3. What Is the Question?

The primary question should be the one the investigators and sponsors are most interested in answering and that is capable of being adequately answered. It is the question upon which the sample size of the study is based, and which must be emphasized in the reporting of the trial results. The primary question may be framed in the form of testing a hypothesis because most of the time an intervention is postulated to have a particular outcome which, on the average, will be different from (or, in the case of noninferiority trials, not worse than) the outcome in a control group [2]. The outcome may be a clinical event such as improving survival, ameliorating an illness or disease complications, reducing symptoms, or improving quality of life; modifying an intermediate or surrogate characteristic such as blood pressure; or changing a biomarker such as a laboratory value.

Sometimes, trials are designed with more than one primary question. This may be appropriate, depending on the trial design. For example, factorial design trials are specifically conducted to answer more than one question. If done in the context of the usual parallel design trial, statistical adjustments might need to be made to account for the additional question(s) and the sample size made adequate. See Chap. 8 for further discussion of the issue of adjustments in parallel design trials.

There may also be a variety of subsidiary, or secondary questions that are usually related to the primary question. The study may be designed to help address these, or else data collected for the purpose of answering the primary question may also elucidate the secondary questions. They can be of two types. In the first, the response variable is different than that in the primary question. For example, the primary question might ask whether mortality from any cause is altered by the intervention. Secondary questions might relate to incidence of cause-specific death (such as cancer mortality), incidence of non-fatal renal failure, or incidence of stroke. Many investigators also assess patient-reported outcomes such as health-related quality of life (see Chap. 13).

The second type of secondary question relates to subgroup hypotheses. For example, in a study of cancer therapy, the investigator may want to look specifically at people by gender, age, stage of disease at entry into the trial or by presence or absence of a particular biomarker or genetic marker. Such subsets of people in the intervention group can be compared with similar people in the control group. Subgroup hypotheses should be 1) specified before data collection begins, 2) based on reasonable expectations, and 3) limited in number. In any event, the number of participants in most subgroups is usually too small to prove or disprove a subgroup hypothesis. One should not expect significant differences in subgroup unless the trial was specifically designed to detect them. Failure to find significant differences should not be interpreted to mean that they do not exist. Investigators should exercise caution in accepting subgroup results, especially when the overall trial results are not significant. A survey of clinical trialists indicated that inappropriate subgroup analyses were considered one of the two major sources of distortion of trial findings [3]. Generally, the most useful reasons for considering subgroups are to examine consistency of results across pre-defined subgroups and to create hypotheses that can be tested in future trials and meta-analyses.

There has been recognition that certain subgroups of people have not been adequately represented in clinical research, including clinical trials [4]. In the United States, this has led to requirements that women and minority populations be included in appropriate numbers in trials supported by federal government agencies [5]. The debate is whether the numbers of participants of each sex and racial/ethnic group must be adequate to answer the key questions that the trial addresses, or whether there must merely be adequate diversity of people. Many trials are international in scope. Whether one should examine outcome data by country or region has been debated [6]. Are observed differences in intervention effect by geographic region true or due to the play of chance [7, 8]? One might expect that culture, medical care system, genetic makeup, and other factors could affect the magnitude, or even existence of benefit from a new intervention. But, as has been noted [9, 10], the design and size of the trial should be driven by reasonable expectations that the intervention will or will not operate materially differently among the various subsets of participants. If such variability is expected, it is appropriate to design the trial to detect those differences. If not, adequate diversity with the opportunity to examine subgroup responses at the end of the trial (and conduct additional research if necessary) is more appropriate.

