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The randomized controlled clinical trial
SPECIAL ARTICLE
The Randomized Controlled Clinical Trial Scientific and Ethical Bases
DAVID H. SPODICK, M.D., D.Sc. Worcester, Massachusetts
Randomized controlled trials are increasingly accepted in principle but not always in practice, particularly for surgical therapies. Successful surgical randomized controlled trials demonstrate their feasibility, and reports of uncontrolled surgical trials now commonly bear a statement that a definitive answer requires a controlled trial. Scientifically, the randomized controlled trial Is the most powerful way to determine a result ascribable only to the trial treatment. Although randomized controlled trials can be imperfect or Improperly conducted, they are designed to circumvent biased behavior by Investigators. With candor in Informed consent, the equal chance not to get a trial treatment makes the randomized controlled trial the most ethical design. Thus, scientific, behavioral, and ethical cases support the randomized controlled trial as the optimal method for Investigation of nearly all therapeutic innovations and as a requirement for publication. CONTROLLED TRIALS IN PERSPECTIVE
From the Cardiology Division, St. Vincent Hospital, and the University of Massachusetts Medical School, Worcester, Massachusetts. Requests for reprints should be addressed to Dr. David H. Spodick, Director, Division of Cardiology, St. Vincent Hospital, 25 Winthrop Street, Worcester, Massachusetts 01604. Manuscript accepted January 20.1982.
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This is the ninth decade of the 20th century. On the subject of controlled trials of therapy, we should be preaching to the converted. Why is this not universally so? Case In Point: Cardiology. Cardiologists came relatively late to the concept of appropriately designed controlled clinical trials, perhaps because “their” organ is unique-the heart responds in milliseconds to challenges at the bedside as well as in the laboratory, giving the cardiologist a special sense of security in his observations. A dozen years ago, the great promise of aortocoronary bypass surgery stimulated debates at national cardiology meetings. To those who had “cut their teeth” on controlled clinical trials, these early debates had an atmosphere of unreality. The surgeon-protagonists were predictably enthusiastic, as they had been for previous techniques. The antagonists, distinguished cardiologists, expressed uneasiness because the pell-mell rush to the new cure was based more on hypothesis than on results. Previous failures of operations that were less attractive but equally enthusiastically pushed had made them predictably wary. Yet, nowhere in the lexicon of either side was a concept already familiar among pharmacologic, gastroenterologic, and other colleaguesrandomized controlled trials. The audience was witnessing a battle of wits between unarmed opponents. A handful of editorialists and writers of letters to the editor, hoping to make objective the success of coronary bypass and define its true
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indications, pleaded with the Cardiology Establishment for trials to generate appropriate denominators for the beguiling numerators-the uncontrolled, hence anecdotal, results-from the burgeoning bypass activity. The first randomized trial was organized by cardiologists and surgeons of the Veterans Administration [ 11. But the lavishly financed, high-volume bypass centers produced critics who alleged suboptimal angiography and operative skills and disparities of a multi-hospital effort [2-41. Any one of these bypass centers could have produced definitive trials more efficiently, but they preferred rather to improve their skills by subjecting vast numbers of patients to trial-and-error surgery. In contrast to surgical practice, there has been some conversion in principle. Even the sharpest critics of the VA study who eschew doing controlled trials admit that random assignment of concurrent control subjects is the ideal method [4]. We also have the advice of numerous outstanding surgeons and cardiologists in the form of escape clauses, which now seem to appear regularly in papers reporting uncontrolled trials of surgical procedures. Toward the end of the report or sometimes at its beginning, there will be a statement to the effect that although the present study is not one, randomized controlled trials remain the optimal approach (Representative escape clauses can be found in Codini MA et al.: Am J Cardiol 1979; 43: 1103; DeWood et al.: Am J Cardiol 1979; 44: 1356; Kloster et al.: N Engl J Med 1979; 300: 149; Oberman et al.: Lancet 1977; I: 137; Sheldon, Loop: Cleve Clin Q 1976; 43: 97; Cohen, Gorlin: Circulation 1975; 52: 275; Rahimtoola: Am J Cardiol 1975; 35: 711; Mundth, Austen: N Engl J Med 1975; 293: 124; Gorlin: Bergen Pines fvled Staff Rep 1975; 9:273; Kouchoukos, Kirklin: Mod Concepts Cardiovasc Dis 1972; 41: 47.) One wonders, was this the authors’ idea? Was its insertion associated with the ubiquitous notation “revision accepted”? If so, journal reviewers as well as authors are finally converted in principle, yet conspire to publish trials of inferior design (read: “uncertain validity”) and exonerate authors via a pious wish for someone else to do the definitive trial-a fine example of the schizoid behavior that permits standards for surgical trials that would be unacceptable for medical trials. This is not because randomized surgical trials are impossible. They have been carried out for a variety of operations including coronary bypass [ 1,5-71, demonstrating that appropriately designed trials of surgery are quite feasible. Controlled Clinical Trials: General Considerations. The prospective, randomized, controlled trial of therapy is not quite the only way to evaluate new treatments. But there are few exceptions for which it is not the best method, and therefore the scientifically and ethically mandatory method, for obtaining a true answer, i.e., what actually happens to the patient as compared with
that same patient, or with a patient who is as comparable as possible, except for the trial treatment. Finally, the randomized controlled trial aims at the outcome; it is not directly concerned with mechanisms or hypotheses leading to that outcome. For example, randomized controlled trials of nitroglycerin as a treatment for angina carried out in 195 1 and in 198 1 would each show significant efficacy. In 195 1, this would have been ascribed solely to coronary vasodilation. In 1981, that would not have to be the mechanism. The point is, the controlled trial produces the same answer irrespective of hypothetical mechanisms. Two interrelated cases support the randomized controlled trial: scientific and ethical. THE SCIENTIFIC
CASE
