Thrombolytic Agents: The Science of the Art of Choosing the Better Treatment

Methodology Should Serve Biology

These elements begin with biology and the mechanisms of disease, cross-fertilized by epidemiology and tempered by humility. Thus, we seek the same, single biological mechanism to explain the superiority of one treatment and the inferiority of its competitor. This mechanism, if found, both provides the intellectual comfort of coherence and identifies the intermediate end points and responses that we should seek in therapeutic reports comparing these treatments. If superior treatment #1 produces its ultimate therapeutic benefit through a biological mechanism that generates the intermediate response R, then even patients receiving the inferior treatment #2 who exhibit this intermediate response R should likewise exhibit the ultimate therapeutic benefit.

Moreover, if this relation holds, it also argues against pooling trial results in meta-analyses or overviews of regimens that produce qualitatively different rates of the intermediate response (that is, high rates with one regimen and very low or zero rates with another). Finally, when invoking biological mechanisms, we must avoid both an ignorance of history (our colleagues in oncology have learned the perils of imputing long-term clinical benefit from short-term tumor responsiveness) and the hubris of subspecialism. We should not forget the Cardiac Arrhythmia Suppression Trial (in which anti-arrhythmic drugs increased rather than decreased mortality) or that internal mammary ligation made splendid biological sense in its day.

Appraising the Validity of the Results

The second element of the science of the art of selecting among therapeutic alternatives critically appraises the validity of the results of the studies that compared them. The objective is not the detection of deliberate deception (for that is the province of scientific auditors, not clinical readers) but the discovery of the innocent, unintentional, and unconscious ways in which the assembly, assignment, management, monitoring, or analysis of patients in therapeutic studies might lead either to the false-positive conclusion that treatments differ in their effects on patients when, in truth, they do not (at least not in any humanly important way) or to the false-negative conclusion that they do not differ in important effects when, in truth, they do. For this reason, patients in different treatment arms ought to be similar at study entry for attributes that materially affect either their risk for important events or their responsiveness to therapy; it is for these reasons that random allocation schemes that conceal the next patient's assignment from those who are contemplating entering the patient have deservedly become the gold standard for such endeavors.

Once entered, study patients should seek and receive only their assigned treatment and no other that might materially affect the target outcomes (thus, the importance of double-blinding in clinical trials). In addition, clinical events and other outcomes of interest should be pursued and ascertained with equal vigor in all treatment groups (another advantage for blinding, at least of the assessors). Moreover, all patients who enter such studies should be accounted for at the conclusion (so that dead men can tell their tales).

In examining the results of therapy among clinically relevant subgroups of patients (prespecified before the trial commenced), statistics should serve, not replace, reason. As a general rule, only qualitative differences in responses (in which the same treatment is effective in one subgroup and is unambiguously useless or harmful in its complementary subgroup) should excite the reader to apply the overall trial conclusion differently to subsets of patients.

Quantitative differences restricted to the degree of responsiveness of prespecified subgroups (even though they result in conventionally statistically significant results in one subgroup and not in the other and even if they produce statistically significant tests for interaction in large trials) should lead to differences in subgroup treatment only in the face of other compelling arguments, such as the relative costs of different treatments. Finally, post hoc data-dredging for subgroups of patients or subsets of events, however qualitatively dramatic their results, should only generate hypotheses for the next trial, not conclusions from this one.

Comparison of the Efforts, Costs, Risks, and Benefits of Different Treatments

The final element that thoughtful clinicians include in the calculus that leads them to initiate one treatment over another consists of a comparison of the efforts, costs, risks, and benefits facing them and their patients as they collaborate in striving for common therapeutic benefits through different therapeutic means. This last step can be opaquely implicit (tarrying with the other remnants of the art of medicine) or transparently explicit (ranging from the elegance of cost utility and clinical decision analyses to the simple comparison of relative risk reductions).

Recently, a half-way technology has come into use for the latter approach that permits the reading clinician to quickly and simply calculate the number of patients one needs to treat with a specific regimen in order to prevent one clinical event (such as an infarction) or to cause a clinically important side effect (such as major bleeding) [2].

