AIDS Research Direction: New Scientific Approach?

The future of AIDS research was the focus of two articles
which appeared on May 12: "AIDS: Time to Turn to Basic
Science," by Bernard N. Fields, M.D., in the scientific
journal NATURE, and "Scientists Say U.S. Research on AIDS
Needs Redirection," by Gina Kolata in THE NEW YORK TIMES. The
TIMES article underlined the importance of the one in NATURE,
by quoting leading scientists -- especially Harold Varmus,
M.D., the new director of the U.S. National Institutes of
Health ("Everyone agrees with Bernie's basic precept"), and
William Paul, M.D., head of the newly strengthened and
centralized Office of AIDS Research ("We take that [the ideas
expressed in the NATURE piece] as our marching orders"). The
impact of the new thinking is likely to be gradual, however,
because of (1) the momentum behind the existing system, and
(2) the fact that the budget for Fiscal 1995 (the year which
begins in October 1994) is already largely completed.

Clearly the NATURE article reflects the views of a number of
leading basic-research scientists -- including the two
officials (Dr. Varmus and Dr. Paul) who will have the most
influence on the future of the U.S. government AIDS research
effort, which is by far the world's largest.

Among AIDS treatment activists, most (but not all) who have
been following this changing emphasis seem to be viewing it
favorably -- especially in welcoming the new involvement in
AIDS research by leading scientists. But few if any believe
that this new thinking is the whole answer. And some fear
that certain problems could be made worse.

What Is Proposed?

Dr. Fields, the author of the NATURE article, is a leading
virologist, and chairman of the Department of Microbiology
and Molecular Genetics of Harvard Medical School; until this
year he was editor of the JOURNAL OF VIROLOGY. The commentary
in NATURE is his first publication on AIDS.

How could an article by someone new to the field have so much
influence? The process may have started on February 17 of
this year, when Dr. Paul's appointment as head of the Office
of AIDS Research was announced. Dr. Paul, a leading
immunologist who had been chief of the Laboratory of
Immunology at the U.S. Institute of Allergy and Infectious
Diseases, was also new to AIDS. (This was neither surprising
nor unwelcome. A number of people, including this writer,
have felt that Federal AIDS research should be led by a well-
regarded scientist from outside the AIDS field.) After being
appointed, Dr. Paul sought the advice of top scientists in
virology and other relevant fields -- many of whom were also
new to AIDS -- about how research and treatment development
could be improved.

Before publishing his article, Dr. Fields showed drafts to
Dr. Varmus, Dr. Paul, and others in the informal group of Dr.
Paul's advisors, and found general agreement with the major
points. Not everyone agreed totally, however.

It is hard to summarize this two-page article, but a quote
from the second paragraph gives a sense of its direction and
tone:

"It is my view that we need to bring fresh scientific thought
to the problem of AIDS. We need change, but what kind? We
need to put increased emphasis on basic science and broaden
our definition of AIDS-related research. In addition, we need
to look critically at the time, effort, and money spent on
many aspects of drug development and vaccine programmes that
have little or no scientific rationale, and are thus unlikely
to lead to effective therapies or prevention. The focus on
drugs and vaccines made sense a decade ago, but it is time to
acknowledge that our best hunches have not paid off and are
not likely to do so."

Dr. Fields mentions a few of a long list of largely
unanswered scientific questions, such as how HIV spreads from
a primary site of infection on mucosal surfaces, and how it
kills cells. He points out that HIV is very different from
other viruses, such as polio. With polio, the critical steps
were the isolation and culturing of the virus; with AIDS this
has already been achieved, but that has not solved the
problem.

Dr. Fields suggests four points to guide future research:

(1) Broaden the definition of AIDS research. For example, he
suggests that a particular virus in mice "provides an
excellent model for studying viral persistence and the host
response." Such studies could be funded as AIDS research,
even though the virus is not HIV.

(2) "Emphasize the basics of the science directly relevant to
HIV and AIDS" -- for example, through studies of AIDS
pathogenesis, and the immune response to HIV.

(3) Expand studies of opportunistic infections, and increase
"longer-term support for high-quality proposals in this
area."

(4) "Continue to look directly for a new drug or effective
vaccine" -- but "concentrate on studies that offer a real
possibility of working... In our zeal to control AIDS, we
have invested enormous resources in the search for drugs and
vaccines. This may have been reasonable 10 years ago, but is
no longer."

