Proving Clinical Benefit in Small, Rapid Trials: Statement to National Task Force on AIDS Drug Development

The February 23-24 meeting of the National Task Force on AIDS Drug Development focused on protease inhibitors; our report on that meeting was not finished in time for publication in this issue. Below is our oral and written testimony to the Task Force.

We were surprised by the widespread agreement with our statement on clinical trial design, in view of the intense disputes in this area. But it did not take long for old, sterile disputes to flare again. The objective has been to develop professional consensus. Now we must move from that consensus to action.

Oral Statement to National Task Force

I am John S. James from AIDS TREATMENT NEWS. I brought a statement that was passed around this morning. Instead of reading it, I will explain the two main points.

One concerns looking for a way through the sometimes- destructive conflict around the issues of "surrogate markers" vs. "clinical endpoints." Here is one approach to consider. Assume provisionally that the markers are working, and use the markers in many small, rapid trials to optimize combinations of some of the treatments that we have; see how low we can get the markers, and eventually see how long we can keep them down. Then -- unless most everything we believe about HIV is wrong -- we can test those treatments without having to wait for people to get sick in the control arm; instead, the [combination, optimized] treatments should be strong enough to get people who are now sick, well. There are a number of recurrent infections, such as thrush, where people are dependent on specific antibiotics or antifungals, and if we can get the viral load down two or three logs and keep it down for weeks or months, will these people no longer depend on their medications? If so, we have shown clinical benefit -- in a small trial (ten, twenty, fifty people), in weeks instead of years, without great expense. This seems like the way to go.

Scolnick (Edward Scolnick, M.D., President, Merck Research Laboratories): We agree with you completely. And we at Merck plan to do studies like that as the drugs become increasingly available. We think it's a good idea.

James: I don't find much disagreement from anybody. But the question is, how to go from agreement to it actually happening?

My other point is to bring in other kinds of treatments besides those in high-profile development; I have a list of about 30 possible treatments [which should be investigated], often prescription drugs approved for other purposes. These are substances already widely in use in people; we know the safety, we know the dose, we know the pharmacokinetics; we don't know the interactions [with drugs commonly used in HIV disease], those will have to be checked. But there is some rationale for testing these substances in HIV treatment, and they are not now being developed. With rapid screening
trials, we can bring some of these in, too; we can add to the effectiveness of treatment combinations.

Written Statement to National Task Force

I started AIDS TREATMENT NEWS in 1987 to report on experimental, "alternative," and mainstream treatments, and have published over 200 twice-monthly issues since. Eight years of AIDS treatment reporting has shown what has worked -- and, far more often, what has not -- and how treatment development could be made to work better.

Today the conventional wisdom says that after the protease inhibitors, the HIV drug pipeline is largely empty -- that there are no good drugs to test. In fact there are dozens of potential treatments to test. But they have fallen through the cracks because there is no big money behind them, and therefore they do not have enough professional momentum to overcome the normal obstacles to the development of any drug. They never reach the first small, well-managed, credible human trials, through which they might prove themselves.

I have kept a list of about 30 such drugs and other treatments for which this initial testing would be exceptionally easily, because these substances are already in widespread human use for other purposes, so the dose, safety, pharmacology, and manufacturing are already well known. All of them have a scientific rationale (sometimes unpublished) as to why they should be tested for HIV. Yet almost none are being developed in any serious way. (And this list of 30 does not include Chinese or other traditional or indigenous medicines, which could provide many additional substances and other treatment strategies to test.)

Today the most notorious of these missed opportunities is hydroxyurea. I do not need to re-tell the story; most of you know it already.

Consider another example. Two major epidemiological studies have found a substantial survival benefit associated with consumption of certain micronutrients. Up to a 50 percent reduction in relative risk of disease progression and of death has been associated with small doses (not megadoses) of vitamins B6, B1, B2, C, niacin, and others. Increased risk was found with almost any intake of zinc. If these associations are causal ones, which is plausible although not proven, then an immense contribution to patient care could be implemented at no risk and almost no expense.

Another epidemiological study unexpectedly found a strong association between use of some but not all antidepressants, and substantially reduced disease progression and increased survival. Apparently no one has any idea of the mechanism of action. This work is not yet published.

How should these and other such treatments be researched, when obviously there are not enough resources for a large clinical trial of every proposed treatment or combination? We
propose two different research strategies for two different cases -- when you believe you know the mechanism of action and have a plausible marker to measure it, and when you do not.