Secondary questions raise several trial methodological issues; for example, if enough statistical tests are done, a few will be significant by chance alone when there is no true intervention effect. An example was provided by the Second International Study of Infarct Survival (ISIS-2), a factorial design trial of aspirin and streptokinase in patients with acute myocardial infarction [11]. To illustrate the hazards of subgroup analyses, the investigators showed that participants born under the Gemini or Libra astrological birth signs had a somewhat greater incidence of vascular and total mortality on aspirin than on no aspirin, whereas for all other signs, and overall, there was an impressive and highly significant benefit from aspirin. Therefore, when a number of tests are carried out, results should be interpreted cautiously as they may well be due to chance. Shedding light or raising new hypotheses, and perhaps conducting meta-analyses, are more proper outcomes of these analyses than are conclusive answers. See Chap. 18 for further discussion of subgroup and meta-analyses.

Both primary and secondary questions should be important and relevant scientifically, medically, or for public health purposes. Participant safety and well-being must always be considered in evaluating importance. Potential benefit and risk of harm should be looked at by the investigator, as well as by local ethical review committees, and often, independent data monitoring committees.

Important questions that can be answered by clinical trials concern adverse effects of or reactions to therapy (Chap. 12). Here, unlike the primary or secondary questions, it is not always possible to specify in advance the questions to be answered. What adverse effects might occur, and their severity, may be unpredictable. Furthermore, rigorous, convincing demonstration of serious toxicity is usually not achieved, because it is generally thought unethical to continue a study to the point at which a drug has been conclusively shown to be more harmful than beneficial [12–14]. Investigators traditionally monitor a variety of laboratory and clinical measurements, look for possible adverse events, and compare these in the intervention and control groups. Some of the most serious adverse effects, however, are rare and do not occur commonly enough to be detected reliably in clinical trials. Statistical significance and the previously mentioned problem of multiple response variables become secondary to clinical judgment and participant safety. While this will lead to the conclusion that some purely chance findings are labeled as adverse effects, responsibility to the participants requires a conservative attitude toward safety monitoring, particularly if an alternative therapy is available. Trials have been stopped early for less than statistically convincing evidence of adverse effects [15–17]. In such cases, only other trials of the identical or related interventions noting the same adverse effect (as were the situations for these examples of antiarrhythmic therapy in people with heart disease, beta carotene in people at high risk of lung cancer, and an angiotensin-converting enzyme inhibitor in acute myocardial infarction) or convincing nonclinical studies will provide irrefutable evidence that the adverse finding is true. In the last case cited, other studies contradicted the finding.

Often a clinical trial can be used to answer questions which do not bear directly on the intervention being tested, but which are nevertheless of interest. The structure of the trial and the ready access to participants may make it the ideal vehicle for such investigations. Large trials, in particular, create databases that offer opportunities to better understand the disease or condition, treatment, predictors of outcomes, and new hypotheses that can be tested. The Group Utilization of Streptokinase and Tissue Plasminogen Activator for Occluded Coronary Arteries (GUSTO-1) trial [18] provides an example of use of a dataset that yielded over 100 subsequent publications, including one identifying predictors of mortality [19]. The Assessment of Pexelizumab in Acute Myocardial Infarction (APEX AMI) trial [20] found no benefit from the complement inhibitor, pexelizumab, but so far, over 50 manuscripts regarding primary angioplasty in acute ST-elevation myocardial infarction have been published.

Clinical trials can also be used to examine issues such as how the intervention works. A small group of participants might undergo mechanistic studies (as long as they are not unduly burdensome or invasive). In the Studies of Left Ventricular Dysfunction (SOLVD) [21], the investigators evaluated whether an angiotensin converting enzyme inhibitor would reduce mortality in symptomatic and asymptomatic subjects with impaired cardiac function. In selected participants, special studies were done with the objective of getting a better understanding of the disease process and of the mechanisms of action of the intervention. These substudies did not require the large sample size of the main studies (over 6,000 participants). Thus, most participants in the main trials had a relatively simple and short evaluation and did not undergo the expensive and time-consuming procedures or interviews demanded by the substudies. This combination of a rather limited assessment in many participants, designed to address an easily monitored response variable, and detailed measurements in subsets, can be extremely effective. An angiographic substudy in the GUSTO trial helped explain how accelerated alteplase treatment resulted in more effective coronary perfusion [22]. The improved survival appeared to be fully explained by this impact on reperfusion [23]. In the Harmonizing Outcomes with Revascularization and Stents in Acute Myocardial Infarction (HORIZONS-AMI) trial [24], lower rates of bleeding with bivalirudin compared with unfractionated heparin plus a glycoprotein IIb/IIIa inhibitor appeared to explain only part of the lower subsequent mortality in the bivalirudin group [25].

