- Email: [email protected]
Choice of clinical outcomes in randomized trials of heart failure therapies: Disease-specific or overall outcomes?
Clinical Investigations
Congestive Heart Failure
Choice of clinical outcomes in randomized trials of heart failure therapies: Disease-specific or overall outcomes? Salim Yusuf, MBBS, DPhil, FRCPC, and Abdissa Negassa, PhD Hamilton, Ontario, Canada
Background There are different views regarding the appropriateness of using cause-specific events or all events as the primary outcome of clinical trials.
Methods This is a methodologic essay in which we discuss the pros and cons of the 2 approaches and provide illustrative examples.
Results Our preference is the use of cause-specific outcomes (as long as they can be classified with reasonable reproducibility and without bias) because they are more likely to be sensitive to change, less likely to lead to spurious conclusions by random variations in categories of outcomes that are unlikely to be affected by treatment, and relatively free from confounding. Overall benefit-risk ratios can be derived by examining the impact of treatment on various categories of outcomes and then developing a general judgment. Such an approach will also allow judgments to be made regarding generalizability of results across various groups of patients who are at differing risks for an event. Conclusions In general, cause-specific outcomes sensitive to the effects of a treatment are to be preferred as the principal outcome in trials of heart failure, as long as they are biologically sensible and can be classified without bias. Other outcomes, not expected to be affected, should also be reported separately. (Am Heart J 2002;143:22-8.)
It is now generally agreed that clinical events are more appropriate than surrogate measures as outcomes in clinical trials. Although improving how a patient feels (eg, symptomatic status) is a worthwhile goal of therapy in itself, preventing significant morbidity or mortality is likely to be of greater impact. It is therefore important to try to reliably ascertain the impact of a treatment on mortality or morbidity in patients with serious diseases. In these assessments, there is some controversy as to which clinically relevant outcomes should be the primary focus of clinical trials. Should the treatment be evaluated in trials that are designed to demonstrate an impact on overall mortality or overall morbidity? Alternatively, is it preferable to design trials to demonstrate an impact on the specific clinical outcomes that may be responsive to the treatment? In this article, we try to explore the advantages and disadvantages of the 2 approaches and consider both statistical and nonstatistiFrom the Division of Cardiology, McMaster University, and the Preventive Cardiology and Therapeutics Program, Hamilton Health Sciences Corporation, Hamilton, Ontario, Canada. Submitted November 20, 2000; accepted April 30, 2001. Reprints not available from the authors. E-mail: [email protected] Copyright © 2002 by Mosby, Inc. 0002-8703/2002/$35.00 + 0 4/1/119770 doi:10.1067/mhj.2002.119770
cal issues. We mainly use examples of heart failure trials but occasionally use other examples from cardiovascular (CV) prevention or therapy because the general principles are broadly applicable. In determining the choice of outcome(s) to be evaluated in a clinical trial, the primary outcome should ideally meet all or most of the following criteria: 1. The outcome should be of clinical importance and directly relevant to how patients feel, any disability they have, or how long they live. 2. The outcome should be related to the postulated mechanism of action of the drug and also sensitive to change (ie, increasing the “signal”). 3. It should be measured with reasonable reproducibility and reliably diagnosed or classified. 4. There should be as little “noise” in the outcome measurement by reducing components unrelated to the disease or unlikely to change. 5. There should be no bias in ascertainment or classification of individual events. 6. There should be no confounding (or masking) of events.
In drawing inferences about an intervention’s effect, we also need to get an overall assessment of the risk/benefit ratio to balance the presence of adverse outcomes. This can be achieved in 1 of 2 ways: first one could assess overall mortality and hospitalizations irre-
American Heart Journal Volume 143, Number 1
Yusuf and Negassa 23
Table I. Causes of death in 3 large heart failure trials
Total No. of deaths No. of non-CV deaths No. of CV deaths No. of noncardiac but vascular deaths No. of cardiac deaths No. of “arrhythmic deaths”* No. of deaths from pump failure No. of deaths from MI
SOLVD treatment trial EF ≤0.35
SOLVD prevention trial EF ≤0.35
DIG trial EF ≤0.40
DIG trial EF ≥0.40
961 102 (11%) 859 (89%) 24 (2.5%) 817 (85.0%) 365 (38.0%) 327 (34.0%) 107 (11.1%)
638 84 (13%) 554 (86.8%) 23 (3.6%) 509 (79.8%) 252 (39.5%) 142 (22.3%) 98 (15.4%)
2375 355 (15%) 2020 (85.1) 95 (4%) 1740 (73%) 645 (27.2%) 844 (35.5%) 251 (10.6%)
231 55 (23.8%) 176 (76.2%) 16 (6.9%) 139 (60.1%) 42 (18.2%) 64 (27.7%) 33 (14.3%)
*Arrhythmic deaths are based on the classification used in each trial. We recognize the difficulty of accurately classifying these types of events. The data are being provided as an example to illustrate the possible relative proportions of different “types” of death. Unknown deaths are included in CV, but further subdivision of this category is not done.
Table II. A theoretical example indicating that the overall impact on mortality is modest even when an agent reduces a specific cause of death (eg, sudden death) substantially
Sudden death CHF deaths MI deaths Cardiac deaths CV deaths Total mortality
Control
Active
67 135 130 332 382 432
135 135 130 400 450 500
Absolute difference
RRR (%)
Z value
50 0 0 17 15 14
5.05 0.00 0.00 3.16 3.09 3.05
–68 0 0 –68 –68 –68
P value .00001 1.000 1.000 .002 .002 .0023
The number of events in each group is provided and the number of patients randomized in each group is 1000.
spective of cause. Alternatively, one could examine the various components of mortality or morbidity. For example, in a trial of an antithrombotic agent, one could examine separately the component of mortality that is expected to be changed (eg, fatal myocardial infarction [MI]) and its related morbidity (eg, nonfatal MI) to assess efficacy. One could then separately assess the impact on the kinds of fatal/nonfatal outcomes that one might expect to be adversely affected (eg, intracranial bleeding, fatal bleeding, bleeding requiring hospitalization) and also those that we expect to be unaffected (eg, cancer). One can derive an overall effect by examining the impact on each of the 3 types of events separately and assess the strength and plausibility of any differences observed. One then combines the information from each component and reaches a summary judgment. Later in the article we will discuss the pros and cons of each approach with specific examples from recent trials. We recognize that when large trials are conducted despite a large body of information not everything about the mechanism of action of a therapy may be known. Recognizing this limitation, we argue that not only should events that are expected to be affected be separately evaluated but additionally the remaining outcomes should be examined by cause.
