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Clinical Trials

So how does the science of medicine bridge the gap between knowing the correlates and potential causes of a disease and finding treatments that work and are safe? Our most important tool is the clinical trial. Clinical trials are simple in concept. One defines a group of patients that will potentially benefit from a particular treatment of unknown value, give some of them the new treatment (added to the existing standard of care) and some of them only the existing standard of care (the “control” group), wait a predefined amount of time, and compare the response of the treatment versus the control group. There are many variations on this theme. The response may be death versus recovery, incidence versus prevention of a known complication, development of an antibody response to a vaccine, etc. One may have more than one active treatment groups using different drugs or different dosages of the same drug. The treatment may not be a drug at all, but rather a surgical procedure, a diet, a vaccine, or even a diagnostic testing strategy. Each study participant may have to be treated only one time or continually and may have to be followed for days, weeks, months, or even years to determine outcomes. The required number of participants in the trial may be 100 or 10,000. But it always boils down to comparing one or more predefined regimens to a predefined control group for a predefined outcome in a predefined target population.

As pointed out by my former division director Michael Lauer in a 2010 presentation, clinical trials have been around for a long time. In 17th-century London, a clinical trial of the ancient practice of bloodletting for treating fevers (an offshoot of the theory of “humors”—nothing to do with comedy) was announced in the following colorful language:

Come down to the contest ye Humorists: Let us take out of the Hospitals or the camps or elsewhere, 200, or 500 poor People, that have Fevers etc. Let us divide them in Halfes, let us cast lots, that one half of them may fall to my share and the other to yours; I will cure them without bloodletting…; but do you do as ye know. We shall see how many Funerals both of us shall have: But let the reward of the contention or wager, be 300 Florens, deposited on both sides: Here your business is decided.¹

The outcome of that particular “contest” is lost to history, but in the 1740s, a Scottish émigré to Maryland, Dr. Alexander Hamilton (no relation to the founding father), published the following account of a similar trial in patients with febrile infections:

It had been so arranged, that this number was admitted, alternately, in such a manner that each of us had one third of the whole. The sick were indiscriminately received and were attended as nearly as possible with the same care and accommodated with the same comforts. Neither Mr. Anderson nor I ever once employed the lancet. He lost two, I four cases; whilst out of the other third [treated with bloodletting by the third surgeon] thirty-five patients died.²

Unfortunately, this resounding rejection of the efficacy of bloodletting, published while George Washington was a teenager, could not save the good general from the ministrations of his physicians in 1799, who treated him for a bacterial infection in which his breathing was obstructed by an inflamed and swollen epiglottis by performing bloodletting and a host of other noxious procedures (emetics, enemas, blistering his throat, forcing him to gargle molasses) instead of a administering a potentially life-saving tracheotomy (which was available in 1799).³ Even in 1892, almost a century later and after the germ theory of infectious diseases had been firmly established, the eminent physician William Osler opined: “During the first five decades of this century the profession bled too much, but during the last decades, we have certainly bled too little.”⁴ So the problem was not only that few clinical trials were done, but that even the wisest and most respected physicians persisted in their mistaken beliefs and practices despite contrary evidence.

As simple as clinical trials are conceptually, they can be extraordinarily complex, resource-intensive, and expensive to operationalize. The fact that clinical trials entail experimental research in human volunteers imposes significant ethical and regulatory requirements. Moreover, clinical trials must be designed to address the following challenges:

1. How can one know that any observed differences between treatment and control groups can be attributed to the treatment itself and not due to extraneous differences between groups (i.e., “confounding” variables)?

2. How can one know that any observed differences between treatment and control groups signify a true treatment effect and not merely the play of chance?

3. How applicable (generalizable) are the results of a clinical trial in a selected group of volunteers to the broad population of patients affected by the condition being studied?

