Clinical Application of Epidemiology

Ideas

Ideas about what might be a useful treatment arise from virtually any activity within medicine. These ideas are called  hypotheses to the extent that they are assertions about the natural world that are made for the purposes of empiric testing.

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may be effective. Aspirin, atropine, and digitalis are examples of naturally occurring substances that have become established as orthodox medicines after rigorous testing. Still other ideas come from trial and error. Some anticancer drugs have been found by methodically screening huge numbers of substances for activity in laboratory models. Ideas about treatment, but more often prevention, have also come from epidemiologic studies of populations. The Framingham Study, a cohort study of risk factors for cardiovascular diseases, was the basis for clinical trials of lowering blood pressure and serum cholesterol.

Testing Ideas

Some treatment effects are so prompt and powerful that their value is self-evident even without formal testing. Clinicians do not have reservations about the effectiveness of antibiotics for bacterial meningitis, or diuretics for edema. Clinical experience is sufficient.

In contrast, many diseases, including most chronic diseases, involve treatments that are considerably less dramatic. The effects are smaller, especially when an effective treatment is tested against another effective treatment. Also outcomes take longer to develop. It is then necessary to put ideas about treatments to a formal test, through clinical research, because a variety of circumstances, such as coincidence, biased comparisons, spontaneous changes in the course of disease, or wishful thinking, can obscure the true relationship between treatment and outcomes.

When knowledge of the pathogenesis of disease, based on laboratory models or physiologic studies in humans, has become extensive, it is tempting to predict effects in humans on this basis alone. However, relying solely on current understanding of mechanisms without testing ideas using strong clinical research on intact humans can lead to unpleasant surprises.

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the physical and social environment, and individual behaviors and preferences.

Of course, it is not always the case that ideas are debunked. The main point is that promising treatments have to be tested by clinical research rather than accepted into the care of patients on the basis of reasoning alone.

STUDIES OF TREATMENT EFFECTS

Treatment is any intervention that is intended to improve the course of disease after it is established. Treatment is a special case of  interventions in general that might be applied at any point in the natural history of disease, from disease prevention to palliative care at the end of life. Although usually thought of as medications, surgery, or radiotherapy, health care interventions can take any form, including relaxation therapy, laser surgery, or changes in the organization and financing of health care. Regardless of the nature of a well-intentioned intervention, the principles by which it is judged superior to other alternatives are the same.

Comparative effectiveness is a popular name for a not-so-new concept, the head-to-head comparison of two or more interventions (e.g., drugs, devices, tests, surgery, or monitoring), all of which are believed to be effective and are current options for care. Comparison is not just for effectiveness, but also for all clinically important end results of the interventions—both beneficial and harmful. Results can help clinicians and patients understand all of the consequences of choosing one or another course of action when both have been considered reasonable alternatives.

Observational and Experimental Studies of Treatment Effects

Two general methods are used to establish the effects of interventions: observational and experimental studies. The two differ in their scientific strength and feasibility.

The patients to be studied are first selected from a larger number of patients with the condition of interest. Using randomization, the patients are then divided into two (or more) groups of comparable prognosis. One group, called the experimental group, is exposed to an intervention that is believed to be better than current alternatives. The other group, called a control (or comparison) group, is treated the same in all ways except that its members are not exposed to the experimental intervention. Patients in the control group may receive a placebo, usual care, or the current best available treatment. The course of disease is then recorded in both groups, and differences in outcome are attributed to the intervention.

The main reason for structuring clinical trials in this way is to avoid confounding when comparing the respective effects of two or more kinds of treatments. The validity of clinical trials depends on how well they have created equal distribution of all determinants of prognosis, other than the one being tested, in treated and control patients.

Individual elements of clinical trials are described in detail in the following text.