Mortality In patients with class II or III heart failure and a low ejection fraction (EF), about 90% of the deaths are classified as being due to CV causes and 10% are documented as being due to non-CV (cancers, etc)1 (Table I). Of the CV deaths, approximately 90% (or about 80% of the total) are from a cardiac cause with about 5% resulting from a noncardiac but vascular cause (strokes, pulmonary embolism). Of the cardiac causes, about 15% are due to an ischemic event, one third may be attributed to an arrhythmic event, one third attributed to progressive pump failure, and the remaining deaths are due to miscellaneous causes. If we had an intervention that was expected to reduce sudden death (eg, an implantable cardiac defibrillator), one would expect to see the entire “benefit” in that category (eg, arrhythmic deaths) with little differences in other categories. A theoretic scenario is outlined in Table II. There appears to be about a 50% relative risk reduction (RRR) in sudden death, with little impact on other causes of death. This translates into a 17% difference in cardiac deaths (P = .002), a 15% difference in CV deaths (P = .002), and only a 14% difference (P = .023) in total deaths. It is obvious that in such a trial, if sudden death could be classified with reasonable accuracy, then this would be
American Heart Journal January 2002
24 Yusuf and Negassa
Table III. SOLVD hospitalizations by primary diagnosis
No. of subjects CHF MI/unstable angina Stroke Other cardiac Noncardiac Total No. of patients hospitalized
Placebo
Enalapril
RRR (%)
P value
3401 729 (21.42%) 679 (20.0%) 110 (3.2%) 859 (25.3%) 1004 (29.5%) 2137 (62.8%)
3396 510 (15.0%) 580 (17.1%) 95 (2.8%) 863 (25.4%) 1007 (29.7%) 2036 (60.0%)
30 14.5 13.5 –0.6 –0.4 5.0
<.001 .002 .292 .883 .905 .015
the most sensitive outcome to test the effect of an implantable cardioverter defibrillator. Furthermore, this trial will also confirm that there is little impact on other causes of death. If the distinction between sudden death and other causes of the deaths is fairly clear and reliable, then it would be reasonable to use sudden death as the primary outcome. However, there may not be a high degree of concordance between 2 physicians trying to distinguish between sudden or nonsudden death. If the discordance is small (about 10% or 20%), the apparent effect size is proportionately reduced by one tenth or one fifth and there would be some loss in statistical power as a result of inclusion of nonsudden deaths in the primary outcome, which could be confused with sudden death. This in turn would tend to decrease the apparent differences in event rates (eg, deaths classified as sudden, which are a priori “sensitive” to treatment) between the 2 groups. In general, random errors in classifying an event tend to diminish the apparent treatment benefits. If the discordance is large, then it may make greater sense to analyze the data using total mortality. It is generally accepted that one could classify deaths into CV and non-CV and perhaps even CV deaths into further categories of cardiac and other vascular with reasonable validity and reliability.2 For these reasons, it would be preferable to use CV (or perhaps cardiac) as the primary categorization of mortality in heart failure trials. This approach is reasonably robust, and cardiac (or CV) death is a major outcome and is more sensitive than use of total mortality as the main outcome of interest. The added sensitivity conferred by using the causespecific event as opposed to total mortality will vary, depending on the proportion of all deaths that would be expected to be CV. For example, in patients with a low EF and class IV congestive heart failure (CHF), >95% of deaths are CV and the difference between using CV or total deaths is small. On the other hand, in those with asymptomatic left ventricular dysfunction, about 85% of the deaths are CV and there could be an important increment in sensitivity by using CV deaths as opposed to total deaths as the outcome of interest in a trial. If one were to examine primary prevention of cardiovascular events, more than one half the events
would be noncardiovascular and hence not be amenable to treatment. In such a case, use of cause-specific mortality substantially improves the sensitivity of the study. Similarly, in patients such as the elderly with other comorbidities (and hence a higher likelihood of deaths from noncardiac causes), it may be preferable to use cardiac deaths as the primary outcome of interest rather than total mortality.
Morbidity Statistical power The most common outcome reflecting morbidity is usually hospitalization. In hospitalized patients, specific diagnoses can be confidently made with the help of careful histories, physical examinations, investigations, response to treatments, etc. (This contrasts with mortality, where such data may be sparse, especially when a death is out of hospital and unwitnessed). In general, there is greater confidence in categories of hospitalizations (eg, for worsening heart failure) than for a similar category of death. Second, in patients with a low EF and CHF only about one third of all those hospitalized are hospitalized for worsening CHF, and this proportion drops to about 15% in patients with CHF with an EF >40% and is about 25% in patients with a low EF and no overt CHF. Therefore even large (eg, 30%) reductions in CHF hospitalizations may not be detected if one only examined all hospitalizations (Tables III and IV). Statistical power and sensitivity are greatly enhanced by examining the specific categories of hospitalizations that one expects treatment to affect rather than including insensitive outcomes (eg, a cancer or stroke hospitalization that is not expected to be affected). A second problem with chiefly focusing on overall hospitalizations is a loss of power when one only counts the first hospitalization per patient (eg, as in a time to event analysis). This is illustrated in Figure 1. Let us assume that a patient is hospitalized for an appendectomy 6 months after randomization and 3 months later has worsening CHF requiring hospitalization and another 3 months later has a stroke. In this case, if one were to only count the first hospitalization for any reason, then the hospitalization for acute appendicitis “masks” the
American Heart Journal Volume 143, Number 1
Yusuf and Negassa 25
Table IV. SOLVD hospitalizations using primary diagnosis demonstrating masking
Only first hospitalization included CHF MI/angina Other cardiac Noncardiac Masked events CHF MI/angina Other cardiac Noncardiac
RRR
P value
Placebo
Enalapril
469 (13.8%) 478 (14.1%) 491 (14.4%) 649 (19.1%)
301 (8.9%) 413 (12.2%) 568 (16.7%) 702 (20.8%)
36.0 13.5 –15.9 –8.3
<.001 .021 .009 .101
260 (7.6%) 201 (5.9%) 368 (10.8%) 355 (10.4%)
209 (6.2%) 167 (4.9%) 295 (8.7%) 305 (9.0%)
19.5 16.8 19.7 14.0
.015 .071 .003 .043
Total number of patients hospitalized for a specific cause. Note that in the top and bottom halves of the table there are consistent reductions in hospitalizations for CHF and MI/angina. However, by using first hospitalizations, there appears to be an apparent “excess” of other cardiac and noncardiac hospitalizations, whereas there is a similar “reduction” in the masked events in these same categories. By using the first event for each category (irrespective of other hospitalizations), these biases could be avoided.
