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Lawrence M. Friedman, Curt D. Furberg, David L. DeMets, David M. Reboussin and Christopher B. GrangerFundamentals of Clinical Trials10.1007/978-3-319-18539-2_1

1. Introduction to Clinical Trials

Lawrence M. Friedman¹, Curt D. Furberg², David L. DeMets³, David M. Reboussin⁴ and Christopher B. Granger⁵

(1)

North Bethesda, MD, USA

(2)

Division of Public Health Sciences, Wake Forest School of Medicine, Winston-Salem, NC, USA

(3)

Department Biostatistics and Medical Informatics, University of Wisconsin, Madison, WI, USA

(4)

Department of Biostatistics, Wake Forest School of Medicine, Winston-Salem, NC, USA

(5)

Department of Medicine, Duke University, Durham, NC, USA

The evolution of the modern clinical trial dates back at least to the eighteenth century [1, 2]. Lind, in his classical study on board the Salisbury, evaluated six treatments for scurvy in 12 patients. One of the two who was given oranges and lemons recovered quickly and was fit for duty after 6 days. The second was the best recovered of the others and was assigned the role of nurse to the remaining ten patients. Several other comparative studies were also conducted in the eighteenth and nineteenth centuries. The comparison groups comprised literature controls, other historical controls, and concurrent controls [2].

The concept of randomization was introduced by Fisher and applied in agricultural research in 1926 [3]. Probably the first clinical trial that used a form of random assignment of participants to study groups was reported in 1931 by Amberson et al. [4]. After careful matching of 24 patients with pulmonary tuberculosis into comparable groups of 12 each, a flip of a coin determined which group received sanocrysin, a gold compound commonly used at that time. The British Medical Research Council trial of streptomycin in patients with tuberculosis, reported in 1948, used random numbers in the allocation of individual participants to experimental and control groups [5, 6].

The principle of blinding was also introduced in the trial by Amberson et al. [4]. The participants were not aware of whether they received intravenous injections of sanocrysin or distilled water. In a trial of cold vaccines in 1938, Diehl and coworkers [7] referred to the saline solution given to the subjects in the control group as a placebo.

One of the early trials from the National Cancer Institute of the National Institutes of Health in 1960 randomly assigned patients with leukemia to either 6-azauracil or placebo. No treatment benefit was observed in this double-blind trial [8].

In the past several decades, the randomized clinical trial has emerged as the preferred method in the evaluation of medical interventions. Techniques of implementation and special methods of analysis have been developed during this period. Many of the principles have their origins in work by Hill [9–12]. For a brief history of key developments in clinical trials, see Chalmers [13].

The original authors of this book have spent their careers at the U.S. National Institutes of Health, in particular, the National Heart, Lung, and Blood Institute, and/or academia. The two new authors have been academically based throughout their careers. Therefore, many of the examples reflect these experiences. We also cite papers which review the history of clinical trials development at the NIH [14–18].

The purpose of this chapter is to define clinical trials, review the need for them, discuss timing and phasing of clinical trials, and present an outline of a study protocol.

Fundamental Point

A properly planned and executed clinical trial is the best experimental technique for assessing the effectiveness of an intervention. It also contributes to the identification of possible harms.

What Is a Clinical Trial?

We define a clinical trial as a prospective study comparing the effects and value of intervention (s) against a control in human beings. Note that a clinical trial is prospective, rather than retrospective. Study participants must be followed forward in time. They need not all be followed from an identical calendar date. In fact, this will occur only rarely. Each participant however, must be followed from a well-defined point in time, which becomes time zero or baseline for that person in the study. This contrasts with a case-control study, a type of retrospective observational study in which participants are selected on the basis of presence or absence of an event or condition of interest. By definition, such a study is not a clinical trial. People can also be identified from medical records or other data sources and subsequent records can be assessed for evidence of new events. With the increasing availability of electronic health records, this kind of research has become more feasible and may involve many tens of thousands of individuals. It is theoretically possible that the participants can be identified at the specific time they begin treatment with one or another intervention selected by the clinician, and then followed by means of subsequent health records. This type of study is not considered to be a clinical trial because it is unlikely that it is truly prospective. That is, many of the participants would have been identified after initiation of treatment and not directly observed from the moment of initiation. Thus, at least some of the follow-up data are retrospective. It also suffers from the major limitation that treatment is not chosen with an element of randomness. Thus associations between treatment and outcome are nearly always influenced by confounding factors, some of which are measured (and thus can be accounted for with adjustment) and others unmeasured (that cannot be). Of course, electronic records and registries can work effectively in collaboration with randomization into clinical trials. As exemplified by the Thrombus Aspiration in ST-Elevation Myocardial Infarction in Scandinavia (TASTE) trial [19], electronic registries greatly simplified the process of identifying and obtaining initial information on those people eligible for the trial. As noted by Lauer and D’Agostino [20], however, translating this approach into other settings will not be easy.