Ethics

Under what circumstances is it ethical to assign treatment at random, rather than as decided by the patient and physician? The general principle, called  equipoise, is that randomization is ethical when there is no compelling reason to believe that either of the randomly allocated treatments is better than the other. Usually it is believed that the experimental intervention  might be better than the control but that has not been conclusively established by strong research. The primary outcome must be benefit; treatments cannot be randomly allocated to discover whether one is more harmful than the other. Of course, as with any human research, patients must fully understand the consequences of participating in the study, know that they can withdraw at any time without compromising their health care, and freely give their consent to participate. In addition, the trial must be stopped whenever there is convincing evidence of effectiveness, harm, or futility in continuing.

Sampling

Clinical trials typically require patients to meet rigorous inclusion and exclusion criteria. These are intended to increase the homogeneity of patients in the study, to strengthen internal validity, and to make it easier to distinguish the “signal” (treatment effect) from the “noise” (bias and chance).

Among the usual  inclusion criteria is that patients really do have the condition being studied. To be on the safe side, study patients must meet strict diagnostic criteria. Patients with unusual, mild, or equivocal manifestations of disease may be left out in the process, restricting generalizability.

Of the many possible  exclusion criteria, several account for most of the losses:

1. Patients with  comorbidity (diseases other than the one being studied) are typically excluded because the care and outcome of these other diseases can muddy the contrast between experimental and comparison treatments and their outcomes.

2. Patients are excluded if they are not expected to live long enough to experience the outcome events of interest.

3. Patients with contraindications to one of the treatments cannot be randomized.

4. Patients who refuse to participate in a trial are excluded, for ethical reasons described earlier in the chapter.

5. Patients who do not cooperate during the early stages of the trial are also excluded. This avoids wasted effort and the reduction in internal validity that occurs when patients do not take their assigned intervention, move in and out of treatment groups, or leave the trial altogether.

For these reasons, patients in clinical trials are usually a highly selected, biased sample of all patients with the condition of interest. As heterogeneity is restricted, the internal validity of the study is improved; in other words, there is less opportunity for differences in outcome that are not related to treatment itself. However, exclusions come at the price of diminished generalizability: Patients in the trial are not like most other patients seen in day-to-day care.

Example

Because of the high degree of selection in trials, it may require considerable faith to generalize the results of clinical trials to ordinary practice settings.

If there are not enough patients with the disease of interest, at one time and place, to carry out a scientifically sound trial, then sampling can be from multiple sites with common inclusion and exclusion criteria. This is done mainly to achieve adequate sample size, but it also increases generalizability, to the extent that the sites are somewhat different from each other.

Large simple trials are a way of overcoming the generalizability problem. Trial entry criteria are simplified so that most patients developing the study condition are eligible. Participating patients have to have accepted random allocation of treatment, but their care is otherwise the same as usual, without a great deal of extra testing that is part of some trials. Follow-up is for a simple, clinically important outcome, such as discharge from the hospital alive. This approach not only improves generalizability, it also makes it easier to recruit large numbers of participants at a reasonable cost so that moderate effect sizes (large effects are unlikely for most clinical questions) can be detected. Pragmatic trials, discussed later in the chapter, are another type of trial that attempts to improve generalizability of results as well.

Intervention

The intervention can be described in relation to three general characteristics: generalizability, complexity, and strength.

First, is the intervention one that is likely to be implemented in usual clinical practice? In an effort to standardize the intervention so that it can be easily described and reproduced in other settings, investigators may cater to their scientific, not their clinical colleagues by studying treatments that are not feasible in usual practice.

Third, is the intervention in question sufficiently different from alternative managements that it is reasonable to expect that the outcome will be affected? Some diseases can be reversed by treating a single, dominant cause. Treating hyperthyroidism with radioisotope ablation or surgery is one example. However, most diseases arise from a combination of factors acting in concert. Interventions that change only one of them, and only a small amount, cannot be expected to result in strong treatment effects. If the conclusion of a trial evaluating such interventions is that a new treatment is not effective when used alone, it should come as no surprise. For this reason, the first trials of a new treatment tend to enroll those patients who are most likely to respond to treatment and to maximize dose and compliance.

