Bonow, et al. ACC/AHA guidelines for the management of patients with valvular heart disease: A report of the American College of Cardiology/American Heart Association Task Force on Practice Guidelines (Committee on Management of Patients With Valvular Heart Disease). J Am Coll Cardiol 1998;32:1486–1588. Dr. Turi’s response: We appreciate Drs. Dighero and Sepúlveda’s defense of their methods and paper. Unfortunately, our criticisms stand. We complained that claiming “99% follow-up,” when data was presented on only 96 of their 160 patients, is bogus. They now inform us that they excluded 54 patients because they “didn’t have the data regarding restenosis at 6 months, simply by the fact that they haven’t reached that time-point yet.” This is confusing to an already confused reader, who unfortunately not only read the manuscript carefully the first time, but with the exhortation to “a more careful reading” reread it equally patiently. Since the patients were enrolled between 1987 and August 1999, and the paper was received in November 2000, the failure of any of the 54 patients (let alone many) to reach the 6-month endpoint is incomprehensible. In addition, the authors state that “some patients” (we are not told how many) did not meet the criterion of “availability of the echocardiographic score before and after the procedure”. The post-procedure echo score is irrelevant to this study. It is hard to conceive that any of the 54 patients did not have echocardiograms obtained before the procedure. It is elementary that the failure to obtain endpoint data does not entitle the authors to censor the patients from their study and claim near 100% follow-up. By this standard, every study would have 100% follow-up; one merely excludes patients on whom there is no follow-up. This of course introduces multiple sources of bias into data analysis. The fact that they hope to complete their study in the future merely highlights the importance of not dumping incomplete and inadequate data into the literature. No amount of rereading will clarify the actual success and complication rates in this paper, nor will the authors’ letter. The authors state that the definition for success they used but did not mention in their paper was the same as “accepted in the literature”. Referring to their citation of the ACC/AHA guidelines, this defines success as “…valve areas > 1.5 cm2 and a decrease in left atrial pressure to = 1.5 cm2 or development of severe mitral regurgitation. We continue to have no way to reconcile this muddle. As to mortality, our statement in our initial editorial stands, and the authors merely confirm our comments. With regard to their belated definition of pulmonary hypertension as “the widely accepted value of >= 35 mmHg,” the literature has a wide variety of definitions, both mean and systolic, both in the context of patients with and without various types of structural heart disease. Finally, the authors apparently misunderstood our critique of their statistical analysis and address issues we did not raise. As to the use of decimal points, this was a sidebar regarding their use of two to three decimal places to report age, functional class, follow-up interval and valve areas (e.g., valve area 1.972 cm2). Valve areas are barely accurate to the nearest one-tenth cm2, let alone the nearest hundredth or thousandth. Reporting 2 or 3 decimal places, whether in clinical practice or in published manuscripts, merely adds noise. We limited our criticism to the most flagrant flaws in this paper. We hope the authors will forgive us for our blunt dissection of their manuscript. With the growing volume of data being published, we think it remains our responsibility to point out how much of the literature fails basic tests of evidence based medicine. Without such criticism, flawed conclusions are potentially accepted by the reader and applied to clinical practice.