Sun Nov 1 16:00:34 1987
THE SECOND CENTURY OF LOUIS PASTEUR:
A GLOBAL AGENDA FOR BIOMEDICAL RESEARCH
JOSHUA LEDERBERG

The Rockefeller University, New York, NY 10021

INTRODUCTION: Louis Pasteur and the Pasteur Institute

Nothing could have given me greater gratification than this
invitation. For me, as for my entire generation of
scientifically inclined youth, Louis Pasteur was a global culture
hero, The Pasteur Institute was an exemplar that insplred the
foundation of the Rockefeller Institute in 1901, In 20th Century
America, Pasteur's work reached popular attention largely through
the writings of Paul de Kruif ~ "Microbe Hunters". The author
was a microblologist who began his career at the Rockefeller,
Rene Dubos, an important admirer and biographer of Pasteur, was
my colleague at the Rockefeller -- and long before that one whose
work and writings I looked up to. Starting in 1946, figures like
Andre Lwoff, Elie Wollman, Jacques Monod and Francols Jacob have
towered at the very top of those scientists who worked in fields
closest to my own interests, who made important discoveries
correcting and enlarging my own, and whose criticism and esteem
counted the highest in extracting the fullest meaning from my own
work. When there was occasion to plan spaceflight missions to
Mars, the search for chiral molecules presented itself as the
most universal of indicators of extra-terrestrial life. I was
presumptuous enough to label that “The Pasteur Probe.“ Many of my
closest friends and colleagues have had the good fortune to be
able to spend a significant time working at the Pasteur
Institute, to their lifelong advantage. Today, the Institute has
continued tn Louls Pasteur’s tradition of providing new
scientific knowledge in infectious disease that is our only hope
of fending off a pandemic that is already a global catastrophe.

These images of Pasteur and his Institute complicate my task
in seeking a worthy topic for such an occasion. He has been the
subject of many biographies; yet there 1s much more to be learned
about the history of his ideas and thetr reception, and how they
related to his contemporary architects of scientific revolutions:
epitomtzed by names like Gregor Mendel, Charles Darwin, and
Friedrich Miescher. The Institute itself deserves a formal
history in more detail than my own scholarship could encompass.
You are fortunate to have many other celebrants who will look up
from their exciting work at the laboratory bench, and by
describing what they know so elegantly, give you a perspective of
the contemporary science that proceeds throughout the world in
these traditions.

As an introductory speaker, I clatm a different canvas. My
questions will include: What can we hope from the next century
of research in the Pasteurtan tradition? What old and new
problems willl we face? What do these tell us about our agenda
for today? I will also comment on the social milieu in which
science now functions, and some of our challenges in sustaining
the utmost creativity and intellectual boldness of the young
minds who are our most important hope for the future.

PROPHECY: as Cassandra told, is a perilous profession, Why
do it?

The best justification I owe to Alex Keynan: that a vision
of the possible motivates many social actions; and our policies
are already permeated by much false prophecy, if only that tacit
one that the future is static. I have committed a few
lamentable, spasms of technological forecasting, starting some 25
years ago. They are lamentable not so much because they were
wrong ~~ for the most part they were accurate -- but because it
4s hard for me to see any difference that it made to enunciate
them, One can urge on any scientist that he will influence the
future far more by what he puts into the permanent record of
scientific experiment and discourse than by what he articulates
to the public. Nevertheless, eloquent writers like Lewis Thomas,
the late Peter Medawar, and your own Jacques Monod and Francois
Jacob have had an important impact on the public mind.

A ceremonial occasion as formidable as this still invites
some reflection. And I will have some excuse to mix in some
prescription,

If we try to look ahead to foresee the development of
science for the next century, we encounter first of all the
overwhelming impact of compound interest, of the exponential
acceleration that already impressed Henry Adams at the beginning
of this century. As Derek Price pointed out we have experienced
a 6% growth rate -- a 12-year doubling time ~- in Western science
throughout the modern era. We have indeed assimilated a 300-fold
increase in the first Pasteurian century. Can we imagine a like
multiple in the second? Probably not for Western Europe and
America: even before we reach the physical limitations of a
growth rate exceeding that of the GNP, we already experience
painful constraints. On the other hand we must consider the
potential development of science in China, India, Eastern Europe
{as it throws off the shackles of Lysenko and his nepotic
offshoots), Latin America, perhaps some of Africa. Recall where
Japan was in 1887 (for that matter the U.S. in medical science)
compared with today. The cultural space for science is in the
process of a tenfold augmentation,

How does such a forecast inform us? To extrapolate for,
say, 20 years may be a reasonable exercise. There will he
surprises, but our baseline is numerically a third of the
estimate; and most of the technology in use in 2007 will be based
on scientific fundamentals now visible. To guess at the
substantive content of science for another century is not
forecasting but divination. Hardly just technology, the very
fabric of global human affairs is subject to the most
unpredictable of perturbations -- a truism that should temper the
assertion of absolute categorical prescriptions about what should
or should not be ethically permitted, based on a projection. of
contemporary circumstance. Geopolitics aside, will we take the
same view of death and dying when it is no longer at the whim of
“natural causes"? Leo Szilard would say that an optimist is one
who believes the future is uncertain: I will proceed with that
admonition.