Comparison Groups

The value of an intervention is judged in relation to some alternative course of action. The question is not only whether a comparison is used, but also how appropriate it is for the research question. Results can be measured against one or more of several kinds of comparison groups.

· No Intervention. Do patients who are offered the experimental treatment end up better off than those offered nothing at all? Comparing treatment with no treatment measures the total effects of care and of being in a study, both specific and nonspecific.

· Being Part of a Study. Do treated patients do better than other patients who just participate in a study? A great deal of special attention is directed toward patients in clinical trials. People have a tendency to change their behavior when they are the target of special interest and attention because of the study, regardless of the specific nature of the intervention they might be receiving. This phenomenon is called the  Hawthorne effect. The reasons are not clear, but some seem likely: Patients want to please them and make them feel successful. Also, patients who volunteer for trials want to do their part to see that “good” results are obtained.

· Usual Care. Do patients given the experimental treatment do better than those receiving usual care—whatever individual doctors and patients decide? This is the only meaningful (and ethical) question if usual care is already known to be effective.

· Another Intervention. The comparator may be the current best treatment. The point of a “comparative effectiveness” study is to find out whether a new treatment is better than the one in current use.

Allocating Treatment

To study the effects of a clinical intervention free of confounding, the best way to allocate patients to treatment groups is by means of  random allocation (also referred to as  randomization). Patients are assigned to either the experimental or the control treatment by one of a variety of disciplined procedures—analogous to flipping a coin—whereby each patient has an equal (or at least known) chance of being assigned to any one of the treatment groups.

Random allocation of patients is preferable to other methods of allocation because only randomization has the ability to create truly comparable groups. All factors related to prognosis, regardless of whether they are known before the study takes place or have been measured, tend to be equally distributed in the comparison groups.

In the long run, with a large number of patients in a trial, randomization usually works as just described. However, random allocation does not guarantee that the groups will be similar; dissimilarities can arise by chance alone, particularly when the number of patients randomized is small. To assess whether “bad luck” has occurred, authors of randomized controlled trials often present a table comparing the frequency in the treated and control groups of a variety of characteristics, especially those known to be related to outcome. These are called  baseline characteristics because they are present after randomization and, therefore, should be equally distributed in the treatment groups.

Example

Differences Arising After Randomization

Not all patients in clinical trials participate as originally planned. Some are found to not have the disease they were thought to have when they entered the trial. Others drop out, do not take their medications, are taken out of the study because of side effects or other illnesses, or somehow obtain the other study treatment or treatments that are not part of the study at all. In this way, treatment groups that might have been comparable just after randomization become less so as time passes.

Patients May Not Have the Disease Being Studied

It is sometimes necessary (both in clinical trials and in practice) to begin treatment without knowing for certain whether the patient actually has the disease for which the treatment is designed.

Example

Randomized trials that include patients without disease could give misleading results. In such studies, because the number of patients with disease is reduced, it is more likely to miss a clinically important difference if it exists. Also, including patients without the diagnosis can lead to inefficiency in enrolling and gathering data on patients who would not contribute to the study's results (although in the gout study, confirming the diagnoses in all cases with joint analysis would likely have been more costly). Nevertheless, this kind of trial has the important advantage of providing information in a realistic setting on the consequences of a decision that a clinician must make with imperfect information.

Compliance

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people because it connotes a less subservient relationship between patient and doctor. Compliance is another characteristic that comes into play after randomization.

Although noncompliance suggests a kind of willful neglect of good advice, other factors also contribute. Patients may misunderstand which drugs and doses are intended, run out of prescription medications, confuse various preparations of the same drug, or have no money or insurance to pay for drugs. Taken together, noncompliance may limit the usefulness of treatments that have been shown to work under favorable conditions.

Compliance is particularly important in medical care outside the hospital. In hospitals, many factors act to constrain patients' personal behavior and render them compliant. Hospitalized patients are generally sicker and more frightened. They are in strange surroundings, dependent upon the skill and attention of the staff for everything, including their life. What is more, doctors, nurses, and pharmacists have developed a well-organized system for ensuring that patients receive what is ordered for them. As a result, clinical experience and medical literature developed on the wards may underestimate the importance of compliance outside the hospital, where most patients and doctors are and where following doctors' orders is less common.

