Stephen P. Glasser, MD, is professor of preventive medicine

Pharmacologic inhibition of the renin-angiotensin aldosterone system (RAAS) has become a widely accepted ap&shy;proach to lowering blood pressure. Angiotensin-converting enzyme (ACE) in&shy;hibitors and angiotensin receptor blockers (ARBs) are two classes of RAAS inhibitors. During the past 5 years or so, and predominantly with the ACE inhibitors, clinical trials have been reported that demonstrate that not only do these drugs lower BP, but they also prevent cardiovascular (CV) events; and this reduction in CV events is likely beyond 

 The clinical trial that had perhaps the greatest impact on the prescribing of ACE inhibitors in patients without elevated BP was the Heart Outcomes Prevention Evaluation (HOPE) trial, which utilized ramipril (Altace) as the ACE inhibitor.

 More recently, perindopril (Aceon) has been studied with regard to its effect on CV and stroke events beyond its important blood pressure-lowering effects. In the Pro&shy;tection Against Recurrent Stroke Study (PROGRESS), perindopril was associated with a 9/4 mm Hg reduction in blood pressure and a 28% and 26% reduction in stroke and CV events, respectively.

     Most recently, the Efficacy of Perindopril in      Reduction of Cardiovascular Events (EUROPA) was      reported.

 The results of this trial resulted in a statement in perindopril’s package insert saying that it is indicated in patients with stable coronary artery disease to reduce the risk of cardiovascular mortality or nonfatal myocardial infarction (MI).

 This is then ad&shy;d&shy;ed to its antihypertensive indication. Per&shy;indopril also remains one of the only ACE inhibitors in which the package insert discusses its role in favorably affecting arterial compliance, in which it is stated that “an increase in the compliance of large arteries was ob&shy;served, suggesting a direct effect on arterial smooth muscle, consistent with the results of animal studies.” 

 The HOPE study evaluated the benefits of ACE inhibition in patients aged 55 years or older at high risk for CV complications, characterized by a high prevalence of diabetes, hypertension, stroke, and peripheral vascular disease. EUROPA evaluated patients with stable coronary artery disease over age 18 and importantly without evidence of heart failure. Patients were randomly assigned to 8 mg perindopril or placebo, added to a background of contemporary usual-care therapy (which was quite extensive and in&shy;cluded platelet inhibitors, lipid-lowering therapy, beta blocking agents, calcium channel antagonists, nitrates, and diuretics). The primary end point was a composite of CV death, nonfatal MI, and cardiac arrest with successful resuscitation. Over 12,000 pa&shy;tients were randomized and 6,107 in the perindopril arm and 6,108 in the placebo group completed the study. Remarkably, in this event-driven study that followed patients for 5 years, only 3 patients were lost to follow-up. A relative risk reduction of 20% was observed in the primary end point, and the number needed to treat to prevent a primary event was 50 patients treated for 4 years to prevent 1 primary end point event. Some other interesting findings in&shy;cluded favorable effects on all secondary end points analyzed and for all age groups (including those below the age of 55) and with hypertension or not. In&shy;terestingly, in this diseased population on usual-care medical therapy, the annual placebo event rate was 2.4%, which amortizes to about 24% in 10 years, while in HOPE the annual placebo event rate was 4.4% or 44% at 10 years. Thus, both studies enrolled patients with a Framingham Risk Score that placed them in the high-risk category, but clearly the HOPE population was at almost twice the risk. 

 The EUROPA results clearly imply that ACE inhibitors should be considered for patients with stable coronary artery disease, and they should be added to baseline usual-care therapy. To date, only ramipril and perindopril have the Food and Drug Admin&shy;is&shy;tration approved indication for coronary artery disease protection, and the argument continues as to whether it is a class effect. Because there are differences among the ACE inhibitors, particularly regarding their tissue penetration and trough-to-peak ratios, one should exercise caution if they prescribe a different ACE inhibitor for this indication. 

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Pharmacologic inhibition of the renin-angiotensin aldosterone system (RAAS) has become a widely accepted ap­proach to lowering blood pressure (BP).

Cardiovascular events in hypertension trials: A focus on perindopril

In the prior installment of this series on clinical research, various study designs were introduced, with a brief description of each.

 In this article, 2 of the more important study designs, cohort studies and randomized controlled trials (RCTs), are highlighted.