Scientifically, the randomized controlled trial compares a trial treatment with alternative treatments or no treatment to achieve results ascribabk only to the trial treatment. It ensures objectivity by excluding preconceptions of the investigator, the referring physician, or the patient. To be sure, innovative treatments are necessarily based on hypotheses, and hypotheses first arise from experimental or uncontrolled (anecdotal) clinical experience. Yet, treatment without proper controls, i.e., based on hypothesis alone, is not appropriate because the hypothesis could be incomplete, flawed, or totally wrong. Uncontrolled trials, like uncontrolled experience, provide only naked numerators-anecdotes [8]. A numerator has no meaning without its denominator, in this case a standard of comparison. But denominators should be appropriate to their numerators: both must be generated without conscious or unconscious biases. In medicine and surgery, this means scientifically valid controls [8]. The very complexity of variables in serious diseases undermines uncontrolled observations. Therefore, strict criteria for entry into a trial of therapy (and stratification into subgroups if appropriate) should account for the known variables. Randomization aims to equally distribute the unknown as well as the known variables. Although not always perfect (therefore to be reviewed after any study is completed), randomization should assign groups as comparable as possible to trial and alternative therapies. Even when a post-trial review may show baselines differences in the known variables, appropriate statistical adjustments usually can be made. Moreover, in association with blinding, no approach better satisfies the assumptions underlying statistical tests. Are there inescapable exceptions to a randomized controlled trial? There are, but these are relatively few: conditions with a very high early mortality: rare diseases in which a large series cannot be attained under controlled conditions: some diseases in paired organs that allow the patient to be his own control; and certain
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conditions producing repetitive emergencies (e.g., syncope due to bradyarrhythmias, demonstrably treatable by pacemaker). Types of Bias. A principal scientific objective of the randomized controlled trial is to minimize at least five kinds of bias: time bias, prognosis bias, observation bias, compliance bias, and skill bias. Time bias involves changes over time in the expression or natural history of a disease, in its diagnosis, and in its direct and supportive management. For example, since 1967, the continuing decline in incidence and death rate of coronary disease and improvements in management of its complications are constantly changing the basis for comparing all treatments. Without concurrent controls, this alone would make any ineffective but harmless treatment look good. Thus, time bias often renders “natural history” unnatural and makes a powerful case against historical controls. Concurrent control patients in a prospective design are most comparable to patients receiving a trial treatment if they are assigned with all biases minimized, i.e., randomized. (Another “time bias” may prejudice the conduct and interpretation of even well designed trials-too short a follow-up period. This is especially true in assessing the effect of treatment on mortality in chronic diseases, like coronary atherosclerosis and its consequences. The Veterans Administration trial of coronary bypass surgery [ 11, for example, began to show statistically improved survival in certain surgical subgroups only after four years. This situation-early “negative” results-poses serious problems of maintaining interest in and support for protracted, costly, large-scale investigations.) Prognosis bias produces unequal prognosis in control subjects and trial patients. This is commonly due to selection for treatment, notably surgery, of patients with a better prognosis and rejection of those considered too ill or otherwise unsuitable. It may be due also to unrecognized cofactors like smoking that are not equally allocated. Stratification or blocking before randomization can more efficiently eliminate prognosis bias. Prognosis bias also arises from patient referral patterns. In the New York trial of anticoagulants for acute infarction, dicumarol was given on the widely accepted hypothesis that it would limit coronary thrombosis, and patients were assigned to treatment by alternate-day admission [9]. The trial result: 50 percent greater mortality in patients admitted on days when anticoagulant was not given. But this was not substantiated by appropriately designed trials and is explained by biased referral [8]. Referring physicians saved their good-risk patients for the days they knew anticoagulant was given, and the sicker, poor-risk patients were referred as they appeared.
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Observation bias may be introduced when one comparison group is examined more frequently or treated more actively with supportive therapy. Blinding seeks to eliminate this bias. Blinding may not be possible in trials of agents with obvious clinical effects (e.g., ,&adrenoceptor blockers); here, third parties can make continued management decisions. Blinding is impossible also in trials of surgical therapy, necessitating strict randomization, “hard” end-points (like mortality) and stringent criteria for “soft”end-points like quality of life. Compliance bias affects patients receiving medical therapy. It is notorious that many patients either do not adhere to prescribed dosing or forget to take medicine (thus a daily injection will produce better compliance than a pill several times a day). Moreover, it has been shown that even those receiving a placebo who rigidly comply with the placebo schedule, like those who rigidly comply with the trial treatment, can have a better outcome than those who do not [lo]. Skill bias conspicuously affects surgical therapy and might confound results. Yet, improving operative skill is easily encompassed in a randomized controlled trial design-surgical results are monitored for improvement over time. Skill bias also applies to medical therapy, with supportive management and recognition of complications better provided by more skillful physicians. THE ETHICAL CASE The physician’s sole ethical imperative is always to do his best for his patient. Yet, what is “best” may be disputed and what seems best is always contingent upon the quality of the physician’s knowledge. Hence, we have an ethical paradox: a poorly informed physician may be as zealous as a well informed physician in using what he considers to be optimal therapy. Ethically, that makes witch doctors our equals. Physicians who plied their trade by bleeding and purging and who used that most popular cure-all of the 19th century, calomel (by mouth!) [ 111, were acting ethically, i.e., according to their faith in the treatment. Thus, although we ought to act ethically, ethical behavior alone cannot assure best treatment. Our ethical, but too often lethal, predecessors can be forgiven for not having adequate tools to assess treatments. Yet, despite the modern availability of such tools, physicians have behaved no differently, using methods in which faith often kindles an enthusiasm that clouds reason-methods discarded only after wasteful trial-and-error finally makes it apparent that they either do not work or are harmful. The list, unfortunately, is long (Table I). Ethical Defense of the Patient. Ethically, patients should not be exposed to jeopardy greater than that of their disease. At the beginning, it is impossible to foretell the outcome of any new trial therapy: ethically, patients
