AIDS Research Strategy: Rapid, Small Trials for Promising Treatment Leads

activists who were to meet with William Paul, M.D., Director
of the Office of AIDS Research. We were invited to the
meeting, but were unable to attend.]

In the history of medicine, advances have often come from
unexpected places -- chance observations or discoveries that
could easily be overlooked because they do not fit into the
prevailing, theories.

We cannot manufacture chance discoveries, we cannot make them
happen. But we can be more receptive to them. We can design a
research system to move quickly to follow up attractive
leads, moving them as far as a small pilot study with a few
to a few dozen people. Then, if the results are promising,
and the study is entirely credible, the treatment lead will
have enough momentum to proceed on its own, through
institutions and arrangements which already exist.

Most of these tests will fail, in that they will not identify
practical treatments. But it only takes one success to make a
big difference -- and with persistent and intelligent
followup of promising leads, such a success is likely. And
even the failures can be important, by providing practical
information about the disease, which may help other
researchers focus their thinking.

Key to Selection of Treatments to Test: Feasibility to
Research, and Feasibility of Use

How should we choose which treatment leads are most important
to test?

When considering ideas which may not fit well within existing
theories, it may be difficult or impossible (almost by
definition) to rationally decide which are most likely to
work. But another approach to prioritization is entirely
possible. We can prioritize based on which treatment leads
are most feasible to test -- meaning that a pilot trial can
be safe, rapid, inexpensive, and not difficult to conduct --
and also on which are most feasible to move quickly into
widespread use, if they are found to work. Since a treatment
which passes one of these tests is likely to also pass the
other, it should be quite possible to choose treatment leads
which are feasible in both respects.

Therefore, this strategy would prefer to test drugs that have
already been used or tested in people in some way. The
toxicology, pharmacokinetics, etc. required for a totally new
compound can be a substantial project. New compounds could
still be included in some cases, however, if the resources
are available.

This is not to say that difficult research ideas should not
be developed -- only that the strategy we are proposing here
will not develop them. When substantial resources are
required to test a treatment lead, other kinds of priority-
setting become necessary. Unfortunately, it is usually
politically impossible to test resource-intensive leads which
are outside the mainstream, prevailing theories -- an
inherent obstacle to rapid progress in medical research. But
when the trials needed are easy to do, then this path to
rapid progress becomes feasible, since unexpected discoveries
and insights can be followed up quickly.

Credibility

These pilot studies will be exploratory; usually they will
not be controlled trials aiming to establish statistical
proof that one treatment is better than another -- that comes
later. The first test of a treatment or strategy might be
with a single patient -- then three or four -- then ten, 20,
or 50.

For the early pilot studies, credibility is established not
with large numbers and small p values, but with excellent
quality control of the research process, under the leadership
and oversight of known, well-regarded researchers or
institutions. For example, top quality labs must be used, and
there must be no question of results looking good because of
selective reporting. If the research is conducted with good
quality control, the results will have the credibility needed
to support the development of larger, controlled trials to
confirm the early results.

Examples

There are dozens, probably hundreds, of credible treatment
ideas published in peer-reviewed journals, usually by
academic scientists, and suggested by the scientists closest
to the work as potential HIV treatments. Almost always the
work stops there. It gets published because the authors are
academics who are very familiar with publishing their work,
and motivated to do so. But they do not have the resources or
background to move the idea further toward human trials.

The examples below focus on research strategies, rather than
particular compounds. This list could be greatly extended.

* Dr. Michael Saag, working with the Merck protease inhibitor
L-524, has reported a few cases of very dramatic benefit
(even at late-stage AIDS) when HIV RNA could be reduced by
100 times or more (compared with a ten-fold reduction which
can often be obtained with AZT). [See interview in AIDS
TREATMENT NEWS #200.] It may be the case that if you reduce
HIV activity enough, perhaps 100 times or more -- no matter
how you do it, as long as the treatment is not seriously
toxic, or immune suppressive -- then major benefits may be
likely. But we do not know this for sure.

One way to explore this area would be a trial to provide top-
quality labs, data management, and support for reporting of
results, and then to allow leading physician-researchers to
follow their intuition and use almost any drug or combination
they wanted to, in patients at any stage of disease. The
investigators could change the treatment when they chose,
with the goal of bringing the HIV RNA down. The likely result
would be (1) finding drug combinations or other treatment
strategies which worked well to reduce HIV activity, and keep
it low, and (2) confirming that doing so confers clinical
benefit -- or learning about the circumstances in which it is
likely to do so.

* It is possible that we have not seen the full benefit of
viral suppression with AZT, as its bone-marrow effects can be
immune suppressive, which may be reducing immune recovery.
The trial setup outlined above could address this question by
exploring strategies with and without AZT. It could also look
at the early switch from AZT to ddI (following up on ACTG
116A), or initial use of the combination, providing practical
guidance in use of these approved drugs.

This differs from large, conventional trials in that
physicians will be able to treat patients individually, under
research conditions, and then report what they learned --
instead of treating groups according to standard protocols,
and then reporting averages.

* Dr. Arthur Pardee's group at the Dana-Farber Cancer
Institute is finding a number of potential AIDS treatments,
by using an established laboratory test to screen for
inhibitors of the long terminal repeat (LTR) of HIV. Many but
not all of the drugs are camptothecin relatives. Most of them
are in human use already. Using the same test, the
researchers have also found a strong synergy between the
abandoned Roche tat drug and pentoxifylline, allowing the
concentrations of each drug to be reduced ten fold and
achieve the same LTR inhibition. But because Dr. Pardee's
background is cancer, not AIDS, leading AIDS researchers have
often not even heard of this work, and little or nothing is
being done to follow it up with human tests.

It would be technically easy to screen some of these drugs
and combinations to see how much they reduce HIV RNA in
patients -- and in which patients, and for how long, and how
the effect is changed by concurrent treatment with AZT, the
Merck protease drug, and other antivirals.

Small, rapid trials of promising treatment leads will not
substitute for better understanding of HIV disease. But they
are something we should do.

The Next Step

This list of examples, of trials which could rapidly produce
information which might lead to major treatment advances, or
at least to practical groundwork for further research, could
easily be extended to several dozen. But usually there are no
plans for any human trials. A critical opportunity is being
lost.

Note that these trials would cost relatively little. The
money could come from either government or private sources.
All the technology needed is already available, all the
facilities exist, the money is there, no special training is
required. All we need is the communication and consensus to
make it happen.

Why, then, has it not happened already? Because this approach
to research has not had a constituency. Pharmaceutical
companies are interested in proprietary drugs, scientists in
high-tech projects -- both of which will take a long time to
be ready. Front-line physicians are usually too busy for
research, and most other physicians avoid AIDS. Patients and
activists are a natural constituency; but they have not yet
organized powerfully enough to overcome the barriers that
make it hard for any trial to happen.

What we can do is to develop this research strategy as a
consensus document, especially in the activist and
professional communities, then use the consensus to bring
about change. By listening to many peoples' input, and
combining the best ideas from all sources, we could build the
consensus to bring such research into the national agenda.