CHF hospitalization, which in turn “masks” a stroke in an analysis that focused on time to first hospitalization. On the basis of Studies of Left Ventricular Dysfunction (SOLVD) trial data, about 38% of hospitalizations for CHF occurred after a hospitalization for another cause. Therefore this approach of using total hospitalizations leads to a loss in statistical power in 2 ways: inclusion of a large number of events that are insensitive and a loss in events that are truly sensitive. In the SOLVD trial, use of first hospitalization instead of CHF hospitalization would have substantially reduced power. In addition to a loss in power by the use of total hospitalization, occasionally one can get biased results from the play of chance, by creating spurious differences in hospitalizations that are unlikely to be affected. This is illustrated by an example from the SOLVD trials (Table V), in which there was no good reason to expect an impact of angiotensin-converting enzyme inhibitors (ACE-I) on non-CV deaths. In the SOLVD treatment trial, there appeared to be a significant reduction in CV hospitalizations (62% vs 55.6%, RRR 10.3%; P = .001).1 A similar result was observed in the SOLVD prevention trial (10.9% vs 7.6%, RRR 30%; P = .004).3 However, there was an apparent “reduction” in non-CV hospitalizations in the SOLVD treatment trial (36.2% vs 31.7%, RRR 12.4%; P = .015), thereby exaggerating the observed effect on total hospitalizations. Conversely, there was an apparent “increase” in hospitalizations for non-CV reasons in the prevention trial, thereby diluting the observed effect on total hospitalizations. Combining the data from the 2 trials indicates a clear reduction in CV hospitalizations (50.9% vs 46%, RRR 9%; P = .001) and no difference in non-CV hospitalizations (29.5% vs 29.6%, RRR 0; P = .91). Therefore, the real effect of ACE-I in preventing hospitalizations would be spuriously exaggerated in the SOLVD treatment trial and spuriously diluted in the prevention trial, by the play of chance if
Figure 1
The problems associated with masking. If only the first event (1a) is counted, then the occurrence of appendicitis or stroke is missed. If the CHF occurrence is delayed from 1a to 1b, appendicitis is “unmasked,” and, because of this bias, a spurious “excess” of appendicitis may become apparent. In both cases, strokes are masked. Therefore it would be preferable to at least examine the first event of each category.
the analysis had focused primarily on total hospitalizations. These data indicate that there is a greater possibility that the apparent effects on the total hospitalizations would be considerably altered by chance variations in outcomes that the treatment does not affect, even in large trials. A second potential source for bias may be a consequence of the “masking” effect that was described earlier (see Figure 1 and Table IV). If a treatment were to delay the development of CHF hospitalization relative to placebo, in the treated group some CHF hospitalizations that were destined to have occurred before a nonCHF hospitalization may occur after it. Assuming that treatment has no real effect on non-CHF hospitalizations, more events in this category will be “unmasked” in the active group relative to the control group. This will create an artifact by which an apparent excess in
American Heart Journal January 2002
26 Yusuf and Negassa
Table V. Number of patients with CV and non-CV hospitalizations in the SOLVD trials demonstrating the “play of chance” CV hospitalization
SOLVD treatment trial
Non-CV hospitalization
Total hospitalizations*
Placebo
Enalapril
Placebo
Enalapril
Placebo
810
729
460
399
959
Z = –3.28 SOLVD prevention trial
967
SOLVD total
867
1777
893 Z = –2.87 1202 1167 Z = 1.19 2161 2060 Z = 2.75
Z = –2.6 534
Z = –3.02
595 Z = 2.2
1596 Z = –4.33
994
Enalapril
994 Z=0
*The discrepancy with the previous 2 columns is because the same patient may have more than one hospitalization.
Table VI. Comparison of treatment impact on specific hospitalizations categorized as primary or secondary Placebo No. of subjects Primary CHF Secondary CHF Primary MI/angina Secondary MI/angina Other primary cardiac Other secondary cardiac Primary noncardiac Secondary noncardiac
3401 668 (19.6%) 219 (6.4%) 635 (18.7%) 113 (3.3%) 756 (22.2%) 329 (9.7%) 932 (27.4%) 309 (9.1%)
non-CHF hospitalizations may be evident. This is obvious by examining the experience in the SOLVD trial. By only counting the first event, there appears to be an excess of “other cardiac” and “noncardiac” hospitalizations in the treated group, whereas exactly the reverse is observed in the “masked” hospitalizations for these causes. When all hospitalizations for a specific cause/category are examined, there is no difference between the 2 randomized groups. Therefore use of any hospitalization leads to a loss in power and there is a greater potential for confounding and artifactual differences in some categories of events.
Does classification of cause of hospitalization as “primary” or “secondary” affect the results? Table VI demonstrates the results of the SOLVD trial by 4 categories of hospitalizations; each category is further subdivided into primary or secondary. Note the consistency of treatment results. Irrespective of whether one focuses on the primary or secondary diagnosis, there is a clear and consistent reduction in CHF and ischemic events with little impact on other categories of hospitalizations. These data suggest that it may be medically sensible and statistically sensitive to include both primary or secondary diagnoses in the analyses of cause-specific hospitalizations. (One expects biology to be “continuous” and it is unlikely that a treatment would truly only be efficacious for an MI or CHF hospitalization classified as a
Enalapril 3396 478 (14.1%) 153 (4.5%) 546 (16.1%) 78 (2.3%) 773 (22.76) 319 (9.4%) 939 (27.7%) 311 (9.2%)
RRR (%)
28.3 30 13.9 30.9 –2.5 2.9 –0.9 –0.8
P value
<.0001 .001 .005 .01 .60 .69 .82 .92
“primary” but not a “secondary” event). These observations add to the robustness of using cause-specific hospitalizations as the outcome of interest.
Other special issues Thus far, we have only discussed the advantages and disadvantages of analyzing cause-specific hospitalizations versus total hospitalizations. In statistical analyses, it is important to analyze the composite outcome of CV death or hospitalization for a specific cause to avoid problems related to competing risks or creating artifacts.4 The standard approach of counting one event per person has the value of robustness but does not distinguish between a patient who has only one hospitalization compared with another who has multiple hospitalizations. Comparing the total number of hospitalizations across the treatment groups is helpful as a descriptive tool but is not statistically valid. There are new methods5,6 that could be validly used to take multiple events in the same patient into account and thereby increase sensitivity.