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should be made aware of this. (In fact, that is also the case with most established treatments, in the sense that in daily practice it is impossible to state the exact outcome for any individual patient; we try to predict it from the documented responses of comparable patients.) Thus, in the very first clinical trial of a new therapy that appears to work in animals or may satisfy hypotheses as to why it should work, there should be strict ethical approaches to obtaining volunteer patients. First, it is intellectually honest (read: “ethical”) to describe an innovation as “experimental” [ 121 as well as “new.” “New” often implies “better,” and we can only hope that a new treatment is better until it is demonstrated-objectively-to be better. Next is optimized informed consent; the situation should be laid out honestly in detail. The ethical imperative to act best for the patient is based on “best evidence” not only before, but also after and during a trial. Thus, it is unethical to expose more human beings than needed to get an answer. Contingency plans for monitoring by an advisory committee should be available in randomized controlled trials to tell the blinded investigator to stop the trial at the first sign that the treatment is significantly superior or inferior to alternate treatment or no treatment. (In an initial surgical trial, close monitoring of the surgeons’ learning curve would be factored into the decision.) The VA stopped the randomized controlled trial of left main coronary disease after the medical cohort experienced excessive mortality. It is equally unethical and unscientific to use too few patients. Indeed, Freiman, Chalmers, and co-workers [13] have shown that a pitfall of many otherwise well designed randomized controlled trials has been investigation of too few subjects to reveal a true therapeutic effect, yielding a “beta” (Type II) error (versus an “alpha” (Type I) error that produces evidence of an effect when there is none.) All trials should be planned and conducted so that the number of patients will be sufficient to permit detection of a clinically important benefit given the available statistical methods. One wonders how many patients would volunteer for a trial of an innovation if they were told at the beginning that the investigators have reasonable hope, but in truth no precise idea, of the immediate result and absolutely no idea of long-term net gains or losses. Thus, bias should not be introduced by physicians already convinced (read: “prejudiced”) before actual testing begins. It is more ethical to explain during the informed consent dialogue that the randomization gives a “50-50 chance” [ 111 to get the more beneficial treatment. It should, in fact, be easier to get the first patients into a randomized than into an uncontrolled “pilot’study if the patients are equally well informed and not influenced by the investigator’s premature enthusiasm. Beecher [ 141 pointed
TABLE I
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Where Are they Now? (Uncontrolled Trials Enthusiastic)
For coronarydisease Pericardiopexy/poudrage Vineberg implant Omentopexy Internalmammary ligation Simple endatierectomy Sympathectomyfor hypertension Gastropexyfor “droppedstomach” Nephropexyfor “droppedkidney” Glomectomyfor asthma Prophylacticportacavalshunt Colon bypassfor hepatic encephalopathy
out that there is no ethical distinction between ends and
means. An experiment is or is not ethical in its design and execution and the most promising ends cannot justify unethical means. In summary, scientifically unsound studies are unethical. Randomized controlled trials make the ethical and scientific courses one and the same. DISSENT/ALTERNATIVES TO RANDOMIZED CDNTRDLLED TRIALS “Alternatives.” There are alternatives, mostly traditional and timedishonored, to appropriately designed randomized prospective controlled trials. Those alternative designs, old and new, that are not downright misleading are weaker than randomized controlled trials. In general they include “pure” hypothesis and hypothesis arising from anecdotal data like personal experience, case reports, and uncontrolled series that are compared with selected historical controls or “natural history.” We have already seen that hypothesis and theory may be weak or dead wrong, that personal experience tends to be biased by observation, selection, or referral biases, and that time bias invalidates historical controls and “natural” history. Alternate controls, such as even-odd patient allocation or every-other-day allocation, have failed to provide answers because, knowledge of the treatment to be given on a particular day has led physicians’ behavior to irreparably bias trials like the New York trial of anticoagulant therapy [8,9]. One seemingly attractive alternative is the matched concurrent control series. For example, patients can be matched for age, sex, and severity of disease. But this design is difficult if attempted for more than two or three characteristics and ordinarily requires a very large pool of patients. More importantly, it does not eliminate bias in matching. Ideally, matching could be done by third parties. But bias could only be minimized by subsequent randomized allocation of patients and this produces a matched randomized controlled trial.
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Straightforward randomized controlled trials are more efficient; physicians and patients are blinded before allocation with prior stratification (if desirable) instead of matching. Other schemes proposed to avoid controlled trials include registries and data banks. These tend to multiply anecdotal data and are wide open to referral bias [ 151. Thus, there is a major problem, already realized in certain cancer registries, of under-reporting, especially of unfavorable results [ 161. Registries may work, just as anecdotal material may chance to work, if the long-term results are spectacular, as in diseases with high early mortality. “Adaptive” methods, retrospective or prospective, mathematically “correct” for differences, with matching used to get identical pairs are appropriate for adjusting modest differences between groups. In some adaptive schemes, decision rules for allocating patients are contingent on cumulative evidence. However, these methods ignore the powerful influence of selection bias. When length of time to an end-point is important, “life table” and actuarial approaches are also useful, but are open to misuse. Their projections for a new treatment’s result do not necessarily encompass comparable populations. Life table analysis often is applied to select populations with high access to sophisticated care from which candidates for treatment have been especially selected and frequently excludes those with cancer, strokes, obesity, chronic disease, and other conditions represented in the general population. On the other hand, life table analysis can be a powerful tool within a randomized controlled trial. Sequential analysis of patient data by an independent monitor can be a powerful tool within a randomized controlled trial, but sequential patient selection has been used instead of randomization. Here, the less promising patients tend to be rejected if the treatment begins to look good. As we have seen, patients and referring physicians respond in direct proportion to the enthusiasm or discouragement of non-blinded investigators who know the nature of the treatment. Thus, for this scheme even to begin to work, zero patient refusal is needed, but observer bias remains. Sequential analysis also does not account for biologic variability. Moreover, the selection process may begin with referring physicians who send hopeless cases that become the untreated historical control subjects in the series. This biased selection is accentuated if there is a bed shortage, the patients with favorable (i.e., treated) cases always tending to get the beds. Dissent. What are the arguments against randomization? Successful randomization provides the basis for comparability of groups for any factor on 95 of 100