While the science of clinical trials is far too complex to cover here, I will provide a primer that will impart a basic understanding of the evidence behind (and perhaps even a critical eye toward) modern clinical recommendations flowing from the myriad of heart disease trials that have been conducted. I encourage readers who want to know more to check out the excellent textbook by Friedman et al.⁵

Controlling for Confounding Variables

When evaluating treatment X for a new or unstudied disease (COVID-19, for example), one starts with an accepted standard of care (e.g., bed rest, Tylenol for fever, hospitalization for those needing oxygen, intensive care for those requiring a ventilator). One knows that a fraction of patients will recover under standard care, and that this fraction may vary from more than 99% in young previously healthy patients with mild symptoms to less than 40% in older or sicker patients in the intensive care unit. Obviously, if we want to know whether treatment X works, we have to be certain that the patients receiving treatment X are comparable those in the control group when the trial begins. We clearly would not believe a study in which treatment X were given only to the sickest patients, while the control group included the full spectrum of disease—or vice versa. Variables that differ between the actively treated and control groups and could affect treatment outcomes are called “confounders.” The surest way to know that our treatment and control groups are comparable when we begin is to assign eligible patients randomly to one group or the other. This process, called randomization, is considered a fundamental attribute of a well-designed clinical trial. While there are some circumstances where randomization to treatment versus control may be unfeasible or unethical (for example, when a disease is 100% fatal under standard care), you should generally look askance at any clinical trial that is not randomized.

But randomization is only the first step to control for confounding. Even if the treatment and control groups are similar when they start the trial, how can we ensure that they remain similar thereafter in all regards except for the one critical difference of whether they are assigned to the group receiving treatment X or to the control group? For example, what if a number of patients who are assigned to the control group start taking treatment Y while those assigned to treatment X do not? How can we be certain that any differences in recovery rate are due to treatment X and not treatment Y? Or what if the study investigators attribute some adverse outcome they observe in control patients to the disease under study, but fail to make the same attribution in patients assigned to treatment X? The surest remedy for this kind of confounding is “blinding”—or the more politically correct (until recently perhaps) “masking.” In a single-blind study, the participants are kept ignorant of whether they are in the control group or the group receiving treatment X. This is generally accomplished by giving the control group a placebo pill that looks, feels, smells, and tastes just like treatment X but contains no active agent. In a double-blind study, which is even better, both the participants and the investigators are kept ignorant of whether a particular person has been assigned to the active treatment or control group. In order to carry out a double-blind study, clinical trial investigators generally outsource the necessary functions of randomization, provision of the assigned treatment (X or placebo) and compiling and analyzing unmasked data to a separate data coordinating center, which reports periodically to an external data and safety monitoring board (DSMB). The DSMB periodically evaluates how the data are trending and judges whether it is safe and necessary to continue the trial.

Confounding may also rear its ugly head in the analysis of a trial. For example, if one is conducting a trial in free-living volunteers, a number of them may move away or decide to withdraw from the study. It is not safe to assume that these “drop-outs” are random or will not create spurious differences between treatment groups. It is therefore incumbent upon investigators to make every effort to find these people and establish at least whether they are dead or alive. Investigators may also be tempted to exclude some participants post hoc because they have not complied with the treatment or because they have certain outcomes that do not fit the original design. One of the important tenets of the science of clinical trials is to analyze data by “intention to treat” rather than by whether participants actually complied with the treatment to which they were randomized. This seems counter-intuitive, but when you start excluding or reclassifying people you have randomized, you no longer have a randomized trial and you open the door for confounding. The better alternative is to build in a margin for non-compliance in the trial design by randomizing more participants than you think are needed and to do everything possible to maximize compliance during the trial, while still respecting the rights of the participants to autonomy in decision-making.

Ruling Out the Play of Chance

When one performs an experiment in the physical sciences, say on the force exerted by the earth’s gravity on a 20-pound iron block, one may assume that one 20-pound iron block is very much like another and eschew the use of multiple blocks and complex statistical analysis to interpret the results. This is not true for clinical trials, which are conducted in human beings, whose characteristics and responses to treatment vary widely. Thus, clinical trial results must necessarily be judged by probabilistic criteria, in which one asks how likely is it that a result at least as good as the one observed could have happened by chance? Typically, a probability (often called the P-value) of 5% (or one in 20) is taken as the arbitrary threshold for statistical significance, that is for rejecting the possibility that the result happened by pure chance. To put this threshold in context, the chance of the number 22 coming up on an honest roulette wheel is one in 38, or roughly 2.6%. The probability of shooting a “natural” 7 or 11 at the crap table is 8/36 or roughly 22%. So clinical trials “pay off” on a probability that is roughly half as stringent as the probability of winning on a single number at roulette and 4.5 times as stringent as that of shooting a natural at the craps table.