Forecasts about the kinetics of science are more credible
than about {ts substance, Apart from its impact on the social
yield, the process of growth is part of the vitality of science:
it has given us the luxury of trying new people, new projects
without making painful choices about the relicts; {t has been an
dinportant factor in the youthfulness and audacity of temperament
of its practitioners. As growth slows down we face almost
drevitably a graying of our culture -- a side-effect of the
control of population growth and of the prolongation of lifespan

WP27)
Sun Nov 1 16:00:34 1987

that we urge as a fundamental policy for Western soclety. We
should also anticipate that 1) sclence will be far more broadly
distributed among cultures and polities of the world, and 2) ever
more attention will need to be given to the integrative measures
needed for some coherence of the research enterprise - matters
rarely attended to in the highly specialized training offered our
young scientists today,

These integrative measures are both external and internal to
science. At one extreme, they speak to a broadening of the
educational base, at least for some professionals, towards
understanding of the socto~ cultural framework of vast
technological expansion: how to stay abreast of accumulated
information, and relate it to the needs both of the professional
discipline and of humanity, These are not the same skilis needed
for bench research, though they overlap it as do the
qualifications for teaching. We do not have an appropriate
balance in our academic status and reward system today. At the
other extreme, we urgently need innovations in mathematics and
computer-science to cope with the complexity of scientific
description itself.

LOOKING BACKWARDS INTO THE FUTURE (which is, so I am told, the
Chinese perspective)

100 years ago, Jules Verne and other science~fictional
utopians gave us fairly accurate Premonitions about mechanical
technology: space travel and submarine warfare. He had little to
say about biology. For Pasteur, the microbe was the concept that
revolutionized medicine, Today, the structure of DNA is the
Paradigm that tnforms every aspect of contemporary biomedical
science, Working out the full detail of DNA structure, its
diversification on the evolutionary landscape, in tndividual
variation, in the development of the organism is already the
undisputed agenda that may well occupy us for much of the next
century, {tn the way that the microbe did for the first.

Such clarity of opportunity for exploitation is a rare good,
and it will have enormous technological Fruits. We have also to
guard against being so dominated by the opportunity that we close
off acts and thoughts that deviate from the mainstream: the very
idols or paradigms that inspire rapid progress. Did this occur
in 20th Century microblology? I can think of a few possible
examples that (needless to say) warrant further debate. The very
success of the established paradigms in the early conquest of
infectious disease gave little encouragement to challenge them,
As Kluyver and Van Niel have pointed out, the view of bacterla as
enemles of humankind helped to obscure the closer examination of
thelr blology.

1. Skepticism about genetic variation in bacteria: this was
too often discounted as contamination, the horror to be avoided
{n microblologica} technique. Here, Pasteur was conceptually
correct in the face of skepticism about his attenuated variants;
though he resisted the pure culture methodology of his teutonic
competitors. A further Consequence was a long lasting muddle
ahout adaptive Phenomena, where bacteria were long regarded as
refuges of Lamarcktan blology.

2. The definition of bacteria as Schizomycetes, namely
fission-fungl devotd of sexual processes, and therefore beyond
the pale of Mendelian genetics. This ido) stemmed tn Part from
Leeuwenhoek’s original description of bacterla, as the stmplest
organisms {tn the Scala Naturae, barely resolvable with the

microscope, (Unfortunately, even the best microscopes are still
of little help in understanding genetic exchange in bacteria.)
The cleavage of bacteria from genetics persisted for a half-
century after Pasteur.
1

3. The discouragement of anti-bacterial chemotherapy,
despite sporadic observations of antibilosis long predating
Fleming. Even Fleming was daunted from pursuing penicillin after
1928 by the expectation of failure. The toxicity of Ehrlich’s
arsenicals and dyestuffs did furnish empirical foundation for
those negative beliefs; but they were prematurely Canonized, in
favor of the virtues of serotherapy.