Detecting unexpected adverse effects Not everything about the potential mechanism of action of an intervention is usually known at the beginning of a trial. It has sometimes been argued that because there is always a potential for unexpected harmful or beneficial effects (for example, on non-CV mortality), and this is best detected by examining the
American Heart Journal Volume 143, Number 1
total number of deaths or hospitalizations. When there is a substantial increase in a common or several common causes of deaths or hospitalizations, examining the total number of events may show an excess in total events, even when a treatment has a beneficial effect on another specific outcome. However, unexpected and clinically important adverse events (eg, significant neutropenia) may have a low frequency (eg, a 1% or 2% rate) and even a doubling or tripling in these rates may be masked when the overall hospitalization rate is severalfold greater (eg, 50%). (Note that most trials would be substantially underpowered to detect an adverse effect on rare outcomes. However, reporting them separately will allow examination of the consistency of any “trends” across several related trials). In general, such excesses in major outcomes are best detected by specifically examining each category of event. For example, in the SOLVD trials there was a significant increase in hospitalizations for hypotension with enalapril compared with placebo (40 active vs 23 control, P < .031), but this would not be detected by examining the overall number of hospitalizations (3988 in the active group vs 4471 in the control group). Let us assume that a given agent doubles the risk of a specific cause of non-CV hospitalization and that this represents a significant proportion of all hospitalization (eg, 5%). Even in such cases, the examination of total hospitalizations will fail to detect an overall difference in the rate of such events. (In trials comparing bolus thrombolytic agents versus thrombolytics administered as an infusion, a one third and highly significant excess in intracranial bleeding is observed. Yet examining all strokes demonstrates only a nonsignificant excess.7) Therefore the best way to detect any real excess in an unexpected cause (eg, non-CV) of death or hospitalization is to examine the rates of cause-specific events.
Issues related to random errors in classification versus biases leading to differential misclassification If the method of classification is truly blinded (either in a blinded trial or with blinded adjudication), then it is hard to imagine the possibility of a bias away from the null even when some events are incorrectly classified. The observed treatment effect on the outcome of interest may be diluted by random and incorrect classification, but an artifact is unlikely. On the other hand, randomly incorrect classification may sometimes lead to an apparent effect (which is spurious) emerging in the outcomes that are the complement of the outcome of interest (eg, the inclusion of outcomes that are not sudden deaths as being classified as a sudden death and some sudden deaths being classified as a nonsudden death). This has the apparent effect of creating a small but spurious decrease in nonsudden deaths. If the degree of incorrect classification of sudden versus nonsudden deaths is modest (eg, <20%), then one might still accept sudden death as the primary outcome of interest. On the other
Yusuf and Negassa 27
hand, if the degree of incorrect classification is large (eg, 50%), there would be no value in using sudden death as a separate category to be examined. One might then examine the next “inclusive” grouping of deaths (either cardiac or cardiovascular) and accept the category where there is a consensus that a reasonable distinction can be made. Several trials have used cardiac or cardiovascular mortality, depending on the reproducibility of the category and the proportion of overall deaths they represent. The lower the proportion of all deaths, the modifiable and specific cause of death represents, the outcome of overall deaths becomes less sensitive (as a smaller overall treatment effect is observed). Therefore, whenever feasible, trying to minimize the inclusion of insensitive outcomes should be considered. Unexpected but rare adverse outcomes such as retroperitoneal fibrosis (as observed with practolol) and intracranial bleeding with thrombolytics are best detected by examining specific categories of events rather than the overall numbers of deaths or hospitalizations.
Recommendations for determining overall risk/ benefit ratio with use of cause-specific events We believe that the most sensitive approach to determining the net benefit and risk of an intervention is to go through 3 separate steps and then to make a summary evaluation: Step 1. Check if there is a convincing difference in the specific events that we expect treatment to be effective. Step 2. Check to see whether there are adverse differences in any unexpected outcomes. (If there are concerns, confirmation in independent data sets is generally needed, unless this is statistically extreme [eg, P < .001] and biologically plausible). Step 3. Check to see whether there are any other differences (beneficial or harmful) that are convincing (again external replication may be needed). Step 4. Make a summary evaluation after examining the first 3 steps. This approach was used in the interpretation of the first generation of cholesterol-lowering trials. In these trials, a clear reduction in nonfatal MI was observed (P < .0001), along with a reduction in CV deaths (P < .02), but there was an apparent excess in noncardiac deaths (P < .02).8 The reduction in CV deaths was believable because it was expected, consistent with the epidemiology and animal experiments, supported by the reduction in nonfatal MI, and demonstrated a dose-response relationship (eg, trials with larger cholesterol reductions had greater reductions in CV deaths/nonfatal MI). Conversely, the excess in non-CV deaths was not convincing because it was distributed across a number of unrelated outcomes, not supported by experimental data or epidemiologic observations, and there was no evidence of an excess in noncardiac morbidity. Therefore it was rea-
American Heart Journal January 2002
28 Yusuf and Negassa
sonable to conclude that cholesterol lowering would not only lower cardiac mortality but would also be expected to a net lower total mortality. This judgement has been subsequently confirmed in the more recent trials with statins.9
Conclusions In general, the use of cause-specific events increases sensitivity and decreases biases when used as the primary outcome measure in clinical trials. The specific cause of mortality or morbidity that should be considered will depend on the diseases and the intervention being evaluated. The choice of the outcome for a trial should balance biologic plausibility, robustness of classification, and relative frequency of events. However, publications should include sufficient details of other events to allow an overall judgement regarding the net benefit/risk. If investigators choose to use total mortality or total hospitalizations, they should be aware of the limitations outlined in this essay and the details of cause-specific events should be provided to allow examination of the biologic consistency and coherence of the data.
References 1. Effect of enalapril on survival in patients with reduced left ventricular ejection fractions and congestive heart failure: the SOLVD Investigators. N Engl J Med 1991;325:293-302. 2. Canner PL, Klimt CR. The Coronary Drug Project. Controlled Clin Trials 1983;4:313-32. 3. SOLVD Investigators. Effect of enalapril on mortality and the development of heart failure in asymptomatic patients with reduced left ventricular ejection fractions. N Engl J Med 1992;327:685-91. 4. Fleiss JL, Bigger JT Jr, McDermott M, et al. Nonfatal myocardial infarction is, by itself, an inappropriate end point in clinical trials in cardiology. Circulation 1990;81:684-5. 5. Zeger SL, Liang KY. The analysis of discrete and continuous longitudinal data. Biometrics 1986;42:121-30. 6. Cook RJ, Lawless JF. Marginal analysis of recurrent events and a terminating event. Stat Med 1997;16:911-24. 7. Mehta SR, Eikelboom JW, Yusuf S. Risk of intracranial haemorrhage with bolus versus infusion thrombolytic therapy: a meta-analysis of over 100,000 patients. Lancet 2000;56:449-54. 8. Yusuf S. Obtaining medically meaningful answers from an overview of randomized clinical trials. Stat Med 1987;6:281-6. 9. LaRosa JC, He J, Vupputuri S. Effect of statins on risk of coronary disease: a meta-analysis of randomized controlled trials. JAMA 1999;282):2340-6.