Every good clinical trial is designed with the objective of having enough patients to yield a strong probability (or “power”) of producing a “significant” (P < 0.05) result if the starting hypothesis is correct. The way to do this is by calculating in advance how many patients you need to enroll to detect the hypothesized effect. Typically, most cardiovascular trials have been designed with at least 80% power, although 85 or 90% is even better. The smaller the effect you wish to detect, the more patients you will need for your trial. If you are evaluating a new antibiotic in patients with a highly lethal infectious disease and you expect an 80–90% cure rate, as few as 50 participants may be sufficient to demonstrate a significant benefit in a matter of weeks or months. In a chronic condition like coronary heart disease, where the standard of care already includes many established effective drugs, establishing the modest incremental benefit of a new drug may require 10,000 patients followed for seven years or more.

The number of patients required for a well-powered cardiovascular trial—i.e., its sample size—depends on the nature and frequency of the primary outcome (or end point) and the nature and size of the treatment effect one is trying to confirm. In general:

• Trials in which the primary outcome is an infrequent discrete event like death or a heart attack require larger sample sizes than trials looking at a continuous outcome (like weight loss) or the incidence of a more frequent event.

• When the primary outcome is a cardiovascular event or death, primary prevention trials—i.e., those performed in participants with risk factors but without known cardiovascular disease—require larger sample sizes than secondary prevention trials—i.e., those performed in participants with known cardiovascular disease.

• Trials in which a new treatment is compared with a known effective standard treatment require larger sample sizes than trials in which the new treatment is compared with a placebo or no treatment.

• Effectiveness trials, which look at the “real world” impact of interventions, tend to require larger sample sizes than efficacy trials, which look at treatment effects under well-controlled conditions.

Most of the cardiovascular trials discussed in this book are in the moderately large (1000–9999 participants) range. The smaller trials tend mostly to be efficacy trials of secondary prevention. Most of the “megatrials”—i.e., those with 10,000 participants or more—are either primary prevention trials in healthy participants or effectiveness trials looking for modest outcome differences in real world settings. Many examples of each of these categories of trials will be discussed in the coming chapters.

Probabilities only make sense if all the relevant parameters—the treatment, the population and outcome of interest, the primary analytic method, and the criteria for stopping—are specified in advance, i.e., before the experiment has begun. No casino that wanted to stay in business would pay a customer who placed his bet after seeing where the ball landed. Likewise, a trial designed to test the effect of a new drug on all-cause mortality cannot claim a positive result if it shows a significant decrease in heart attacks but no change in mortality. A trial may specify more than one primary outcome or a subgroup of especial interest, just as a roulette player may gamble on a group of numbers (odd or even, red or black). But just as the payoff is less for the roulette player who hedges his bet, the statistical criteria for claiming a significant result become stricter when multiple primary outcomes are specified.

Generalizability

Every trial designer is faced at the outset with a decision on how to define the trial’s target population. At one extreme, a trial may target a very specific group of patients—for example COVID-19 patients on a ventilator for at least 24 hours or 35- to 59-year-old men with no history of heart attack or diabetes and serum cholesterol > 265 mg/dL. This may give you a better chance (in theory at least) to get a positive result but will leave a lot of unanswered questions about whether your therapy works in other groups. At the opposite extreme, you may include all comers with the condition in question at the risk of getting a muddled result if the treatment works better in some groups than others. Sometimes one can strive for the best of both worlds by incorporating a broad population and including enough members of key subgroups to power at least exploratory analyses in those groups, but often this means making the studies prohibitively large and expensive. A good rule of thumb is to design the study with specificity when prior lab or animal studies provide ample grounds to predict that a treatment might work better in one group than another but not to make arbitrary exclusions when such grounds are lacking.

Factorial Designs

Factorial trials are a somewhat arcane wrinkle on clinical trials, which have grown more popular as cardiovascular trials have grown ever more complex and expensive. Readers who are in a hurry may skip over this section now and refer back to it when the subject comes up in later chapters.

Basically, the factorial design is a clever strategy to do two or more trials for the price of one. In the simplest version, the 2×2 factorial trial (Figure 3.1), there are two treatments (A and B), each with its own control, and participants are randomized independently to Active or Control for each treatment.

