Clinical trials in neuroprotection$

Introduction

A clinical trial is a planned experiment in humans, designed to assess the safety or efficacy of a

$Adapted with permission from Whitcup, S.M. (2003). Clinical trials in neuroprotection. In: Levin L. and Di Polo A. (Eds.), Ocular Neuroprotection. Informa Healthcare, New York, pp. 291–301.

Corresponding author. Tel.: +1 714 246 4919;

Fax: +1 714 246 6987; E-mail: Whitcup_Scott@Allergan.com

treatment. Well-designed clinical trials should control for bias that can corrupt the interpretation of clinical data. Unfortunately, a great deal of medical practice is based on anecdotal clinical reports or poorly designed studies. Much of the scientific dogma we read in textbooks is actually based on retrospective reviews of inconclusive data obtained from a handful of patients. This is especially true of new therapies in medicine, where clinical experience and published data are lacking.

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Over the last two decades, there has been a great deal of interest in protecting neural tissue from loss of function and cell death in a number of neurodegenerative diseases including Alzheimer’s disease, Parkinson’s disease, amyotrophic lateral sclerosis (ALS), and glaucoma. Neural tissue in humans fails to regenerate and completely restore function; therefore, strategies to prevent the loss of neuronal cells are critical to the management of degenerative neurological disease. Neuroprotection is a therapeutic approach to prevent degeneration and prolong function. Clinical trials of neuroprotective therapies pose unique problems to study design. This chapter will review key principles in the design and conduct of clinical trials with a focus on the challenges of clinical trials in neuroprotection.

Methods of clinical studies

There are four basic types of clinical studies: case series, case–control studies, cohort studies, and randomized clinical trials. Case reports or case series are usually retrospective reviews that detail the clinical findings and outcomes of patients with a particular disease. Although these reports can help define the manifestations of a disease, they are prone to bias and can mislead the reader. Since the data are collected retrospectively from patient charts, critical information is often missing. The disease may not be well defined in the report, and some of the reported patients may actually have a different condition. There may be bias in acquiring the patients, and the reported patients may be dissimilar from the general patient population. Case series tend to be written by specialists who treat patients with more severe or atypical disease. Importantly, case series lack a control group for comparison. For example, a physician could report two patients with nonarteritic anterior ischemic optic neuropathy (NAION) who had substantial improvement in their vision after starting multivitamins. It would be difficult to conclude that vitamins improve vision in patients with this disease without knowing how many patients with NAION on vitamins had no improvement in vision.

Occasionally, investigators will try to compensate for the lack of an appropriate control group in a study by comparing their study results to a group of historical controls. The investigators agree that a control group is needed, but are still reluctant to randomly assign patients to the new treatment or to a standard therapy or placebo for a number of reasons. First, it is much more difficult to conduct a well-controlled, randomized clinical trial. A protocol needs to be written; institutional review board (IRB) approval is required; and the methods for patient randomization, conduct of the trial, collection of the data, and analysis of the results need to be detailed. Second, many investigators truly believe that the new treatment is better and that it would be unethical to keep patients from receiving it.

The main problem with the use of historical controls is that data from historical controls tend to be biased. Historical data are often collected differently from patients enrolled in a trial and followed prospectively (information bias). Patients in a trial can also differ clinically from the patients in a historical control group (selection bias), not only in recognized important clinical parameters like disease severity, but also in potentially unrecognized or undocumented parameters that could affect clinical outcome — diet or other environmental factors, for example.

In fact, there are numerous other sources of bias in clinical studies (Sackett, 1979). Observer bias leads to a systematic alteration in the measuring of a response in patients. Invalidated or inappropriate instruments for measurement can also bias the results of a study. In a properly designed trial, controlling for confounding factors can minimize bias. Randomization, for example, can help to distribute these factors evenly in the treatment groups. Importantly, randomization helps to balance unrecognized sources of bias between groups.

In a case–control study, the investigator compares a group of patients with a given disorder to a control group without this condition. The clinical records of both groups are then compared to see if certain factors occur more commonly in one group. A classic example of a case–control study is a comparison of the smoking history of a group

of patients with lung cancer and an ageand sexmatched control group. One can then calculate an odds ratio that states the relative risk for a condition like lung cancer given a specific risk factor like smoking. For example, an odds ratio of 6.7 would mean that people who smoke are 6.7 times more likely to develop lung cancer than people who do not smoke.

Case–control studies, although more powerful than case series, also rely on a retrospective review of patient records. Again, bias may systematically alter the data and lead to inappropriate conclusions. There may be a recording bias in the information collected from patients and controls. For example, patients with cancer may spend more time thinking about their medical history and reasons why they might have developed their disease than would a person without the disease. Physicians may spend a great deal of time detailing clinical information from patients that may not be collected from controls. Despite this potential bias, well-conducted case–control studies can provide useful clinical information, especially when standard procedures for data collection are followed. Furthermore, case– control studies may be the only feasible method for studying certain rare conditions.