In clinical trials, patients are typically selected to be compliant. During a  run-in period, in which placebo is given and compliance monitored, noncompliant patients can be detected and excluded before randomization.

Crossover

Patients may move from one randomly allocated treatment to another during follow-up, a phenomenon called  crossover. If exchanges between treatment groups take place on a large scale, it can diminish the observed differences in treatment effect compared to what might have been observed if the original groups had remained intact.

Cointerventions

After randomization, patients may receive a variety of interventions other than the ones being studied. For example, in a study of asthma treatment, they may receive not only the experimental drug but also different doses of their usual drugs and make greater efforts to control allergens in the home. If these occur unequally in the two groups and affect outcomes, they can introduce systematic differences between the groups that were not present when the groups were formed.

Blinding

Participants in a trial may change their behavior or reporting of outcomes in a systematic way (i.e., be biased) if they are aware of which patients are receiving which treatment. One way to minimize this effect is by  blinding, an attempt to make the various participants in a study unaware of the treatment group patients have been randomized to so that this knowledge cannot cause them to act differently, and thereby diminish the internal validity of the study.  Masking is a more appropriate metaphor, but blinding is the time-honored term.

The terms  single-blind (patients) and  doubleblind are sometimes used, but their meanings are ambiguous. It is better simply to describe what was done. A trial in which there is no attempt at blinding is called an  open trial or, in the case of drug trials, an  open label trial.

In drug studies, blinding is often made possible by using a placebo. However, for many important clinical questions, such as the effects of surgery, radiotherapy, diet, or the organization of medical care, blinding of patients and their physicians is difficult if not impossible.

Even when blinding appears to be possible, it is more often claimed than successful. Physiologic effects, such as lowered pulse rate with beta-blocking drugs and gastrointestinal upset or drowsiness with other drugs, may signal to patients whether they are taking the active drug or placebo.

Assessment of Outcomes

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reported along with hard measures such as death and recurrence of disease.

EFFICACY AND EFFECTIVENESS

First, can treatment help under  ideal circumstances? Trials that answer this question are called  efficacy trials or explanatory trials. Elements of ideal circumstances include patients who accept the interventions offered to them, follow instructions faithfully, get the best possible care, and do not have care for other diseases. Most randomized trials are designed in this way.

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may drop out of the study, and others find ways to take the treatment they were not assigned. The doctors and facilities may not be the best. In short, these trials describe results as most patients would experience them. The difference between efficacy and effectiveness has been described as the “implementation gap,” the gap between ideal care and ordinary care, and is a target for improvement in its own right.

Example

Efficacy trials often precede effectiveness trials. The rationale is that if treatment under the best circumstances is not effective, then effectiveness under ordinary circumstances is impossible. Also, if an effectiveness trial was done first and it showed no effect, the result could have been because the treatment at its best is just not effective or that the treatment really is effective but was not received.

Intention-to-Treat and Explanatory Trials

One question is: Which treatment choice is best at the time the decision must be made? To answer this question, analysis is according to which group the patients were assigned (randomized), regardless of whether these patients actually received the treatment they were supposed to receive. This way of analyzing trial results is called an  intention-totreat analysis. An advantage of this approach is that the question corresponds to the one actually faced by clinicians; they either offer a treatment or not. Also, the groups compared are as originally randomized, so this comparison has the full strength of a randomized trial. The disadvantage is that to the extent that many patients do not receive the treatment to which they were randomized, differences in effectiveness will tend to be obscured, increasing the chances of observing a misleadingly small effect or no statistical effect at all. If the study shows no difference, it will be uncertain whether the problem is the treatment itself or that it was not received.