 Recall that a cohort study is much like an RCT except that the intervention in an RCT is investigator controlled, while the intervention in a cohort study is a naturally occurring phenomenon. In a cohort study, it is assumed that the subject at the beginning of the study is “disease free” of the outcome of interest. For example, if the outcome of interest is recurrent myocardial infarction, the subject would have already had an initial myocardial infarction (in that sense, he or she is not disease free); in terms of the outcome of interest (a second infarction), at study outset the subject is obviously free of recurrent infarction. Using colon cancer as another example, one assumes at study outset that the subject is disease free (normal) at the time of enrollment; in fact, he or she may already have undiagnosed colon cancer. This could bias the study results because the exposure of interest (eg, a low-fiber diet) may have nothing to do with the outcome of interest (colon cancer), as the subject already has the outcome irrespective of the exposure. This also raises the question of what is a normal person. It has wittily been suggested that a normal subject is one that has been insufficiently studied! It is assumed that the incorrect assumption of no disease at study outset is equally balanced in the treatment and control groups; that is the expectation but not always the fact. What distinguishes the RCT from other study designs is that the exposure of interest (intervention) is controlled by the investigator. 

 The RCT is believed to yield the highest level of evidence for causality, particularly when the results of the RCT demonstrate positive findings. This has led to the consideration of RCT results as “gospel.” In fact, there are numerous problems that may adversely affect the results of an RCT. DeMets and Califf

 outlined 11 principles gleaned from RCT analyses, which are briefly summarized as follows: (1) Most current treatment effects are modest at best, and it is becoming more difficult to differentiate outcomes from the natural history of disease. More clinical trial subjects are receiving multiple therapies, and the interaction of therapies may positively or negatively affect the intervention of interest, confounding the results. Because treatment effects are small, it is important to differentiate statistically significant differences from clinically meaningful effects. (2) High-risk patients generally receive the most benefit from interventions, but clinical trials tend to exclude these patients, which limits the generalizability of the study results to the population of patients who might benefit from the investigational therapy. Selection bias is present in all trials, and RCTs are no exception. (3) Most clinical trials are short-term studies, and long-term effects may be more important. Fin&shy;ally, disagreement abounds regarding the definition of an RCT, the most appropriate analytic method, the use of surrogate end points in lieu of the true outcome of interest, and the issue of causal inference as it relates to the application of the study results to “truth,” which will be discussed in a subsequent article. 

 The strengths of RCTs are numerous. One of the greatest problems in clinical research is the attempt to identically match the subjects in the exposure group to those in the control or comparator group, in order to avoid confounding the trial results. Known dissimilarities can, in part, be accounted for in the study design or analysis. Unknown confounders are the bigger problem. If the sample size is large, randomization tends to balance known and unknown confounders. Consider the example of a trial studying the relationship between coffee drinking (the exposure or “intervention”) and myocardial infarction (the outcome). Suppose an association is found, but in fact more coffee drinkers than nondrinkers smoked cigarettes and it was actually the smoking that was associated with MI. If smoking was a known potential confounder, stratification of coffee drinkers and nondrinkers who smoked versus those who did not smoke would have clarified the ob&shy;served association. If confounding by smoking was unknown, randomization likely would have balanced the number of smokers in the exposed versus the unexposed groups, and confounding of the association with coffee drinking would have been avoided. 

 Another issue in RCTs is the selection of a control group; when it is ethical, the control group should receive placebo in a double-blind manner. The role of placebo in clinical trials is complex, and the reader is referred to a review of this subject.

 Other considerations are the use of surrogate end points and the method of intention-to-treat analysis, which will be discussed in a subsequent article. 

 Also important is whether RCTs are designed as superiority trials, equi&shy;v&shy;alency trials, or noninferiority trials. Classically, RCTs were designed as superiority trials, in which it is tested whether the investigational treatment is superior to the comparator treatment. Equivalency trials have in&shy;creased in popularity, and test whether a new treatment is the same as some standard treatment (eg, an equivalency trial might be used when there is no evidence that the new treatment is more effective, but it might be less expensive or associated with fewer adverse effects). Noninferiority studies seek proof that the new treatment is not inferior to standard treatment. The appropriateness of the choice of trial designs is beyond the scope of this discussion but is based on the existent literature, on statistical considerations, and on sample sizes. 

 Finally, many RCTs are multicenter studies. Despite standard protocols, between-center differences in recruitment, patient selection, culture, and socioeconomics come into play. Each center likely recruits a different number of patients, despite attempts to equalize this and other variables. Although there is no panacea, several design methods minimize this problem. Consider a multicenter trial looking to enroll 100 patients, 10 at each of 10 centers. Should randomization of patients into the control and investigational arms be among the 100 patients, with the possibility that at some centers 8 of the 10 patients might be enrolled in one arm and 2 in the other arm? Or would it be better to use a blocked randomization scheme, with 5 of the 10 patients at each center in each arm? Many considerations influence these decisions. 