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occasions. In the Duke artificial simulation of randomization [ 171, patients allocated to one control group could further be split into two groups with different prognoses. The authors reasoned that the patients were perhaps inadequately characterized to begin with, that the statistical method had been inadequate to show baseline differences, or that the differences were due to chance or the combined effect of small distribution imbalances in several prognostic factors [ 171. Yet it was shown that, within limits, the magnitude of the artificial Duke results could be manipulated in either direction, that the authors did not necessarily select appropriate adjustment factors, and that they may have introduced new biases [ 181. When randomization is appropriately performed, no other method can equally ensure predictably unbiased allocation and comparability of baseline characteristics. The corollary is that statistics used for other types of allocation are not applied to a verifiable model. New operations tend to have an early excessive risk, and surgeons understandably believe they must practice before there can be an adequate trial. This is so, but tell this truthfully (ethically) to patients-that they are “practice cases” or that you have to “get the bugs out”-and you will get few volunteers who are not desperate. Moreover, since improving skill can be allowed for in a randomized controlled trial [ 191, this objection falls. Finally, one observer holds modern medicine to be “so sophisticated” that “only physiologically sound operations” could achieve wide use [20]. The answer to this is the continuing modern history of prejudiced behavior by physicians (necessitating randomization and, when possible, blinding) and the tenuous quality of hypotheses as to what is “physiologically sound.” Most operations and medical therapies that appeared to work and have since been discarded had physiologic hypotheses provided before or supplied after their initial, uncontrolled “success.” It is physiologically sound, for example, to hypothesize that increased coronary flow improves myocardial oxygenation. Yet this is not necessarily so. Dipyridamole and nitroglycerin comparably increase subendocardial blood flow, but only nitroglycerin increases myocardial tissue oxygen [21]. Originally promoted specifically to increase myocardial oxygenation, dipyridamole does not and-worse-can cause a coronary “steal”
[=I-
A tendentious objection is that patients are being deceived in a randomized controlled trial [23]. This notion fails if the wording of the informed consent discussion is honest and complete. Others believe that a placebo should be provided only if there is a chance for spontaneous remission. That argument ignores the fact that the trial treatment may be immediately or ultimately
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harmful, and is generally added to other direct or supportive treatment. Another objection is that the mutual trust involved brings unequal parties into a joint venture. But this is always the case every time a physician talks a patient into taking any kind of treatment. A more reasonable objection is that failure to adjust dosage might eliminate a good drug either from overdosage or underdosage. This can be accommodated, if necessary, in a rising dosage design. One might claim that introducing a blinded randomized trial “ignores past knowledge,” but that argument ignores the tenuous quality of knowledge that is not derived from appropriately designed trials. If it is held that the result may pertain strictly to the groups studied, this applies equally to all kinds of therapeutic trials, controlled or uncontrolled. Finally, blinding can be imperfect, as in the case of a drug with detectable effects like beta-blocking agents. Quite so, but randomized allocation remains superior to biased allocation, and the trial design can provide third-party (“triple-blind”) evaluation of results.
2. 3.
4.
5.
6.
7.
6.
9.
10. 11.
Hultgren HH, Takaro T, Detre KM, Murphy ML: Evaluation of the efficacy of coronary bypass surgery. Am J Cardioll976; 42: 157-160. Proudfit WL: Criticisms of the VA randomized study of coronary bypass surgery. Clin Res 1978; 26: 236-240. DeBakey ME, Lawrie GM: Response to commentary of Hultgren et al. on aortocoronary-artery-bypass: assessment after 13 vears. JAMA 1979: 241: 2393-2395. Sheldon WC; Loop FD: Direct myocardial revascularization-1978. Progress report on the Cleveland Clinic experience. Cleve Clin Q 1976; 43: 97-108. Mathur VS, Guinn GA: Prospective randomized study of coronary bypass surgery in stable angina. The first 100 patients. Circulation 1975; 52 (suppl I): 1133-1140. Russell RO, Group Members: Unstable angina pectoris: natiil study gray, to compare surgical and medical therapy. II. In-hospital experience and initial follow-up results in patients with one, two and three vessel disease. Am J Cardiol 1978; 42: 839-848. Kloster RE, Kremkau EL, Ritzmann LW, Rahirntoola SH, Rosch J, Kanarek PH: Coronary bypass for stable angina. A prospective randomized study. N Engl J Mecl 1979; 300: 149-157. Spodick DH: Revascularization of the heart-numerators in search of denominators (editorial). Am Heart J 1971; 81: 149-157. Wright IS, Marple CD, Seek DF: Report of the Committee for Evaluation of Anticoagutants in Coronary Thrombosis. Am Heart J 1948; 38: 801-815. Sackett M, Gent M: Controversy in counting and attributing events in clinical trials. N Engl J Med 1979; 301: 1410. Hall TB: Medicine on the Santa Fe Trail. Dayton, Ohio: Mor-
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TRIALS-SPODICK
CONCLUSIONS Randomized controlled trials are increasingly accepted in principle but not always in practice, particularly for surgical therapies. Successful surgical randomized controlled trials demonstrate their feasibility, and reports of uncontrolled surgical trials now commonly bear a statement that a definitive answer requires a controlled ‘trial. Scientifically, the randomized controlled trial is the most powerful way to determine a result ascribable only to the trial treatment. Although randomized controlled trials can be imperfect or improperly conducted, they are designed to circumvent biased behavior by investigators. With candor in informed consent, the equal chance not to get a trial treatment makes the randomized controlled trial the most ethical design. Thus, scientific, behavioral, and ethical cases support the randomized controlled trial as the optimal method for investigation of nearly all therapeutic innovations and as a requirement for publication.
12. 13.
14. 15. 16.
17.
18. 19. 20. 21.
22.
23.
September 1962
ningside. 1971. Chalmers TC: Randomization of the first patient. Med Clin North Am 1975; 59: 1035-1038. Freiman JA, Chalmers TC. Smfth HS Jr, Kuebler RR: The importance of beta, the Type II error and sample size in the design and interpretation of the randomized control trial. N Engl J Med 1978; 299: 690-694. Beecher HK: Ethics and clinical research. N Engl J Med 1966; 274: 1354-1369. Lyon LJ, Zion MM: Randomized trials vs. data banking. Chest 1974; 50: 641-642. Cornfield J: Approaches to assessment of the efficacy of surgical revascularization. Bull NY Acad Med 1972; 48: 1126-1134. Lee KL, McNeer F, Starmer F, Harris PJ, Rosati RA: Clinical judgment and statistics. Lessons from a simulated randomized trial in coronary artery disease. Circulation 1980; 61: 508-515. Detre KM, Peduzzi P. Chan Y-K: Clinical judgment and statistics. Circulation 1981; 63: 239-240. Spodick DH: Medical journals and randomized trials. Am J Cardiol 1980; 45: 528-529. Etoncheck LI: Are randomized trials appropriate for evaluating new operations? N Engl J Med 1979; 301: 44-45. Winbury MM, Howe BB, Weiss HR: Effect of nitroglycerin and dipyridamole on epicardial and endocardlal oxygen tension. J Pharmacol Exp Ther 1971; 176: 184-199. Flameng W, Wunsten B, Schaper W: On the distribution of myocardial flow. Part II. Effects of arterial stenosis and vasodilation. Basic Res Cardiol 1974; 69: 435-446. Editorial: Controlled trials: planned deception? Lancet 1979; I: 534.