Another question is whether the experimental treatment itself is better. For this question, the proper analysis is according to the treatment each patient actually received, regardless of the treatment to which they were randomized. Trials analyzed in this way are called  per-protocol analyses (also called  explanatory analyses) because they assess whether actually taking the treatments, rather than just being offered them, makes a difference. The problem with this approach is that unless most patients receive the treatment to which they are assigned, the study no longer represents a randomized trial; it is simply a cohort study. One must be concerned about dissimilarities among groups, other than the experimental treatment, and must use methods such as restriction, matching, stratification, or adjustment to achieve comparability, just as one would for any nonexperimental study.

In general, intention-to-treat analyses are more relevant to effectiveness questions, whereas per-protocol analyses are consistent with the purposes of efficacy trials, although aspects of the trial other than how they are analyzed matter too. The primary analysis is usually intention-to-treat, but both are reported. Both approaches are legitimate, with the right one depending on the question being asked. To the extent that patients in a trial follow the treatment to which they were randomized, these two analyses will give similar results.

SUPERIORITY, EQUIVALENCE, AND NONINFERIORITY

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important question is whether a treatment is no less effective than another. A typical example is when a new drug is safer, cheaper, or easier to administer than the established one and would, therefore, be preferable if it were as effective. In  noninferiority trials, the purpose is to show that a new treatment is unlikely to be less effective, at least to a clinically important extent, than the currently accepted treatment, which has been shown in other studies to be more effective than placebo. The focus of the question is one directional—whether a new treatment is not worse—without regard to whether it might be better.

It is statistically impossible to establish that a treatment is not at all inferior to another. However, a study can rule out an effect that is less than a predetermined “minimum clinically important difference,” also called an  noninferiority margin, the smallest difference in effect that is still considered clinically important. The noninferiority margin actually takes into account both this clinical difference plus the statistical imprecision of the study. The following is an example of a noninferiority trial.

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care units and not in others when physicians see patients in both settings over time? For these reasons, randomizing clusters rather than patients can be the best approach in some circumstances.

There are other variations on the usual (“parallel group”) randomized controlled trials.  Crossover trials expose patients first to one of two randomly allocated treatments and later to the other. If it can be assumed that effects of the first exposure are no longer present by the time of the second exposure, perhaps because treatment is short-lived or there has been a “wash-out” period between exposures, then each patient will have been exposed to each treatment in random order. This controls for differences in responsiveness among patients not related to treatment effects.

A  stepped wedge cluster trial combines aspects of crossover and cluster designs. Like other cluster trials, randomization occurs at the group level. Unlike traditional cluster trials (where half of the clusters are randomized to treatment or controls throughout the trial), all clusters at the beginning of the trial are controls. Then, at regular intervals (steps), some clusters are randomized to crossover and receive the intervention, and continue the intervention thereafter. At each interval, more clusters move from control to intervention status, until by the end of the trial all clusters are exposed to the intervention.

TAILORING THE RESULTS OF TRIALS TO INDIVIDUAL PATIENTS

Clinical trials describe what happens on average. They involve pooling the experience of many patients who may be dissimilar, both to one another and to the patients to whom the trial results will be generalized. How can estimates of treatment effect be obtained that more closely match individual patients?

Subgroups

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(or  N = 1), is an improvement over the time-honored process of trial and error. A patient is given one treatment or another, such as an active treatment or placebo, in random order, each for a brief period of time. The patient and physician are blinded to which treatment is given. Outcomes, such as a simple preference for a treatment or a symptom score, are assessed after each period. After many repetitions patterns of responses are analyzed statistically, much as one would for a more usual randomized controlled trial. This method is useful for deciding on the care of individual patients when activity of disease is unpredictable, response to treatment is prompt, and there is no carryover effect from period to period. Examples of diseases for which the method can be used include migraine headaches, asthma, and fibromyalgia. For all their intellectual appeal, however,  N of 1 trials are uncommon and even less often published.

ALTERNATIVES TO RANDOMIZED CONTROLLED TRIALS

Randomized controlled trials are the gold standard for studies of the effectiveness of interventions. Only large randomized trials can definitively eliminate confounding as an alternative explanation for observed results.

