Randomized CLinical Trail

Editor's Notes

• #4: Our objective, both in clinical practice and in public health, is to modify the natural history of a disease so as to prevent or delay death or disability and to improve the health of the patient or the population. The challenge is to select the best available preventive or therapeutic measures to achieve this goal. To do so, we need to carry out studies that determine the value of these measures. The randomized trial is considered the ideal design for evaluating both the efficacy and the side effects of new forms of intervention.
• #5: The notion of using a rigorous methodology to assess the efficacy of new drugs, or of any new modalities of care, is not recent. In 1883, Sir Francis Galton, the British anthropologist, explorer, and eugenicist, who had a strong interest in human intelligence, wrote as follows: It is asserted by some, that men possess the faculty of obtaining results over which they have little or no direct personal control, by means of devout and earnest prayer, while others doubt the truth of this assertion. The question regards a matter of fact, that has to be determined by observation and not by authority; and it is one that appears to be a very suitable topic for statistical inquiry. … Are prayers answered, or are they not? … [D]o sick persons who pray, or are prayed for, recover on the average more rapidly than others? As with many pioneering ideas in science and medicine, many years were to pass before this suggestion was actually implemented. In 1965 Joyce and Welldon reported the results of a double-blind randomized trial of the efficacy of prayer. The findings of this study did not indicate that patients who were prayed for derived any special benefits from that prayer. However, a more recent study by Byrd evaluated the effectiveness of intercessory prayer in a coronary care unit population using a randomized double-blind protocol. The findings from this study suggested that prayer had a beneficial therapeutic effect. Which is correct? the randomized trial design also has major applicability to studies outside the clinical setting, such as community-based trials. The principles apply equally to evaluations of preventive (such as screening programs for the early detection of disease) and other measures (e.g., behavioral interventions). Trials are essentially experiments which are under the control of the investigator. While in observational studies the investigator watches what unfolds but does not interfere or control. In 1537 Ambroise Paré was responsible for the treatment of the wounded after the capture of the castle of Villaine. At length my oil lacked and I was constrained to apply in its place a digestive made of yolks of eggs, oil of roses and turpentine. That night I could not sleep at my ease, fearing that by lack of cauterization I would find the wounded upon which I had not used the said oil, dead from the poison. I raised myself early to visit them, when beyond my hope I found those to whom I had applied the digestive medicament feeling but little pain, their wounds neither swollen nor inflamed, and having slept through the night. The others to whom I had applied the boiling oil were feverish with much pain and swelling about their wounds. Then I determined never again to burn thus so cruelly the poor wounded. Such unplanned trials, has been carried out many times when a therapy thought to be the best available has been in short supply and has not been available for all of the patients who needed it.
• #6: Scottish surgeon James Lind in 1747 Lind became interested in scurvy, which killed thousands of British seamen each year. He was intrigued by the story of a sailor who had developed scurvy and had been put ashore on an isolated island, where he subsisted on a diet of grasses and then recovered from the scurvy. Lind conducted an experiment, which he described as follows: I took 12 patients in the scurvy on board the Salisbury at sea. The cases were as similar as I could have them … they lay together in one place and had one diet common
• #7: Interestingly, the idea of a dietary cause of scurvy proved unacceptable in Lind’s day. Only 47 years later did the British Admiralty allow the experiment to be repeated—this time on an entire fleet of ships. The results were so dramatic that, in 1795, the Admiralty made lemon juice a required part of the standard diet of British seamen and later changed this to lime juice. Scurvy essentially disappeared from British sailors, who, even today, are referred to as “limeys.” The issue of comparison is important because we want to be able to derive a causal inference regarding the relationship of a treatment and subsequent outcome. The problem of inferring a causal relationship from a sequence of events without any comparison is demonstrated in a story – One day when I was a junior medical student, a very important Boston surgeon visited the school and delivered a great treatise on a large number of patients who had undergone successful operations for vascular reconstruction. At the end of the lecture, a young student at the back of the room timidly asked, “Do you have any controls?” Well, the great surgeon drew himself up to his full height, hit the desk, and said, “Do you mean did I not operate on half of the patients?” The hall grew very quiet then. The voice at the back of the room very hesitantly replied, “Yes, that’s what I had in mind.” Then the visitor’s fist really came down as he thundered, “Of course not. That would have doomed half of them to their death.” God, it was quiet then, and one could scarcely hear the small voice ask, “Which half?
