CORRESPONDENCE: LETTER TO THE EDITOR
A Meta-Analysis That Misses the Mark
Vladimír D avík, MD, FRCPC, FSCAI,
P. Gabriel Steg, MD, FESC, FACC, FCCP,
Bruce Barton, PhD,
Gervasio Lamas, MD, FACC, FAHA and
Judith S. Hochman, MD, FACC, FAHA*
* Department of Medicine, New York University School of Medicine, 530 First Avenue, Skirball 9R, New York, New York 10016 (Email: Judith.hochman{at}mednyu.edu).
In the February 7, 2008, issue of the Journal, Abbate et al. (1) present a meta-analysis with a stated goal of including randomized controlled trials of late percutaneous coronary intervention (PCI) of the infarct-related artery (IRA) in stable patients >12 h after onset of myocardial infarction (MI) (1). A fundamental principle of meta-analysis is inclusion of all studies that meet stated eligibility criteria with common end point definitions. The meta-analysis should address a relevant clinical question. Whether totally occluded IRAs should be opened in stable patients late after MI onset (the late open artery hypothesis) is an important question, and the authors introduce this concept early in the report. However, of the 10 studies included in the Abbate et al. (1) analysis, only 6 set out specifically to test the late opening of occluded IRA hypothesis, while 4 studies (TOPS [Treatment of Post-Thrombolytic Stenosis], BRAVE 2 [Beyond 12 Hours Reperfusion Alternative Evaluation], SWISSI II [Swiss Interventional Study on Silent Ischemia Type II], and ALKK [Arbeitsgemeinschaft Leitende Kardiologische Krankenhausärzte]) were examining whether or not to perform PCI in patients beyond the acute phase of MI when the IRA was often patent after fibrinolytic therapy or patients were randomized in order to evaluate a global invasive versus selective, ischemia-driven, invasive care strategy (the BRAVE 2 trial). For example, the BRAVE 2 trial is not applicable to address the late open artery hypothesis, since one-half of those enrolled in the BRAVE 2 trial did not have initial angiography, one-half of those with angiograms had open arteries, and PCI, coronary artery bypass grafting, or no procedure was performed in the invasive group. The SWISSI II trial selectively enrolled patients with silent ischemia and 1- to 2-vessel disease, with no information on the status of the IRA provided, up to 3 months after ST-segment elevation myocardial infarction (STEMI) or non–ST-segment elevation myocardial infarction (NSTEMI) and was included despite the entry criterion of 60 days post-MI noted in the meta-analysis abstract.
By the authors' report, 16% of the patients in the meta-analysis had open IRAs at initial angiography. While the OAT (Occluded Artery Trial) study provided 60% of the total population, and all IRAs in the OAT study were occluded, 40% of the non-OAT study patients added to form this meta-analysis represent a different population, not addressing the open artery hypothesis. If the authors had wanted to address a different topic—late revascularization in all patients (with closed or open IRAs) after STEMI and NSTEMI—they could have included thousands of additional patients in post-MI revascularization studies worldwide. This exclusion of numerous other eligible studies with thousands of patients enrolled in trials of PCI versus medical therapy only, or an invasive strategy versus conservative strategy for post-STEMI (after fibrinolytic therapy, with open or closed IRAs after MI), or NSTEMI that meets their criteria is not consistent with meta-analytic principles. In addition to the numerous sources of heterogeneity cited, the studies spanned too great a time, introducing additional heterogeneity in regard to advances in concomitant medical therapies that have been shown to prolong life. Our analysis of the studies selected by Abbate et al. (1) reveals such a degree of heterogeneity (p < 0.001) as to cast doubt on the scientific validity of the meta-analysis above and beyond the problems cited in the previous text with study selection. Recognizing the different pathophysiology and evidence bases for assessment of interventional management of the wide variety of post-MI patients included in the Abbate et al. (1) meta-analysis, the American College of Cardiology/American Heart Association guidelines have separate recommendations for those with open versus closed arteries, and based on ischemia, coronary anatomy, stress testing, and left ventricular (LV) function (2,3). Indeed, the clinical heterogeneity of all patients post-MI is simply not suitable to a one-size-fits-all approach.