A clinical trial must employ one or more intervention techniques. These may be single or combinations of diagnostic, preventive, or therapeutic drugs, biologics, devices, regimens, procedures, or educational approaches. Intervention techniques should be applied to participants in a standard fashion in an effort to change some outcome. Follow-up of people over a period of time without active intervention may measure the natural history of a disease process, but it does not constitute a clinical trial. Without active intervention the study is observational because no experiment is being performed.

Early phase studies may be controlled or uncontrolled. Although common terminology refers to phase I and phase II trials, because they are sometimes uncontrolled, we will refer to them as clinical studies. A trial, using our definition, contains a control group against which the intervention group is compared. At baseline, the control group must be sufficiently similar in relevant respects to the intervention group in order that differences in outcome may reasonably be attributed to the action of the intervention. Methods for obtaining an appropriate control group are discussed in Chaps. 5 and 6. Most often a new intervention is compared with, or used along with, best current standard therapy. Only if no such standard exists or, for several reasons discussed in Chap. 2, is not available, is it appropriate for the participants in the intervention group to be compared to participants who are on no active treatment. “No active treatment” means that the participant may receive either a placebo or no treatment at all. Obviously, participants in all groups may be on a variety of additional therapies and regimens, so-called concomitant treatments, which may be either self-administered or prescribed by others (e.g., other physicians).

For purposes of this book, only studies in human beings will be considered as clinical trials. Certainly, animals (or plants) may be studied using similar techniques. However, this book focuses on trials in people, and each clinical trial must therefore incorporate participant safety considerations into its basic design. Equally important is the need for, and responsibility of, the investigator to inform fully potential participants about the trial, including information about potential benefits, harms, and treatment alternatives [21–24]. See Chap. 2 for further discussion of ethical issues.

Unlike animal studies, in clinical trials the investigator cannot dictate what an individual should do. He can only strongly encourage participants to avoid certain medications or procedures which might interfere with the trial. Since it may be impossible to have “pure” intervention and control groups, an investigator may not be able to compare interventions, but only intervention strategies. Strategies refer to attempts at getting all participants to adhere, to the best of their ability, to their originally assigned intervention. When planning a trial, the investigator should recognize the difficulties inherent in studies with human subjects and attempt to estimate the magnitude of participants’ failure to adhere strictly to the protocol. The implications of less than perfect adherence are considered in Chap. 8.

As discussed in Chaps. 6 and 7, the ideal clinical trial is one that is randomized and double-blind. Deviation from this standard has potential drawbacks which will be discussed in the relevant chapters. In some clinical trials compromise is unavoidable, but often deficiencies can be prevented or minimized by employing fundamental features of design, conduct, and analysis.

A number of people distinguish between demonstrating “efficacy” of an intervention and “effectiveness” of an intervention. They also refer to “explanatory” trials, as opposed to “pragmatic” or “practical” trials. Efficacy or explanatory trials refer to what the intervention accomplishes in an ideal setting. The term is sometimes used to justify not using an “intention-to-treat” analysis. As discussed in Chaps. 8 and 18, that is insufficient justification. Effectiveness or pragmatic trials refer to what the intervention accomplishes in actual practice, taking into account inclusion of participants who may incompletely adhere to the protocol or who for other reasons may not respond to an intervention. Both sorts of trials may address relevant questions and both sorts need to be properly performed. Therefore, we do not consider this distinction between trials as important as the proper design, conduct, and analysis of all trials in order to answer important clinical or public health questions, regardless of the setting in which they are done.

The SPIRIT 2013 Statement (Standard Protocol Items: Recommendations for Interventional Trials) [25], as well as the various International Conference on Harmonisation (ICH) documents [26] devote considerable attention to the quality of trials, and the features that make for high quality. Poorly designed, conducted, analyzed, and reported trials foster confusion and even erroneous interpretation of results. People have argued over what key elements deserve the most attention versus those that expend resources better used elsewhere. However, unless certain characteristics such as unbiased assignment to treatment of sufficient numbers of adequately characterized participants, objective and reasonably complete assessment of the primary and secondary outcomes, and proper analysis are performed, the trial may not yield interpretable results. Much of the rest of this book expands on these issues.

Clinical Trial Phases

In this book we focus on the design and analysis of randomized trials comparing the effectiveness and adverse effects of two or more treatments. Several steps or phases of clinical research, however, must occur before this comparison can be implemented. Classically, trials of pharmaceutical agents have been divided into phases I through IV. Studies with other kinds of interventions, particularly those involving behavior or lifestyle change or surgical approaches, will often not fit neatly into those phases. In addition, even trials of drugs may not fit into a single phase. For example, some may blend from phase I to phase II or from phase II to phase III. Therefore, it may be easier to think of early phase studies and late phase studies. Nevertheless, because they are in common use, and because early phase studies, even if uncontrolled, may provide information essential for the conduct of late phase trials, the phases are defined below.