FIGURE 3.1. A Simple 2×2 Factorial Design

When the trial is analyzed, all participants randomized to Active A are compared to all participants randomized to Control A (irrespective of whether they were randomized to Active B or Control B). Similarly, all participants randomized to Active B are compared to all participants randomized to Control B (irrespective of whether they were randomized to Active A or Control A). This design requires a study population in whom it is appropriate to randomize every member to all four possible combinations of treatments A and B. An example of a simple 2×2 factorial trial is the Women’s Health Study (WHS), in which almost 40,000 women with no prior history of a heart attack were randomized to receive low-dose-aspirin versus placebo and vitamin E versus placebo; neither reduced subsequent major cardiovascular events (the primary outcome) significantly.⁶ The validity of this design rests on the assumption that the efficacy of treatment A is not influenced by treatment B and vice versa; i.e., the treatments do not interact. If this assumption were false, the trial would have to be analyzed as four separate groups and the efficiency of the factorial design would be lost.

More complicated versions of the factorial design exist. In a partial factorial design, not everyone is randomized to treatment B. The ACCORD diabetes trial (illustrated in Figure 3.2) is a variant of this partial factorial design, in which all participants who are not randomized to Treatment B versus control are randomized instead to Treatment C versus control.

FIGURE 3.2. A 2×2 Partial Factorial Design

This trial, in which the primary objective was to compare mortality rates in diabetic patients receiving intensive versus standard diabetes management in 10,251 diabetic patients will come up in Chapters 4, 7, and 9.⁷ The ACCORD design required that every participant have either high blood pressure (BP) or a lipid disorder called metabolic syndrome in addition to diabetes. The subset of participants with high BP were randomized secondarily to receive intensive versus standard BP management, while the subset with metabolic syndrome was randomized secondarily to receive the drug fenofibrate or a placebo. So everyone was randomized twice, but only the first randomization was the same for every participant. Other variants of factorial designs include the 2×2×2 factorial, in which each participant is randomized independently with respect to three treatments, the 2×3 factorial design, in which there are two independent randomizations, but one of them involves comparing two dosage versus placebo, and many others. However, the more complicated the design, the harder it becomes to identify and recruit the appropriate population, and the more likely that the treatments will interact. So, mercifully, more complicated factorial trials are rare.

Negative Trials

It is safe to say that everyone who participates in a clinical trial is thrilled when their trial’s result is positive and disappointed when it is negative. After all, who among us would not prefer to have their ideas proven right than proven wrong? However, one must not conflate a negative trial with a bad trial. There are many reasons a trial may be negative. Some trials turn out to be negative because of flaws in their design—most often, overly optimistic assumptions about how many participants they will need, how many they can recruit, compliance, and the choice of primary endpoint. Even the best designed trial may fail if it is poorly executed. However, a well-designed and well-executed trial that obtains a robust negative result may be just as valuable as a positive trial by establishing unequivocally that the new treatment is not beneficial, or even harmful. Such a result may even produce a paradigm shift that leads to new ways of thinking about a disease and new avenues of research to explore. Disappointing as this may be to the investigators and sponsors of such a trial, these results may save millions of future patients from receiving an ineffective or harmful treatment and redirect societal resources to finding a treatment that works. The story of the Cardiac Arrhythmia Suppression Trial (CAST) illustrates this point.⁸

The normal heart has a network of specialized fibers that generates and conducts the electrical signals that initiate and regulate the heartbeat so that fresh oxygen-carrying blood is pumped into the arteries about once every second (see Figure 12.1). When a heart attack occurs, this specialized conducting system in the heart may get damaged and put out stray signals even after the heart recovers its pumping capacity. These stray signals may generate runs of irregular heartbeats (arrhythmias), which at best are upsetting and at worst may commandeer the heart to beat too rapidly (tachycardia) or even to beat chaotically (ventricular fibrillation) in a way that disables its function as a pump. When this happens, the heart must be quickly shocked to restore normal rhythm and prevent death.

Given these dire possibilities, the development of well-tolerated orally administered drugs that reduced the frequency of irregular heartbeats in heart attack survivors was welcomed in the 1980s as a potential game changer. Intravenously administered anti-arrhythmic drugs like lidocaine were widely used at that time in the intensive coronary care setting but were not suitable for outpatient use. So it was broadly assumed that anti-arrhythmic drugs that could be prescribed to outpatients would save lives—so much so that many physicians had ethical reservations about even doing a randomized trial with a placebo control group. Nevertheless, the NIH undertook the CAST trial in June 1987, and set out to randomize 4400 post-heart attack patients to receive one of three anti-arrhythmic drugs (encainide, flecainide, moricizine) or placebo. The fact that any given patient was roughly three times as likely to receive an active drug than a placebo helped ease some of the ethical reservations about including a placebo control group.

