Prespecified Subgroup Analyses

Lee and the GUSTO investigators disagree with Fuster [7], Rapaport [5], Sleight [4], and ourselves [3] that the benefit of accelerated tissue plasminogen activator (tPA) observed in the GUSTO trial may be limited to select patient subgroups; Lee and colleagues imply that such subgroup analyses are flawed and, therefore, should not be done.

We fully concur with concerns about the interpretation of multiple, post hoc subgroup analyses. However, the disputed analyses based on age, infarction location, and time to treatment were not done post hoc but were prespecified in the GUSTO protocol and were published by the investigators themselves. As clearly described in the primary GUSTO paper [1], a significant mortality benefit of accelerated tPA compared with streptokinase was found among patients 75 years or younger (but not among those 75 years or older), among patients with anterior infarctions (but not among those with inferior infarctions), and among those treated early (but not among those treated late).

Despite these published data, the GUSTO investigators dispute our statement [3] that no thrombolytic regimen in the GUSTO trial showed any mortality advantage for patients treated 4 or more hours after symptom onset, a critical issue because most patients with acute myocardial infarction in the United States come to the hospital during this time frame. Lee and associates [2] appropriately stress that such subgroup effects can only be properly interpreted after tests for heterogeneity have been done that show a true difference between strata. We agree with this scientific approach to data analysis. However, substantial heterogeneity was noted in the GUSTO trial for time-to-treatment effects; as published in The New England Journal of Medicine, "a significant interaction was observed between time to treatment and reduction in mortality (P = 0.015), with a greater reduction in mortality associated with early treatment with tPA" [1]. Thus, the important time-to-treatment by drug mortality interactions, which we [3] and others [5] have discussed, appear to be accurate and justified using the same criteria that Lee and colleagues state should be applied to this subgroup analysis.

Ironically, had this heterogeneity principle been applied to the original GUSTO report, then the published statement—during the time intervals of "0 to 2 hours, 2 to 4 hours, and 4 to 6 hours, there was a consistent benefit for accelerated tPA as compared with streptokinase" [1]—should never have been made because the data do not show a mortality benefit of tPA compared with streptokinase for patients treated between 4 and 6 hours. Further, the mortality for patients treated after 6 hours was actually higher for tPA, although this difference was not statistically significant. As with GISSI-2 (Gruppo Italiano per lo Studio dell Streptochinasi nell'Infarto Miocardico) [8, 9] and ISIS-3 (Third International Study of Infarct Survival) [10], the GUSTO data also indicate statistically significant higher rates of stroke among patients receiving tPA; thus, it seems improbable that patients treated after 4 hours obtain any net clinical benefit by receiving this agent rather than streptokinase.

Open-Label Design of GUSTO

The second major theme raised by Lee and colleagues [2] concerns issues of inadvertent bias that may have affected the GUSTO trial because of its open-label rather than double-blind design. An important goal in designing any trial is to attempt to ensure that all therapeutic modalities that may affect study end points are distributed among the various arms of a trial in an equal and unbiased manner. If blinding is not done and the treating physician is aware of what drug is given (as occurred in the GUSTO trial), then it is impossible to control for any actions (good or bad) that the physician may take simply because he or she is aware of the study protocol and which drug a given patient is receiving. For example, physicians observing a patient with hypotension in the setting of thrombolysis may be more likely to ascribe this side effect to an allergic complication if they know the patient received streptokinase (a bacterial protein) rather than to tPA (a human protein).

Recognizing the importance of this issue, clinical researchers often go to extraordinary lengths to assure blinding; such efforts routinely exceed the "insertion of an extra intravenous line" that Lee and associates [2] state could have achieved blinding in the GUSTO trial had it been done. Although the GUSTO investigators [2] state that "the operational and economic practicalities of doing a blinded trial" dictated the open-label approach because "double-blinding was not practical without adding enormously to the complexity and expense of the study," the thrombolytic comparisons in ISIS-3 were double-blinded and this trial was substantially less expensive than GUSTO for a similar number of patients randomized.