• #8: If the new treatment is associated with a better outcome, we would expect to find better outcomes in more persons of the new treatment group than the current treatment group. Some of the issues that must be considered in the design of randomized trials. Chief among them is specification of the study “arms,” or treatments. These must be clearly stated with criteria for their measurement, as well as the duration of the treatments and how long the study will last. First, let’s start with who is eligible to be studied.
• #10: If the new treatment is associated with a better outcome, we would expect to find better outcomes in more of the new treatment group than the current treatment group.
• #12: Issues in Historical Controls we may set up a very meticulous system for data collection from the patients currently being treated. But, of course, we cannot do that for the patients who were treated in the past, for whom we must abstract data from medical records which are likely useful for managing individual care but are fraught with error and omissions when used for research purposes. if we observe a difference in outcome between the early group and the later group, we will not be sure that the difference is due to the therapy because many things other than the therapy hange over calendar time (e.g., ancillary supportive therapy, living conditions, nutrition, and lifestyles). However, at times, this type of design may be useful. For example, when a disease is uniformly fatal and a new drug becomes available, a decline in case-fatality that parallels use of the drug would strongly support the conclusion that the new drug is having an effect. Examples include the discovery of insulin to treat diabetes, of penicillin to treat serious infections, and of tyrosine kinase inhibitors (TKIs) such as imatinib (Gleevec) to treat chronic myelocity leukemia.
• #14: Because of the importance of the problems posed by historical controls and the difficulties of dealing with changes over calendar time, an alternative approach is to use simultaneous controls that are not selected in a randomized manner. The problem with selecting simultaneous controls in a nonrandomized manner is illustrated by the following story: A sea captain was given samples of anti-nausea pills to test during a voyage. The need for controls was carefully explained to him. Upon return of the ship, the captain reported the results enthusiastically. “Practically every one of the controls was ill, and not one of the subjects had any trouble. Really wonderful stuff.” A skeptic asked how he had chosen the controls and the subjects. “Oh, I gave the stuff to my seamen and used the passengers as controls.” In a trial of anticoagulant therapy after World War II, in which this day-of-the-month method was used, it was discovered that more patients than expected were admitted on odd-numbered days. The investigators reported that “as physicians observed the benefits of anticoagulant therapy, they speeded up, where feasible, the hospitalization of those patients … who would routinely have been hospitalized on an even day in order to bring as many as possible under the odd-day deadline.”
• #15: The goal of randomization is to eliminate the possibility that the investigator will know what the assignment of the next patient will be, because such knowledge introduces the possibility of bias on the part of the investigator regarding the treatment group to which each participant will be assigned. Recognizing that the vaccinations were selectively performed in children from families that were more likely to be conscious of health and related issues, the investigators realized that it was possible that the mortality rate from tuberculosis was lower in the vaccinated group not because of the vaccination itself but because these children were selected from more health-conscious families that had a lower risk of mortality from tuberculosis, with or without vaccination. To address this problem, a change was made in the study design: alternate children were vaccinated and the remainder served as controls. This does not constitute randomization, but it was a marked improvement over the initial design.
• #18: The columns are numbered along the top, 00–04, 05–09, and so on. This means that the number in Column 00 is 5, the number in Column 01 is 6, the number in Column 04 is 8, etc Similarly, the rows are numbered along the left, 00, 01, 02, and so on. Thus it is possible to refer to any digit in the table by giving its column and row numbers. Let us say that we are conducting a study in which there will be two groups: therapy A and therapy B. In this example, we will consider every odd number an assignment to A and every even number an assignment to B. We close our eyes and put a finger anywhere on the table, and write down the column and row number that was our starting point. We also write down the direction we will move in the table from that starting point (horizontally to the right, horizontally to the left, up, or down). Let us assume that we point to the “5” at the intersection of column 07 and row 07 and move horizontally to the right. The first patient, then, is designated by an odd number, 5, and will receive therapy A. The second patient is also designated by an odd number, 3, and will receive therapy A. The third is designated by an even number, 8, and will receive therapy B, and so on.