4, In related fashion, the mystique attached to antibody
globulins ~-- do but recall the Jargon of “lysins, agglutinins,
eopsonins, ablastins, amboceptors, ..." -- supported the
presumption that they were infinite in variety, and helped
sustain the instructive theories of their specificity that
dominated the field until 30 years ago, We could not have
monoclonal antibodies, nor the conceptual framework of modern
immunology, until those idols were superseded by contemporary
insights based on cell selection. One must admit that English
invention, Occam’s razor, the precept of minimizing new
suppositions, has been a poor guide to discovery of the divers
cell types involved in the immune response,

5. The concept of a “toxin" as a lethal weapon ~- the
military jargon itself accents the idol -- long obscured the
recognition of cholera exotoxin as a substance that "merely*
promotes the intestinal secretion of water. It took the clinical
acumen of a far-from-mainstream Indian pathologist, 8S. N. De to
overturn the Kochian ikon, no longer ago than 1951.

These iconoclasms are no mere academic exercise. Tens of
millions of human lives have been hostage to the intellectual
confusion of the prior mythology. Is there a common thread to
them? Dimly I see some vestiges of vitalism, a refusal to
recognize mechanistic explanations of living cells’ behavior, and
a resistance to Darwinian theory. Pasteur himself, in his
quarrel with von Liebig, denying cell-free fermentation,
exemplified that tendency. Even when they repudiate vitalism in
principle, some biologists still act as if life is so complex as
to be beyond the scope of the human intellect. There is also the
idol of the “Dragons of Eden“, that the tree of life is guarded
by sacred guardians that humanity dare not challenge. Do not
smile: in Washington, suits have been filed against the US
Department of Agriculture for infringements on the "Telos" of
barnyard animal species. In some quarters, "Evolution" has been
deified. (Not that we dare disregard the delicacy of evolved
ecological webs.) If that god prevail, we should not rely,on the
human species having any privileged place in its purposes for the
future of the planet,

Other fields, most notably genetics and neurobfology, have
been impeded in similar fashion,

6. It 1s an extraordinary anomaly in the history of biology
that the human chromosome number was erroneously recorded, as 48,
until 1956. The human cell was simply not a place one probed.
Until) that number could be accurately rectified, 22 pairs of
autosomes and one pair of sex chromosomes, the field of human
cytogenetics could hardly be initiated, Promptly after 46 was
understood came the reports that f{lluminated Downs syndrome as a
redandant 21° chromosome, and we contd heatn tha man thr antira
Sun Nov 1 16:00:34 1987
set.

7. When Johannsen tntroduced the term "gene" in 1909, he
promptly cautloned against assuming it had a material basis,
Further, he insisted that many genes might influence a given
character and vice versa. At a time when “protoplasm” was widely
assumed to have vital properties (rather scantily veiled
vitalism), he was perhaps defending against the expected
criticisms of others rather than exposing his own convictions.
Those cautions were justified for many characters that are
manifest as the end results of a long epigenetic chain of
cellular events. They were nevertheless an unwonted source of
resistance to the tdeas finally enunctated by Beadle and Tatum in
1941, that all enzymes are erimary products of chromosomal genes.
Data to support that view had been tabled long since by Garrod,
but he barely hinted at a like theory of gene action. I believe
that as a physictan he felt intimidated by the world-view of the
genetic professian.

Mechanism {is now firmly in the saddle in contemporary
biochemical research. This is no guarantee against mythical
errors. I confine myself to biological studies,

8. The presumption that only proteins could have enzymatic
activity has made even more exciting the recent findings of
ribozymes -- RNA molecules that mediate their own chemical
transformations,

9. Who would have doubted the dependence of terrestrial
life on energy inputs from the sun -- until the recent discovery
of the thermal vents on the ocean floor, and a rich biota that is
fueled by chemical seepage from primordial sources beneath the
crust. These findings may give additional credit to Tom Gold’s
geological iconoclasm that some natural gas and petroleum may not
be of paleoblologic origin,

10. Have we discovered all the major taxons on earth? We
thought so until Carl Woese’s Increasingly persuasive arguments
for elevating the archebacterla to major phyletic status. Should
we believe that is the end of natural historic discovery?

SOME SPECULATIONS ABOUT CURRENT RESEARCH DIRECTIONS

Keeping in mind these historical repudiations of common
wisdom, I offer some unconventional and speculative challenges to
how we think about some large problems in contemporary biology.
Most of them are not new thoughts, but to my knowledge have not
been refuted. I know they are mostly wrong; but I am not sure
all are, They will surely be addressed, and most of them solved,
during the next century. If I could foretell exactly how, I
would be wasting no time getting to work on them in the
laboratory. .