The number needed to treat (NNT) requires only the calculation of the arithmetic difference in the rates of events (good or bad) between treatment groups and the division of this difference into 1 (thus, if the rates of death by 1 month are 6.3% on treatment #1 and are 7.3% on treatment #2, the NNT to prevent 1 death by using treatment #1 instead of treatment #2 is 1/[0.073 − 0.063] or 100; and, if the rates of hemorrhagic stroke are 0.72% using treatment #1 and are 0.52% using treatment #2, then the NNT to cause a hemorrhagic stroke by using treatment #1 instead of treatment #2 is 1/[0.0072 − 0.0052] or 500). (Readers may have noted that these examples are based on data published in the primary report [1] of the GUSTO trial.)

Additionally, one could factor approximate costs into the NNT calculation. Thus, if other upstream and downstream costs were equal, but the charges for drugs #1 and #2 were $2800 and $400, respectively, the NNT of 100 to save 1 additional life would carry a price tag of a bit less than a quarter of a million dollars, money that might be spent elsewhere. (Those who are offended by this last comment and deny that rationing does or ought to exist in the lives of doctors and their patients deny reality. Skeptical readers should consider the opportunity cost for reading this editorial; they could be seeing another patient, reading another journal, completing their delinquent clinical records, or at play.)

Choosing a Thrombolytic Agent

What happens when we apply these elements of the science of the art of medicine to choosing a thrombolytic agent? For one thing, previous casual opinions can change (as they did for the authors of this editorial!).

Our biological argument invokes all three of the components described above. First, in the angiographic substudy, left ventricular function was the same among patients with equivalent degrees of coronary artery patency at 90 minutes, regardless of treatment group, supporting patency as the single biological mechanism. If this is matched by similarities in mortality, the biologic explanation would become convincing.

Second, this substudy suggests that the accelerated tPA regimen is quantitatively (but not qualitatively) different from other tPA or streptokinase regimens. On these grounds, a meta-analysis combining the tPA regimen in GUSTO with that of other trials appears appropriate. The counterargument is that the accelerated tPA regimen is pharmacologically so different as to render a combined meta-analysis biologically inappropriate. Competent scientists disagree on this point, and it remains unresolved. Third, hubris abounds! The pronouncement that we now know the mechanism by which thrombolytic agents work is bold and maybe even true.

Could Bias Have Affected the Results of Thrombolytic Trials?

We are not scientific auditors and begin from the premise that any threats to the validity of the results that we might encounter in the thrombolytic trials at issue here stem from innocent, unintentional, and unconscious bias. The trials at issue were randomized, and, as nearly as we can tell, all of them concealed the next assignment from participating clinicians, so no bias here.

Neither GUSTO nor the earlier thrombolytic trial, GISSI-I, was blinded. As a result, we must consider what would happen if participating clinicians in these trials harbored hunches that one treatment (say, tPA) really was superior to another (say, streptokinase). Might their hunches be innocently, even unconsciously, expressed by administering patients in that favored arm some additional, efficacious therapy (cointervention) that materially improved their clinical outcomes? If so, this would at least lead to an overestimate of the favored drug's efficacy and might even generate a false-positive conclusion about it.

Is there evidence that this might have occurred in GUSTO? Yes, more tPA (9.0%) than streptokinase (8.3%) patients underwent coronary artery bypass surgery (although this could be attributed to patient need rather than provider bias). Readers should not be reassured by the GUSTO team's report that the 30-day mortality was identical for tPA and streptokinase patients undergoing bypass surgery (for that is what we would expect); the issue is that more tPA than streptokinase patients enjoyed the mortality-reducing effects of this procedure.

This difference in bypass surgery rates cannot explain away the tPA results, but if a high-intensity, North American practice of early invasive interventions is a prerequisite for reaping the benefit of tPA, it will become a less attractive regimen in other, less invasive settings. Moreover, the reminders by the GUSTO team about random allocation and objective outcome assessments are not relevant to this concern. Thus, clinical readers might want to ease their estimates of the most likely relative risk reduction from tPA downward from 14% into the lower portion of its 95% confidence interval (which extends to about 6%); we shall see the effects of this on the NNT shortly.