 In summary, cohort investigations and RCTs offer the best likelihood that study results reflect the truth. However, the clinician needs to be aware of the many strengths and limitations of these study designs and approach the results of any trial with healthy skepticism. 

Fundamentals of clinical research: Cohort studies and randomized controlled trials

A patient’s response to drugs may be influenced by many factors, including age, race, sex, ethnic background, metabolic phenotype, body fat content and distribution, and body size. Drug—drug and drug–disease interactions are also important. As it relates to sex, the hormonal milieu is an important consideration, particularly for women.

 Just a little more than decade ago, concern over the underrepresentation of women in clinical trials began to increase, especially trials focusing on cardiovascular disease. In the 1990s, a number of initiatives were put in place to correct this. The National Institutes of Health (NIH), the Food and Drug Ad&shy;min&shy;istration (FDA), and the pharmaceutical in&shy;dustry all developed guidelines to address the underrepresentation of women in clinical trials. By many measures, these efforts have been partially successful. One survey showed an increase in research on women’s health by the pharmaceutical industry and that there were 371 medicines in development for diseases that disproportionately afflict women, including 48 for obstetric/gynecologic conditions, 41 for diabetes, 41 for breast cancer, and 34 for ovarian cancer.

 In 1993, the FDA published “Guidelines for the Study and Evaluation of Gender Dif&shy;ferences in the Clinical Evaluation of Drugs,” in response to the growing concerns that the drug development process did not produce adequate information about the ef&shy;fects of drugs in women.

 The NIH Re&shy;vitaliza&shy;tion Act, which strengthened NIH policies to ensure that women and other minority groups be included in clinical trials and, if appropriate, that they be included in adequate numbers to ensure valid analyses of sex and ethnic differences in the effect of therapies, was enacted at about the same time. 

 One area in which the underrepresentation of women has not been corrected is 

 and colleagues, that of evidence-based pharmacotherapy. There is good reason to be concerned about this, in particular, the differing proportion of body fat compared with men and the generally smaller size of women, along with smaller heart size and sex-specific differences in some of the drug-metabolizing enzymes, as discussed by the authors. In addition, hormones may influence both the pharmacokinetic and pharmacodynamic para&shy;meters of drugs. Factors such as the variation of gonadotropins and circulating steroidal hormones (eg, estradiol and progesterone) during the menstrual cycle, differences in hormones between the premenopausal and postmenopausal state, and the use of exogenous hormone replacement postmenopausally or for contraception all affect pharmacokinetics and pharmacodynamics. Thus, the re&shy;view by Stangl and colleagues is timely in pointing out what is and is not known about the pharmacotherapy of cardiovascular drugs in women, in particular, beta-blocking agents, angio&shy;tensin-converting enzyme inhibitors, angio&shy;tensin receptor blockers, calcium channel blocking agents, digitalis, antiarrhythmics, platelet aggregation inhibitors, and HMG-CoA reductase inhibitors (statins). An area not discussed by the authors be&shy;cause it is still not evidence-based relates to anticoagulants. For example, one of the many questions needing a definitive answer is whether thrombolytic therapy acts the same way in women as in men. As early as 1993, White and colleagues suggested that the use of thrombolytic therapy after acute myocardial infarction for wom&shy;en resulted in morbidity and mortality similar to men, but that women suffered from a higher incidence of hemorrhagic stroke.

 Clearly, this is an important issue requiring further study. Hopefully, the article by Stangl and colleagues will focus interest on this most important area. 

A patient's response to drugs may be influenced by many factors, including age, race, sex, ethnic background, metabolic phenotype, body fat content and distribution, and body size. Drug–drug and drug–disease interactions are also important.

Pharmacotherapy for chronic cardiovascular disease

 on clinical research highlighted some important fundamentals in cohort studies and randomized controlled trials (RCTs).

 In this article, additional issues that are critical to the understanding of RCTs are discussed, including causal inference, the use of surrogate measures, and the principle of intention to treat (ITT).

In an earlier installment, various clinical research study designs were discussed, and the differing “levels of scientific evidence” that are associated with each were ad&shy;dressed.