A good summary of phases of clinical trials and the kinds of questions addressed at each phase was prepared by the International Conference on Harmonisation [26]. Figure 1.1, taken from that document, illustrates that research goals can overlap with more than one study phase.

Fig. 1.1

Correlation between development phases and types of study [26]

Thus, although pharmacology studies in humans that examine drug tolerance, metabolism, and interactions, and describe pharmacokinetics and pharmacodynamics, are generally done as phase I, some pharmacology studies may be done in other trial phases. Therapeutic exploratory studies, which look at the effects of various doses and typically use biomarkers as the outcome, are generally thought of as phase II. However, sometimes, they may be incorporated into other phases. The usual phase III trial consists of therapeutic confirmatory studies, which demonstrate clinical usefulness and examine the safety profile. But such studies may also be done in phase II or phase IV trials. Therapeutic use studies, which examine the drug in broad or special populations and seek to identify uncommon adverse effects, are almost always phase IV (or post-approval) trials.

Phase I Studies

Although useful pre-clinical information may be obtained from in vitro studies or animal models, early data must also be obtained in humans. People who participate in phase I studies generally are healthy volunteers, but may be patients who have already tried and failed to improve on the existing standard therapies. Phase I studies attempt to estimate tolerability and characterize pharmacokinetics and pharmacodynamics. They focus on questions such as bioavailability and body compartment distribution of the drug and metabolites. They also provide preliminary assessment of drug activity [26]. These studies may also assess feasibility and safety of pharmaceutical or biologic delivery systems. For example, in gene transfer studies, the action of the vector is an important feature. Implantable devices that release an active agent require evaluation along with the agent to assess whether the device is safe and delivers the agent in appropriate doses.

Buoen et al. reviewed 105 phase I dose-escalation studies in several medical disciplines that used healthy volunteers [27]. Despite the development of new designs, primarily in the field of cancer research, most of the studies in the survey employed simple dose-escalation approaches.

Often, one of the first steps in evaluating drugs is to estimate how large a dose can be given before unacceptable toxicity is experienced by patients [28–33]. This is usually referred to as the maximally tolerated dose. Much of the early literature has discussed how to extrapolate animal model data to the starting dose in humans [34] or how to step up the dose levels to achieve the maximally tolerated dose.

In estimating the maximally tolerated dose, the investigator usually starts with a very low dose and escalates the dose until a prespecified level of toxicity is obtained. Typically, a small number of participants, usually three, are entered sequentially at a particular dose. If no specified level of toxicity is observed, the next predefined higher dose level is used. If unacceptable toxicity is observed in any of the three participants, additional participants, usually three, are treated at the same dose. If no further toxicity is seen, the dose is escalated to the next higher dose. If additional unacceptable toxicity is observed, then the dose escalation is terminated and that dose, or perhaps the previous dose, is declared to be the maximally tolerated dose. This particular design assumes that the maximally tolerated dose occurs when approximately one-third of the participants experience unacceptable toxicity. Variations of this design exist, but most are similar.

Some [32, 35–37] have proposed more sophisticated designs in cancer research that specify a sampling scheme for dose escalation and a statistical model for the estimate of the maximally tolerated dose and its standard error. The sampling scheme must be conservative in dose escalation so as not to overshoot the maximally tolerated dose by very much, but at the same time be efficient in the number of participants studied. Many of the proposed schemes utilize a step-up/step-down approach; the simplest being an extension of the previously mentioned design to allow step-downs instead of termination after unacceptable toxicity, with the possibly of subsequent step-ups. Further increase or decrease in the dose level depends on whether or not toxicity is observed at a given dose. Dose escalation stops when the process seems to have converged around a particular dose level. Once the data are generated, a dose response model is fit to the data and estimates of the maximally tolerated dose can be obtained as a function of the specified probability of a toxic response [32].

Bayesian approaches have also been developed [38, 39]. These involve methods employing continual reassessment [35, 40] and escalation with overdose control [41]. Bayesian methods involve the specification of the investigators’ prior opinions about the agent’s dose-toxicity profile, which is then used to select starting doses, and escalation rules. The most common Bayesian phase I design is called the continual reassessment method, [35] in which the starting dose is set to the prior estimate of the maximally tolerated dose. After the first cohort of participants (typically of size 1, 2, or 3, though other numbers are possible), the estimate is updated and the next participant(s) assigned to that estimate. The process is repeated until a prespecified number of participants have been assigned. The dose at which a hypothetical additional participant would be assigned constitutes the final estimate of the maximally tolerated dose. Bayesian methods that constrain the number of total toxicities have also been developed (escalation with overdose control) as have designs that allow for two or more treatments [42] and methods that allow for incomplete follow-up of long-term toxicities (time-to-event continual reassessment method) [43]. Many variations have been proposed. An advantage of Bayesian phase I designs is that they are very flexible, allowing risk factors and other sources of information to be incorporated into escalation decisions. A disadvantage is their complexity, leading to unintuitive dose assignment rules.