I. If you have a proposed mechanism and markers. This case would apply to an antiviral like hydroxyurea -- and also to combinations of approved and/or experimental antivirals, such as combinations of protease inhibitors, AZT plus 3TC plus a protease inhibitor, etc. First, use the markers (plasma HIV RNA and other assays in the case of antivirals) in small, rapid trials (for example, 10 to 20 patients each, lasting about six weeks plus additional followup) to compare and optimize different treatments, combinations, and strategies. The rapid "turnover" of information (possible because of rapid recruitment, conduct, and analysis of such trials) allows new trial designs to quickly benefit from the results of earlier trials. This creates an ideal environment for developing combinations (of both conventional and new treatments) which maximize impact on the markers.

But since the markers have not yet been validated, how do we know that the combinations which best affect the markers actually benefit patients? One way would be to test the winning combinations against standard treatment in a conventional clinical-benefit trial. But there may a much faster, less objectionable, and less expensive way.

All indications suggest that if a treatment can impact viral markers strongly enough, and for long enough (e.g. reducing viral load by more than 100 fold for a year or more), then it will show benefit not only by preventing disease progression and death (which requires many subjects and a long time to see), but also by getting certain sick people well (which can be observed much more quickly). Many patients, for example, have ongoing infections such as thrush or sinusitis, which require continuing suppressive treatment with antifungals or antibiotics. A truly effective antiviral or immune-based
treatment might visibly improve such infections, even though it had no specific effect against the organism. (We have already seen hints of such effects in trials of existing treatments, such as thymopentin, which are probably far weaker than an optimized combination could be.)

This strategy, of optimizing marker responses to produce combination treatments powerful enough to get people well, could then produce statistical proof of clinical benefit in a small, rapid, ethical, controlled trial comparing the optimized combination to standard treatment for the infection. We would no longer need to wait for death or disease progression.

And if this strategy should fail, what is the worst-case scenario? The strategy could fail in two ways. First, it may not be possible to find any combination treatment which can greatly and lastingly lower viral load. Or this approach could fail because combinations which do lower the viral load do not show quick benefit in patients. In either case, we will have wasted little time and diverted few resources, and will have produced information of great value in planning future research.

II. If you do not know the mechanism of action, or have no markers. The conventional approach to studying an accidental discovery when no mechanism is known is to wait until laboratory advances somehow discover the mechanism of action. The wait may be indefinite, however, since without a suspected mechanism, laboratory research may not even get under way. And if it does, funding may delay it for years.

We would suggest a different strategy for cases such as the micronutrients, or the antidepressants -- treatments already in routine human use, which have a rationale for testing in HIV disease, though they may have no known mechanism of action in this context. Start with exploratory trials looking at viral load, immunological tests, hematological tests, blood chemistries, etc. -- any marker which is operationally feasible, because it well standardized, known to be reliable, readily available, not too expensive, etc. Empirically test, many markers (possibly hundreds) by running the tests before starting the mystery treatment, and then at intervals after the treatment is started. The results of this initial trial would provide hints, derived from human data, as to what the mechanism might be -- as well as leads for further research. And this early trial might also identify markers which could be used in optimization trials, as in strategy #1, above.

In other words, when evidence suggests that a treatment might be helpful but no mechanism is known, consider testing markers empirically during a small, rapid trial of the treatment, to provide realistic, human data as a basis for further thinking and research. Note that a treatment with no known mechanism may be exceptionally valuable, as it may open a window onto an entire new class of therapy.

Nothing suggested above is very expensive, nor dangerous to volunteers. But these strategies have not yet been used in AIDS. I would like to work with the National Task Force to see that such approaches receive serious professional evaluation, and are implemented if justified.

List of Potential Treatments to Test

We did not distribute this list at the hearing, but we had it available in case anybody asked for it. These are substances already in human use, with a rationale for testing in HIV disease, which currently are not being tested at all, or are not being developed rapidly.

Our current list: Acyclovir (for survival); certain antidepressants (perhaps some tricyclics, such as amitriptyline and/or others); aspirin; camptothecin; coenzyme Q10; curcumin; DHEA; DNCB; doxycycline (at least three rationales proposed); garlic; HCG; hydroxyurea; hypericin; isoprinosine; ketotifen; NAC; naltrexone; niacin; papaverine; peptide T; ribavirin; sulfasalazine; thalidomide; thymomodulin, etc.; tobramycin; topotecan; vitamin B1; vitamin B2; vitamin B6; vitamin C; warfarin.