• #19: Let us assume, for example, that a decision has been made that odd digits will designate assignment to treatment A and even digits will designate treatment B. The treatment assignment that is designated by the random number is written on a card, and this card is placed inside an opaque envelope. Each envelope is labeled on the outside: Patient 1, Patient 2, Patient 3, and so on, to match the sequence in which the patients are enrolled in the study. For example, if the first random number is 2, a card for therapy B would be placed in the first envelope; if the next random number is 7, a card for therapy A in the second one, and so on, as determined by the random numbers. The envelopes are then sealed. When the first patient is enrolled, envelope 1 is opened and the assignment is read; this process is repeated for each of the remaining patients in the study. However, this process is not foolproof. The following anecdote illustrates the need for careful quality control of any randomized study: In a randomized study comparing radical and simple mastectomy for breast cancer, one of the surgeons participating was convinced that radical mastectomy was the treatment of choice and could not reconcile himself to performing simple mastectomy on any of his patients who were included in the study. When randomization was carried out for his patients and an envelope was opened that indicated simple mastectomy for the next assignment, he would set the envelope aside and keep opening envelopes until he reached one with an assignment to radical mastectomy. What is reflected here is the conflict experienced by many clinicians who enroll their own patients in randomized trials. On the one hand, the clinician has the obligation to do the best he or she can for the patient; on the other hand, when a clinician participates in a clinical trial, he or she is, in effect, asked to step aside from the usual decision-making role and essentially to “flip a coin” to decide which therapy the patient will receive. Thus there is often an underlying conflict between the clinician’s role and the role of the physician participating in a clinical trial, and as a result, unintentional biases may occur.
• #23: First, we would like the subjects not to know which group they are assigned to. This is of particular importance when the outcome is a subjective measure, such as self-reported severity of headache or low back pain. If the patient knows that he or she is receiving a new therapy, enthusiasm and certain psychological factors on the part of the patient may operate to elicit a positive response even if the therapy itself had no positive biologic or clinical effect. How can subjects be masked? One way is by using a placebo, an inert substance that looks, tastes, and smells like the active agent. However, use of a placebo does not automatically guarantee that the patients are masked (blinded). Some participants may try to determine whether they are taking the placebo or active drug. For example, in a randomized trial of vitamin C for the common cold, patients were blinded by use of a placebo and were then asked whether they knew or suspected which drug they were taking. As seen in Table 10.4, of the 52 people who were receiving vitamin C and were willing to make a guess, 40 stated they had been receiving vitamin C. Of the 50 who were receiving placebo, 39 said they were receiving placebo. How did they know? They had bitten into the capsule and could tell by the bitter taste. Some years ago, a study was being conducted to evaluate coronary care units as compared to domiciliary care in the treatment of myocardial infarction. It was planned in the following manner: Patients who met strict criteria for categories of myocardial infarction [were to] be randomly assigned either to the group that was admitted immediately to the coronary care unit or to the group that was returned to their homes for domiciliary care. When the preliminary data were presented, it was apparent in the early phases of the experiment that the group of patients labeled as having been admitted to the coronary care unit did somewhat better than the patients sent home. An enthusiast for coronary care units was uncompromising in his insistence that the experiment was unethical and should be terminated and that the data showed that all such patients should be admitted to the coronary care unit. The statistician then revealed the headings of the data columns had been interchanged and that really the home care group seemed to have a slight advantage. The enthusiast then changed his mind and could not be persuaded to declare coronary care units unethical. Does it make any difference that they knew? The data suggest that the rate of colds was higher in subjects who received vitamin C but thought they were receiving placebo than in subjects who received placebo but thought they were receiving vitamin C. Thus we must be very concerned about lack of masking or blinding of the subjects and its potential effects on the results of the study, particularly when we are dealing with subjective end points. Use of a placebo is also important for studying the rates of side effects and reactions. The Physicians’ Health Study was a randomized trial of the use of aspirin to prevent myocardial infarctions. Table shows the side effects that were reported in groups receiving aspirin and those receiving placebo in this study. Note the high rates of reported reactions in people receiving placebo. Thus it is not sufficient to say that 34% of the people receiving aspirin had gastrointestinal symptoms; what we really want to know is the extent to which the risk of side effects is increased in people taking aspirin compared with those not taking aspirin (i.e., those taking placebo). Thus the placebo plays a major role in identifying both the real benefits of an agent and its side effects. In addition to blinding the subjects, we also want to mask (or blind) the observers or data collectors in regard to which group a patient is in. The masking of both participants and study personnel is called “double blinding.”
