Snyder S. H., The Audacity Principle in Science, 2005.pdf

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The Audacity Principle in Science
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SOLOMON H. SNYDER
Department of Neuroscience
Johns Hopkins University
School of Medicine
Dedicated to Julius Axelrod
a humble, gentle scientist who nonetheless epitomized the
Audacity Principle in Science. He died 29 December 2004.
M
Y MENTOR, Julius Axelrod, often commented, “Ninety-
nine percent of the discoveries are made by one percent of
the scientists.” This may sound like an exaggeration. How-
ever, a brief examination of the major advances in any branch of science
reveals the truth of this dictum. Axelrod himself is a prime example. In
the field of molecular pharmacology, many of the key advances are
attributable to his own efforts. He elucidated the metabolism of the
major psychoactive drugs, in the process laying the groundwork for
the emergence of acetominophen (Tylenol) as a major analgesic and then
uncovering the family of drug-metabolizing enzymes, now known as
the P450 enzymes. He accomplished most of this while working as a
laboratory technician without a Ph.D. Following receipt of his doctor-
ate at age forty-two, Axelrod proceeded to revolutionize neurotrans-
mitter research. Consider the catecholamine neurotransmitters such as
norepinephrine and dopamine. After norepinephrine was established
as the neurotransmitter of sympathetic nerves in the late 1940s, advances
were relatively modest. The enzymatic processes leading to its biosyn-
thesis from the dietary amino acid tyrosine were gradually elucidated
by multiple investigators over a period of several decades. Classical
pharmacologic studies comparing the effects of different drugs on sym-
pathetic neurotransmission had led to an appreciation that there were
at least two subtypes of receptors for norepinephrine, designated alpha
version of this paper was read at the Autumn General Meeting on 9 November 2002.
Acknowledgments: Supported by USPHS grants MH18501, DA00266, MH068830 and
Research Scientist Award DA00074. I thank Susan Arellano for helpful suggestions.
PROCEEDINGS OF THE AMERICAN PHILOSOPHICAL SOCIETY
VOL. 149, NO. 2, JUNE 2005
1
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and beta, which subsequently led to important new drugs. Then, in
roughly half a decade, Axelrod had a series of insights that drastically
altered our thinking about norepinephrine and, indeed, all neurotrans-
mitters. In 1957 he discovered catechol-O-methyltransferase, a key en-
zyme in metabolizing the catecholamines. This led him to question the
prevailing assumption that the only other known enzyme that metabo-
lizes catecholamines, monoamine oxidase, accounts for inactivation of
norepinephrine after it is released by sympathetic nerves. Inactivating
neurotransmitters is of crucial importance, for it serves to remove them
from the vicinity of receptors on adjacent neurons so that successive
nerve impulses will be effective. In the early 1960s the only neurotrans-
mitter known besides norepinephrine was acetylcholine, discovered in
the late 1920s. It was well established that the actions of acetylcholine
are terminated by enzymatic degradation via an enzyme called acetyl-
cholinesterase. Drugs that inhibit this enzyme potentiate the actions of
acetylcholine at synapses, sites where nerves communicate with each
other. Such acetylcholinesterase inhibitors provide important therapy for
diseases such as myasthenia gravis that are characterized by muscle weak-
ness because of deficient neurotransmission at acetylcholine synapses.
Because of the well-established role of acetylcholinesterase in inacti-
vating acetylcholine, it was accepted wisdom that enzymes would inac-
tivate norepinephrine at its synapses. But no one had directly evaluated
whether monoamine oxidase was in fact responsible for norepineph-
rine inactivation. To compare the roles of catechol-O-methyltransferase
and acetylcholinesterase, Axelrod utilized drugs that inhibit the two
enzymes and was surprised to find that neither enzyme could explain
synaptic inactivation. About this time, radioactive forms of norepineph-
rine became available. Instead of pursuing convoluted biochemical
experiments with the radiolabeled molecule, Axelrod simply injected it
into rats. He was amazed to find that organs enriched in sympathetic
nerves, such as the heart, enormously concentrated the radioactive
norepinephrine. When sympathetic nerves were severed, these organs
no longer took up the neurotransmitter, indicating that it was the sym-
pathetic nerve endings that had been concentrating norepinephrine.
Based on his experimental findings, Axelrod formulated a simple model
to explain neurotransmitter inactivation. He proposed that uptake of
the norepinephrine into the nerve endings that had released it mediates
synaptic inactivation. His theory was rapidly proven right by experi-
ments showing that cutting the nerve endings to eliminate the uptake
process markedly potentiated neurotransmission. He wondered whether
drugs that could mimic the effects of sympathetic nerve firing might act
by inhibiting this uptake process, thereby potentiating actions of nor-
epinephrine. Utilizing radiolabeled norepinephrine, he soon showed that
the audacity principle in science
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agents such as cocaine, amphetamines, and, most important, the major
antidepressants, exert their effects by inhibiting the uptake process. Soon,
other scientists showed that uptake mechanisms account for inactiva-
tion of virtually all the major neurotransmitters, with enzymatic degra-
dation, as with acetylcholine, being the exception rather than the rule.