We have no reason not to trust equal vigor in pursuing and ascertaining the clinical events in these trials. We also are content that insufficient patients who entered the relevant trials were subsequently lost to materially affect their results or interpretations. Much of the argument between the GUSTO team and its detractors has to do with subgroup analyses, and we find fault and merit on both sides. Restricting our comments to the prespecified subgroup analyses (because the detractors have demonstrated that data dredging is not the exclusive domain of a treatment's enthusiasts), the site of the infarction may be important and the time elapsed between symptom onset and treatment is at least as crucial for tPA as it is for other thrombolytic agents, if not more so. Both agents need to be given sooner rather than later, and the statistically significant relation between elapsed time and the efficacy of tPA in GUSTO is matched by other thrombolytic agents in other trials. Indeed, for front-line clinicians, the vital role of early treatment may be the most important message in this entire debate.

So, Which Thrombolytic Agent Is Best?

Just about any analysis invoking NNT or its more sophisticated effort-yield cousins has to favor streptokinase as the overall treatment, although the cost-effectiveness ratios are comparable to those of many other interventions. Nonetheless, the opportunity costs (that is, the other things that we could not do for patients because the necessary resources were consumed by a tPA treatment policy for all patients) will be just too great for most providers to accept (whether individual physicians, institutions, or payers), especially in health care systems that reject the ability of patients ability to pay as the measure of whether they deserve to be treated. The 95% confidence interval on the NNT to save 1 life by using tPA rather than streptokinase centers on about 100 patients but runs as high as 240 patients, and it may be useful, given the concern that the efficacy of tPA may have been overestimated in the GUSTO trial, to select an NNT nearer the upper value. The NNT with tPA to cause a hemorrhagic stroke is about 500 (and for streptokinase is about 1000).

How does this compare with the NNT for other treatments? Bearing in mind the implications of different treatment duration, using streptokinase and aspirin (rather than nothing) among patients with suspected heart attacks in the ISIS-2 trial, the NNT is about 20 to prevent 1 death at 5 weeks; and for either drug alone, the NNT is about 40. Using enalapril in patients with class IV heart failure (New York Heart Association), the NNT is 6 to prevent 1 death at 1 year; and using enalapril in patients with class I or II (or both) disease, the NNT is 100. Using coronary artery bypass surgery in patients with left main coronary stenosis, the NNT is 6 to prevent 1 death at 2 years. Using carotid endarterectomy in patients with high-grade symptomatic carotid stenosis, the NNT is 9 to prevent 1 stroke or death during the next 2 years. Using simple antihypertensive agents for patients with severe hypertension, the NNT is about 15 to prevent 1 stroke, myocardial infarction, or death in the next year; and for patients with mild hypertension, the NNT can run as high as 700. Using aspirin in patients with unstable angina, the NNT is about 25 to prevent a myocardial infarction or death during the next year, but the NNT is about 500 to prevent a myocardial infarction in a healthy U.S. physician. Administering thrombolytic therapy 5 hours earlier would generate an NNT of about 100 to save 1 life. These NNTs, tempered by the costs, risks, and inconvenience of their interventions, help place the relative roles of streptokinase and tPA in perspective.

Clinical Conclusions

If the foregoing elements capture the science of the art of making clinical judgments about which of a set of competing therapies ought to be the treatment of choice, four conclusions can be drawn about thrombolytic agents:

1. Front-line clinicians should pay far more attention to when patients with possible infarctions are treated with thrombolytic agents than to what thrombolytic agent they receive. Myriad lives can be saved by shortening the “door-to-needle” time in the emergency room.

2. As administered in GUSTO, tPA is marginally more efficacious than streptokinase.

3. However, a policy of treating everyone with tPA rather than streptokinase would require switching agents for a very large number of patients to save a single life. On this basis, it can be argued that whether tPA really is more efficacious than streptokinase is not a humanly important question, given their large differences in cost.

4. On the other hand, a selective treatment policy based on the prespecified subgroup analyses, in which, for example, younger patients with large anterior infarctions presenting within 4 hours of symptom onset received tPA, could minimize additional cost while focussing on those patients most likely to benefit from the more expensive thrombolytic agent.