Congestive Heart Failure
Choice of clinical outcomes in randomized trials of heart failure therapies: Disease-specific or overall outcomes? Salim Yusuf, MBBS, DPhil, FRCPC, and Abdissa Negassa, PhD Hamilton, Ontario, Canada
Background There are different views regarding the appropriateness of using cause-specific events or all events as the primary outcome of clinical trials.
Methods This is a methodologic essay in which we discuss the pros and cons of the 2 approaches and provide illustrative examples.
Results Our preference is the use of cause-specific outcomes (as long as they can be classified with reasonable reproducibility and without bias) because they are more likely to be sensitive to change, less likely to lead to spurious conclusions by random variations in categories of outcomes that are unlikely to be affected by treatment, and relatively free from confounding. Overall benefit-risk ratios can be derived by examining the impact of treatment on various categories of outcomes and then developing a general judgment. Such an approach will also allow judgments to be made regarding generalizability of results across various groups of patients who are at differing risks for an event. Conclusions In general, cause-specific outcomes sensitive to the effects of a treatment are to be preferred as the principal outcome in trials of heart failure, as long as they are biologically sensible and can be classified without bias. Other outcomes, not expected to be affected, should also be reported separately. (Am Heart J 2002;143:22-8.)
It is now generally agreed that clinical events are more appropriate than surrogate measures as outcomes in clinical trials. Although improving how a patient feels (eg, symptomatic status) is a worthwhile goal of therapy in itself, preventing significant morbidity or mortality is likely to be of greater impact. It is therefore important to try to reliably ascertain the impact of a treatment on mortality or morbidity in patients with serious diseases. In these assessments, there is some controversy as to which clinically relevant outcomes should be the primary focus of clinical trials. Should the treatment be evaluated in trials that are designed to demonstrate an impact on overall mortality or overall morbidity? Alternatively, is it preferable to design trials to demonstrate an impact on the specific clinical outcomes that may be responsive to the treatment? In this article, we try to explore the advantages and disadvantages of the 2 approaches and consider both statistical and nonstatistiFrom the Division of Cardiology, McMaster University, and the Preventive Cardiology and Therapeutics Program, Hamilton Health Sciences Corporation, Hamilton, Ontario, Canada. Submitted November 20, 2000; accepted April 30, 2001. Reprints not available from the authors. E-mail: [email protected] Copyright © 2002 by Mosby, Inc. 0002-8703/2002/$35.00 + 0 4/1/119770 doi:10.1067/mhj.2002.119770
cal issues. We mainly use examples of heart failure trials but occasionally use other examples from cardiovascular (CV) prevention or therapy because the general principles are broadly applicable. In determining the choice of outcome(s) to be evaluated in a clinical trial, the primary outcome should ideally meet all or most of the following criteria: 1. The outcome should be of clinical importance and directly relevant to how patients feel, any disability they have, or how long they live. 2. The outcome should be related to the postulated mechanism of action of the drug and also sensitive to change (ie, increasing the “signal”). 3. It should be measured with reasonable reproducibility and reliably diagnosed or classified. 4. There should be as little “noise” in the outcome measurement by reducing components unrelated to the disease or unlikely to change. 5. There should be no bias in ascertainment or classification of individual events. 6. There should be no confounding (or masking) of events.
In drawing inferences about an intervention’s effect, we also need to get an overall assessment of the risk/benefit ratio to balance the presence of adverse outcomes. This can be achieved in 1 of 2 ways: first one could assess overall mortality and hospitalizations irre-
American Heart Journal Volume 143, Number 1
Yusuf and Negassa 23
Table I. Causes of death in 3 large heart failure trials
Total No. of deaths No. of non-CV deaths No. of CV deaths No. of noncardiac but vascular deaths No. of cardiac deaths No. of “arrhythmic deaths”* No. of deaths from pump failure No. of deaths from MI
SOLVD treatment trial EF ≤0.35
SOLVD prevention trial EF ≤0.35
DIG trial EF ≤0.40
DIG trial EF ≥0.40
961 102 (11%) 859 (89%) 24 (2.5%) 817 (85.0%) 365 (38.0%) 327 (34.0%) 107 (11.1%)
638 84 (13%) 554 (86.8%) 23 (3.6%) 509 (79.8%) 252 (39.5%) 142 (22.3%) 98 (15.4%)
2375 355 (15%) 2020 (85.1) 95 (4%) 1740 (73%) 645 (27.2%) 844 (35.5%) 251 (10.6%)
231 55 (23.8%) 176 (76.2%) 16 (6.9%) 139 (60.1%) 42 (18.2%) 64 (27.7%) 33 (14.3%)
*Arrhythmic deaths are based on the classification used in each trial. We recognize the difficulty of accurately classifying these types of events. The data are being provided as an example to illustrate the possible relative proportions of different “types” of death. Unknown deaths are included in CV, but further subdivision of this category is not done.
Table II. A theoretical example indicating that the overall impact on mortality is modest even when an agent reduces a specific cause of death (eg, sudden death) substantially
Sudden death CHF deaths MI deaths Cardiac deaths CV deaths Total mortality
Control
Active
67 135 130 332 382 432
135 135 130 400 450 500
Absolute difference
RRR (%)
Z value
50 0 0 17 15 14
5.05 0.00 0.00 3.16 3.09 3.05
–68 0 0 –68 –68 –68
P value .00001 1.000 1.000 .002 .002 .0023
The number of events in each group is provided and the number of patients randomized in each group is 1000.
spective of cause. Alternatively, one could examine the various components of mortality or morbidity. For example, in a trial of an antithrombotic agent, one could examine separately the component of mortality that is expected to be changed (eg, fatal myocardial infarction [MI]) and its related morbidity (eg, nonfatal MI) to assess efficacy. One could then separately assess the impact on the kinds of fatal/nonfatal outcomes that one might expect to be adversely affected (eg, intracranial bleeding, fatal bleeding, bleeding requiring hospitalization) and also those that we expect to be unaffected (eg, cancer). One can derive an overall effect by examining the impact on each of the 3 types of events separately and assess the strength and plausibility of any differences observed. One then combines the information from each component and reaches a summary judgment. Later in the article we will discuss the pros and cons of each approach with specific examples from recent trials. We recognize that when large trials are conducted despite a large body of information not everything about the mechanism of action of a therapy may be known. Recognizing this limitation, we argue that not only should events that are expected to be affected be separately evaluated but additionally the remaining outcomes should be examined by cause.