Exploratory genetic studies are commonly conducted to examine possible mechanisms of action of the intervention. Genetic variants of the cytochrome P450 CYP2C19 metabolic pathway of clopidogrel were related to the level of the active metabolite and reduction in platelet aggregation for participants treated with clopidogrel in the database from the Trial to Assess Improvement in Therapeutic Outcomes by Optimizing Platelet Inhibition with Prasugrel-Thrombolysis in Myocardial Infarction (TRITON-TIMI) [26].

Traditionally, most trials of new interventions have collected extensive information about participants, have detailed inclusion and exclusion criteria, involve considerable quality assurance measures, and assess many, carefully measured outcomes. These sorts of trials, although they address major questions and are well-conducted, are quite expensive and often very time-consuming. Therefore, given the needed resources, trial sponsors can afford to address only some of the many important questions can be answered, often in limited kinds of participants and clinical settings.

As discussed by Tricoci et al. [27] with respect to clinical practice guidelines in cardiology, but undoubtedly similar in other medical fields, many of these guidelines are based on inadequate data. One of the rationales for large, simple clinical trials is that they can provide data relevant to clinical practice, since they are typically conducted in practice settings [28]. The general idea is that for common conditions, and important outcomes, such as total mortality, even modest benefits of intervention, particularly interventions that are easily implemented in a large population, are important. Because an intervention is likely to have similar effects (or at least effects that trend in the same direction) in most participants, extensive characterization of people at entry may be unnecessary. The study must have unbiased allocation of participants to intervention or control and unbiased and reasonably complete ascertainment of outcomes. Sufficiently large numbers of participants are more important in providing the statistical power necessary to answer the question(s) than careful attention to quality and completeness of data. This model depends upon a relatively easily administered intervention, brief forms, and an easily ascertained outcome, such as a fatal or unambiguous nonfatal event. Neither the trials that collect extensive information nor the simple ones are better. Rather, both types are essential. The proper design depends on the condition being studied, the nature of the question, and the kind of intervention.

As mentioned, major efforts are being devoted to conducting comparative effectiveness research. Although comparative effectiveness studies can be of various sorts, encompassing several kinds of clinical research, we will limit our discussion to clinical trials. Much medical care has not been rigorously evaluated, meaning that trials comparing ongoing preventive and treatment approaches are needed. And of course, when new interventions are developed, they must be compared against existing therapy. Additionally, the increasing cost burden of medical care means that even if several treatments are equally effective, we need to consider factors such as cost, tolerability, and ease of administration. Therefore, comparative effectiveness trials are commonly of the noninferiority sort.

Much of the literature on comparative effectiveness research advocates conducting the studies in usual practice settings (often called pragmatic trials) [29, 30] (see Chap. 4). Because these trials are conducted in clinical practice settings, they must be relatively simple, demanding little in the way of effort to screen and assess outcomes. The goal is to compare two interventions, both of which are considered standard care.

Response variables are outcomes measured during the course of the trial, and they define and answer the questions. A response variable may be total mortality, death from a specific cause, incidence of a disease, a complication or specific adverse effect, symptomatic relief, quality of life, a clinical finding, a laboratory measurement, or the cost and ease of administering the intervention. If the primary question concerns total mortality, the occurrence of deaths in the trial clearly answers the question. If the primary question involves severity of arthritis, on the other hand, extent of mobility or a measure of freedom from pain may be reasonably good indicators. In other circumstances, a specific response variable may only partially reflect the overall question. As seen from the above examples, the response variable may show a change from one discrete state (living) to another (dead), from one discrete state to any of several other states (changing from one stage of disease to another) or from one level of a continuous variable to another. If the question can be appropriately defined using a continuous variable, the required sample size may be reduced (Chap. 8). However, the investigator needs to be careful that this variable and any observed differences are clinically meaningful and relevant and that the use of a continuous variable is not simply a device to reduce sample size.