A detailed description of the design and conduct of dose escalating trials for treatments of cancer is found in Chaps. 1–5 of a book edited by Crowley and Ankerst [44]. A book edited by Ting contains a more general discussion of dose-selection approaches [45].

Phase II Studies

Once a dose or range of doses is determined, the next goal is to evaluate whether the drug has any biological activity or effect. The comparison may consist of a concurrent control group, historical controls, or pre-treatment status versus post-treatment status. Because of uncertainty with regard to dose-response, phase II studies may also employ several doses, with perhaps four or five intervention arms. They will look, for example, at the relationship between blood level and activity. Genetic testing is common, particularly when there is evidence of variation in rate of drug metabolism. Participants in phase II studies are usually carefully selected, with narrow inclusion criteria [26].

Although sometimes phase II studies are used for regulatory agency approval of a product, generally phase II studies are performed to make a decision as to whether to further develop a new drug or device. As such, the purpose is to refine an estimate of the probability of success in phase III. Success depends on a variety of factors, including estimated beneficial and adverse effects, feasibility, and event rates of the target population. Because phase II trials by definition do not have adequate power to define the effect on major clinical outcomes, the estimate of treatment effect and harm may depend on multiple inputs, including effects on biomarkers, on more common but less definitive clinical outcomes (like unstable angina rather than myocardial infarction) and on more minor safety signals (like minor bleeding or modest elevation in liver function tests).

The phase II design depends on the quality and adequacy of the phase I study. The results of the phase II study will, in turn, be used to design the phase III trial. The statistical literature for phase II studies, which had been rather limited [46–52] has expanded [53, 54] and, as with phase I studies, includes Bayesian methods [55, 56].

One of the traditional phase II designs in cancer is based on the work of Gehan [46], which is a version of a two stage design. In the first stage, the investigator attempts to rule out drugs which have no or little biologic activity. For example, he may specify that a drug must have some minimal level of activity, say, in 20% of patients. If the estimated activity level is less than 20%, he chooses not to consider this drug further, at least not at that maximally tolerated dose. If the estimated activity level exceeds 20%, he will add more participants to get a better estimate of the response rate. A typical study for ruling out a 20% or lower response rate enters 14 participants. If no response is observed in the first 14 participants, the drug is considered not likely to have a 20% or higher activity level. The number of patients added depends on the degree of precision desired, but ranges from 10 to 20. Thus, a typical cancer phase II study might include fewer than 30 people to estimate the response rate. As is discussed in Chap. 8, the precision of the estimated response rate is important in the design of the controlled trial. In general, phase II studies are smaller than they ought to be.

Some [32, 47, 57] have proposed designs which have more stages or a sequential aspect. Others [50, 58] have considered hybrids of phase II and phase III designs in order to enhance efficiency. While these designs have desirable statistical properties, the most vulnerable aspect of phase II, as well as phase I studies, is the type of person enrolled. Usually, phase II studies have more exclusion criteria than phase III comparative trials. Furthermore, the outcome in the phase II study (e.g., tumor response) may be different than that used in the definitive comparative trial (e.g., survival). Refinements may include time to failure [54] and unequal numbers of participants in the various stages of the phase II study [59]. Bayesian designs for phase II studies require prior estimates, as was the case for phase I studies, but differ in that they are priors of efficacy measures for the dose or doses to be investigated rather than of toxicity rates. Priors are useful for incorporating historical data into the design and analysis of phase II trials. Methods are available for continuous [60], bivariate [60], and survival outcomes [61]. These methods can account not only for random variations in participant responses within institutions but also for systematic differences in outcomes between institutions in multicenter trials or when several control groups are combined. They also acknowledge the fact that historical efficacy measures of the control are estimated with error. This induces larger sample sizes than in trials which assume efficacy of the control to be known, but with correspondingly greater resistance to false positive and false negative errors. Bayesian methods can also be used in a decision-theoretic fashion to minimize a prespecified combination of these errors for a given sample size [62, 63].

Although not generally considered phase II studies, some pilot (or feasibility or vanguard) studies may serve similar functions. Particularly for studies of non-pharmacologic interventions, these pilot studies can uncover possible problems in implementing and assessing an intervention. Here, we distinguish pilot studies conducted for this purpose from those done to see if a design for a later phase trial is feasible. For example, can participant screening and enrollment and maintenance of adherence be successfully implemented?

Phase III/IV Trials

The phase III and phase IV trials are the clinical trials defined earlier in the chapter. They are generally designed to assess the effectiveness of new interventions or existing interventions with new indications and thereby, their value in clinical practice. They also examine adverse effects, but, as described below and in Chap. 12, assessment of harm in clinical trials has limitations. The focus of most of this book is on these late phase trials. However, many design assumptions depend on information obtained from phase I and phase II studies, or some combination of early phase studies.

