Ординатура / Офтальмология / Английские материалы / Ocular Neuroprotection_Levin, Polo _2003

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 diseases. Importantly, case series lack a control group for comparison. For example, a physician could report two patients with non-arteritic 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. There are a number of reasons for this reluctance. 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 the new treatment.

The main problem with the use of historical controls is that data from historical controls tend to be biased. Data from historical controls 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 a clinical outcome—for example, diet or other environmental factors.

There are numerous other sources of bias in clinical studies [1]. Observer bias leads to a systematic alteration in the measuring of a response in patients. Unvalidated 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 balance these factors in the treatment groups. Importantly, randomization helps to balance unrecognized sources of bias between groups.

In the 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 would compare the smoking history of a group of patients with lung cancer and an ageand sex-matched 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 the controls. Despite this potential bias, well-con- ducted 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; for example, one cohort receives a treatment and the other cohort does not receive the therapy. The two groups of patients or cohorts are then followed prospectively for the development of a specific outcome. However, because 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 severely ill 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 normal volunteers, often in males. In the field of cancer, Phase 1 trials are often conducted in more severely ill 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 dosages if they are tolerated.

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, are conducted in patients with the disease, but still may examine several dosages or treatment regimens.

The Phase 3 clinical trial is the pivotal clinical study for the approval of the medication. These studies almost always are 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 conducted after a medicine is approved and marketed are called Phase 4 trials. These studies are conducted in patient populations for which the medicine is intended and may compare the medicine to currently available therapies. These studies are also used to elucidate additional clinical data that supplements the results of the Phase 1, 2, and 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, 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 because it controls for both known and unknown sources of bias.

III.ISSUES IN THE DESIGN AND CONDUCT OF CLINICAL TRIALS

Table 1 lists the components of a well-designed clinical study. It is important that the investigators be experienced in conducting clinical trials and have clinical expertise in the disease being studied. The primary outcome variable of the study, also known as the primary endpoint, should be clearly stated. This primary outcome variable is the main parameter on which the investigator plans to judge the efficacy of the intervention. Therefore, it is important to prospectively choose the primary outcome variable, even if multiple clinical outcomes are examined. The procedure for enrolling patients into the study should be detailed, and the inclusion and exclusion criteria listed, because the patient population will determine how generalizable the results are 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 of 40 mmHg or above may not be generalizable to patients with open angle glaucoma with pressures in the range of 22 to 30 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 dosage of the control regimen should also be appropriately chosen. It would be inappropriate to compare a new glaucoma medication to pilocarpine 1% dosed once daily.

Table 1 Components of a Randomized Clinical Trial

Study approved by Institutional Review Board. Appropriate informed consent obtained from patients. Disease well defined with specific diagnostic criteria.

Patient population well defined with specific inclusion and exclusion criteria. Patients randomly assigned to new treatment and control treatment according to

standardized procedures.

Patients and investigators appropriately masked from treatment assignment. Sample size accurately determined to control for type I and type II error.

Outcome measures specified and minimum differences to be considered as clinically important detailed.

Procedures for the conduct of the trial well detailed.

Timing of study visits and collection of data strictly specified.

Statistical analysis plan specified prior to locking the database and unmasking of treatment assignments. Results of an intent-to-treat analysis, where all randomized patients are included in the analysis should be provided, even if additional analyses performed.

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 error. Type I error (alpha) occurs when the study falsely concludes that the therapies tested are different when in fact they are the same. Especially when a standard therapy for a disease currently exists, most clinical trials protect more strongly against this type of error, since one would not want a new treatment to be wrongly administered when an effective therapy is available. Most studies limit the possibility of type I error to less than 0.05 (5%). Type II error (beta) 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 are different although the study shows no significant difference. The number of patients greatly affects type 2 error. Statistical power (1-beta) is the chance of proving the difference between the two groups that is 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 two treatments can be extremely misleading. The treatment effect could be 40% higher with the new treatment, but if the numbers of patients are small and the variability of response high, this difference may not be statistically significant, yet clearly be clinically meaningful. In analyzing study results, look at the actual data, and do not be misled by an insignificant

P value, especially if the study is inadequately powered to detect a clinically meaningful difference. Remember that clinical studies can never definitively prove that two treatments are the same.

IV. CLINICAL TRIALS OF NEUROPROTECTION

IN OPHTHALMOLOGY

Proof of neuroprotection in ophthalmology will require a well-designed clinical trial employing many of the strategies detailed above. The most definitive evidence will require a randomized clinical trial comparing the potential neuroprotective treatment to a control treatment or placebo. Although there are difficulties in conducting any clinical trial, studies of potential neuroprotective medications will encompass several additional challenges.