The Abbate et al. (1) meta-analysis of the LV ejection fraction and volume end points also has substantial flaws. Relevant studies that showed no benefit or harm from PCI, such as the second randomization cohort of the TAMI-6 (Thrombolysis and Angioplasty in Myocardial Infarction-6) trial (4) and the TOAT (The Open Artery Trial) study (5), were excluded. The TAMI-6 trial was apparently excluded because it allowed randomization <12 h after symptom onset (which the PCI portion of the protocol did not—mean symptom to randomization time was 25 h). The TOAT study had paired data between 6 weeks and 1 year and showed harm from PCI; this study was apparently excluded because the first echocardiogram was obtained at 6 weeks post-MI, even though this timing of the first echocardiogram was not a pre-specified exclusion criterion. Most importantly, several of the included studies did not report paired change data (i.e., change data for patients with both a baseline and follow-up value) for LV ejection fraction or end-systolic and -diastolic volume indexes, but rather reported the means of all baseline values and all follow-up values, with different numbers of observations in each. Some studies had between-group imbalances in missing data. In the Horie et al. (6) study, for example, while all patients underwent follow-up LV function assessment, only 17 of 39 (44%) no-PTCA and 32 of 44 (73%) PTCA patients had this assessment at baseline. Similarly, in the SWISSI II trial, only 69 of 105 (72%) of PCI and 38 of 105 (36%) of drug therapy patients underwent follow-up LV function assessment. Yet Abbate et al. (1) appear to have constructed the difference in mean change between the 2 groups by subtracting the baseline and follow-up values of each group and then calculating the difference between these. This procedure is highly fraught with the risk of misleading results due to selection bias. For example, a study could have all patients with a baseline ejection fraction, but only the healthier ones return to obtain a follow-up value. Even if there is no change from baseline to follow-up in individual patients, the means will appear to show an improvement because sicker patients were included in the baseline mean (reducing that mean) but were excluded from the follow-up mean (so that only the values of healthier patients were included in that mean). The use of unpaired values or subtracting means to obtain a difference in "change" renders the analysis invalid. No imputation technique can correct for 64% (and imbalanced) missing data. Finally, Table 4 of their paper, which the text refers to as supporting the validity of the analysis, is not in the publication. Perhaps that demonstrated that some patient level paired data were obtained instead of sole reliance on published aggregate data.
Other errors that warrant correction include incorrect data reported for the TOMIIS (Total Occlusion Post-Myocardial Infarction Intervention Study) trial and the TOPS trial in Tables 2 and 3 of their paper, incorrect 95% confidence intervals for the TOMIIS trial in Figure 2 of their paper, and an incorrect number of total deaths (there are 6 not 3) in the interventional arm of the SWISSI II trial used in the risks of outcomes analysis illustrated in Figure 1 of their paper.
The authors raise a methodological issue in their discussion of the OAT study and its angiographic ancillary study the TOSCA-2 (Total Occlusion Study of Canada) trial (7,8) that also merits clarification. Abbate et al. (1) state that the OAT study results were marred by "construction" of the survival curves. All survival curves in the OAT study were based on the commonly accepted Kaplan-Meier product-limit estimates of survival probabilities (9). The OAT study used the Kaplan-Meier procedure because of the existence of different lengths of follow-up among the patients. The Kaplan-Meier procedure must be utilized to analyze survival data; the use of simple proportions of events (ignoring different lengths of follow-up and times to events) can lead to inaccurate and potentially misleading results. While the authors are correct that the relatively small number of patients (533 at 4 years [7]) available for long-term analysis in the OAT study could underestimate a potential late benefit from PCI, it could just as easily underestimate late harm. The addition of substantially smaller studies to this meta-analysis that set out to answer a different question and that deals with a different patient population cannot possibly correct this potential deficiency. Only long-term follow-up of the full OAT study cohort or cohorts of other studies specifically testing the open artery hypothesis can do this, and the OAT study is, in fact, currently in a long-term follow-up phase.
In this regard, however, Abbate et al. (1) violate another meta-analytic principle by using very different lengths of follow-up in the analysis. The technique utilized by the authors for calculating a simple proportion of mortality based on the number of patients dead divided by the number of patients in the study (or treatment arm) can create a serious bias in reporting a long-term study. When deaths occur at any point over a several-year follow-up period and there are censored data throughout the period, the simple proportion of mortality will underestimate the hazard rate in a long-term clinical trial. Depending on the joint distribution of deaths and censored observations, a substantial underestimate can be created. Using estimates from a long-term trial creates a downward bias in the event rates and potentially affects the results and interpretation of a meta-analysis. Furthermore, potential imbalances in the pattern of events and censoring will change the relative rates between the 2 groups.