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The Randomized Controlled Clinical Trial Scientific and Ethical Bases
DAVID H. SPODICK, M.D., D.Sc. Worcester, Massachusetts
Randomized controlled trials are increasingly accepted in principle but not always in practice, particularly for surgical therapies. Successful surgical randomized controlled trials demonstrate their feasibility, and reports of uncontrolled surgical trials now commonly bear a statement that a definitive answer requires a controlled trial. Scientifically, the randomized controlled trial Is the most powerful way to determine a result ascribable only to the trial treatment. Although randomized controlled trials can be imperfect or Improperly conducted, they are designed to circumvent biased behavior by Investigators. With candor in Informed consent, the equal chance not to get a trial treatment makes the randomized controlled trial the most ethical design. Thus, scientific, behavioral, and ethical cases support the randomized controlled trial as the optimal method for Investigation of nearly all therapeutic innovations and as a requirement for publication. CONTROLLED TRIALS IN PERSPECTIVE
From the Cardiology Division, St. Vincent Hospital, and the University of Massachusetts Medical School, Worcester, Massachusetts. Requests for reprints should be addressed to Dr. David H. Spodick, Director, Division of Cardiology, St. Vincent Hospital, 25 Winthrop Street, Worcester, Massachusetts 01604. Manuscript accepted January 20.1982.
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This is the ninth decade of the 20th century. On the subject of controlled trials of therapy, we should be preaching to the converted. Why is this not universally so? Case In Point: Cardiology. Cardiologists came relatively late to the concept of appropriately designed controlled clinical trials, perhaps because “their” organ is unique-the heart responds in milliseconds to challenges at the bedside as well as in the laboratory, giving the cardiologist a special sense of security in his observations. A dozen years ago, the great promise of aortocoronary bypass surgery stimulated debates at national cardiology meetings. To those who had “cut their teeth” on controlled clinical trials, these early debates had an atmosphere of unreality. The surgeon-protagonists were predictably enthusiastic, as they had been for previous techniques. The antagonists, distinguished cardiologists, expressed uneasiness because the pell-mell rush to the new cure was based more on hypothesis than on results. Previous failures of operations that were less attractive but equally enthusiastically pushed had made them predictably wary. Yet, nowhere in the lexicon of either side was a concept already familiar among pharmacologic, gastroenterologic, and other colleaguesrandomized controlled trials. The audience was witnessing a battle of wits between unarmed opponents. A handful of editorialists and writers of letters to the editor, hoping to make objective the success of coronary bypass and define its true
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indications, pleaded with the Cardiology Establishment for trials to generate appropriate denominators for the beguiling numerators-the uncontrolled, hence anecdotal, results-from the burgeoning bypass activity. The first randomized trial was organized by cardiologists and surgeons of the Veterans Administration [ 11. But the lavishly financed, high-volume bypass centers produced critics who alleged suboptimal angiography and operative skills and disparities of a multi-hospital effort [2-41. Any one of these bypass centers could have produced definitive trials more efficiently, but they preferred rather to improve their skills by subjecting vast numbers of patients to trial-and-error surgery. In contrast to surgical practice, there has been some conversion in principle. Even the sharpest critics of the VA study who eschew doing controlled trials admit that random assignment of concurrent control subjects is the ideal method [4]. We also have the advice of numerous outstanding surgeons and cardiologists in the form of escape clauses, which now seem to appear regularly in papers reporting uncontrolled trials of surgical procedures. Toward the end of the report or sometimes at its beginning, there will be a statement to the effect that although the present study is not one, randomized controlled trials remain the optimal approach (Representative escape clauses can be found in Codini MA et al.: Am J Cardiol 1979; 43: 1103; DeWood et al.: Am J Cardiol 1979; 44: 1356; Kloster et al.: N Engl J Med 1979; 300: 149; Oberman et al.: Lancet 1977; I: 137; Sheldon, Loop: Cleve Clin Q 1976; 43: 97; Cohen, Gorlin: Circulation 1975; 52: 275; Rahimtoola: Am J Cardiol 1975; 35: 711; Mundth, Austen: N Engl J Med 1975; 293: 124; Gorlin: Bergen Pines fvled Staff Rep 1975; 9:273; Kouchoukos, Kirklin: Mod Concepts Cardiovasc Dis 1972; 41: 47.) One wonders, was this the authors’ idea? Was its insertion associated with the ubiquitous notation “revision accepted”? If so, journal reviewers as well as authors are finally converted in principle, yet conspire to publish trials of inferior design (read: “uncertain validity”) and exonerate authors via a pious wish for someone else to do the definitive trial-a fine example of the schizoid behavior that permits standards for surgical trials that would be unacceptable for medical trials. This is not because randomized surgical trials are impossible. They have been carried out for a variety of operations including coronary bypass [ 1,5-71, demonstrating that appropriately designed trials of surgery are quite feasible. Controlled Clinical Trials: General Considerations. The prospective, randomized, controlled trial of therapy is not quite the only way to evaluate new treatments. But there are few exceptions for which it is not the best method, and therefore the scientifically and ethically mandatory method, for obtaining a true answer, i.e., what actually happens to the patient as compared with
that same patient, or with a patient who is as comparable as possible, except for the trial treatment. Finally, the randomized controlled trial aims at the outcome; it is not directly concerned with mechanisms or hypotheses leading to that outcome. For example, randomized controlled trials of nitroglycerin as a treatment for angina carried out in 195 1 and in 198 1 would each show significant efficacy. In 195 1, this would have been ascribed solely to coronary vasodilation. In 1981, that would not have to be the mechanism. The point is, the controlled trial produces the same answer irrespective of hypothetical mechanisms. Two interrelated cases support the randomized controlled trial: scientific and ethical. THE SCIENTIFIC
CASE