There are very few randomized clinical trials of neuroprotective medications in medicine. One such study, the Glycine Antagonist in Neuroprotection (GAIN) Americas trial, was a randomized, double-masked placebo-controlled trial conducted to examine the efficacy of gavestinel, an antagonist of the glycine site of the N-methyl-D-aspartate receptor, as a neuroprotective therapy for acute ischemic stroke [2]. The main outcome measure was functional capability at 3 months, measured by the Barthel Index. This study concluded that gavestinel administered up to 6 h after an acute ischemic stroke did not improve functional outcome at 3 months. Memantine, an uncompetitive N-methyl-D-aspartate (NMDA) antagonist has been studied in patients with severe dementia, both Alzheimer type and vascular type [3]. In this study, neuroprotection with memantine led to functional improvement and reduced care dependence in severely demented patients.

There are even fewer randomized controlled clinical trials of neuroprotection in ophthalmology. One example is the Ischemic Optic Neuropathy Decompression Trial (IONDT) [4]. This was a National Eye Institute–sponsored multicenter clinical trial designed to assess the safety and efficacy of optic nerve decompression surgery compared with careful follow-up alone in patients with nonarteritic ischemic optic neuropathy (NAION). Prior to this study, several nonrandomized trials showed benefits of optic nerve decompression; however, none of these were randomized studies [5–8]. Interestingly, results from the IONDT showed that patients assigned to surgery did no better when compared with patients assigned to careful follow-up [4]. Improved visual acuity of three or more lines of visual acuity was achieved by 23.6% of the surgery group compared with 42.7% of the careful follow-up group. In fact, patients receiving surgery had a significantly greater risk of losing three or more lines of vision at 6 months: 23.9% in the surgery group worsened compared with 12.4% in the careful followup group.

The IONDT illustrates the need for a well-controlled clinical study to adequately assess neuroprotective therapy. Prior to this trial, improvement in visual acuity in patients with NAION was thought to be rare: less than 10% [9,10]. In the IONDT, 42.7% of patients in the careful follow-up group had a three line or greater improvement in visual acuity [4]. Furthermore, optic nerve decompression surgery was found to be ineffective and potentially harmful to patients with this disease.

A. Endpoints

A critical factor in designing clinical trials for neuroprotection is endpoint selection. The primary outcome measures in the IONDT were gain or loss of three or more lines of visual acuity on the New York Lighthouse chart at 6 months after randomization [4]. This is a functional endpoint that has been used in a number of ophthalmology trials and is felt to be clinically meaningful. Visual acuity has also been used as a standard clinical endpoint for clinical trials in macular degeneration, where central acuity can be affected early in the course of the disease. Unfortunately, changes in central acuity may be an insensitive endpoint for many ophthalmic diseases. For example, central visual acuity loss occurs relatively late in the course of some diseases including glaucoma and retinitis pigmentosa. Although visual field loss can be used as a functional endpoint, visual field loss progresses slowly and may require many years before meaningful changes occur.

Identification and validation of surrogate endpoints will improve our ability to assess neuroprotective therapies. In a sense, intraocular pressure has been used as a surrogate endpoint for glaucoma treatments. Without well-controlled data, lowering intraocular pressure was felt to reduce the risk of vision loss in patients with glaucoma. Data from randomized clinical trials that support the benefits of lowering intraocular pressure are now becoming available. In a recent report from the Advanced Glaucoma Intervention Study (AGIS), investigators showed that eyes with intraocular pressure less than 18 mmHg for 100% of visits over 6 years had mean changes from baseline in visual field defect score close to zero during follow-up, whereas eyes with intraocular pressure less than 18 mmHg for less than 50% of visits had an estimated worsening over follow-up of 0.63 units of visual field defect score [11].

There are a number of new methods for assessing visual function that may be useful as endpoints in clinical trials for neuroprotection. Depending on the disease, endpoints may change at differing rates and have a large impact on length of clinical trials and the required sample size. Other studies have documented that rates of change differ among measures of visual function. In a trial of patients with retinitis pigmentosa, investigators assessed changes in measures of visual function in patients over time [12]. The smallest amount of change occurred for

visual acuity and hue discrimination, and the greatest amount of change occurred for visual field area.