Eoblology {origin of life}: Conventional theory makes this
a photochemical process of the early atmosphere of our own earth.
But the cosmic condensation necessarily involves preeminent ly
light elements, Including H, C, N, O. The aggregation of stars
and planets 1s already an exercise in organic chemistry. Many
large molecules have now been observed in space. Should we not
look there for early chemical evolution, perhaps even of the
rudiments of nucleic acids and proteins or their predecessors?

Exoblology (“are we alone in universe"), The cost of radio
recelvers and of computation may finally be reaching an asymptote

that would justify some modest investment ~~ if not now, in the
next decade or two ~- in acquiring and processing potentially
intelligent signals. We have no way to assess the probability of
their occurrence, As to the solar system, the 1975 Viking
mission gave a discouraging report on Mars; but it 41s wrong to
foreclose the possibility of microhabitat refuges -- especially
at modest subsurface depth -- perhaps from a more hospitable
epoch in that planet’s history, The thermal vents on our ocean
floors offer an interesting analogue of such habitats.

The Epigenetic Dilemma.

The central model of cellular differentiation must
reconcile:
a) the orderly delimitation of gene expression in embryonic cell
lineages.
b) the clonal inheritance of these self-sustaining differences,
c) the apparent reversibility of these effects in some stages.

On account of (c), we usually assume the genetic uniformity
of all somatic cells, and therefore that epigenetic cell changes
are epinucleic, 1,.e., they do not alter the primary
informational sequence of the DNA, but involve secondary
structures or lateral attachments like methylation, histones,
etc. However, the dogma of genetic uniformity of somatic cells
was overthrown with modern concepts of antibody formation. This
is unlikely to be the only exploitation of nucleic
diversification of somatic cells. Many mechanisms of reversible
nucleic differentiations are now known in prokaryotes. Should we
abandon the search for epinucleic explanations? I favor an
eclectic perspective; but we have still to find a robust example
and rationale of epinucleic transmission. We seek a consensually
accepted experimental model, not just of modulation of gene
expression, but also of its quasi-stable inheritance without
nucleic alteration, The field might look for a Max Delbruck who
would establish some discipline about the models to be pursued,
as he did in plying phage T2 forty years ago.

More attention should be given to grossly obvious
histological differentiation of nuclear and chromosomal
structures ~- the bands in polymorphs, the dimples in monocytes
must be epiphenomena of underlying chemical differentiation; and
I will be rather surprised if they are not associated with fairly
specific segments of DNA information and their current
expression. The recent explorations of human fraglle-x
chromosomes show the value of correlating morphological and
molecular-biological observations.

Aging

Here too, we have yet to establish a consensus on what .
phenomenon we are investigating, what would constitute an
explanation. I suggest we use as a standard the difference in
lifespan between human and mouse: are there any cellular
attributes that can be correlated with that outcome?

Cancer

The paradigm of the oncogene is properly taking hold, and I
do not dispute it. My remarks are on another tack: to ask
whether chemotherapy or radiotherapy can really be explained as
eradication of all tumor cells. This seems very doubtful, and
the collaboration of endogenous biological defenses must be
involved. If so, it has been mischievous to focus on modifiers
Sun Nov 1 16:00:34 1987,

like interferons or interleukins as sole therapeutic agents to be
tested as single agents. They must be examined as adjuvants to
cytocidal agents,

Heart Disease

The HDL/LDL (Q1{poprotein) ratio has been established as the
best Predictor of atherosclerosis, Almost no therapeutic
research 1s founded on efforts to modify this ratio, which is
certainly a question of differential gene expression under
metabolic regulation in the liver,

Psychiatric disease

Our ONLY leads are a) psychotropic drugs’ mode of action,
and b)genetic Influences tn disease, We are beginning to see
important studies On DNA probes for polymorphisms linked to
disease susceptibility. However, almost noone is looking at
polymorphism in drug metabolism, although there are many clinical
hints of it. This would reflect the handling of endogenous
metabolites, :

On Human Intelligence

Are we too wedded to the prewired switchboard model? There
fs abundant evidence for extensive cell migration, during
development , Could this continue throughout adult life, be Part
of learning? There {s recent evidence of cel] turnover, at least
in song nuclet in birds, Ig human cerebral function merely a
numerical extrapolation of the neurobiology of lower mammals, or
are there higher orders of differentiation of neuronal types in
the human brain? Else, Why is so much nucleic informat ton
untquely expressed in the brain?