In general, a single response variable should be identified to answer the primary question. If more than one are used, the probability of getting a nominally significant result by chance alone is increased (Chap. 18). In addition, if the different response variables give inconsistent results, interpretation becomes difficult. The investigator would then need to consider which outcome is most important, and explain why the others gave conflicting results. Unless she has made the determination of relative importance prior to data collection, her explanations are likely to be unconvincing.

Although the practice is not advocated, there may be circumstances when more than one “primary” response variable needs to be looked at. This may be the case when an investigator truly cannot decide which of several response variables relates most closely to the primary question. Ideally, the trial would be postponed until this decision can be made. However, overriding concerns, such as increasing use of the intervention in general medical practice, may compel her to conduct the study earlier. In these circumstances, rather than arbitrarily selecting one response variable which may, in retrospect, turn out to be suboptimal or even inappropriate, investigators prefer to list several “primary” outcomes. An old example is the Urokinase Pulmonary Embolism Trial [37], where lung scan, arteriogram and hemodynamic measures were given as the “primary” response variables in assessing the effectiveness of the agents urokinase and streptokinase. Chapter 8 discusses the calculation of sample size when a study with several primary response variables is designed.

Commonly, investigators prepare an extensive list of secondary outcomes, allowing them to claim that they “prespecified” these outcomes when one or more turn out to reach nominally significant differences. Although prespecification provides some protection against accusations that the findings were data-derived, a long list does not protect against likely play of chance. Far better is a short list of outcomes that are truly thought to be potentially affected by the intervention. Combining events to make up a response variable might be useful if any one event occurs too infrequently for the investigator reasonably to expect a significant difference without using a large number of participants. In answering a question where the response variable involves a combination of events, only one event per participant should be counted. That is, the analysis is by participant, not by event.

One kind of combination response variable involves two kinds of events. This has been termed a composite outcome. It must be emphasized, however, that the composite outcome should be capable of meaningful interpretation such as where all components are related through a common underlying condition or respond to the same presumed mechanism of action of the agent. In a study of heart disease, combined events might be death from coronary heart disease plus nonfatal myocardial infarction. This is clinically meaningful since death from coronary heart disease and nonfatal myocardial infarction might together represent a measure of serious coronary heart disease. Unfortunately, as identified in a survey of 40 trials using composite outcomes by Cordoba et al. [38], there was considerable lack of clarity as to how components were combined and results reported. Difficulties in interpretation can arise if the results of each of the components in such a response variable are inconsistent [39]. In the Physicians’ Health Study report of aspirin to prevent cardiovascular disease, there was no difference in mortality, a large reduction in myocardial infarction, and an increase in stroke, primarily hemorrhagic [40]. In this case, cardiovascular mortality was the primary response variable, rather than a combination. If it had been a combination, the interpretation of the results would have been even more difficult than it was [41]. Even more troublesome is the situation where one of the components in the combination response variable is far less serious than the others. For example, if occurrence of angina pectoris or a revascularization procedure is added, as is commonly done, interpretation can be problematic. Not only are these less serious than cardiovascular death or myocardial infarction, they often occur more frequently. Thus, if overall differences between groups are seen, are these results driven primarily by the less serious components? What if the results for the more serious components (e.g., death) trend in the opposite directions? This is not just theoretical. For example, the largest difference between intervention and control in the Myocardial Ischemia Reduction with Aggressive Cholesterol Lowering (MIRACL) trial was seen in the least serious of the four components; the one that occurred most often in the control group [42]. A survey of published trials in cardiovascular disease that used composite response variables showed that half had major differences in both importance and effect sizes of the individual components [43]. Those components considered to be most important had, on average, smaller benefits than the more minor ones. See Chap. 18 for a discussion of analytic and interpretation issues if the components of the composite outcome go in different directions or have other considerable differences in the effect size.