Electrophysiologic testing, newer methods of visual field testing, and contrast sensitivity are just a few examples of potential endpoints for clinical trials in neuroprotection. The electroretinogram was used as the primary outcome measure in a randomized clinical trial of vitamin A and vitamin E supplementation for retinitis pigmentosa [13]. This was a National Eye Institute–sponsored randomized, double-masked trial to determine whether supplements of vitamin A or vitamin E alone or in combination affect the course of retinitis pigmentosa. In this study, the main outcome measure was the cone electroretinogram amplitude. Patients receiving 15,000 IU/day of vitamin A were 32% less likely to have a decline in amplitude of 50% or more from baseline than those not receiving this dosage (P 0.03). Although not statistically significant, similar trends were observed for rates of decline of visual field area. These data support the potential benefit of identifying endpoints that may be more sensitive or less variable in clinical trials.

More accurate and sensitive measures of visual function will improve our ability to test neuroprotective therapies. Use of the scanning laser ophthalmoscope to assess perimetry [14] or of the multifocal electroretinogram [15] may be useful endpoints in trials of retinal disease. Similarly, new methods of assessing glaucomatous damage such as the Heidelberg retinal tomograph (HRT), the GDx nerve fiber analyzer (GDx), and the optical coherence tomograph (OCT) may be important measures of visual function in neuroprotection trials in patients with glaucoma [16–19]. New methods of measuring visual field using short-wave- length automated perimetry or multifocal visual evoked potential could also improve our ability to accurate assess changes in visual function in these patients [20,21]. However, it is important to remember that all of these endpoints need to be extensively evaluated and validated before widespread use in clinical trials.

Increasingly, there is an interest in assessing the effect of new therapies on quality of life. Questionnaires are often employed to determine quality of life; however, it is important to make sure that the questionnaires are validated for the disease of interest. The visual function questionnaire is one such quality of life measure that has been validated in a number of diseases, including diabetes mellitus, macular degeneration, glaucoma, and cytomegalovirus retinitis [22].

B.Neuroprotection and Glaucoma

A number of scientists are trying to develop neuroprotective therapies for glaucoma. However, data suggest that lowering IOP can decrease visual loss, and in a sense, provide neuroprotection. Therefore, in studying neuroprotection in glaucoma, it will be important to assess preservation of vision while controlling for intraocular pressure. For example, there are a number of laboratory studies of glaucoma medications that demonstrate neuroprotection in animal models of

optic nerve disease. It is important to compare these drugs to control medications that similarly lower IOP but reportedly have no neuroprotective effects. For example, in an animal model of ocular hypertension, systemic administration of brimonidine or timolol had equivalent effect on IOP [23]. Nevertheless, brimonidine significantly reduced the progressive loss of retinal ganglion cells by greater than 50%, whereas timolol had no effect. These considerations should also apply to human clinical trials. Two Phase 3 randomized, double-masked clinical trials are in progress assessing the neuroprotective effects of memantine, a drug that blocks the NMDA receptor. In this trial, the neuroprotective effects of the drug will be assessed independently from IOP.

Although definitive proof of a neuroprotective medication in ophthalmology will probably require data from a randomized, clinical trial, there are some instances where an open-label trial of a medication could lead to believable evidence. In diseases where the clinical outcome is well documented with little to no variability, an open-label trial with historical controls could provide convincing data, using historical controls. Unfortunately, there are few such conditions. One potential disorder is central retinal artery occlusion in patients lacking a cilioretinal artery. If a treatment were studied that preserved 20/20 vision in even a relatively small number of patients, the data could be fairly convincing, because the visual outcome of this condition is usually catastrophic. However, there is still the opportunity for bias, and one should be very careful about misinterpreting data from trials without a concurrent control group and random assignment of treatment.

V.CONCLUSIONS

In conclusion, neuroprotection offers an exciting therapeutic approach to a number of diseases. Clearly, patients with disorders affecting the retina or optic nerve may benefit from neuroprotective medications. One must be careful in interpreting data from small, uncontrolled studies. As can be seen, there are a multitude of issues that must be considered. Well-designed clinical trials with validated endpoints will provide the best insight on the neuroprotective effects of medications and provide new treatment options that, one hopes, will save vision.

REFERENCES

1.Sackett DL. Bias in analytic research. J Chronic Dis 1979; 32:51–63.

2.Sacco RL, DeRosa JT, Haley ED Jr, Levin B, Ordronneau P, Phillips SJ, Rundek T, Snipes RG, Thompson JL. The Glycine Antagonist in Neuroprotection Americas Investigators. Glycine antagonist in neuroprotection for patients with acute stroke: GAIN Americas: a randomized controlled trial. JAMA 2001; 285:1719–1728.