Mortality In patients with class II or III heart failure and a low ejection fraction (EF), about 90% of the deaths are classified as being due to CV causes and 10% are documented as being due to non-CV (cancers, etc)1 (Table I). Of the CV deaths, approximately 90% (or about 80% of the total) are from a cardiac cause with about 5% resulting from a noncardiac but vascular cause (strokes, pulmonary embolism). Of the cardiac causes, about 15% are due to an ischemic event, one third may be attributed to an arrhythmic event, one third attributed to progressive pump failure, and the remaining deaths are due to miscellaneous causes. If we had an intervention that was expected to reduce sudden death (eg, an implantable cardiac defibrillator), one would expect to see the entire “benefit” in that category (eg, arrhythmic deaths) with little differences in other categories. A theoretic scenario is outlined in Table II. There appears to be about a 50% relative risk reduction (RRR) in sudden death, with little impact on other causes of death. This translates into a 17% difference in cardiac deaths (P = .002), a 15% difference in CV deaths (P = .002), and only a 14% difference (P = .023) in total deaths. It is obvious that in such a trial, if sudden death could be classified with reasonable accuracy, then this would be
American Heart Journal January 2002
24 Yusuf and Negassa
Table III. SOLVD hospitalizations by primary diagnosis
No. of subjects CHF MI/unstable angina Stroke Other cardiac Noncardiac Total No. of patients hospitalized
Placebo
Enalapril
RRR (%)
P value
3401 729 (21.42%) 679 (20.0%) 110 (3.2%) 859 (25.3%) 1004 (29.5%) 2137 (62.8%)
3396 510 (15.0%) 580 (17.1%) 95 (2.8%) 863 (25.4%) 1007 (29.7%) 2036 (60.0%)
30 14.5 13.5 –0.6 –0.4 5.0
<.001 .002 .292 .883 .905 .015
the most sensitive outcome to test the effect of an implantable cardioverter defibrillator. Furthermore, this trial will also confirm that there is little impact on other causes of death. If the distinction between sudden death and other causes of the deaths is fairly clear and reliable, then it would be reasonable to use sudden death as the primary outcome. However, there may not be a high degree of concordance between 2 physicians trying to distinguish between sudden or nonsudden death. If the discordance is small (about 10% or 20%), the apparent effect size is proportionately reduced by one tenth or one fifth and there would be some loss in statistical power as a result of inclusion of nonsudden deaths in the primary outcome, which could be confused with sudden death. This in turn would tend to decrease the apparent differences in event rates (eg, deaths classified as sudden, which are a priori “sensitive” to treatment) between the 2 groups. In general, random errors in classifying an event tend to diminish the apparent treatment benefits. If the discordance is large, then it may make greater sense to analyze the data using total mortality. It is generally accepted that one could classify deaths into CV and non-CV and perhaps even CV deaths into further categories of cardiac and other vascular with reasonable validity and reliability.2 For these reasons, it would be preferable to use CV (or perhaps cardiac) as the primary categorization of mortality in heart failure trials. This approach is reasonably robust, and cardiac (or CV) death is a major outcome and is more sensitive than use of total mortality as the main outcome of interest. The added sensitivity conferred by using the causespecific event as opposed to total mortality will vary, depending on the proportion of all deaths that would be expected to be CV. For example, in patients with a low EF and class IV congestive heart failure (CHF), >95% of deaths are CV and the difference between using CV or total deaths is small. On the other hand, in those with asymptomatic left ventricular dysfunction, about 85% of the deaths are CV and there could be an important increment in sensitivity by using CV deaths as opposed to total deaths as the outcome of interest in a trial. If one were to examine primary prevention of cardiovascular events, more than one half the events
would be noncardiovascular and hence not be amenable to treatment. In such a case, use of cause-specific mortality substantially improves the sensitivity of the study. Similarly, in patients such as the elderly with other comorbidities (and hence a higher likelihood of deaths from noncardiac causes), it may be preferable to use cardiac deaths as the primary outcome of interest rather than total mortality.
Morbidity Statistical power The most common outcome reflecting morbidity is usually hospitalization. In hospitalized patients, specific diagnoses can be confidently made with the help of careful histories, physical examinations, investigations, response to treatments, etc. (This contrasts with mortality, where such data may be sparse, especially when a death is out of hospital and unwitnessed). In general, there is greater confidence in categories of hospitalizations (eg, for worsening heart failure) than for a similar category of death. Second, in patients with a low EF and CHF only about one third of all those hospitalized are hospitalized for worsening CHF, and this proportion drops to about 15% in patients with CHF with an EF >40% and is about 25% in patients with a low EF and no overt CHF. Therefore even large (eg, 30%) reductions in CHF hospitalizations may not be detected if one only examined all hospitalizations (Tables III and IV). Statistical power and sensitivity are greatly enhanced by examining the specific categories of hospitalizations that one expects treatment to affect rather than including insensitive outcomes (eg, a cancer or stroke hospitalization that is not expected to be affected). A second problem with chiefly focusing on overall hospitalizations is a loss of power when one only counts the first hospitalization per patient (eg, as in a time to event analysis). This is illustrated in Figure 1. Let us assume that a patient is hospitalized for an appendectomy 6 months after randomization and 3 months later has worsening CHF requiring hospitalization and another 3 months later has a stroke. In this case, if one were to only count the first hospitalization for any reason, then the hospitalization for acute appendicitis “masks” the
American Heart Journal Volume 143, Number 1
Yusuf and Negassa 25
Table IV. SOLVD hospitalizations using primary diagnosis demonstrating masking
Only first hospitalization included CHF MI/angina Other cardiac Noncardiac Masked events CHF MI/angina Other cardiac Noncardiac
RRR
P value
Placebo
Enalapril
469 (13.8%) 478 (14.1%) 491 (14.4%) 649 (19.1%)
301 (8.9%) 413 (12.2%) 568 (16.7%) 702 (20.8%)
36.0 13.5 –15.9 –8.3
<.001 .021 .009 .101
260 (7.6%) 201 (5.9%) 368 (10.8%) 355 (10.4%)
209 (6.2%) 167 (4.9%) 295 (8.7%) 305 (9.0%)
19.5 16.8 19.7 14.0
.015 .071 .003 .043
Total number of patients hospitalized for a specific cause. Note that in the top and bottom halves of the table there are consistent reductions in hospitalizations for CHF and MI/angina. However, by using first hospitalizations, there appears to be an apparent “excess” of other cardiac and noncardiac hospitalizations, whereas there is a similar “reduction” in the masked events in these same categories. By using the first event for each category (irrespective of other hospitalizations), these biases could be avoided.