Physiology, Anatomy -- Some orphans,

That exercise influences muscle hypertrophy ts an everyday
observation, To understand it and other banalities at a
molecular level] could have great practical application: not just
for Olympic competition, but for maintenance and rehabilitation
of the heart and of that organ so uniquely vulnerable in the
human, the intervertebral disk. To refer to “compensatory
hypertrophy" of muscle or any other organ as a response to
functional demand is hardly to explain its mechanism,

Toxlcology

Toxic “side effects are no longer incidental in the process
of adoption of new drugs, pesticides and other chemicals: they
are the central issue, Toxicology must be elevated from a
stepchild of Pharmacology to a central position in the health
sclences, as one of the most important applications of
fundamental molecular blological insight. Most of our
expenditure on empirical toxicology is Wasted, would better be
devoted to mechanistic analysis of toxic effects, especially the
tnteraction of exogenous chemicals with oncogene mutation and
expression, :

The paradigm of comparative toxicology would seek a
fundamental understanding of the similarities and differences of
‘uman responses to chemicals compared to other species. We can
‘rotect human health only by well founded extrapolation from
‘!mpler models. Historically, toxic substances {metaholtc
ohibitors} had been central to the UNraVvAd trie oF

Pathways. The study of colchicine helped uncover tubulin;
neurotoxins did the same for synaptic mechanisms. However,
metabolic inhibitors have been displaced by more sophisticated
tools of microanalysis, tracer methodology, genetic lesions for
Pathway analysis, and the direct isolation of enzymes, These
have left a generation only dimly aware of that history.

Public Health and Epidemiology:

We have no good alternative to the blind clinical trial: but
this 1s devoid of mechanistic content. Therefore it tests only
the narrowest of hypotheses: the efficacy of the specific
treatment, conducted precisely according to the Protocol. Its

of adoption of therapeutic regimes,
Parasitology:

When I started compiling this list a decade ago, I felt it
important to press not only the humanistic importance but the
scientific excitement that would attach to intensified research
on protozoan and helminthic Parasites. That lesson is one I
would hardly have needed to bring to the Pasteur Institute, It
was a privilege to work with Jacques Monod and many others on the
advisory committees to the WHO that helped support the Tropical
Disease Research initiative, and with financial support from many
foundations there is now a global scientific network devoted to
these problems. The effort stil} needs much more Support and
especially from governments, There is no doubt that the flLeld
will be one of the most challenging and effective for the
application of the modern tools of molecular blology.

The bio-political myth of aggression versus altruism.

It is commonplace to hear how human evolution has not kept
Pace with and therefore cannot Properly control the technologies
of destruction tn modern warfare. The “ghost in the machine# is
purportedly the aggressive instinct, insufficiently tempered by
altruism, I can Scarcely challenge the Problematics of today’s
human condition; but 1 challenge the blopolitical model so
Presented. The root problem may be too much altruism, too little
individual aggressiveness, as deepseated human instincts. The
main technologies of warfare entail mass mobilization in response
to threats to the defined group. some of the most altruistic
self-sacrifices in historical record are those of combatants on
behalf of their fellows. It is beyond imagination that organized
warfare could be conducted if each recruit aggressively pursued
his own narrow self-interest, 1 offer, further, the gloomy
Speculation that emergence of altruism, intelligence and *
mythopotesis -- the signatures of humanity ~~ had, as its primary
selective driver in human evolution, the pressures of I{ntra-~
specific conflict, viz., warfare with other human groups. This
is not a cheerful contemplation; but if we are to seek remedies
for the psychic roots of global Problems, better that they be
correctly diagnosed, one answer 1s of course the global
cultivation of human intelligence, and the accumulation of a
culture of socializing traditions, to harness aggression and
transcend misplaced altruism. The prescriptions are futile,
however, until they can be symmetrically applied to competing
groups,
NN

Sun Nov 1 16:00:34 1987

Partly on account of the anxieties raised by international
economic competitiveness we are experiencing a new debate about
the optimal styles of organization of science. This is a
reflection of old controversies about needs for relevance or
early application, which have caused much grief in many
countries, perhaps most of all in the U.K. Biomedical science
has been stressed by such demands, but far less than, say pure
chemistry or mathematics. The debate now has a new wrinkle: the
availability of intricate but costly technology -~- like the
supercomputer -- has raised questions about the need to
restructure even basic research. It is said that existing
academic departments interfere with cooperative work across
disciplines, and that regroupings are necessary to share in the
justification of costly equipment. This is not controversial for
“Big Science” instruments like particle accelerators or large
telescopes. But there is an itch to invoke simtlar principles to
establish new “centers" devoted to particularized objectives for
science on a smaller scale than the national laboratories.