Well, it turned out that the patients who received the placebo were the lucky ones. In April 1989, less than two years into the trial, the study’s DSMB stopped the trial because of a 3.6-fold increase in arrhythmic deaths in the patients randomized to the encainide and flecainide groups—a highly significant finding, which turned expectations on their head.⁹ Indeed, the DSMB almost failed to act because they had elected to be blinded as to which group was which (a terrible idea) and had blithely assumed that it was the placebo group with the higher mortality until a junior statistician at the coordinating center alerted them to the truth. The findings were less stark in the patients assigned to moricizine, who were allowed to continue in the trial until August 1991, when it was learned that they too were experiencing more harm (excess deaths) than good from their anti-arrhythmic drug treatment.¹⁰

So was CAST a failure? It was certainly a harrowing experience, in which some trial participants died who might not have died if they had been left untreated. But would they have been left untreated if they had not been enrolled in CAST? Almost certainly not! The three drugs used in CAST were widely prescribed in clinical practice by physicians who thought they KNEW that suppressing arrhythmia saved lives. In clinical practice, where there would be no DSMB monitoring their experience and comparing them with a control group, far more undoubtedly would have died. And because of CAST, thousands of later patients did not receive these harmful drugs. Therefore, I would argue that CAST was just as important as the positive trials we will talk about later, which established the benefit of many of the drugs and medical procedures we use today.

What’s in a Name?

Cardiovascular clinical trialists often express their latent creativity by giving their trials a descriptive name, that encapsulates what their trial is about and lends itself to a catchy acronym. In a few instances, like the MRFIT acronym (pronounced Mister Fit) for the Multiple Risk Factor Intervention Trial, the inconclusive non-blinded 1972–82 NHLBI trial of a multi-pronged special intervention strategy involving lifestyle changes and antihypertensive medication versus “usual care” in high-risk 35- to 57-year-old men, the marriage of trial and acronym is perfect.¹¹ More often, as in CAST, the acronym is serviceable if not particularly relatable to the nature of the trial. In some trials, like the Lipid Research Clinics Coronary Primary Prevention Trial (LRC-CPPT), the investigators didn’t even try to come up with a creative acronym.¹² Other trialists have gone into great contortions to add extra words to the name of their trial or hopscotch through its name, taking an initial here and three interior letters there, to create a catchy acronym. For example, a trial of the anti-diabetes drug pioglitazone was named the PROspective pioglitAzone Clinical Trial In macroVascular Events, which becomes “PROactive,” when one selects the bolded letters.¹³ Perhaps the most extreme example of runaway creativity is when the pharmaceutical company AstraZeneca gave names lending themselves to celestial acronyms to an entire constellation of rosuvastatin trials, under the umbrella name Galaxy.¹⁴ I’m not a big fan, but acronyms like JUPITER, METEOR, and STELLAR are catchy and pronounceable, even if they tell you nothing of what the trials are about. In any case, you will come to know many cardiovascular trials by name in the course of reading this book.

Meta-Analysis

Cardiovascular trials that address major health outcomes like mortality, heart attack, stroke, etc., are dauntingly complex, lengthy, and expensive enterprises, which always leave some questions unanswered, even when they are successful overall. They may show a significant overall benefit but may lack sufficient power to address important subgroups of interest. Or they may be negative overall but show promising effects in some important subgroup. Or they may show benefit for some outcome not specified in the study design. Meta-analysis is a statistical technique for combining the results of multiple similar trials to tease out beneficial or adverse effects of treatment that no single trial is large enough to address.

Unfortunately, meta-analysis is easy to manipulate or misuse. Most meta-analyses are performed after the fact—sometimes by investigators with an axe to grind—leaving the meta-analyst free to cherry-pick results by including trials that fit his/her hypothesis while finding sensible sounding reasons to exclude trials with inconvenient results. Before the statin trials came along (Chapter 5), the cholesterol field was full of competing meta-analyses drawing diametrically opposite conclusions from the same body of evidence.¹⁵ Indeed, one-time Framingham director William Castelli once threw up his hands in mock despair at a 1992 research conference and wittily proclaimed that “meta-analysis is to analysis as meta-physics is to physics.” The problem with retrospective meta-analysis is similar to that of analyzing the results of a horse race the following day. With the benefit of hindsight, one can think of all sorts of rationalizations for why one horse exceeded expectations and another disappointed. But the only analysis that matters is the one you make before the race is run.