Phase III trials of chronic conditions or diseases often have a short follow-up period for evaluation, relative to the period of time the intervention might be used in practice. In addition, they focus on efficacy or effectiveness, but knowledge of safety is also necessary to evaluate fully the proper role of an intervention in clinical practice. A procedure or device may fail after a few years and have adverse sequelae for the patient. In 2014, the FDA warned that morcellation to treat uterine fibroids by laparoscopic means, a procedure that had been used for years, could lead to spreading of unsuspected uterine sarcoma [64]. Thus, long-term surveillance of an intervention believed to be effective in phase III trials is often necessary. Such long-term studies or studies conducted after regulatory agency approval of the drug or device are referred to as phase IV trials. Drugs may be approved on the basis of intermediate or surrogate outcomes or biomarkers, such as blood pressure or cholesterol lowering. They may also be approved after relatively short term studies (weeks or months), even though in practice, in the case of chronic conditions, they may be taken for years or even decades. Even late phase clinical trials are limited in size to several hundred or thousand (at most, a few tens of thousands) of participants. Yet the approved drugs or devices will possibly be used by millions of people. This combination of incomplete information about clinical outcomes, relatively short duration, and limited size means that sometimes the balance between benefit and harm becomes clear only when larger phase IV studies are done, or when there is greater clinical experience. One example is some of the cyclooxygenase 2 (COX 2) inhibitors, which had been approved for arthritis pain, but only disclosed cardiovascular problems after larger trials were done. These larger trials were examining the effects of the COX 2 inhibitors on prevention of colon cancer in those with polyps [65, 66]. Similarly, only after they had been on the market were thiazolidinediones, a class of drugs used for diabetes, found to be associated with an increase in heart failure [67].

Regulatory agency approval of drugs, devices, and biologics may differ because, at least in the United States, the regulations for these different kinds of interventions are based on different laws. For example, FDA approval of drugs depends greatly on at least one well-designed clinical trial plus supporting evidence (often, another clinical trial). Approval of devices relies less on clinical trial data and more on engineering characteristics of the device, including similarity with previously approved devices. (For further discussion of regulatory issues, see Chap. 22.) Devices, however, are often implanted, and unless explanted, may be present for the life of the participant. Therefore, there are urgent needs for truly long-term data on performance of devices in vivo. Assessment of devices also depends, more so than drugs, on the skill of the person performing the implantation. As a result, the results obtained in a clinical trial, which typically uses primarily well-trained investigators, may not provide an accurate balance of harm and benefit in general practice.

The same caution applies to clinical trials of procedures of other sorts, whether surgical or lifestyle intervention, where only highly skilled practitioners are investigators. But unlike devices, procedures may have little or no regulatory oversight, although those paying for care often consider the evidence.

Why Are Clinical Trials Needed?

Well-designed and sufficiently large randomized clinical trials are the best method to establish which interventions are effective and generally safe and thereby improve public health. Unfortunately, a minority of recommendations in clinical practice guidelines are based on evidence from randomized trials, the type of evidence needed to have confidence in the results [68]. Thus, although trials provide the essential foundation of evidence, they do not exist for many commonly used therapies and preventive measures. Improving the capacity, quality and relevance of clinical trials is a major public health priority.

Much has been written about the advent of individualized medicine, where an intervention (usually a drug or biologic) is used specifically in a person for whom it was designed or who has a specific genetic marker. We may someday reach the point where that is possible for many conditions and therapies. But we are not there yet. With rare exceptions, the best we can generally do is to decide to use or not use a treatment that has been evaluated in a clinical trial in a given population. Even when we better understand the genetic components of a condition, the interaction with the environment usually precludes full knowledge of a disease’s patterns and course. Therefore, almost always, a clinical trial is the most definitive method of determining whether an intervention has the postulated effect. Even when a drug is designed to be used in people with selected genetic markers, clinical trials are still commonly conducted. An example is trastuzumab, which is beneficial in women with HER2 receptors in breast cancer [69–71]. Even here, treatment is only partly successful and can have major adverse effects. Benefits of using pharmacogenetics in the decisions to achieve optimum dosing of warfarin have been claimed from some studies, but not in others [72–75]. Given the uncertain knowledge about disease course and the usual large variations in biological measures, it is often difficult to say on the basis of uncontrolled clinical observation whether a new treatment has made a difference to outcome, and if it has, what the magnitude is. A clinical trial offers the possibility of such judgment because there exists a control group which, ideally, is comparable to the intervention group in every way except for the intervention being studied.

The consequences of not conducting appropriate clinical trials at the proper time can be both serious and costly. An example was the uncertainty as to the efficacy and safety of digitalis in congestive heart failure. Only in the 1990s, after the drug had been used for over 200 years, was a large clinical trial evaluating the effect of digitalis on mortality mounted [76]. Intermittent positive pressure breathing became an established therapy for chronic obstructive pulmonary disease without good evidence of benefits. One trial suggested no major benefit from this very expensive procedure [77]. Similarly, high concentration of oxygen was used for therapy in premature infants until a clinical trial demonstrated that it could cause blindness [78].