This is not the place to prolong a parochial discussion of
one country’s science policies; but I do wish to register my
concern that today’s solutions may be tomorrow’s larger problems.
Some of the root difficulties of inter-disciplinary effort and
other itnnovations are that, in the US, support for science is too
much tied to specific, pre-approved projects, If we could just
identify the most creative people and give them the freedom to
Make thelr own affiliations, they will do a better job than
imposing fixed structures on them. There are mega-projects
looming that will, nevertheless, impinge directly on how we go
about the pursuit of molecular blology during the next century:
in particular the proposed sequencing of the human genome.

This 1s a structure of formidable complexity: 3 billion
nucleotide pairs of DNA, a full theeé meters of double-helix if A
unravelled from a single cell. If, as is widely assumed, about

one percent of that total length 1s transcriptionally active,

about 100,000 gene products will have to be accounted for. The
ultimate reductionism would be to build an analytical factory

that could complete the reading of all 3 billion units as one
technical exercise, A price tag of a few billion dollars is

cited, perhaps Jess if there is prior investment in new

technology to automate the task.

Is it worth the cost? Undoubtedly. Is {tt the wisest use of
that level of expenditure? I have very grave doubts. Part of my
reservations have to do with the style of research {tt encourages,
part with a misunderstanding about what we need to learn in
“mapping the genome".

We have by now profound information concerning a score or so
human proteins; each of them is at least a life’s work. At a
modest $10 MM each, that would amount to a trillion dollars for
the full set; and obviously we must make discriminating
selections of targets before committing to the task. About a
hundred human proteins are now discernable as agents of {mportant
biological activity; that number will soon grow to perhaps a
thousand, these should be the priority list for further inquiry.
It will be far more important and more feasible to learn in depth
about that percentile of the human genome than to have an
exhaustive listing of a sequence of 3 billion nucleotides. For
these, we will look In detail into regulation, three-dimensional
structure, genetic variability within and between species,
Physiological interrelationships and therapeutic applications.

To pursue such enquiries will take much more than the engineering
mentality that would apply a single methodology for a single
sweep. It will need a sense of the organism, and a focussed
expertise on, even fascination for the parts under scrutiny.

This mega-proposal is, however, a plausible extension of the
“project mentality" I mentioned before. It is most appropriate
to what I call the exploitative phase of discovery. Exploratory
research engenders revolutionary breakthroughs with new
perspectives; the agenda for exploitative science then becomes
fairly obvious. Exquisite technical skills are to be recruited,
but not too much imagination. Such projects can then be fairly
readily judged by objective reviewers. There is little
likelihood of plans being disrupted by totally unexpected
discoveries -- though this may happen even in the best regulated
laboratory. Precisely because the DNA-sequence paradigm is so
central to modern biology, it does set the agenda for almost all
of the foreseeable, the plannable research at least of the next
couple of decades. My fear is that it may also submerge new
revolutions, not unlike the ones that initiated us into this
phase of the history of biology.

DNA~sequencing is, however, so central to biotechnology that
I have little concern whether it will be adequately supported

over the next few decades. I heartily agree that desperate
exigencies like AIDS and the need for vaccines for third world
disease require a large public investment as well.

My recipe is that we not overlook exploratory research, en
often best done in the context of natural historical observation
-- the field of vlew may be under the microscope, or at the
hospital bedside, as well as the open countryside or the oceans. cys
Such research is often not informed by a prior theory (or one not
much more than a hunch, like my own 40 years ago that bacterla
might in fact be crossable). It must of course be supported by
much the same conceptual intricacies and instrumental methods as

is exploitative work; but 1t takes the past less for granted; it
waits for Nature to show new tricks. a

For many years we have taught that advances in medical
practice would be the fruit of prior scientific progress, This
was surely the Pasteurian lesson, and it had much truth in ' v
dealing with infectious disease through its culmination in
vacelnes and antibiotics. Sometimes forgotten was the historical
fact that much scientific advance, much of the foundations of the
germ theory for example, eventuated from feedback from clinical
observation raising scientific questions and offering some clues
to their solution. The eptc instance fs the discovery of the
genetic function of DNA by Avery, MacLeod and McCarty in 1944. pro’
This was a product of a research program that had its roots in
seeking serotherapy of pneumonia. That in turn required looking
at antigenic variation in the pneumococcus, and an inspired
stroke by Griffith to trying transforming one variety with
extracts of another. Only the medical significance of the
pneumococcus could have justified so much attention to its
natural history. But if Avery had been obliged to defend his
group’s quest for the transforming factor, it is doubtful any
group of experts, reviewing such a research proposal, could have
forecast its significance.

