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March 21, 2006

Can a biologist fix a radio

Can a biologist fix a radio?—Or,what I
learned while studying apoptosis
As a freshly minted Assistant Professor,I feared that everything
in my field would be discovered before I even had a chance to
set up my laboratory.Indeed,the field of apoptosis,which I had
recently joined,was developing at a mind-boggling speed.
Components of the previously mysterious process were being
discovered almost weekly,frequent scientific meetings had little
overlap in their contents,and it seemed that every issue of Cell,
Nature,or Sciencehad to have at least one paper on apoptosis.
My fear led me to seek advice from David Papermaster (cur-
rently at the University of Connecticut),who I knew to be a per-
son with pronounced common sense and extensive experience.
David listened to my outpouring of primal fear and explained
why I should not worry.
David said that every field he witnessed during his decades
in biological research developed quite similarly.At the first
stage,a small number of scientists would somewhat leisurely
discuss a problem that would appear esoteric to others,such as
whether cell cycle is controlled by an oscillator or whether cells
can commit suicide.At this stage the understanding of the prob-
lem increases slowly,and scientists are generally nice to each
other,a few personal antipathies notwithstanding.Then,an
unexpected observation,such as the discovery of cyclins or the
finding that apoptosis failure can contribute to cancer,makes
many realize that the previously mysterious process can be dis-
sected with available tools and,importantly,that this effort may
result in a miracle drug.At once,the field is converted into a
Klondike gold rush with all the characteristic dynamics,mentali-
ty,and morals.A major driving force becomes the desire to find
the nugget that will secure a place in textbooks,guarantee an
unrelenting envy of peers,and,at last,solve all financial prob-
lems.The assumed proximity of this imaginary nugget easily
attracts both financial and human resources,which results in a
rapid expansion of the field.The understanding of the biological
process increases accordingly and results in crystal clear mod-
els that often explain everything and point at targets for future
miracle drugs.People at this stage are not necessarily nice,
though,as anyone who has read about a gold rush can expect.
This description fit the then current state of the apoptosis field
rather well,which made me wonder why David was smiling so
reassuringly.He took his time to explain.
At some point,David said,the field reaches a stage at
which models,that seemed so complete,fall apart,predictions
that were considered so obvious are found to be wrong,and
attempts to develop wonder drugs largely fail.This stage is
characterized by a sense of frustration at the complexity of the
process,and by a sinking feeling that despite all that intense
digging the promised cure-all may not materialize.In other
words,the field hits the wall,even though the intensity of
research remains unabated for a while,resulting in thousands
of publications,many of which are contradictory or largely
descriptive.The flood of publications is explained,in part,by the
sheer amount of accumulated information (about 10,000 papers
on apoptosis were published yearly over the last few years),
which makes reviewers of the manuscripts as confused and
overwhelmed as their authors.This stage can be summarized
by the paradox that the more facts we learn the less we under-
stand the process we study.
It becomes slowly apparent that even if the anticipated gold
deposits exist,finding them is not guaranteed.At this stage,the
Chinese saying that it is difficult to find a black cat in a dark
room,especially if there is no cat,comes to mind too often.If
you want to continue meaningful research at this time of wide-
spread desperation,David said,learn how to make good tools
and how to keep your mind clear under adverse circumstances.
I am grateful to David for his advice,which gave me hope and,
eventually,helped me to enjoy my research even after my field
did reach the state he predicted.
At some point I began to realize that David ’s paradox has a
meaning that is deeper than a survival advice.Indeed,it was
puzzling to me why this paradox manifested itself not only in
studies of fundamental processes,such as apoptosis or cell
cycle,but even in studies of individual proteins.For example,
the mystery of what the tumor suppressor p53 actually does
seems only to deepen as the number of publications about this
protein rises above 23,000.