A clinical trial can determine the incidence of adverse effects or complications of the intervention. Few interventions, if any, are entirely free of undesirable effects. However, drug toxicity might go unnoticed without the systematic follow-up measurements obtained in a clinical trial of sufficient size. The Cardiac Arrhythmia Suppression Trial documented that commonly used anti-arrhythmic drugs were harmful in patients who had a history of myocardial infarction, and raised questions about routine use of an entire class of anti-arrhythmic agents [79]. Corticosteroids had been commonly used to treat people with traumatic brain injury. Small clinical trials were inconclusive, and a meta-analysis of 16 trials showed no difference in mortality between corticosteroids and control [80]. Because of the uncertainty as to benefit, a large clinical trial was conducted. This trial, with far more participants than the others combined, demonstrated a significant 18% relative increase in mortality at 14 days [81] and a 15% increase at 6 months in the corticosteroid group [82]. As a result, an update of the meta-analysis recommended against the routine use of corticosteroids in people with head injury [83]. Niacin was widely believed to be a safe and effective treatment to improve lipid parameters and reduce coronary heart disease events for patients at risk [84, 85]. The Atherothrombosis Intervention in Metabolic Syndrome with Low HDL/High Triglycerides: Impact on Global Health Outcomes (AIM-HIGH) trial failed to show added benefit from long-acting niacin in 3,414 participants with cardiovascular disease receiving statin therapy [86]. A concern with that trial was that it might have been underpowered. The Heart Protection Study 2-Treatment of HDL to Reduce the Incidence of Vascular Events (HPS2-THRIVE) [87] was designed to provide definitive information regarding the clinical effects of a combination formulation of niacin and laropiprant, an agent to prevent flushing side effects, on top of simvastatin. That trial of 25,673 participants also showed no reduction in the primary outcome of vascular events, but increases in serious adverse gastrointestinal events, infection, and onset and poor control of diabetes.

In the final evaluation, an investigator must compare the benefit of an intervention with its other, often unwanted effects in order to decide whether, and under what circumstances, its use should be recommended. The financial implications of an intervention, particularly if there is limited benefit, must also be considered. Several studies have indicated that drug eluting stents have somewhat less restenosis than bare metal stents in percutaneous coronary intervention [88, 89]. The cost difference, however, can be considerable, especially since more than one stent is typically inserted. The Comparison of Age-Related Macular Degeneration Treatments Trials (CATT) showed that ranibizumab and bevacizumab were similarly effective at the 1-year point with respect to visual acuity in people with age-related macular degeneration [90]. Bevacizumab appeared to have various more serious adverse effects, but was one-fortieth the cost of ranibizumab. Whether the difference in the adverse events is real is uncertain, as another trial of the same agents in the same population did not show it [91]. In both examples, are the added benefits or possibly fewer adverse events, which may be defined and measured in different ways, of the more expensive interventions worth the extra cost? Such assessments are not statistical in nature. They must rely on the judgment of the investigator and the medical practitioner as well as on those who pay for medical care. Clinical trials rarely fully assess costs of the interventions and associated patient care, which change over time, and cannot replace clinical judgment; they can only provide data so that decisions are evidence-based.

People suffering from or being treated for life-threatening diseases for which there are no known effective therapies and those caring for them often argue that controlled clinical trials are not needed and that they have a right to experimental interventions. Because there may be little hope of cure or even improvement, patients and their physicians want to have access to new interventions, even if those interventions have not been shown to be safe and effective by means of the usual clinical trial. They want to be in studies of these interventions, with the expectation that they will receive the new treatment, rather than the control (if there is a control group). Those with the acquired immunodeficiency syndrome (AIDS) used to make the case forcefully that traditional clinical trials are not the sole legitimate way of determining whether interventions are useful [92–95]. This is undeniably true, and clinical trial researchers need to be willing to modify, when necessary, aspects of study design or management. Many have been vocal in their demands that once a drug or biologic has undergone some minimal investigation, it should be available to those with life-threatening conditions, should they desire it, even without late phase clinical trial evidence [96]. If the patient community is unwilling to participate in clinical trials conducted along traditional lines, or in ways that are scientifically “pure,” trials are not feasible and no information will be forthcoming. When the situation involves a rare, life-threatening genetic disorder in children, what level of evidence is needed for patients and their families, clinicians, and regulatory authorities to approve use of new agents? When should accelerated or “fast track” approval occur? Should there be interim approval based on less rigid criteria, with use restricted to specific cases and situations? When should post-approval trials be required? The U.S. FDA approved bedaquiline for drug-resistant tuberculosis on the basis of a randomized trial of 160 patients with time to culture conversion as the primary outcome, even though the study was too small to reliably detect clinical outcomes [97, 98]. This was done because of the urgent need for new drugs and with the requirement that a “confirmatory trial” would be conducted. Investigators need to involve the relevant communities or populations at risk, even though this could lead to some compromises in design and scientific purity. Investigators need to decide when such compromises so invalidate the results that the study is not worth conducting. It should be noted that the rapidity with which trial results are demanded, the extent of community involvement, and the consequent effect on study design, can change as knowledge of the disease increases, as at least partially effective therapy becomes available, and as understanding of the need for valid research designs, including clinical trials, develops. This happened to a great extent with AIDS trials.