Constitutional disease (heart disease, cancer, psychiatric
disorder) surpassed infection as a public health problem around
mid-century. At that point, the teaching “science first“ was no
longer an accurate portrayal of therapeutic advance. In fact the
Sun Nov. 1 16:00:34 1987

sctence of the human constitution was hardly up to the task. The
most important advances in practice were semi- empirical, e.g.
the drugs used tn cancer chemotherapy. To this day, we have no
insight into thelr organ specificity or their therapeutic index;
and I have grave doubts whether their cytocidal effects are more
than the beginning of their mode of action, From 1950-1980 most
pharmaceutical innovations were substantially empirical, the
result of vast screening programs. The quest for antibiotics was
rationalized by the perception that they could be found as
secondary metabolites of soll microbes, We still argue what
their ecological function may be; and we learn a good deal of
cytophysiology by exploring their mode of action after the fact,
Subsequently, structures (like beta-lactams) found to be
bactericidal may be the subject of random synthetic chemical
variation in a quest for further activities,

The same applies a fortiori in the development of
psychopharmaceuticals., Without exception these were empirically
discovered; in some cases they prompted further studies of mode
of action that have contributed importantly to neurobiochemistry.

A similar story can be told of one of our most important
drugs: aspirin. The elucidation of willow bark as an inhibitor
of the prostaglandin synthetase system was a most worthy citation
for a recent Nobel prize.

In this decade, we are seeing a turn-around. Just when
there has been accumulated skepticism about so much investment in
basic research, it has begun to bear abundant fruit. Most recent
pharmaceuticals have been the product of calculated search for
compounds that would bind to targetted receptors, like
anglotensin-convert ing-enzyme or beta-receptors or calcium-
channels, or enzymes in the blosynthesis of cholesterol. And
biotechnology has offered the means of production, increasingly
often even discovery, of polypeptides and proteins important in
functional regulation.

I have already offered a recipe, to sustain an eclectic
balance between deductive and inductive approaches to sclentific
discovery, in some sense between the Appollonian and Dionysian
styles, This is not accomplished very well in our current
educational regimes. The Ph. D, degree is all too specialized:
students in a blochemistry department even in a medical school
are unlikely ever to see a patient; the M.D. students rarely
visit a research laboratory. To wait for both degrees is to be a
perpetual student. In the U.S. there are almost {nsurmountable
financial incentives for M.D.s to enter the high-earning
specialties, and pay their educational debts, and against going
into a research career, whose material compensation is in inverse
proportion to its fundamental significance, Undergraduate
education 1s an ever narrowing strait between remedial makeup for
the failings of the secendary schools and premature enrollment in
a graduate specialty.

The Ph.D. graduate must look forward to a lifelong career of
seeking project grants. His most promising years may be those in
graduate school and as a postdoctoral fellow when he at least has
the administrative and financia) shelter of an established
laboratory, We should not lose sight of the often contradictory
demands on the scientific personality: antitheses such as
imagination vs, critical rigor; 1conoclasm vs. respect for
established truth; humility and generosity to colleagues vs.
arrogant audacity to nature; efficient specialization vs. broad
interest; doing experiments vs. reflection; ambition vs. sharing

of ideas and tools -- all these and more must be reconciled
within the professional persona, They are intrinsic to the
nature of sclence, We should work hard to avoid piling on
gratuitous stresses that discourage, perhaps even deter, some of
the worthiest young people seeking scientific careers today.

The M.D. contemplating research today faces the added
complication of widespread confusion about the nature and future
of clinical investigation. Research ON patients is indispensable
for answers to many urgent medical problems; it is also very
difficult to conduct with the rigor and efficiency of laboratory
studies. No wonder that the majority of papers in the Journal of
Clinical Investigation concern animal, tissue-culture, or cell-
free models! Lamentably, many M.D.s who remain in research have
fled clinical problems altogether, with an obvious wastage of
individual and social investment in their clinical education.

The ideal example is clinically informed investigation, conducted
with the most efficient tools on the part of medical sctentists
who remain involved in clinical practice, are inspired by their
observation of disease, and may return to experiments on patients
at the appropriate stage of elaboration of principles worked out
on more amenable models.

In our role as mentors, there is one unlversal: we can set a
good example of not fearing to display our ignorance: {fn the way
we present our seminars, and how we ask even "dumb" questions.
Some may feel that is no voluntary calculation on my part. Too
Many presentations are self-congratulation about what we have
accomplished rather than a sharing of perplexity about what
remains to be learned.