• #26: We are studying 1,000 patients and are concerned that sex and age are important determinants of prognosis. If we randomize, we do not know what the composition of the groups may be in terms of sex and age; therefore we decide to use stratified randomization. We first stratify the 1,000 patients by sex into 600 males and 400 females. We then separately stratify the males by age and the females by age. We now have four groups (strata): younger males, older males, younger females, and older females. We now randomize within each group (stratum), and the result is a new treatment group and a current treatment group for each of the four groups. As in randomization without stratification, we end up with two intervention groups, but having initially stratified the groups, we increase the likelihood that the two groups will be comparable in terms of sex and age.
• #27: In this example, a new treatment is being compared with current treatment. Subjects are randomized to new treatment or current treatment. After being observed for a certain period of time on one therapy and after any changes are measured, the patients are switched to the other therapy. Both groups are then again observed for a certain period of time. Changes in group 1 patients while they are on the new treatment can be compared with changes in these patients while they are on the current treatment. Changes in group 2 patients while they are on the new treatment can also be compared with changes in these patients while they are on the current treatment. Thus each patient can serve as his or her own control, holding constant the variation between individuals in many characteristics that could potentially affect a comparison of the effectiveness of two agents. This type of design is very attractive and useful provided that certain cautions are taken into account. First is that of carryover: For example, if a subject is changed from therapy A to therapy B and observed under each therapy, the observations under therapy B will be valid only if there is no residual carryover from therapy A. There must be enough of a “washout period” to be sure none of therapy A, or its effects, remains before starting therapy B. Second, the order in which the therapies are given may elicit psychological responses. Patients may react differently to the first therapy given in a study as a result of the enthusiasm that is often accorded a new study; this enthusiasm may diminish over time. We therefore want to be sure that any differences observed are indeed due to the agents being evaluated, and not to any effect of the order in which they were administered. Finally, the planned crossover design is clearly not possible if the new therapy is surgical or if the new therapy cures the disease. A more important consideration is that of an unplanned crossover. Fig. 10.6A shows the design of a randomized trial of coronary bypass surgery, comparing it with medical care for coronary heart disease.
• #29: Carryover effect: For example, if a subject is changed from therapy A to therapy B and observed under each therapy, the observations under therapy B will be valid only if there is no residual carryover from therapy A. There must be enough of a “washout period” to be sure none of therapy A, or its effects, remains before starting therapy B. Second, the order in which the therapies are given may elicit psychological responses. Patients may react differently to the first therapy given in a study as a result of the enthusiasm that is often accorded a new study; this enthusiasm may diminish over time. We therefore want to be sure that any differences observed are indeed due to the agents being evaluated, and not to any effect of the order in which they were administered. Finally, the planned crossover design is clearly not possible if the new therapy is surgical or if the new therapy cures the disease.
• #30: Unplanned crossovers pose a serious challenge in analyzing the data. If we analyze according to the original assignment (called an intention to treat analysis), we will include in the surgical group some patients who received only medical care, and we will include in the medical group some patients who had surgery. In other words, we would compare the patients according to the treatment to which they were originally randomized, regardless of what treatment actually occurred. Fig. 10.6E shows an intention to treat analysis in which we compare the group in pink (randomized to surgical treatment) with the group in yellow (randomized to medical treatment). If, however, we analyze according to the treatment that the patients actually receive (as treated analysis), we will have broken, and therefore lost the benefits of, the randomization. No perfect solution is available for this dilemma. Current practice is to perform the primary analysis by intention to treat—according to the original randomized assignment. We would hope that the results of other comparisons would be consistent with this primary approach. The bottom line is that because there are no perfect solutions, the number of unplanned crossovers must be kept to a minimum. Obviously, if we analyze according to the original randomization and there have been many crossovers, the interpretation of the study results will be questionable. If the number of crossovers becomes large, the problem of interpreting the study results may become insurmountable.