Scientifically, the randomized controlled trial compares a trial treatment with alternative treatments or no treatment to achieve results ascribabk only to the trial treatment. It ensures objectivity by excluding preconceptions of the investigator, the referring physician, or the patient. To be sure, innovative treatments are necessarily based on hypotheses, and hypotheses first arise from experimental or uncontrolled (anecdotal) clinical experience. Yet, treatment without proper controls, i.e., based on hypothesis alone, is not appropriate because the hypothesis could be incomplete, flawed, or totally wrong. Uncontrolled trials, like uncontrolled experience, provide only naked numerators-anecdotes [8]. A numerator has no meaning without its denominator, in this case a standard of comparison. But denominators should be appropriate to their numerators: both must be generated without conscious or unconscious biases. In medicine and surgery, this means scientifically valid controls [8]. The very complexity of variables in serious diseases undermines uncontrolled observations. Therefore, strict criteria for entry into a trial of therapy (and stratification into subgroups if appropriate) should account for the known variables. Randomization aims to equally distribute the unknown as well as the known variables. Although not always perfect (therefore to be reviewed after any study is completed), randomization should assign groups as comparable as possible to trial and alternative therapies. Even when a post-trial review may show baselines differences in the known variables, appropriate statistical adjustments usually can be made. Moreover, in association with blinding, no approach better satisfies the assumptions underlying statistical tests. Are there inescapable exceptions to a randomized controlled trial? There are, but these are relatively few: conditions with a very high early mortality: rare diseases in which a large series cannot be attained under controlled conditions: some diseases in paired organs that allow the patient to be his own control; and certain
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conditions producing repetitive emergencies (e.g., syncope due to bradyarrhythmias, demonstrably treatable by pacemaker). Types of Bias. A principal scientific objective of the randomized controlled trial is to minimize at least five kinds of bias: time bias, prognosis bias, observation bias, compliance bias, and skill bias. Time bias involves changes over time in the expression or natural history of a disease, in its diagnosis, and in its direct and supportive management. For example, since 1967, the continuing decline in incidence and death rate of coronary disease and improvements in management of its complications are constantly changing the basis for comparing all treatments. Without concurrent controls, this alone would make any ineffective but harmless treatment look good. Thus, time bias often renders “natural history” unnatural and makes a powerful case against historical controls. Concurrent control patients in a prospective design are most comparable to patients receiving a trial treatment if they are assigned with all biases minimized, i.e., randomized. (Another “time bias” may prejudice the conduct and interpretation of even well designed trials-too short a follow-up period. This is especially true in assessing the effect of treatment on mortality in chronic diseases, like coronary atherosclerosis and its consequences. The Veterans Administration trial of coronary bypass surgery [ 11, for example, began to show statistically improved survival in certain surgical subgroups only after four years. This situation-early “negative” results-poses serious problems of maintaining interest in and support for protracted, costly, large-scale investigations.) Prognosis bias produces unequal prognosis in control subjects and trial patients. This is commonly due to selection for treatment, notably surgery, of patients with a better prognosis and rejection of those considered too ill or otherwise unsuitable. It may be due also to unrecognized cofactors like smoking that are not equally allocated. Stratification or blocking before randomization can more efficiently eliminate prognosis bias. Prognosis bias also arises from patient referral patterns. In the New York trial of anticoagulants for acute infarction, dicumarol was given on the widely accepted hypothesis that it would limit coronary thrombosis, and patients were assigned to treatment by alternate-day admission [9]. The trial result: 50 percent greater mortality in patients admitted on days when anticoagulant was not given. But this was not substantiated by appropriately designed trials and is explained by biased referral [8]. Referring physicians saved their good-risk patients for the days they knew anticoagulant was given, and the sicker, poor-risk patients were referred as they appeared.
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Observation bias may be introduced when one comparison group is examined more frequently or treated more actively with supportive therapy. Blinding seeks to eliminate this bias. Blinding may not be possible in trials of agents with obvious clinical effects (e.g., ,&adrenoceptor blockers); here, third parties can make continued management decisions. Blinding is impossible also in trials of surgical therapy, necessitating strict randomization, “hard” end-points (like mortality) and stringent criteria for “soft”end-points like quality of life. Compliance bias affects patients receiving medical therapy. It is notorious that many patients either do not adhere to prescribed dosing or forget to take medicine (thus a daily injection will produce better compliance than a pill several times a day). Moreover, it has been shown that even those receiving a placebo who rigidly comply with the placebo schedule, like those who rigidly comply with the trial treatment, can have a better outcome than those who do not [lo]. Skill bias conspicuously affects surgical therapy and might confound results. Yet, improving operative skill is easily encompassed in a randomized controlled trial design-surgical results are monitored for improvement over time. Skill bias also applies to medical therapy, with supportive management and recognition of complications better provided by more skillful physicians. THE ETHICAL CASE The physician’s sole ethical imperative is always to do his best for his patient. Yet, what is “best” may be disputed and what seems best is always contingent upon the quality of the physician’s knowledge. Hence, we have an ethical paradox: a poorly informed physician may be as zealous as a well informed physician in using what he considers to be optimal therapy. Ethically, that makes witch doctors our equals. Physicians who plied their trade by bleeding and purging and who used that most popular cure-all of the 19th century, calomel (by mouth!) [ 111, were acting ethically, i.e., according to their faith in the treatment. Thus, although we ought to act ethically, ethical behavior alone cannot assure best treatment. Our ethical, but too often lethal, predecessors can be forgiven for not having adequate tools to assess treatments. Yet, despite the modern availability of such tools, physicians have behaved no differently, using methods in which faith often kindles an enthusiasm that clouds reason-methods discarded only after wasteful trial-and-error finally makes it apparent that they either do not work or are harmful. The list, unfortunately, is long (Table I). Ethical Defense of the Patient. Ethically, patients should not be exposed to jeopardy greater than that of their disease. At the beginning, it is impossible to foretell the outcome of any new trial therapy: ethically, patients