Limitations of Randomized Trials

However, the availability of several well-conducted randomized controlled trials does not necessarily settle a question. For example, after five decades and dozens of randomized controlled trials the effectiveness of corticosteroids for septic shock remains controversial. The heterogeneity of trial results seems partly related to differences in dose and duration of the drug, the proportion of patients with relative adrenal insufficiency, and whether the outcome is reversal of shock or survival. That is, the trials were of the same general questions but very different specific questions.

Clinical trials also suffer from practical limitations. They are expensive; major drug trials often cost tens of millions of dollars. Logistics can be daunting, especially in maintaining similar methods across sites in multicenter trials and in maintaining the integrity of allocation concealment. Randomization itself remains a hindrance, if not to the conduct of trials at all then to full, unbiased participation. It is particularly difficult to convince patients to be randomized when a practice has become well established in the absence of conclusive evidence of its benefit.

For these reasons, clinical trials are not available to guide clinicians in many important treatment decisions, but clinical decisions must be made nonetheless. What are the alternatives to randomized controlled trials, and how credible are they?

Observational Studies of Interventions

In the absence of a consensus favoring one mode of treatment over others, various treatments are given according to the preferences of each individual patient and doctor. As a result, in the course of ordinary patient care, large numbers of patients are treated in various ways and go on to manifest the effects. When experience with these patients is captured and properly analyzed, it can complement the information available from randomized trials, suggest where new trials are needed, and provide answers where trials are not yet available.

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receiving the various treatments are likely to differ not only in their treatment but in other ways as well.

Especially troubling is  confounding by indication (sometimes called “reverse causation”), which occurs when whatever prompted the doctor to choose a treatment (the “indication”) is a cause of the observed outcome, not just the treatment itself. For example, patients may be offered a new surgical procedure because they are at a good surgical risk or have less aggressive disease and, therefore, seem especially likely to benefit from the procedure. To the extent that the reasons for treatment choice are known, they can be taken into account like any other confounders.

Example

Clinical Databases

Sometimes, databases are available that include baseline characteristics and outcomes for a large number of patients. Clinicians can match characteristic of a specific patient to similar patients in the database and see what their outcomes were. When use of the database is not part of formal research, there is no accounting for confounding and effect modification, but the predictions do have the advantage of being about real-world patients, not those as highly selected as in most clinical trials.

Randomized Versus Observational Studies?

Are observational studies a reliable substitute for randomized controlled trials? With controlled trials as the gold standard, most observational studies of most questions get the right answer. However, there are dramatic exceptions. For example, observational studies have consistently shown that antioxidant vitamins are associated with lower cardiovascular risk, but large randomized controlled trials have found no such effect. Therefore, clinicians can be guided by observational studies of treatment effects when there are no randomized trials to rely on, but they should maintain a healthy skepticism.

Well-designed observational studies of interventions have some strengths that complement the limitations of usual randomized trials. They count the effects of actual treatment, not just of offering treatment, which is a legitimate question in its own right. They commonly include most people as they exist in naturally occurring populations, in either clinical or community settings, without severe inclusion and exclusion criteria. They can often accomplish longer follow-up than trials, matching the time it takes for disease and outcomes to develop. By taking advantage of treatments and outcomes as they happen, observational studies (especially case control studies and historical cohort studies using health records) can answer clinical questions more quickly than it takes to complete a randomized trial. Of course, they are also less expensive.

PHASES OF CLINICAL TRIALS

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that is well tolerated and safe (at least for high-frequency, severe side effects) and include very small numbers of patients (perhaps a dozen) without a control group.  Phase II trials provide preliminary information on whether the drug is efficacious and the relationship between dose and efficacy. These trials may be controlled but include too few patients in treatment groups to detect any but the largest treatment effects.  Phase III trials are randomized trials and can provide definitive evidence of efficacy and rates of common side effects. They include enough patients, sometimes thousands, to detect clinically important treatment effects and are usually published in biomedical journals.