Cohort studies identify two groups of patients, or cohorts; for example, one cohort receives a treatment and the other cohort does not receive the therapy. The two cohorts are then followed prospectively for the development of a specific outcome. However, since the treatment is not randomly assigned, the two groups of patients may differ greatly in certain critical clinical parameters. For example, maybe the treatment is given only to the most severe patients who have ‘‘nothing to lose.’’ These patients may be unlikely to respond to any treatment, no matter how effective.

Pharmaceutical drug development, therefore, includes a number of clinical studies, but final determination of safety and efficacy is based predominantly on pivotal randomized clinical trials. Clinical studies during the development of a new medicine are often divided into four phases. Phase 1 clinical trials are the initial safety trials of a new medicine. These are usually conducted in healthy volunteers, often in males. In the field of cancer, phase 1 trials are often conducted in more

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severe patients. The trials can be open label, where patients and investigators are unmasked to the treatment allocation. Multiple doses may be tested in a phase 1 trial, often starting with the lowest dose and escalating to higher doses if they are tolerable.

Phase 2 trials are designed to study the safety and efficacy of a new medication. These trials are often double-masked, where both the patient and investigators do not know what treatment is being administered. Classically, these studies are called double-blind studies; however, in ophthalmology we prefer the term ‘‘double-masked,’’ since it is difficult to get a patient with an eye disease to enroll in a study with ‘‘double-blind’’ in the title. Phase 2 trials typically have more patients than phase 1 trials, and are conducted in patients with the disease, but still may examine several doses or treatment regimens.

The phase 3 clinical trials are the pivotal clinical trials for approval of the medication. These studies are almost always larger randomized clinical trials comparing the new medication to the standard treatment or to placebo. The United States Food and Drug Administration (FDA) usually requires two phase 3 trials prior to the approval of a new drug.

Studies that are conducted after a medicine is approved and marketed are called phase 4 trials. These studies are conducted in patient populations for whom the medicine is intended and may compare the medicine to currently available therapies. These studies are also used to elucidate additional clinical data that supplement the results of the phase 1–3 trials.

The randomized clinical trial provides the most robust evidence about the safety and efficacy of a new treatment. Because patients are randomly assigned to the new treatment or to the control treatment and if the number of patients in the study is large enough, the treatment groups are usually similar. This is a critical point, since treatment outcome could be affected if the groups differed in clinically relevant parameters. Although one could try to control or compensate for imbalances using certain statistical analyses, this only works for the parameters that are thought to affect outcome and for which data are available. As stated before, randomization is powerful

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because it controls for both known and unknown sources of bias.

Issues in the design and conduct of clinical trials

Table 1 lists the components of a well-designed clinical study. It is important that investigators are experienced in conducting clinical trials and possess clinical expertise in the disease being studied. The primary outcome variable should be prospectively chosen, even if multiple clinical outcomes are assessed. The procedure for enrolling patients into the study should be detailed, and the inclusion and exclusion criteria listed, since the patient population will determine the extent to which the results can be generalized to a larger patient population outside of the trial. For example, results of a potential neuroprotective medication studied in patients with narrow-angle glaucoma and intraocular pressures (IOPs) of 40 mmHg or above may not be generalizable to patients with open-angle glaucoma and pressures in the range of 22–32 mmHg.

The treatment and dosing regimen should be clearly stated. Choice of the control treatment is also critical to the value of the study. Patients in the control group should be treated according to the current best standard of care. If no proven treatment is available, a placebo could be considered. The dose of the control regimen should also be appropriately chosen. For example, it would be inappropriate to compare a new

Table 1. Components of a randomized clinical trial

glaucoma medication to pilocarpine 1% dosed once daily.

It is extremely important to perform appropriate sample-size calculations for all clinical trials. Sample size is based not only on the event rate expected in the two groups, but also on the desired level of protection against type I and type II errors. Type I error (a) occurs when the study falsely concludes that the therapies tested have different effects when, in fact, they are the same. Especially when a standard therapy for a disease currently exists, most clinical trials protect most strongly against this type of error, since one would not want a new treatment to be wrongly administered when an effective therapy is already available. Most studies limit the possibility of type I error to less than 0.05 (5%). Type II error (b) occurs when a study falsely concludes that there is no difference between the treatments when, in fact, a difference exists. Typically, type II error for many clinical trials is set at 0.2 (20%). This means that there is a 20% chance that the treatments have different degrees of effect although the study shows no significant difference. The number of patients greatly affects type II error. Statistical power (1 b) is the chance of proving the difference between the two groups defined in the sample-size calculations. Many studies in the literature are underpowered — they do not have sufficient patients to have a reasonable chance of detecting a meaningful difference between the two groups. A small study that concludes that there is no significant difference between the two treatments