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should be made aware of this. (In fact, that is also the case with most established treatments, in the sense that in daily practice it is impossible to state the exact outcome for any individual patient; we try to predict it from the documented responses of comparable patients.) Thus, in the very first clinical trial of a new therapy that appears to work in animals or may satisfy hypotheses as to why it should work, there should be strict ethical approaches to obtaining volunteer patients. First, it is intellectually honest (read: “ethical”) to describe an innovation as “experimental” [ 121 as well as “new.” “New” often implies “better,” and we can only hope that a new treatment is better until it is demonstrated-objectively-to be better. Next is optimized informed consent; the situation should be laid out honestly in detail. The ethical imperative to act best for the patient is based on “best evidence” not only before, but also after and during a trial. Thus, it is unethical to expose more human beings than needed to get an answer. Contingency plans for monitoring by an advisory committee should be available in randomized controlled trials to tell the blinded investigator to stop the trial at the first sign that the treatment is significantly superior or inferior to alternate treatment or no treatment. (In an initial surgical trial, close monitoring of the surgeons’ learning curve would be factored into the decision.) The VA stopped the randomized controlled trial of left main coronary disease after the medical cohort experienced excessive mortality. It is equally unethical and unscientific to use too few patients. Indeed, Freiman, Chalmers, and co-workers [13] have shown that a pitfall of many otherwise well designed randomized controlled trials has been investigation of too few subjects to reveal a true therapeutic effect, yielding a “beta” (Type II) error (versus an “alpha” (Type I) error that produces evidence of an effect when there is none.) All trials should be planned and conducted so that the number of patients will be sufficient to permit detection of a clinically important benefit given the available statistical methods. One wonders how many patients would volunteer for a trial of an innovation if they were told at the beginning that the investigators have reasonable hope, but in truth no precise idea, of the immediate result and absolutely no idea of long-term net gains or losses. Thus, bias should not be introduced by physicians already convinced (read: “prejudiced”) before actual testing begins. It is more ethical to explain during the informed consent dialogue that the randomization gives a “50-50 chance” [ 111 to get the more beneficial treatment. It should, in fact, be easier to get the first patients into a randomized than into an uncontrolled “pilot’study if the patients are equally well informed and not influenced by the investigator’s premature enthusiasm. Beecher [ 141 pointed
TABLE I
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Where Are they Now? (Uncontrolled Trials Enthusiastic)
For coronarydisease Pericardiopexy/poudrage Vineberg implant Omentopexy Internalmammary ligation Simple endatierectomy Sympathectomyfor hypertension Gastropexyfor “droppedstomach” Nephropexyfor “droppedkidney” Glomectomyfor asthma Prophylacticportacavalshunt Colon bypassfor hepatic encephalopathy
out that there is no ethical distinction between ends and
means. An experiment is or is not ethical in its design and execution and the most promising ends cannot justify unethical means. In summary, scientifically unsound studies are unethical. Randomized controlled trials make the ethical and scientific courses one and the same. DISSENT/ALTERNATIVES TO RANDOMIZED CDNTRDLLED TRIALS “Alternatives.” There are alternatives, mostly traditional and timedishonored, to appropriately designed randomized prospective controlled trials. Those alternative designs, old and new, that are not downright misleading are weaker than randomized controlled trials. In general they include “pure” hypothesis and hypothesis arising from anecdotal data like personal experience, case reports, and uncontrolled series that are compared with selected historical controls or “natural history.” We have already seen that hypothesis and theory may be weak or dead wrong, that personal experience tends to be biased by observation, selection, or referral biases, and that time bias invalidates historical controls and “natural” history. Alternate controls, such as even-odd patient allocation or every-other-day allocation, have failed to provide answers because, knowledge of the treatment to be given on a particular day has led physicians’ behavior to irreparably bias trials like the New York trial of anticoagulant therapy [8,9]. One seemingly attractive alternative is the matched concurrent control series. For example, patients can be matched for age, sex, and severity of disease. But this design is difficult if attempted for more than two or three characteristics and ordinarily requires a very large pool of patients. More importantly, it does not eliminate bias in matching. Ideally, matching could be done by third parties. But bias could only be minimized by subsequent randomized allocation of patients and this produces a matched randomized controlled trial.
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Straightforward randomized controlled trials are more efficient; physicians and patients are blinded before allocation with prior stratification (if desirable) instead of matching. Other schemes proposed to avoid controlled trials include registries and data banks. These tend to multiply anecdotal data and are wide open to referral bias [ 151. Thus, there is a major problem, already realized in certain cancer registries, of under-reporting, especially of unfavorable results [ 161. Registries may work, just as anecdotal material may chance to work, if the long-term results are spectacular, as in diseases with high early mortality. “Adaptive” methods, retrospective or prospective, mathematically “correct” for differences, with matching used to get identical pairs are appropriate for adjusting modest differences between groups. In some adaptive schemes, decision rules for allocating patients are contingent on cumulative evidence. However, these methods ignore the powerful influence of selection bias. When length of time to an end-point is important, “life table” and actuarial approaches are also useful, but are open to misuse. Their projections for a new treatment’s result do not necessarily encompass comparable populations. Life table analysis often is applied to select populations with high access to sophisticated care from which candidates for treatment have been especially selected and frequently excludes those with cancer, strokes, obesity, chronic disease, and other conditions represented in the general population. On the other hand, life table analysis can be a powerful tool within a randomized controlled trial. Sequential analysis of patient data by an independent monitor can be a powerful tool within a randomized controlled trial, but sequential patient selection has been used instead of randomization. Here, the less promising patients tend to be rejected if the treatment begins to look good. As we have seen, patients and referring physicians respond in direct proportion to the enthusiasm or discouragement of non-blinded investigators who know the nature of the treatment. Thus, for this scheme even to begin to work, zero patient refusal is needed, but observer bias remains. Sequential analysis also does not account for biologic variability. Moreover, the selection process may begin with referring physicians who send hopeless cases that become the untreated historical control subjects in the series. This biased selection is accentuated if there is a bed shortage, the patients with favorable (i.e., treated) cases always tending to get the beds. Dissent. What are the arguments against randomization? Successful randomization provides the basis for comparability of groups for any factor on 95 of 100