In previous brief discussions of the open-label design of GUSTO, we [3] and Rapaport [5] pointed out that rates of potentially life-saving coronary artery bypass surgery were higher among patients receiving tPA than among those receiving streptokinase, raising the possibility that at least some of the apparent benefit of tPA might be because of a more aggressive approach for patients in this arm of the trial. In the original GUSTO report, it was stated that "the use of coronary revascularization procedures was similar in the four treatment groups" [1], even though, as Lee and colleagues confirm, the actual difference in rates for bypass surgery was larger than any reported mortality difference in the trial. This inconsistency raises the question of whether other major interventions, such as angiography and early angioplasty, were also differentially done in the GUSTO trial.

Instead of acknowledging this discrepancy and providing data about procedure use in each of the four treatment arms of the trial, Lee and colleagues present an analysis of patients not receiving bypass surgery and conclude that the differential in bypass rates could not have accounted for the small, absolute mortality difference between tPA-treated patients and streptokinase-treated patients. On the other hand, they also provide data showing that among those who had bypass surgery, the choice of thrombolytic therapy was not related to survival. If the analysis by Lee and associates is accepted—that coronary revascularization after thrombolysis for acute myocardial infarction does not decrease mortality—then the clinical implication of this line of reasoning is that increased rates of bypass surgery (and perhaps angiography and angioplasty) are an unexpected but serious complication of therapy with tPA. Because we believe that emergency bypass is likely to save lives, the simplest interpretation of these data remains that, in the GUSTO trial, more patients receiving tPA than streptokinase obtained the benefit of this life-saving procedure, making interpretation of the available mortality data difficult.

In further discussing the use of an open-label rather than double-blind design, Lee and colleagues [2] state that "it is important to keep in mind. (that) patients enrolled in GUSTO were randomly allocated to the treatment arms, thus eliminating bias in the selection of thrombolytic therapy." Clinicians do need to know that patients in the GUSTO trial were randomly assigned. Moreover, we believe the GUSTO investigators have adhered to a high standard for quality control in large-scale trials, particularly with respect to the assessment of stroke. However, randomization of patients is done to try to ensure that no major differences exist in baseline characteristics between treatment groups before treatment is initiated; double-blinding is done to ensure that no differential effects occur after treatment is given. Thus, the fact that GUSTO was a randomized trial does not address the issue that physicians knew what drug they were giving and appear to have, either inadvertently or because of clinical need, treated patients differentially on this basis.

Complete Analysis and Reporting of Trial Data

Practicing physicians want to know which patients, if any, truly obtain a net clinical benefit from accelerated tPA with intravenous heparin compared with any of the other three thrombolytic regimens tested in the GUSTO trial. Such an analysis requires that the four treatment regimens in the trial be compared with each other for the prespecified net clinical benefit end point of mortality plus nonfatal stroke. In turn, this combined end point needs to be analyzed for each arm of the trial according to age, time to treatment, and infarction location, the three important subgroup analyses prespecified by the investigators. In this manner, the "best" tPA regimen would be appropriately compared with the "best" streptokinase regimen.

Unfortunately, because neither the original GUSTO report [1] nor the commentary by Lee and associates [2] presents these clinically relevant comparisons, researchers and clinicians are confused about the proper scientific interpretation of the GUSTO data. For the prespecified end point of death plus nonfatal stroke, the GUSTO paper [1] and that by Lee and colleagues [2] report tests of statistical significance comparing front-loaded tPA with intravenous heparin to the combined streptokinase arms of the trial (streptokinase with intravenous heparin and streptokinase with subcutaneous heparin), a comparison that artificially increases the mortality difference in favor of tPA while simultaneously decreasing the stroke difference against tPA. This approach to data presentation is unusual because the GUSTO investigators [11] reported in 1992—before the GUSTO data [1] were available—that the streptokinase with subcutaneous heparin arm of the trial was incorporated to "provide an authentic and contemporary reference with which the other three experimental arms can be compared in order to appropriately test the probability of lower mortality without an undue increase in the risk of intracerebral hemorrhage."