• #31: Assuming that two drugs are to be tested, the anticipated outcomes for the two drugs are different, and their modes of action are independent, one can economically use the same study population for testing both drugs. If the effects of the two treatments are indeed completely independent, we could evaluate the effects of treatment A by comparing the results in cells a + c to the results in cells b + d (Fig. 10.8A). Similarly, the results for treatment B could be evaluated by comparing the effects in cells a + b to those in cells c + d (see Fig. 10.8B). In the event that it is decided to terminate the study of treatment A, this design permits continuing the study to determine the effects of treatment B.
• #34: An example of a factorial design is seen in the Physicians’ Health Study. More than 22,000 physicians were randomized using a 2 × 2 factorial design that tested aspirin for primary prevention of cardiovascular disease and beta carotene for primary prevention of cancer. Each physician received one of four possible interventions: both aspirin and beta carotene, neither aspirin nor beta carotene, aspirin and beta carotene placebo, or beta carotene and aspirin placebo. The resulting four groups are shown in Figs. 10.9 and 10.10. The aspirin part of the study (Fig. 10.11A) was terminated early, on the advice of the external data monitoring board, because a statistically significant 44% decrease in the risk of first myocardial infarction was observed in the group taking aspirin. The randomized beta carotene component (see Fig. 10.11B) continued until the originally scheduled date of completion. After 12 years of beta carotene supplementation, no benefit or harm was observed in terms of the incidence of cancer or heart disease or death from all causes. Subsequent reports have shown greater risk of cancer with beta carotene in smokers.17
• #35: Patients may agree to be randomized, but following randomization they may not comply with the assigned treatment. Noncompliance may be overt or covert: On the one hand, people may overtly articulate their refusal to comply or may stop participating in the study. These noncompliers are also called dropouts from the study. On the other hand, people may just stop taking the agent assigned without admitting this to the investigator or the study staff. Whenever possible, checks on potential noncompliance are built into the study. These may include, for example, urine tests for the agent being tested or for one of its metabolites. Another problem in randomized trials has been called drop-ins. Patients in one group may inadvertently take the agent assigned to the other group. For example, in a trial of the effect of aspirin for prevention of myocardial infarction, patients were randomized to aspirin or to no aspirin. However, a problem arose in that, because of the large number of over-the-counter preparations that contain aspirin, many of the control patients might well be taking aspirin without knowing it. Two steps were taken to address this problem: (1) controls were provided with lists of aspirin-containing over-the-counter preparations that they should avoid, and (2) urine tests for salicylates were carried out both in the aspirin group and in the controls. The net effect of noncompliance on the study results will be to reduce any observed differences (i.e., driving the difference toward the null) because the treatment group will include some who did not receive the therapy, and the no-treatment group may include some who received the treatment. Thus the groups will be less different in terms of therapy than they would have been had there been no noncompliance, so that even if there is a difference in the effects of the treatments, it will appear much smaller. One approach that was used in the Veterans Administration Study of the Treatment of Hypertension was to carry out a pilot study in which compliers and noncompliers were identified. When the actual full study was later carried out, the study population was limited to those who had been compliers during the pilot study (sometimes referred to as a “run-in period”). The problem with this approach is that when we want to generalize from the results of such a study, we can only do so to other populations of compliers, which may be different from the population in any free-living community, which would consist of both compliers and noncompliers. Table 10.6 shows data from the Coronary Drug Project reported by Canner and coworkers.18 This study was a comparison of clofibrate and placebo for lowering cholesterol. The table presents the mortality in the two groups. No large difference in 5-year mortality was seen between the two groups. The investigators speculated that perhaps this was the result of the patients not having taken their medication. Table 10.7 shows the results of separating the clofibrate subjects into good compliers and poor compliers. Here we see the 5-year mortality was 24.6% in the poor-complier group