When this kind of combination response variable is used, the rules for interpreting the results and for possibly making regulatory claims about individual components should be established in advance. A survey of the cardiovascular literature found that the use of composite outcomes (often with three or four components) is common, and the components vary in importance [44]. One possible approach is to require that the most serious individual components show the same trend as the overall result. Some have suggested giving each component weights, depending on the seriousness [45, 46]. However, this may lead to trial results framed as unfamiliar scores that are difficult to interpret by clinicians. Although it has sample size implications, it is probably preferable to include in the combined primary response variable only those components that are truly serious, and to assess the other components as secondary outcomes. If an important part of a composite outcome goes in the wrong direction, as occurred with death in the Sodium-Hydrogen Exchange Inhibition to Prevent Coronary Events in Acute Cardiac Conditions (EXPEDITION) trial [47], even benefit in the composite outcome (death or myocardial infarction), is insufficient to conclude that the intervention (in this case, sodium-hydrogen exchange inhibition by means of cariporide during coronary artery bypass graft surgery) should be used. Adding to the concern was an adverse trend for cerebrovascular events.

Another kind of combination response variable involves multiple events of the same sort. Rather than simply asking whether an event has occurred, the investigator can look at the frequency with which it occurs. This may be a more meaningful way of looking at the question than seeking a yes-no outcome. For example, frequency of recurrent transient ischemic attacks or epileptic seizures within a specific follow-up period might comprise the primary response variable of interest. Simply adding up the number of recurrent episodes and dividing by the number of participants in each group in order to arrive at an average would be improper. Multiple events in an individual are not independent, and averaging gives undue weight to those with more than one episode. One approach is to compare the number of participants with none, one, two, or more episodes; that is, the distribution of the number of episodes, by individual.

Sometimes, study participants enter a trial with a condition that is exhibited frequently. For example, they may have had several episodes of transient atrial fibrillation in the previous weeks or may drink alcohol to excess several days a month. Trial eligibility criteria may even require a minimum number of such episodes. A trial of a new treatment for alcohol abuse may require participants to have at least six alcoholic drinks a day for at least 7 days over the previous month. The investigator needs to decide what constitutes a beneficial response. Is it complete cessation of drinking? Reducing the number of drinks to some fixed level (e.g., no more than two on any given day)? Reducing alcohol intake by some percent, and if so, what percent? Does this fixed level or percent differ depending on the intake at the start of the trial? Decisions must be made based on knowledge of the disease or condition, the kind of intervention and the expectations of how the intervention will work. The clinical importance of improvement versus complete “cure” must also be considered.

Regardless of whether an investigator is measuring a primary or secondary response variable, certain rules apply. First, she should define and record the questions in advance, being as specific as possible. She should not simply ask, “Is A better than B?” Rather, she should ask, “In population W is drug A at daily dose X more efficacious in improving Z by Q amount over a period of time T than drug B at daily dose Y?” Implicit here is the magnitude of the difference that the investigator is interested in detecting. Stating the questions and response variables in advance is essential for planning of study design and calculation of sample size. As shown in Chap. 8, sample size calculation requires specification of the response variables as well as estimates of the intervention effect. In addition, the investigator is forced to consider what she means by a successful intervention. For example, does the intervention need to reduce mortality by 10 or 25% before a recommendation for its general use is made? Since such recommendations also depend on the frequency and severity of adverse effects, a successful result cannot be completely defined beforehand. However, if a 10% reduction in mortality is clinically important, that should be stated, since it has sample size implications. Specifying response variables and anticipated benefit in advance also eliminates the possibility of the legitimate criticism that can be made if the investigator looked at the data until she found a statistically significant result and then decided that that response variable was what she really had in mind all the time