CHF hospitalization, which in turn “masks” a stroke in an analysis that focused on time to first hospitalization. On the basis of Studies of Left Ventricular Dysfunction (SOLVD) trial data, about 38% of hospitalizations for CHF occurred after a hospitalization for another cause. Therefore this approach of using total hospitalizations leads to a loss in statistical power in 2 ways: inclusion of a large number of events that are insensitive and a loss in events that are truly sensitive. In the SOLVD trial, use of first hospitalization instead of CHF hospitalization would have substantially reduced power. In addition to a loss in power by the use of total hospitalization, occasionally one can get biased results from the play of chance, by creating spurious differences in hospitalizations that are unlikely to be affected. This is illustrated by an example from the SOLVD trials (Table V), in which there was no good reason to expect an impact of angiotensin-converting enzyme inhibitors (ACE-I) on non-CV deaths. In the SOLVD treatment trial, there appeared to be a significant reduction in CV hospitalizations (62% vs 55.6%, RRR 10.3%; P = .001).1 A similar result was observed in the SOLVD prevention trial (10.9% vs 7.6%, RRR 30%; P = .004).3 However, there was an apparent “reduction” in non-CV hospitalizations in the SOLVD treatment trial (36.2% vs 31.7%, RRR 12.4%; P = .015), thereby exaggerating the observed effect on total hospitalizations. Conversely, there was an apparent “increase” in hospitalizations for non-CV reasons in the prevention trial, thereby diluting the observed effect on total hospitalizations. Combining the data from the 2 trials indicates a clear reduction in CV hospitalizations (50.9% vs 46%, RRR 9%; P = .001) and no difference in non-CV hospitalizations (29.5% vs 29.6%, RRR 0; P = .91). Therefore, the real effect of ACE-I in preventing hospitalizations would be spuriously exaggerated in the SOLVD treatment trial and spuriously diluted in the prevention trial, by the play of chance if
Figure 1
The problems associated with masking. If only the first event (1a) is counted, then the occurrence of appendicitis or stroke is missed. If the CHF occurrence is delayed from 1a to 1b, appendicitis is “unmasked,” and, because of this bias, a spurious “excess” of appendicitis may become apparent. In both cases, strokes are masked. Therefore it would be preferable to at least examine the first event of each category.
the analysis had focused primarily on total hospitalizations. These data indicate that there is a greater possibility that the apparent effects on the total hospitalizations would be considerably altered by chance variations in outcomes that the treatment does not affect, even in large trials. A second potential source for bias may be a consequence of the “masking” effect that was described earlier (see Figure 1 and Table IV). If a treatment were to delay the development of CHF hospitalization relative to placebo, in the treated group some CHF hospitalizations that were destined to have occurred before a nonCHF hospitalization may occur after it. Assuming that treatment has no real effect on non-CHF hospitalizations, more events in this category will be “unmasked” in the active group relative to the control group. This will create an artifact by which an apparent excess in
American Heart Journal January 2002
26 Yusuf and Negassa
Table V. Number of patients with CV and non-CV hospitalizations in the SOLVD trials demonstrating the “play of chance” CV hospitalization
SOLVD treatment trial
Non-CV hospitalization
Total hospitalizations*
Placebo
Enalapril
Placebo
Enalapril
Placebo
810
729
460
399
959
Z = –3.28 SOLVD prevention trial
967
SOLVD total
867
1777
893 Z = –2.87 1202 1167 Z = 1.19 2161 2060 Z = 2.75
Z = –2.6 534
Z = –3.02
595 Z = 2.2
1596 Z = –4.33
994
Enalapril
994 Z=0
*The discrepancy with the previous 2 columns is because the same patient may have more than one hospitalization.
Table VI. Comparison of treatment impact on specific hospitalizations categorized as primary or secondary Placebo No. of subjects Primary CHF Secondary CHF Primary MI/angina Secondary MI/angina Other primary cardiac Other secondary cardiac Primary noncardiac Secondary noncardiac
3401 668 (19.6%) 219 (6.4%) 635 (18.7%) 113 (3.3%) 756 (22.2%) 329 (9.7%) 932 (27.4%) 309 (9.1%)
non-CHF hospitalizations may be evident. This is obvious by examining the experience in the SOLVD trial. By only counting the first event, there appears to be an excess of “other cardiac” and “noncardiac” hospitalizations in the treated group, whereas exactly the reverse is observed in the “masked” hospitalizations for these causes. When all hospitalizations for a specific cause/category are examined, there is no difference between the 2 randomized groups. Therefore use of any hospitalization leads to a loss in power and there is a greater potential for confounding and artifactual differences in some categories of events.
Does classification of cause of hospitalization as “primary” or “secondary” affect the results? Table VI demonstrates the results of the SOLVD trial by 4 categories of hospitalizations; each category is further subdivided into primary or secondary. Note the consistency of treatment results. Irrespective of whether one focuses on the primary or secondary diagnosis, there is a clear and consistent reduction in CHF and ischemic events with little impact on other categories of hospitalizations. These data suggest that it may be medically sensible and statistically sensitive to include both primary or secondary diagnoses in the analyses of cause-specific hospitalizations. (One expects biology to be “continuous” and it is unlikely that a treatment would truly only be efficacious for an MI or CHF hospitalization classified as a
Enalapril 3396 478 (14.1%) 153 (4.5%) 546 (16.1%) 78 (2.3%) 773 (22.76) 319 (9.4%) 939 (27.7%) 311 (9.2%)
RRR (%)
28.3 30 13.9 30.9 –2.5 2.9 –0.9 –0.8
P value
<.0001 .001 .005 .01 .60 .69 .82 .92
“primary” but not a “secondary” event). These observations add to the robustness of using cause-specific hospitalizations as the outcome of interest.
Other special issues Thus far, we have only discussed the advantages and disadvantages of analyzing cause-specific hospitalizations versus total hospitalizations. In statistical analyses, it is important to analyze the composite outcome of CV death or hospitalization for a specific cause to avoid problems related to competing risks or creating artifacts.4 The standard approach of counting one event per person has the value of robustness but does not distinguish between a patient who has only one hospitalization compared with another who has multiple hospitalizations. Comparing the total number of hospitalizations across the treatment groups is helpful as a descriptive tool but is not statistically valid. There are new methods5,6 that could be validly used to take multiple events in the same patient into account and thereby increase sensitivity.