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occasions. In the Duke artificial simulation of randomization [ 171, patients allocated to one control group could further be split into two groups with different prognoses. The authors reasoned that the patients were perhaps inadequately characterized to begin with, that the statistical method had been inadequate to show baseline differences, or that the differences were due to chance or the combined effect of small distribution imbalances in several prognostic factors [ 171. Yet it was shown that, within limits, the magnitude of the artificial Duke results could be manipulated in either direction, that the authors did not necessarily select appropriate adjustment factors, and that they may have introduced new biases [ 181. When randomization is appropriately performed, no other method can equally ensure predictably unbiased allocation and comparability of baseline characteristics. The corollary is that statistics used for other types of allocation are not applied to a verifiable model. New operations tend to have an early excessive risk, and surgeons understandably believe they must practice before there can be an adequate trial. This is so, but tell this truthfully (ethically) to patients-that they are “practice cases” or that you have to “get the bugs out”-and you will get few volunteers who are not desperate. Moreover, since improving skill can be allowed for in a randomized controlled trial [ 191, this objection falls. Finally, one observer holds modern medicine to be “so sophisticated” that “only physiologically sound operations” could achieve wide use [20]. The answer to this is the continuing modern history of prejudiced behavior by physicians (necessitating randomization and, when possible, blinding) and the tenuous quality of hypotheses as to what is “physiologically sound.” Most operations and medical therapies that appeared to work and have since been discarded had physiologic hypotheses provided before or supplied after their initial, uncontrolled “success.” It is physiologically sound, for example, to hypothesize that increased coronary flow improves myocardial oxygenation. Yet this is not necessarily so. Dipyridamole and nitroglycerin comparably increase subendocardial blood flow, but only nitroglycerin increases myocardial tissue oxygen [21]. Originally promoted specifically to increase myocardial oxygenation, dipyridamole does not and-worse-can cause a coronary “steal”
[=I-
A tendentious objection is that patients are being deceived in a randomized controlled trial [23]. This notion fails if the wording of the informed consent discussion is honest and complete. Others believe that a placebo should be provided only if there is a chance for spontaneous remission. That argument ignores the fact that the trial treatment may be immediately or ultimately
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harmful, and is generally added to other direct or supportive treatment. Another objection is that the mutual trust involved brings unequal parties into a joint venture. But this is always the case every time a physician talks a patient into taking any kind of treatment. A more reasonable objection is that failure to adjust dosage might eliminate a good drug either from overdosage or underdosage. This can be accommodated, if necessary, in a rising dosage design. One might claim that introducing a blinded randomized trial “ignores past knowledge,” but that argument ignores the tenuous quality of knowledge that is not derived from appropriately designed trials. If it is held that the result may pertain strictly to the groups studied, this applies equally to all kinds of therapeutic trials, controlled or uncontrolled. Finally, blinding can be imperfect, as in the case of a drug with detectable effects like beta-blocking agents. Quite so, but randomized allocation remains superior to biased allocation, and the trial design can provide third-party (“triple-blind”) evaluation of results.
2. 3.
4.
5.
6.
7.
6.
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10. 11.
Hultgren HH, Takaro T, Detre KM, Murphy ML: Evaluation of the efficacy of coronary bypass surgery. Am J Cardioll976; 42: 157-160. Proudfit WL: Criticisms of the VA randomized study of coronary bypass surgery. Clin Res 1978; 26: 236-240. DeBakey ME, Lawrie GM: Response to commentary of Hultgren et al. on aortocoronary-artery-bypass: assessment after 13 vears. JAMA 1979: 241: 2393-2395. Sheldon WC; Loop FD: Direct myocardial revascularization-1978. Progress report on the Cleveland Clinic experience. Cleve Clin Q 1976; 43: 97-108. Mathur VS, Guinn GA: Prospective randomized study of coronary bypass surgery in stable angina. The first 100 patients. Circulation 1975; 52 (suppl I): 1133-1140. Russell RO, Group Members: Unstable angina pectoris: natiil study gray, to compare surgical and medical therapy. II. In-hospital experience and initial follow-up results in patients with one, two and three vessel disease. Am J Cardiol 1978; 42: 839-848. Kloster RE, Kremkau EL, Ritzmann LW, Rahirntoola SH, Rosch J, Kanarek PH: Coronary bypass for stable angina. A prospective randomized study. N Engl J Mecl 1979; 300: 149-157. Spodick DH: Revascularization of the heart-numerators in search of denominators (editorial). Am Heart J 1971; 81: 149-157. Wright IS, Marple CD, Seek DF: Report of the Committee for Evaluation of Anticoagutants in Coronary Thrombosis. Am Heart J 1948; 38: 801-815. Sackett M, Gent M: Controversy in counting and attributing events in clinical trials. N Engl J Med 1979; 301: 1410. Hall TB: Medicine on the Santa Fe Trail. Dayton, Ohio: Mor-
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CONCLUSIONS Randomized controlled trials are increasingly accepted in principle but not always in practice, particularly for surgical therapies. Successful surgical randomized controlled trials demonstrate their feasibility, and reports of uncontrolled surgical trials now commonly bear a statement that a definitive answer requires a controlled ‘trial. Scientifically, the randomized controlled trial is the most powerful way to determine a result ascribable only to the trial treatment. Although randomized controlled trials can be imperfect or improperly conducted, they are designed to circumvent biased behavior by investigators. With candor in informed consent, the equal chance not to get a trial treatment makes the randomized controlled trial the most ethical design. Thus, scientific, behavioral, and ethical cases support the randomized controlled trial as the optimal method for investigation of nearly all therapeutic innovations and as a requirement for publication.
12. 13.
14. 15. 16.
17.
18. 19. 20. 21.
22.
23.
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ningside. 1971. Chalmers TC: Randomization of the first patient. Med Clin North Am 1975; 59: 1035-1038. Freiman JA, Chalmers TC. Smfth HS Jr, Kuebler RR: The importance of beta, the Type II error and sample size in the design and interpretation of the randomized control trial. N Engl J Med 1978; 299: 690-694. Beecher HK: Ethics and clinical research. N Engl J Med 1966; 274: 1354-1369. Lyon LJ, Zion MM: Randomized trials vs. data banking. Chest 1974; 50: 641-642. Cornfield J: Approaches to assessment of the efficacy of surgical revascularization. Bull NY Acad Med 1972; 48: 1126-1134. Lee KL, McNeer F, Starmer F, Harris PJ, Rosati RA: Clinical judgment and statistics. Lessons from a simulated randomized trial in coronary artery disease. Circulation 1980; 61: 508-515. Detre KM, Peduzzi P. Chan Y-K: Clinical judgment and statistics. Circulation 1981; 63: 239-240. Spodick DH: Medical journals and randomized trials. Am J Cardiol 1980; 45: 528-529. Etoncheck LI: Are randomized trials appropriate for evaluating new operations? N Engl J Med 1979; 301: 44-45. Winbury MM, Howe BB, Weiss HR: Effect of nitroglycerin and dipyridamole on epicardial and endocardlal oxygen tension. J Pharmacol Exp Ther 1971; 176: 184-199. Flameng W, Wunsten B, Schaper W: On the distribution of myocardial flow. Part II. Effects of arterial stenosis and vasodilation. Basic Res Cardiol 1974; 69: 435-446. Editorial: Controlled trials: planned deception? Lancet 1979; I: 534.
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