Second, the primary response variable must be capable of being assessed in all participants. Selecting one response variable to answer the primary question in some participants, and another response variable to answer the same primary question in other participants is not a legitimate practice. It implies that each response variable answers the question of interest with the same precision and accuracy; i.e., that each measures exactly the same thing. Such agreement is unlikely. Similarly, response variables should be measured in the same way for all participants. Measuring a given variable by different instruments or techniques implies that the instruments or techniques yield precisely the same information. This rarely, if ever, occurs. If response variables can be measured only one way in some participants and another way in other participants, two separate studies are actually being performed, each of which is likely to be too small.

Third, unless there is a combination primary response variable in which the participant remains at risk of having additional events, participation generally ends when the primary response variable occurs. “Generally” is used here because, unless death is the primary response variable, the investigator may well be interested in certain events, including adverse events, subsequent to the occurrence of the primary response variable. These events will not change the analysis of the primary response variable but may affect the interpretation of results. For example, deaths taking place after a nonfatal primary response variable has already occurred, but before the official end of the trial as a whole, may be of interest. On the other hand, if a secondary response variable occurs, the participant should remain in the study (unless, of course, it is a fatal secondary response variable). He must continue to be followed because he is still at risk of developing the primary response variable. A study of heart disease may have, as its primary question, death from coronary heart disease and, as a secondary question, incidence of nonfatal myocardial infarction. If a participant suffers a nonfatal myocardial infarction, this counts toward the secondary response variable. However, he ought to remain in the study for analytic purposes and be at risk of developing the primary response variable and of having other adverse events. This is true whether or not he is continued on the intervention regimen. If he does not remain in the study for purposes of analysis of the primary response variable, bias may result. (See Chap. 18 for further discussion of participant withdrawal.)

Fourth, response variables should be capable of unbiased assessment. Truly double-blind studies have a distinct advantage over other studies in this regard. If a trial is not double-blind (Chap. 7), then, whenever possible, response variable assessment should be done by people who are not involved in participant follow-up and who are blinded to the identity of the study group of each participant. Independent reviewers are often helpful. Of course, the use of blinded or independent reviewers does not entirely solve the problem of bias. Unblinded investigators sometimes fill out forms and the participants may be influenced by the investigators. This may be the case during a treadmill exercise performance test, where the impact of the person administering the test on the results may be considerable. Some studies arrange to have the intervention administered by one investigator and response variables evaluated by another. Unless the participant is blinded to his group assignment (or otherwise unable to communicate), this procedure is also vulnerable to bias. One solution to this dilemma is to use only “hard,” or objective, response variables (which are unambiguous and not open to interpretation, such as total mortality or some imaging or laboratory measures read by someone blinded to the intervention assignment). This assumes complete and honest ascertainment of outcome. Double-blind studies have the advantage of allowing the use of softer response variables, since the risk of assessment bias is minimized.

Fifth, it is important to have response variables that can be ascertained as completely as possible. A hazard of long-term studies is that participants may fail to return for follow-up appointments. If the response variable is one that depends on an interview or an examination, and participants fail to return for follow-up appointments information will be lost. Not only will it be lost, but it may be differentially lost in the intervention and control groups. Death or hospitalizations are useful response variables because the investigator can usually ascertain vital status or occurrence of a hospital admission, even if the participant is no longer active in a study. However, only in a minority of clinical trials are they appropriate.

Sometimes, participants withdraw their consent to be in the trial after the trial has begun. In such cases, the investigator should ascertain whether the participant is simply refusing to return for follow-up visits but is willing to have his data used, including data that might be obtained from public records; is willing to have only data collected up to the time of withdrawal used in analyses; or is asking that all of his data be deleted from the study records.