Comment

When AIDS research began, the leading, established scientists
in the various relevant fields, such as virology and
immunology, did not choose to work in AIDS. This is
understandable; they already had a full plate of projects
going, and in the early days there was much fear for the
safety of laboratory workers, because no one knew what
precautions were necessary for working with the new disease.
Later, it seems to have been difficult for new people to
enter AIDS work, because funding has been short, and already
spoken for. We believe that as a result, AIDS research never
recovered from the early lack of senior people.

Now Dr. Paul has brought in leading researchers. Dr. Fields'
article outlines his assessment (with which many others
agree) of the research so far, and proposes directions for
reform. It is asking for a more rational research program,
with clinical trials based on scientific knowledge. (This
would replace a system in which the trials that actually
happen are determined partly by accident, but largely by
which drugs have the commercial clout to push through the
random obstacles in their way.) The high-level attention
reflected in Dr. Fields' article opens the door to new
scientific leadership to address the major problems in AIDS
treatment and vaccine research and development.

But this new thinking has not fully addressed what we believe
is the biggest single problem in AIDS research -- the nearly
complete lack of movement of potential new treatments from
the stage of academic papers to the earliest test for
antiviral or other activity in humans. Ideally, scientific
consensus could provide the missing momentum, leading to
early development and small human trials which, if
successful, will generate enough industry or other interest
to assure further development. But it may take years to
understand the basic science; in the beginning, there may be
only a scientific hunch.

In this case, we believe that there is another legitimate
criterion, besides conclusive science, for picking candidate
drugs for further development -- namely, practical
feasibility. If the potential drug or combination is already
in human use, and well known to be safe; if a small trial
could be run safely, quickly, inexpensively, and easily; and
if the treatment, if successful, could quickly be brought
into wide use -- then a pilot, screening trial may make
excellent human and public-health sense, even if the
scientific mechanism is not fully understood -- and even if
the probability of success is small.

Why has AIDS treatment development been so disappointing?
Some of the thinking behind current AIDS trials was based on
the relative success of treatment development in certain
leukemias and some other cancers. What worked there was to
keep comparing different drug combinations, looking for small
differences in effectiveness; eventually these small
treatment improvements added up to major advances. For this
trial-and-error process, it was not necessary to understand
why a combination worked.

But cancer research has much better procedures than AIDS
research for getting new treatments into testing, and into
combination testing -- whether or not a pharmaceutical
company is interested at the early stages. In AIDS, each
potential new agent is usually just dropped, and never
developed or seriously evaluated. And no wonder; usually the
only available path in AIDS is that first a company must
become interested enough to foresee taking a drug through the
whole process -- on the basis of no human data. Cancer
research has much more flexible ways of getting new agents to
physician-researchers earlier; this allows rational planning
of further research, based on actual human experience.

In AIDS this has not worked because it has not been tried.
New agents are not allowed to begin development. And early
combination experience has been inordinately difficult to
arrange, because of the difficulty of getting competing
companies to work together, and because of FDA reluctance to
allow combination trials early in the development process.
This is why we are concerned with the conclusion that "our
best hunches have not paid off and are not likely to do so"
(quoted from Dr. Fields, above). Few hunches have failed or
been rejected; many have been blocked or dropped arbitrarily.
The solution is to unblock this process, to allow an orderly
flow of feasible ideas into small pilot trials -- not to
abandon this research until the science is perfected.

We agree that scientific understanding is the best basis for
designing clinical trials. We hope that the new basic-science
viewpoint will not make the mistake of considering it the
only legitimate basis.

[Note: Before going to press, AIDS Treatment News discussed a
draft of this article with Dr. Fields. He emphasized that the
NATURE article represents his views, which a number of people
agree with, but that there was no total agreement or formal
consensus process.

[Dr. Fields was a candidate to be the director of the Office
of AIDS Research, but removed himself for health reasons. He
wrote the NATURE article because, as a general virologist who
has closely followed AIDS, he thought that some points needed
to be stressed -- and since he is not conducting AIDS
research himself, he could speak from a certain distance.

[Dr. Fields emphasized that basic science is not a substitute
for the clinical research now going on -- that we must do
everything we can to find new drugs and vaccines. The
question is how to get there fastest. We must balance the
total resources available, to cover areas we are now missing.
He gave the example of whether we should spend $20 million to
$30 million on a vaccine trial when the data strongly suggest
that it will not work -- instead of using the resources to
learn what is critical about immunity to HIV.]