In the 1990s, researchers at Oxford have developed and refined a technique called “prospective meta-analysis,” which enables us to combine the results of multiple similar clinical trials without falling prey to selection bias.¹⁶ In a prospective meta-analysis, a written protocol explicitly laying out all rules about which trials to include, which subgroups to analyze, etc., is published before the results of any component trial are known. Ideally, patient-level data (not just the published group-level data) are provided by the investigators of each participating trial. Then, when the results of the meta-analysis are published, the scientific audience can see for themselves that the meta-analyst has adhered to the protocol and has not cherry-picked which trials to include after the fact. As we shall see later, prospective meta-analysis has played a major role in amplifying and extending the power of cardiovascular trials to address multiple subgroups and positive and adverse outcomes that no single trial can adequately address.

In the coming chapters, we will see how insights gained from the laboratory, population science, and targeted clinical trials, and meta-analysis have gone hand in hand to tame the many-headed monster of cardiovascular disease over the past 50 years.

1. JA Van Helmont. Oriatrike. London: Lodowick-Loyd, 1662, p. 526.

2. I Milne, I Chalmers. A controlled clinical trial in 1809? J Epidemiol Community Health 2002; 56:1a.

3. The Mysterious Death of George Washington, Constitution Daily, December 14, 2019, https://constitutioncenter.org/blog/the-mysterious-death-of-george-washington.

4. M Bliss. William Osler: A Life in Medicine. Oxford: Oxford University Press, 1999, p. 188.

5. LM Friedman, CD Furberg, DL DeMets, DM Reboussin, CB Granger. Fundamentals of Clinical Trials. New York: Springer Science & Business Media, 5th edition, 2015.

6. ClinicalTrials.gov. The Women’s Health Study (WHS). https://clinicaltrials.gov/ct2/show/NCT00000479.

7. ClinicalTrials.gov. Action to Control Cardiovascular Risk in Diabetes (ACCORD). https://clinicaltrials.gov/ct2/show/NCT00000620?term=accord&draw=2&rank=1.

8. ClinicalTrials.gov. The Cardiac Arrhythmia Suppression Trial (CAST). https://clinicaltrials.gov/ct2/show/record/NCT00000526?term=flecanide&draw=5&rank=33&view=record.

9. Cardiac Arrhythmia Suppression Trial (CAST) Investigators. Preliminary report: effect of encainide and flecainide on mortality in a randomized trial of arrhythmia suppression after myocardial infarction. N Engl J Med 1989; 32:406–12.

10. HL Greene, DM Roden, RJ Katz, DM Slerno, RW Henthorn. The Cardiac Arrhythmia Suppression Trial: first CAST-I … then CAST-II. J Am Coll Cardiol 1992; 19:894–98, https://clinicaltrials.gov/ct2/show/record/NCT00000526?term=flecanide&draw=5&rank=33&view=record.

11. Multiple Risk Factor Intervention Trial Research Group. Multiple Risk Factor Intervention Trial. Risk factor changes and mortality results. JAMA 1982; 248:1465–77.

12. ClinicalTrials.gov. Lipid Research Clinics Coronary Primary Prevention Trial (LRC-CPPT). https://clinicaltrials.gov/ct2/show/NCT00000488?term=Lipid+Research+Clinics&draw=2&rank=2.

13. ClinicalTrials.gov. Efficacy of pioglitazone on macrovascular outcome in patients with type 2 diabetes (PROactive). https://clinicaltrials.gov/ct2/show/NCT00174993?term=PROactive+pioglitazone&draw=2&rank=1.

14. Editorial. The statin wars: why AstraZeneca must retreat. Lancet 2003; 362:1341.

15. DJ Gordon. Cholesterol and Mortality: What Can Meta-Analysis Tell Us? Cardiovascular Disease 2: Cellular and Molecular Mechanisms, Prevention, and Treatment, LL Gallo (ed.). New York: Plenum Press, 1995, pp. 333–340. DJ Gordon. Cholesterol Lowering Reduces Mortality. Cholesterol Lowering Therapies 1999. SM Grundy (ed.). New York: Marcel Dekker, Inc., 1999, pp. 299–311.

16. Cholesterol Treatment Trialists (CTC) Collaboration. Protocol for a prospective collaborative overview of all current and planned randomized trials of cholesterol treatment regimens. Am J Cardiol 1995; 75:1130–1134.