All clinical trials are compromises between the ideal and the practical. This is true in the selection of primary response variables. The most objective or those most easily measured may occur too infrequently, may fail to define adequately the primary question, or may be too costly. To select a response variable which can be reasonably and reliably assessed and yet which can provide an answer to the primary question requires judgment. If such a response variable cannot be found, the wisdom of conducting the trial should be re-evaluated.

A common criticism of clinical trials is that they are expensive and of long duration. This is particularly true for trials which use the occurrence of clinical events as the primary response variable. It has been suggested that response variables which are continuous in nature might substitute for the binary clinical outcomes. Thus, instead of monitoring cardiovascular mortality or myocardial infarction an investigator could examine progress of atherosclerosis by means of angiography or ultrasound imaging, or change in cardiac arrhythmia by means of ambulatory electrocardiograms or programmed electrical stimulation. In the cancer field, change in tumor size might replace mortality. In AIDS trials, change in CD-4 lymphocyte level has been used as a response to treatment instead of incidence of AIDS in HIV positive patients or mortality. Improved bone mineral density has been used as a surrogate for reduction in fractures.

A rationale for use of these “surrogate response variables” is that since the variables are continuous, the sample size can be smaller and the study less expensive than otherwise. Also, changes in the variables are likely to occur before the clinical event, shortening the time required for the trial. Wittes et al. [48] discuss examples of savings in sample size by the use of surrogate response variables.

It has been argued that in the case of truly life-threatening diseases (e.g., AIDS in its early days, certain cancers, serious heart failure), clinical trials should not be necessary to license a drug or other intervention. Given the severity of the condition, lesser standards of proof should be required. If clinical trials are done, surrogate response variables ought to be acceptable, as speed in determining possible benefit is crucial. Potential errors in declaring an intervention useful may therefore not be as important as early discovery of a truly effective treatment.

Even in such instances, however, one should not uncritically use surrogate endpoints [49, 50]. It was known for years that the presence of ventricular arrhythmias correlated with increased likelihood of sudden death and total mortality in people with heart disease [51], as it was presumably one mechanism for the increased mortality. Therefore, it was common practice to administer antiarrhythmic drugs with the aim of reducing the incidence of sudden cardiac death [52, 53]. The Cardiac Arrhythmia Suppression Trial demonstrated, however, that three drugs that effectively treated ventricular arrhythmias were not only ineffective in reducing sudden cardiac death, but actually caused increased mortality [54, 15].

A second example concerns the use of inotropic agents in people with heart failure. These drugs had been shown to improve exercise tolerance and other symptomatic manifestations of heart failure [55]. It was expected that mortality would also be reduced. Unfortunately, clinical trials subsequently showed that mortality was increased [56, 57].

Another example from the cardiovascular field is the Investigation of Lipid Level Management to Understand its Impact in Atherosclerotic Events (ILLUMINATE). In this trial, the combination of torcetrapib and atorvastatin was compared with atorvastatin alone in people with cardiovascular disease or diabetes. Despite the expected impressive and highly statistically significant increase in HDL-cholesterol and decrease in LDL-cholesterol in the combination group, there was an increase in all-cause mortality and major cardiovascular events [58]. Thus, even though it is well-known that lowering LDL-cholesterol (and possibly increasing HDL-cholesterol) can lead to a reduction in coronary heart disease events, some interventions might have unforeseen adverse consequences. Recent studies looking at the raising of HDL-cholesterol have also been disappointing, despite the theoretical grounds to expect benefit [59]. The Atherothrombosis Intervention in Metabolic Syndrome with Low HDL/High Triglycerides and Impact on Global Health Outcomes (AIM-HIGH) trial [60] and the Second Hearth Protection Study (HPS-2 THRIVE) [61] did not reduce cardiovascular outcomes in the context of lowering LDL-cholesterol.