My final remark about scientific process: we don’t
understand it very well; and we have not been much helped so far
by those few Olympian philosophers who have attempted to analyze
it. There is little authentic descriptive data on how discovery
was actually accomplished. Even when there has been a singular
“Eureka!", there is usually a more complex process of
confirmation, refinement, reconstruction of context, social;
dialectic of acceptance, resistance, and remolding. Ina
tradition solidified by Claude Bernard, our publications are
racipes and rationalizations after the fact; rarely do they
describe the stumblings and false starts: so Medawar called them
lies. They do little to teach how science is done; and they give
too much inappropriate support to those who think that sclentific
discovery can be planned and written up in advance in project
proposals,

SOCIAL MILIEU

The sporadic campaigns for a return to primitive nature and
against technology notwithstanding, there is no sign of a
diminished appetite of the world’s people for the fruits of
scientific and technological advance. People are worried that
they may have to make ethically difficult choices which probe
thelr innermost values -~ and these are often bitterly argued.
They also worry (appropriately) about the shadow of nuclear
destruction, We have to tell them it is the unrepealable laws of
physics that make bombs possible -~ and that would be at least
half right. The most Lrrational demands are for perfect
environmental safety, for zero pollution (in the face of the
immensity of Avogadro’s number). All of these issues are
amenable to public education about the substance of science --
much has been written about the disgraceful state of that, at
least in American schools.
Sun Nov 1 16:00:34 1987

More deepseated are cultural changes that challenge
authority: the secular priesthood of scientific expertise no less
than that of abandoned beliefs in traditional religion. Personal
privacy 1s jealously guarded even in the face of overwhelming
threats to public health, Animals are being invested with
ethical and legal rights in an extension of democratic
principles. Many people expect to get all the benefits of
medical innovation while encumbering the process with an ever-
increasing bureaucracy; and ofcourse many livings are to be made
by the officers and lawyers who police science and medicine, I
do not expect much amelioration in these tensions: they are
almost inevitable byproducts of the disestablishment of given
authority. Science will be slowed down, but it can accomodate to
these challenges.

I am more morally troubled by the individualists’ selfish
preoccupation with micro-ethical issues. There 1s enormous
publicity given to the fate of one frozen embryo; the avertable
death of 3 million children per year, from disease that can be
prevented with known vaccines, is all but ignored.

Fears about the hazards of recombinant DNA are recurrently
incited, and they take ready root in a public that has an almost
theological (or diabolical) preoccupation with DNA, and one which
especially has no competence in the assessment of risk under
uncertainty. It should be understood that work with recombinant
DNA is not an idle game: without it, for example, we would be
virtually helpless in dissecting the AIDS virus.

We can argue that our HIV predicament has followed almost
syllogistically from our neglect of the health problems of the
third world. It was predictable that those populations would be
ideal foci for the evolution and seeding of novel infectious
agents, HIV has an insidious quality that transcends what anyone
could have imagined for an emergent virus, I am certain that it
will not be the last,

The hazards of monoculture of our main food crops, their
consequent vulnerability to devastating plant diseases, have had
much comment (but Little responsive action). The global
conditions of modern life : the combination of crowding, an
underclass of neglected people exposed to zoonotic infections,
primitive health facilities, rapid jet transport and selfish
individual behavior are almost designed for similar evolutionary
outbreaks of human disease, Our enormous advances in
chemotherapy for bacterial infection are so far not matched for
viruses; we are barely beginning to learn the specializations of
viral metabolism that would provide targets, and there is no
assurance they will work.

That the apocalyptic challenges to humanity are hunger,
overpopulation, pestilence, and war is so truistic that one may
be shy about repeating the reminder. We have all dedicated our
scientific endeavors to do all possible to meet them -- we do not
often get requisite political and social attention. I am all the
more grateful that President Mitterand and M. Elie Wiesel will
be holding a convocation here in Paris in January for a serious
mobilization of intellectual and moral concern about humanity’s
needs,

Their program would be in wonderful harmony with Louis
Pasteur’s remarks on his 70th birthday:
‘'..-Do not let yourselves be tainted by a deprecat{ng and barren

skepticism, do not let yourselves be discouraged by the sadness
of certain hours which pass over nations. Live in the serene
peace of laboratories and libraries. Say to yourselves first:
“what have I done for my instruction?" and, as you gradually
advance, “What have I done for my country?" until the time comes
when you may have the immense happiness of thinking that you have
contributed in some way to the progress and good of humanity.
But, whether or not your efforts are smiled upon by fate, what
really matters in the end 1s to be able to say: "I did what I was
able." ¢ :