 A comparison of study designs is complex, with the metric being that the study design providing the highest level of scientific evidence is the one that yields the greatest likelihood of cause and effect between the exposure and the outcome. The basic tenet of science is that it is almost impossible to prove something, but it is much easier to disprove it. Causal effect focuses on outcomes among exposed individuals, but what would have happened had they not been exposed? The outcome among exposed individuals is called the factual outcome. To draw inferences, exposed and nonexposed individuals are compared. Ideally, one would go back in time and repeat the same experiment among the same individuals but without the exposure to observe the counterfactual outcome. Because this is impossible, replication of results with multiple studies is the norm. Another basic tenet is that association does not denote causation (even when the association is statistically significant). Consider the finding of an association between coffee drinking and myocardial infarction (MI). Coffee drinking may precipitate (and be causal of) an MI. However, some persons who have had an MI may serendipitously begin to drink more coffee, in which case (instead of a cause-effect relationship) the association would be an “effect-cause” relationship (sometimes referred to as reverse causation). The association between coffee drinking and MI might be mediated by some confounder (eg, persons who drink more coffee may smoke more cigarettes, and it is the smoking that precipitates the MI) (

). Therefore, observed associations may be spurious as a result of chance (random error) or because of some systematic error (bias) in the study design. In the first conceptual association in the Table, coffee drinking leads to MI, so it is causal. The second association represents a scenario in which MI leads to coffee drinking. An association exists, but coffee drinking is not causal of MI. In the third association, the variable x re&shy;sults in coffee drinking and MI, so it confounds the association between coffee drinking and MI. In the fourth and fifth associations, the results are spurious because of chance or some bias in the way in which the trial was conducted or the subjects were selected. 

Because causation cannot be proved, how does one approach the concept of proof? The Bradford Hill criteria for judging causality remain the guiding principles. The replication of studies in which the magnitude of effect is large, biologic plausibility for the cause-effect relationship is provided, temporality and a dose response exist, similar suspected causality is associated with similar exposure outcomes, and systematic bias is avoided go a long way in suggesting that an association is truly causal. 

It has been said that “death is a fact, the rest is inference.” Specifi&shy;cation of the outcome of an experimental intervention can be complex. Long-term outcome trials are expensive, loss to follow-up is problematic, and the development of medical and surgical innovations during the course of a long-term trial may present ethical issues that were nonexistent at the initiation of the trial. Shorter-term trials using a surrogate end point may be appropriate. A classic example is the use of blood pressure as a surrogate end point for an outcome of interest such as MI or stroke. Many other examples exist, including fasting glucose level for diabetic complications, bone mineral density for fractures, and a reduction in tumor size for cancer survival. However, the surrogate end point may not reflect the true outcome of interest. An example is the Cardiac Arrhythmia Suppression Trial.

 At the initiation of the trial, a reduction in the frequency and complexity of premature ventricular contractions by means of antiarrhythmic therapy was considered to be an adequate surrogate of a reduction in arrhythmic sudden cardiac death. Many antiarrhythmic therapies were approved using the surrogate end point, until the complete study results suggested otherwise. Changes in the surrogate end point must be predictive of the relevant clinical outcome and should reflect the effect of the experimental intervention on the outcome. These criteria are frequently difficult to fully appreciate, compounded by the fact that many treatments have several effect pathways. 

Analytic issues regarding RCTs are also frequently misunderstood. Three common approaches are ITT analysis, compliers-only analysis, and as-treated analysis. With ITT analysis (sometimes referred to as analysis as randomized), everyone assigned to a treatment is counted in a treatment group whether or not he or she received that treatment. This seems counterintuitive because why would one consider a patient as having received a treatment when he or she did not? Is a compliers-only analysis (in which only those patients who were randomized to, received, and complied with the treatment intervention are counted) more logical? The answer lies in randomization, which is the most important reason why RCTs lead to the highest level of scientific evidence. The power of randomization is its ability to balance known and unknown confounders in the intervention and control groups. If all patients randomized to each group are not counted, the integrity of the randomization is compromised, and the strength of the RCT is reduced. Results obtained using a compliers-only analysis would only be equivalent if the same numbers of intervention and control subjects (and for the same reasons) were not compliant, which is unlikely and is why ITT is the preferred analytic method. If a patient was randomized to the intervention group but did not receive the intervention, one can argue that the outcome difference in the control group would be reduced. On the other hand, it is the outcome difference between the intervention and control groups that suggests that the intervention is beneficial. Finally, the as-treated analysis is generally used in a situation in which a medical intervention is compared with a surgical intervention and the medically treated patients cross over at some point to the surgical approach. 

The previous installment of this series on clinical research highlighted some im­portant fundamentals in cohort studies and randomized controlled trials (RCTs). In this article, additional issues that are critical to the understanding of RCTs are discussed, including causal inference, the use of surrogate measures, and the principle of intention to treat (ITT).

Stephen P. Glasser, MD, is professor of preventive medicine

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