It was noted that the level of CD-4 lymphocytes in the blood is associated with severity of AIDS. Therefore, despite some concerns [62] a number of clinical trials used change in CD-4 lymphocyte concentration as an indicator of disease status. If the level rose, the drug was considered to be beneficial. Lin et al., however, argued that CD-4 lymphocyte count accounts for only part of the relationship between treatment with zidovudine and outcome [63]. Choi et al. came to similar conclusions [64]. In a trial comparing zidovudine with zalcitabine, zalcitabine was found to lead to a slower decline in CD-4 lymphocytes than did zidovudine, but had no effect on the death rate from AIDS [65]. Also troubling were the results of a large trial which, although showing an early rise in CD-4 lymphocytes, did not demonstrate any long-term benefit from zidovudine [66]. Whether zidovudine or another treatment was, or was not, truly beneficial is not the issue here. The main point is that the effect of a drug on a surrogate endpoint (CD-4 lymphocytes) is not always a good indicator of clinical outcome. This is summarized by Fleming, who noted that the CD-4 lymphocyte count showed positive results in seven out of eight trials where clinical outcomes were also positive. However, the CD-4 count was also positive in six out of eight trials in which the clinical outcomes were negative [50].

Similar seemingly contradictory results have been seen with cancer clinical trials. In trials of 5-fluorouracil plus leucovorin compared with 5-fluorouracil alone, the combination led to significantly better tumor response, but no difference in survival [67]. Fleming cites other cancer examples as well [50]. Sodium fluoride, because of its stimulation of bone formation, was widely used in the treatment of osteoporosis. Despite this, it was found in a trial in women with postmenopausal osteoporosis to increase bone fragility [68].

These examples do not mean that surrogate response variables should never be used in clinical trials. Nevertheless, they do point out that they should only be used after considering the advantages and disadvantages, recognizing that erroneous conclusions about interventions might occasionally be reached.

Prentice has summarized two key criteria that must be met if a surrogate response variable is to be useful [69]. First, the surrogate must correlate with the true clinical outcome, which most proposed surrogates would likely do. Second, for a surrogate to be valid, it must capture the full effect of the intervention. For example, a drug might lower blood pressure or serum LDL-cholesterol, but as in the ILLUMINATE trial example, have some other deleterious effect that would negate any benefit or even prove harmful.

Another factor is whether the surrogate variable can be assessed accurately and reliably. Is there so much measurement error that, in fact, the sample size requirement increases or the results are questioned? Additionally, will the evaluation be so unacceptable to the participant that the study will become infeasible? If it requires invasive techniques, participants may refuse to join the trial, or worse, discontinue participation before the end. Measurement can require expensive equipment and highly trained staff, which may, in the end, make the trial more costly than if clinical events are monitored. The small sample size of surrogate response variable trials may mean that important data on safety are not obtained [70]. Finally, will the conclusions of the trial be accepted by the scientific and medical communities? If there is insufficient acceptance that the surrogate variable reflects clinical outcome, in spite of the investigator’s conviction, there is little point in using such variables.

Many drugs have been approved by regulatory agencies on the basis of surrogate response variables, including those that reduce blood pressure and blood sugar. In the latter case, though, the Food and Drug Administration now requires new diabetes drugs to show that cardiovascular events are not increased [71]. We think that, except in rare instances, whenever interventions are approved by regulatory bodies on the basis of surrogate response variables, further clinical studies with clinical outcomes should be conducted afterward. As discussed by Avorn [72], however, this has not always been the case. He cites examples not only of major adverse effects uncovered after drugs were approved on the basis of surrogate outcomes, but lack of proven clinical benefit. In all decisions regarding approval, the issues of biologic plausibility, risk, benefits, and history of success must be considered.

When are surrogate response variables useful? The situation of extremely serious conditions has been mentioned. Particularly, when serious conditions are also rare, it may be difficult or even impossible to obtain enough participants to use a clinical outcome. We may be forced to rely on surrogate outcomes. Other than those situations, surrogate response variables are useful in early phase development studies, as an aid in deciding on proper dosage and whether the anticipated biologic effects are being achieved. They can help in deciding whether, and how best, to conduct the late phase trials which almost always should employ clinical response variables.