A meta-analysis of all open artery hypothesis trials is certainly reasonable, although the OAT and TOSCA-2 studies will dominate such analyses of clinical outcomes and function respectively because of their large numbers. A recently published meta-analysis of the 6 trials that included only studies of patients with total occlusions showed no effect of the study intervention on death, MI, heart failure, or their composite (10). The Abbate et al. (1) meta-analysis, with its selective inclusion and exclusion of studies, methodological limitations of aggregate, nonpatient level data, and the marked and statistically significant heterogeneity of populations, duration of follow-up and of treatment effect, contributes little to inform medical practice.
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Footnotes
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Editor's Note
Our usual policy at JACC is to limit Letters to the Editor and their replies to a total of 400 words. However, we have recently encountered 2 letters which considerably exceeded this limit and provoked replies of similar length. Both interchanges dealt with issues of substantial current interest and importance: the role of intervention following infarction, particularly for patients with total coronary occlusion, and the role of percutaneous intervention versus surgery for unprotected left main coronary stenosis. Therefore, we have decided to make an exception and to publish the letters and replies as submitted. We believe that a thorough airing of these topics more than justifies this exception.
Please note: Dr. Davík was the study chair for TOMIIS and TOSCA-2; Dr. Steg was study chair for DECOPI; and Dr. Hochman was study chair and Dr. Lamas co-chair for The Occluded Artery Trial (OAT). OAT received support from the following; NHLBI, Bristol-Myers Squibb Medical Imaging, and Eli Lilly. Product donations to enrolling sites from: Boston Scientific, Johnson & Johnson, Guidant, Medtronic, Merck, Millenium Pharmaceuticals, Schering-Plough, and Eli Lilly.
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References
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1. Abbate A, Biondi-Zoccai G, Appleton D, et al. Survival and cardiac remodeling benefits in patients undergoing late percutaneous coronary intervention of the infarct-related artery: evidence from a meta-analysis of randomized controlled trials J Am Coll Cardiol 2008;51:956-964.[Abstract/Free Full Text]2. Antman EM, Anbe DT, Armstrong PW, et al. ACC/AHA guidelines for the management of patients with ST-elevation myocardial infarction: a report of the American College of Cardiology/American Heart Association Task Force on Practice Guidelines (Committee to Revise the 1999 Guidelines for the Management of Patients With Acute Myocardial Infarction) J Am Coll Cardiol 2004;44:E1-E211.[CrossRef][Medline] 3. Antman EM, Hand M, Armstrong PW, et al. 2007 focused update of the ACC/AHA 2004 guidelines for the management of patients with ST-elevation myocardial infarction: a report of the American College of Cardiology/American Heart Association Task Force on Practice Guidelines (Writing Group to Review New Evidence and Update the ACC/AHA 2004 Guidelines for the Management of Patients With ST-Elevation Myocardial Infarction) J Am Coll Cardiol 2008;51:210-247.[Free Full Text] 4. Topol EJ, Califf RM, Vandormael M, et al. A randomized trial of late reperfusion therapy for acute myocardial infarction. Thrombolysis and Angioplasty in Myocardial Infarction-6 Study Group. Circulation 1992;85:2090-2099.[Abstract/Free Full Text] 5. Yousef ZR, Redwood SR, Bucknall CA, Sulke AN, Marber MS. Late intervention after anterior myocardial infarction: effects on left ventricular size, function, quality of life, and exercise tolerance: results of The Open Artery Trial (TOAT study) J Am Coll Cardiol 2002;40:869-876.[Abstract/Free Full Text] 6. Horie H, Takahashi M, Minai K, et al. Long-term beneficial effect of late reperfusion for acute anterior myocardial infarction with percutaneous transluminal coronary angioplasty Circulation 1998;98:2377-2382.[Abstract/Free Full Text] 7. Hochman JS, Lamas GA, Buller CE, et al. Coronary intervention for persistent occlusion after myocardial infarction N Engl J Med 2006;355:2395-2407.[Abstract/Free Full Text] 8. Dzavik V, Buller CE, Lamas GA, et al. Randomized trial of percutaneous coronary intervention for subacute infarct-related coronary artery occlusion to achieve long-term patency and improve ventricular function: the Total Occlusion Study of Canada (TOSCA)-2 trial Circulation 2006;114:2449-2457.[Abstract/Free Full Text] 9. Kaplan E, Meier P. Nonparametric estimation from incomplete observations J Am Stat Assoc 1958;53:457-481.[CrossRef][Web of Science] 10. Ioannidis JP, Katritsis DG. Percutaneous coronary intervention for late reperfusion after myocardial infarction in stable patients Am Heart J 2007;154:1065-1071.[CrossRef][Web of Science][Medline]
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