For these contributions, Axelrod shared the Nobel Prize in Physiology
or Medicine in 1970 with Ulf von Euler, who established norepineph-
rine as a transmitter, and Bernard Katz, who showed that neurotrans-
mitters are stored in and released from synaptic vesicles.
What do we learn from the above anecdote? First, in this field one
scientist with a tiny laboratory comprising no more than three or four
postdoctoral fellows could make many if not most of the key break-
throughs in a large field of research. Second, we learn to wonder what
differentiates individuals such as Axelrod from others in the field. This
leads us to the focus of this essay: what makes for greatness in scientific
research?
Clearly Axelrod manifested an abundance of creative insights. He
conceptualized principles never previously enunciated. The notion that
neurotransmitters were inactivated by being taken back into the nerve
that had released them initially met with ridicule. Axelrod saw through
dogma as gerrymandered as the Ptolemaic planetary system and, like
Galileo, provided radical simplification. But creativity isn’t enough.
Whenever a major new discovery is published, dozens of scientists
exclaim, “I thought of that a long time ago but just didn’t do the right
experiment.” Original ideas are only a part of the story. A special sort
of energy is required to overcome the fear or inertia that hinders scien-
tists from essaying risky, unprecedented experiments. Of course, devising
the optimal experiment is crucial, and all experimental breakthroughs
involve simplification. One could conceptualize intricate, year-long ap-
proaches to experiments to explore neurotransmitter uptake. Axelrod
simply injected radiolabeled norepinephrine into rats and came up with
the “answer” in a day or two. Experimental ingenuity, a shrewdness in
experimental design, and “good hands” all play a role in coming up
with the “right” experiment. But I have known many talented experi-
mentalists who never make major advances.
Much has been written about the nature of scientific discovery. The
rigor of scientific hypothesis formulation and testing, as well as critical
thinking to rule out artefactual explanations of data, is often high-
lighted. My personal experience over three to four decades tells me that
the real breakthroughs don’t happen this way. The greatest scientists
tend to resemble artists in certain ways, but with notable differences.
Artists see the world differently than the rest of us. They find wonder
in the seemingly mundane. They detect commonalities among objects
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that most viewers see as notably disparate. Similarly, the finest researchers
view with puzzlement established principles that are taken for granted
by the scientific community. In particular, they become irritated by
overly convoluted explanatory principles. They seek simplicity, where-
upon novel concepts emerge. The ability to divine unifying notions out
of a morass of data seems critical.
Equally important is the intellectual and often emotional courage
to enunciate such simplifications. Courage is requisite for many rea-
sons. Challenging established authority is always risky. The challenge
is even more complex in science because, when first presented, a new
unifying concept can rarely account for all the available data. One must
be willing to proffer and defend a novel hypothesis in the face of some
contradictions, based simply on the argument that the virtues of a new
model, compared with older formulations, exceed its drawbacks. Often
history bears out the validity of the new paradigm, but sometimes the
innovative notion proves false; hence the risk. Positing something new
even in the presence of discrepancies is justified, for often such discrep-
ancies fade away as new data emerge. The late Francis Crick was a
lover of elegant, simple, and revolutionary hypotheses. He believed
strongly in the beauty and simplicity of nature and thus favored simple
explanatory models. In an informal group in which he and I participated
years ago, he put it roughly this way, “If the theory has a beautiful feel
and makes good sense despite some ugly data which don’t agree, per-
haps the data are wrong!”
All these factors seem to be relevant. Originality and simplicity are
certainly crucial elements. Even more important are the intellectual
fearlessness and emotional drive to put it all together, step forward, do
the right experiment, promulgate it to the world, defend the new
insights, and go forward to further innovation. A simple designation
for this behavioral pattern might be the Audacity Principle. Audacious
behavior is usually regarded as a form of hubris or chuzpah, an off-
putting and overly aggressive behavior that we don’t usually link to
creativity. Here I use the term to focus on the intellectual qualities of
audacity that enable individuals of talent to implement their own
native ability. In other words, scientific originality may not be so rare a
commodity as is the capacity to appreciate the importance of one’s
own ideas and to put them into practice.
Lineage
One way to seek the qualities that make for scientific discovery is to
examine what is conveyed in the mentor-apprentice relationship. The
eminent sociologist Harriet Zuckerman has provided compelling evidence

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