Although investigators should design clinical trials using the fundamentals discussed in this book, they must consider the context in which the trial is being conducted. The nature of the disease or condition being studied and the population and setting in which it is being done will influence the outcomes that are assessed, the kind of control, the size, the duration, and many other factors.

Clinical trials are conducted because it is expected that they will influence practice and therefore improve health [99–104]. Traditionally, there has been considerable delay in adoption of evidence from trials, depending on the direction of the results, strength of the findings, methods of dissemination of results, and other evidence. There is indirect evidence, though, that the results of clinical trials can affect practice, which in turn may improve health outcomes. Ford et al. [105] estimated that about half of the reduction in death from coronary artery disease in the United States between 1980 and 2000 was due to better control of risk factors. The other half of the reduction was due to improved treatments, most of which were based on clinical trial results. A specific example of change in practice based on evidence from trials and improved survival comes from a national registry in Sweden during 1996–2007. Increase use of reperfusion therapy, revascularization, and medications such as aspirin, beta blockers, clopidogrel, and statins in treatment of ST segment elevation myocardial infarction was associated with a 50% decrease in mortality over this relatively short period [106]. In the United States, a registry that included 350 hospitals from 2001 to 2003 showed 11% lower in-hospital mortality for each 10% improvement in hospital-level adherence to guideline-based treatment, with most of those treatment recommendations based on clinical trial results [107].

There is no such thing as a perfect study. However, a well thought-out, well-designed, appropriately conducted and analyzed clinical trial is an effective tool. While even well designed clinical trials are not infallible, they generally provide a sounder rationale for intervention than is obtainable by other research methods. On the other hand, poorly designed, conducted, and reported trials can be misleading. Also, without supporting evidence, no single study ought to be definitive. When interpreting the results of a trial, consistency with data from laboratory, animal, epidemiological, and other clinical research must be considered.

Some have claimed that observational studies provide the “correct” answer more often than not and that therefore clinical trials are often superfluous [108, 109]. Others have pointed out that sometimes, results of observational studies and clinical trials are inconsistent. Observational studies, many of them large, suggested that use of antioxidants would reduce the risk of cancer and heart disease. These agents began to be widely used as a result. Later, large randomized controlled trials evaluating many of the antioxidants demonstrated no benefit or even harm [110]. Similarly, because of the results from observational studies, hormone therapy was advocated for post-menopausal women as a way to prevent or reduce heart disease. Results of large clinical trials [111–113] cast considerable doubt on the findings from the observational studies. Whether the differences are due to the inherent limitations of observational studies (see Chap. 5) or more specifically to the “healthy user bias” has been debated, but these and numerous other examples [114] support the belief that observational studies are unreliable in determining modest intervention effects.

We believe that pitting one kind of clinical research against another is inappropriate. Both observational epidemiology studies, including registries, and clinical trials have their strengths and weaknesses; both have their place [115]. Proper understanding of the strengths and weaknesses of clinical trials, and how the results of well-designed and conducted trials can be used in conjunction with other research methodologies, is by far the best way of improving public health and scientific understanding.

Problems in the Timing of a Trial

Once drugs and procedures of unproved clinical benefit have become part of general medical practice, performing an adequate clinical trial becomes difficult ethically and logistically. Some people advocate instituting clinical trials as early as possible in the evaluation of new therapies [116, 117]. The trials, however, must be feasible. Assessing feasibility takes into account several factors. Before conducting a trial, an investigator needs to have the necessary knowledge and tools. He must know something about the expected adverse effects of the intervention and what outcomes to assess and have the techniques to do so. Well run clinical trials of adequate magnitude are costly, and therefore almost always require sponsors willing to pay for them, and should be done only when preliminary evidence of the efficacy and harm of an intervention looks promising enough to warrant the effort and expense involved.

Another aspect of timing is consideration of the relative stability of the intervention. If active research will be likely to make the intended intervention outmoded in a short time, studying such an intervention may be inappropriate. This is particularly true in long-term clinical trials, or studies that take many months to develop. One of the criticisms of trials of surgical interventions has been that surgical methods are constantly being improved. Evaluating an operative technique of several years past, when a study was initiated, may not reflect the current status of surgery [118–120].