Detecting unexpected adverse effects Not everything about the potential mechanism of action of an intervention is usually known at the beginning of a trial. It has sometimes been argued that because there is always a potential for unexpected harmful or beneficial effects (for example, on non-CV mortality), and this is best detected by examining the
American Heart Journal Volume 143, Number 1
total number of deaths or hospitalizations. When there is a substantial increase in a common or several common causes of deaths or hospitalizations, examining the total number of events may show an excess in total events, even when a treatment has a beneficial effect on another specific outcome. However, unexpected and clinically important adverse events (eg, significant neutropenia) may have a low frequency (eg, a 1% or 2% rate) and even a doubling or tripling in these rates may be masked when the overall hospitalization rate is severalfold greater (eg, 50%). (Note that most trials would be substantially underpowered to detect an adverse effect on rare outcomes. However, reporting them separately will allow examination of the consistency of any “trends” across several related trials). In general, such excesses in major outcomes are best detected by specifically examining each category of event. For example, in the SOLVD trials there was a significant increase in hospitalizations for hypotension with enalapril compared with placebo (40 active vs 23 control, P < .031), but this would not be detected by examining the overall number of hospitalizations (3988 in the active group vs 4471 in the control group). Let us assume that a given agent doubles the risk of a specific cause of non-CV hospitalization and that this represents a significant proportion of all hospitalization (eg, 5%). Even in such cases, the examination of total hospitalizations will fail to detect an overall difference in the rate of such events. (In trials comparing bolus thrombolytic agents versus thrombolytics administered as an infusion, a one third and highly significant excess in intracranial bleeding is observed. Yet examining all strokes demonstrates only a nonsignificant excess.7) Therefore the best way to detect any real excess in an unexpected cause (eg, non-CV) of death or hospitalization is to examine the rates of cause-specific events.
Issues related to random errors in classification versus biases leading to differential misclassification If the method of classification is truly blinded (either in a blinded trial or with blinded adjudication), then it is hard to imagine the possibility of a bias away from the null even when some events are incorrectly classified. The observed treatment effect on the outcome of interest may be diluted by random and incorrect classification, but an artifact is unlikely. On the other hand, randomly incorrect classification may sometimes lead to an apparent effect (which is spurious) emerging in the outcomes that are the complement of the outcome of interest (eg, the inclusion of outcomes that are not sudden deaths as being classified as a sudden death and some sudden deaths being classified as a nonsudden death). This has the apparent effect of creating a small but spurious decrease in nonsudden deaths. If the degree of incorrect classification of sudden versus nonsudden deaths is modest (eg, <20%), then one might still accept sudden death as the primary outcome of interest. On the other
Yusuf and Negassa 27
hand, if the degree of incorrect classification is large (eg, 50%), there would be no value in using sudden death as a separate category to be examined. One might then examine the next “inclusive” grouping of deaths (either cardiac or cardiovascular) and accept the category where there is a consensus that a reasonable distinction can be made. Several trials have used cardiac or cardiovascular mortality, depending on the reproducibility of the category and the proportion of overall deaths they represent. The lower the proportion of all deaths, the modifiable and specific cause of death represents, the outcome of overall deaths becomes less sensitive (as a smaller overall treatment effect is observed). Therefore, whenever feasible, trying to minimize the inclusion of insensitive outcomes should be considered. Unexpected but rare adverse outcomes such as retroperitoneal fibrosis (as observed with practolol) and intracranial bleeding with thrombolytics are best detected by examining specific categories of events rather than the overall numbers of deaths or hospitalizations.
Recommendations for determining overall risk/ benefit ratio with use of cause-specific events We believe that the most sensitive approach to determining the net benefit and risk of an intervention is to go through 3 separate steps and then to make a summary evaluation: Step 1. Check if there is a convincing difference in the specific events that we expect treatment to be effective. Step 2. Check to see whether there are adverse differences in any unexpected outcomes. (If there are concerns, confirmation in independent data sets is generally needed, unless this is statistically extreme [eg, P < .001] and biologically plausible). Step 3. Check to see whether there are any other differences (beneficial or harmful) that are convincing (again external replication may be needed). Step 4. Make a summary evaluation after examining the first 3 steps. This approach was used in the interpretation of the first generation of cholesterol-lowering trials. In these trials, a clear reduction in nonfatal MI was observed (P < .0001), along with a reduction in CV deaths (P < .02), but there was an apparent excess in noncardiac deaths (P < .02).8 The reduction in CV deaths was believable because it was expected, consistent with the epidemiology and animal experiments, supported by the reduction in nonfatal MI, and demonstrated a dose-response relationship (eg, trials with larger cholesterol reductions had greater reductions in CV deaths/nonfatal MI). Conversely, the excess in non-CV deaths was not convincing because it was distributed across a number of unrelated outcomes, not supported by experimental data or epidemiologic observations, and there was no evidence of an excess in noncardiac morbidity. Therefore it was rea-
American Heart Journal January 2002
28 Yusuf and Negassa
sonable to conclude that cholesterol lowering would not only lower cardiac mortality but would also be expected to a net lower total mortality. This judgement has been subsequently confirmed in the more recent trials with statins.9
Conclusions In general, the use of cause-specific events increases sensitivity and decreases biases when used as the primary outcome measure in clinical trials. The specific cause of mortality or morbidity that should be considered will depend on the diseases and the intervention being evaluated. The choice of the outcome for a trial should balance biologic plausibility, robustness of classification, and relative frequency of events. However, publications should include sufficient details of other events to allow an overall judgement regarding the net benefit/risk. If investigators choose to use total mortality or total hospitalizations, they should be aware of the limitations outlined in this essay and the details of cause-specific events should be provided to allow examination of the biologic consistency and coherence of the data.
References 1. Effect of enalapril on survival in patients with reduced left ventricular ejection fractions and congestive heart failure: the SOLVD Investigators. N Engl J Med 1991;325:293-302. 2. Canner PL, Klimt CR. The Coronary Drug Project. Controlled Clin Trials 1983;4:313-32. 3. SOLVD Investigators. Effect of enalapril on mortality and the development of heart failure in asymptomatic patients with reduced left ventricular ejection fractions. N Engl J Med 1992;327:685-91. 4. Fleiss JL, Bigger JT Jr, McDermott M, et al. Nonfatal myocardial infarction is, by itself, an inappropriate end point in clinical trials in cardiology. Circulation 1990;81:684-5. 5. Zeger SL, Liang KY. The analysis of discrete and continuous longitudinal data. Biometrics 1986;42:121-30. 6. Cook RJ, Lawless JF. Marginal analysis of recurrent events and a terminating event. Stat Med 1997;16:911-24. 7. Mehta SR, Eikelboom JW, Yusuf S. Risk of intracranial haemorrhage with bolus versus infusion thrombolytic therapy: a meta-analysis of over 100,000 patients. Lancet 2000;56:449-54. 8. Yusuf S. Obtaining medically meaningful answers from an overview of randomized clinical trials. Stat Med 1987;6:281-6. 9. LaRosa JC, He J, Vupputuri S. Effect of statins on risk of coronary disease: a meta-analysis of randomized controlled trials. JAMA 1999;282):2340-6.