Despite this statement of intent, no statistical analyses were published comparing accelerated tPA with intravenous heparin to streptokinase with subcutaneous heparin for the prespecified end point of death plus nonfatal stroke. In fact, of the several "net clinical benefit" end points that the GUSTO investigators did prespecify in their protocol, only those dealing with death plus disabling stroke were published using an appropriate statistical comparison. Thus, an important piece of information clinicians require from the GUSTO trial is a statistical assessment of death plus any nonfatal stroke comparing tPA with intravenous heparin to streptokinase with subcutaneous heparin. As appropriately prespecified in the statistical section of the GUSTO protocol [12], this analysis requires adjustment for multiple comparisons.

In addition, the method of analysis used in examining the time-to-treatment effects has also made the GUSTO trial data confusing. Rather than assessing for evidence of a net clinical benefit among the four treatment regimens, the GUSTO report analyzes mortality alone (thus omitting stroke data) and again does so only after combining the two streptokinase arms. Because each of these analytic strategies tends to maximize the apparent benefit of tPA, it is impossible to discern whether true differences exist in terms of net clinical benefit between the two treatment arms of accelerated tPA with intravenous heparin and streptokinase with subcutaneous heparin. Thus, an analysis of the time-to-treatment effects comparing each arm of the trial separately for the combined end point of death plus nonfatal stroke also needs to be presented so that clinicians can adequately interpret the GUSTO data.

Finally, clinicians look forward to publication of GUSTO data for actual rates of angiography, angioplasty, and bypass surgery according to each arm of the trial so that a true assessment of just how large or small these differences actually were can be made. Such an analysis should optimally be stratified by U.S. compared with non-U.S. centers because regimen-specific differences in rates of invasive procedures may help to explain why tPA-treated patients had a mortality benefit in the United States but not elsewhere. Although such a finding could be attributable to the play of chance, differential use of invasive procedures on different sides of the Atlantic for tPA-treated patients and streptokinase-treated patients merits thorough analysis and presentation.

Clinical Relevance of the GUSTO Trial

The GUSTO investigators are to be congratulated for swiftly completing an important large-scale trial of thrombolytic therapy that has added to the understanding of coronary reperfusion [13, 14]. We also believe that critical and informed evaluation of study results is essential to advancing scientific understanding, and we eagerly await presentation of the important pieces of information outlined above. However, until persuaded otherwise, we see no reason to depart from our scientifically grounded and clinically relevant conclusions as follows:

1. Findings from the GISSI-2, ISIS-3, and GUSTO-1 trials consistently indicate that the choice of thrombolytic therapy is much less important to ultimate survival than is the delay in time to onset of treatment.

2. Any potential differences in efficacy among thrombolytic agents are at most small in absolute benefit and are unlikely to pertain to most patients with myocardial infarction who present more than 4 hours after the onset of pain.

3. All thrombolytic agents appear effective when given up to 12 hours after the onset of symptoms; clinical strategies must, therefore, be adopted to increase thrombolytic use among persons arriving later regardless of which agent is chosen.

4. Because the in-hospital delay for patients treated with thrombolytic therapy is almost 90 minutes in the United States, the development of local programs in emergency departments designed to decrease the time delay in thrombolytic treatment is probably the most effective way to save the greatest number of lives.

Finally, we reiterate that underutilization of thrombolytic therapy in the United States [15] is the most important clinical issue confronting investigators in the medical treatment of acute myocardial infarction. A recent comprehensive overview [16] indicates that the benefit of initiating thrombolytic therapy 1 or 2 hours earlier leads to an absolute decrease in mortality similar to the between-drug difference found in an overview of the three large-scale trials that directly compared different regimens [5]. In this regard, we remain firm in our belief that "any small differences among agents in terms of efficacy, safety, and ease of administration must be recognized as being of far less clinical importance than is the wider use of thrombolytic therapy with any of the available agents" [3].