These issues were raised years ago in connection with the Veterans Administration study of coronary artery bypass surgery [121]. The trial showed that surgery was beneficial in subgroups of patients with left main coronary artery disease and three vessel disease, but not overall [121–123]. Critics of the trial argued that when the trial was started, the surgical techniques were still evolving. Therefore, surgical mortality in the study did not reflect what occurred in actual practice at the end of the long-term trial. In addition, there were wide differences in surgical mortality between the cooperating clinics [124] that may have been related to the experience of the surgeons. Defenders of the study maintained that the surgical mortality in the Veterans Administration hospitals was not very different from the national experience at the time [125]. In the Coronary Artery Surgery Study [126] surgical mortality was lower than in the Veterans Administration trial, suggesting better technique. The control group mortality, however, was also lower. Despite continuing evolving technology, including the development of drug-eluting stents, many trials of coronary stents have been successfully undertaken [127, 128]. The changes in stent design and use of medications to limit stent thrombosis have been incorporated into each new trial.

Review articles show that surgical trials have been successfully undertaken [129, 130] and, despite challenges, can and should be conducted [131, 132]. While the best approach might be to postpone a trial until a procedure has reached is the point where it is unlikely to change greatly, at least in the near term, such a postponement will probably mean waiting until the procedure has been widely accepted as efficacious for some indication, thus making it difficult, if not impossible to conduct the trial. However, as noted by Chalmers and Sacks [133], allowing for improvements in operative techniques in a clinical trial is possible. As in all aspects of conducting a clinical trial, judgment must be used in determining the proper time to evaluate an intervention.

Study Protocol

Every well-designed clinical trial requires a protocol. The study protocol can be viewed as a written agreement between the investigator, the participant, and the scientific community. The contents provide the background, specify the objectives, and describe the design and organization of the trial. Every detail explaining how the trial is carried out does not need to be included, provided that a comprehensive manual of procedures contains such information. The protocol serves as a document to assist communication among those working in the trial. It should also be made available to others upon request. Many protocols are now being published in on-line journals.

The protocol should be developed before the beginning of participant enrollment and should remain essentially unchanged except perhaps for minor updates. Careful thought and justification should go into any changes. Major revisions which alter the direction of the trial should be rare. If they occur, the rationale behind such changes and the process by which they are made need to be clearly described. An example is the Cardiac Arrhythmia Suppression Trial, which, on the basis of important study findings, changed intervention, participant eligibility criteria, and sample size [134].

Numerous registries of clinical trials now exist. The WHO International Clinical Trials Registry Platform (ICTRP) [135] lists those registries, including ClinicalTrials.gov [136], one of the original registries that are acceptable to the International Committee of Medical Journal Editors. Registration of all late phase trials and many early phase studies is now advocated, and indeed required by many journals and sponsors. Journals will not publish results of trials or study design papers unless the study has been registered at one of the many sites. The U.S. National Institutes of Health requires that trials that it funds be registered [137], as does the Food and Drug Administration for trials it oversees [138]. The registry sites have, at a minimum, information about the study population, intervention and control, response variables, and other key elements of the study design. Reasons for registering trials include reducing the likelihood that trial results are not published or otherwise made known, providing a way to compare the study design as initially described with what was published, and allowing other researchers to determine what else is happening in their area of interest. From the ClinicalTrials.gov registry, we know that the majority (62%) of registered trials enroll 100 or fewer participants, the majority of trials (66%) are single center, and there is substantial variability in use of randomization, blinding, and use of monitoring committees [139]. We applaud the practice of registration, and encourage all investigators to go further by including links to their protocols at the registry sites. See Chap. 22 for a further discussion of trial registration.

A guidance for developing a clinical trials protocol has been published by the Standard Protocol Items: Recommendations for Interventional Trials (SPIRIT 2013 Statement) [25]. Topic headings of a typical protocol which also serve as an outline of the subsequent chapters in this book are given below:

A.

Background of the study
B.
Objectives
1.

Primary question and response variable

2.

Secondary questions and response variables

3.

Subgroup hypotheses

4.

Adverse effects
C.
Design of the study
1.

Study population

(a)

Inclusion criteria

(b)

Exclusion criteria

2.

Sample size assumptions and estimates

3.

Enrollment of participants

(a)

Informed consent

(b)

Assessment of eligibility

(c)

Baseline examination

(d)

Intervention allocation (e.g., randomization method)

4.

Intervention(s)

(a)

Description and schedule

(b)

Measures of compliance

5.

Follow-up visit description and schedule

6.

Ascertainment of response variables

(a)

Training

(b)

Data collection

(c)

Quality control

7.

Assessment of Adverse Events

(a)

Type and frequency

(b)

Instruments

(c)

Reporting

8.

Data analysis

(a)

Interim monitoring, including data monitoring committee role

(b)

Final analysis

9.

Termination policy
D.
Organization
1.

Participating investigators

(a)

Statistical unit or data coordinating center

(b)

Laboratories and other special units

(c)

Clinical center(s)

2.

Study administration

(a)

Steering committees and subcommittees

(b)

Monitoring committee

(c)

Funding organization

Appendices

Definitions of eligibility criteria

Definitions of response variables

Informed Consent Form

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