The notion that your work will create more confusion is not
particularly stimulating,which made me look for guidance
again.Joe Gall at the Carnegie Institution,who started to pub-
lish before I was born,and is an author of an excellent series of
essays on the history of biology (Gall,1996),relieved my mental
suffering by pointing out that a period of stagnation is eventual-
ly interrupted by a new development.As an example,he
referred to the studies of cell death that took place in the nine-
teenth century (Gall,1996,chapter 29),faded into oblivion,and
reemerged a century later with about 60,000 studies on the
subject published during a single decade.Even though a
prospect of a possible surge in activity in my field was relieving,
I started to wonder whether anything could be done to expedite
this event,which brought me to think about the nature of David ’s
paradox.The generality of the paradox suggested some com-
mon fundamental flaw of how biologists approach problems.
To understand what this flaw is,I decided to follow the
advice of my high school mathematics teacher,who recom-
mended testing an approach by applying it to a problem that has
a known solution.To abstract from peculiarities of biological
experimental systems,I looked for a problem that would involve
a reasonably complex but well understood system.Eventually,I
thought of the old broken transistor radio that my wife brought
from Russia.Conceptually,a radio functions similarly
to a signal transduction pathway in that both convert a signal
from one form into another (a radio converts electromagnetic
waves into sound waves).My radio has about a hundred various
components,such as resistors,capacitors,and transistors,
which is comparable to the number of molecules in a reason-
ably complex signal transduction pathway.I started to contem-
plate how biologists would determine why my radio does not
work and how they would attempt to repair it.Because a majori-
ty of biologists pay little attention to physics,I had to assume
that all we would know about the radio is that it is a box that is
supposed to play music.
How would we begin?First,we would secure funds to
obtain a large supply of identical functioning radios in order to
dissect and compare them to the one that is broken.We would
eventually find how to open the radios and will find objects of
various shape,color,and size.We would describe
and classify them into families according to their appearance.
We would describe a family of square metal objects,a family
of round brightly colored objects with two legs,round-shaped
objects with three legs and so on.Because the objects would
vary in color,we would investigate whether changing the col-
ors affects the radio ’s performance.Although changing the
colors would have only attenuating effects (the music is still
playing but a trained ear of some can discern some distortion)
this approach will produce many publications and result in a
lively debate.
A more successful approach will be to remove components
one at a time or to use a variation of the method,in which a
radio is shot at a close range with metal particles.In the latter
case radios that malfunction (have a “phenotype ”)are selected
to identify the component whose damage causes the pheno-
type.Although removing some components will have only an
attenuating effect,a lucky postdoc will accidentally find a wire
whose deficiency will stop the music completely.The jubilant fel-
low will name the wire Serendipitously Recovered Component
(Src)and then find that Src is required because it is the only link
between a long extendable object and the rest of the radio.The
object will be appropriately named the Most Important
Component (Mic)of the radio.A series of studies will definitive-
ly establish that Mic should be made of metal and the longer the
object is the better,which would provide an evolutionary expla-
nation for the finding that the object is extendable.
However,a persistent graduate student from another labo-
ratory will discover another object that is required for the radio to
work.To the delight of the discoverer,and the incredulity of the
flourishing Mic field,the object will be made of graphite and
changing its length will not affect the quality of the sound signif-
icantly.Moreover,the graduate student would convincingly
demonstrate that Mic is not required for the radio to work,and
will suitably name his object the Really Important Component
(Ric).The heated controversy,as to whether Mic or Ric is more
important,will be fueled by the accumulating evidence that
some radios require Mic while other,apparently identical ones,
need Ric.The fight will continue until a smart postdoctoral fellow
will discover a switch,whose state determines whether Mic or
Ric is required for playing music.Naturally,the switch will
become the Undoubtedly Most Important Component (U-Mic).
Inspired by these findings,an army of biologists will apply the
knockout approach to investigate the role of each and every
component.Another army will crush the radios into small pieces
to identify components that are on each of the pieces,thus pro-
viding evidence for interaction between these components.The
idea that one can investigate a component by cutting its con-
nections to other components one at a time or in a combination
(“alanine scan mutagenesis ”)will produce a wealth of informa-
tion on the role of the connections.
Eventually,all components will be cataloged,connections
between them will be described,and the consequences of
removing each component or their combinations will be docu-
mented.This will be the time when the question,previously
obscured by the excitement of productive research,would have
to be asked:Can the information that we accumulated help us to
repair the radio?It will turn out that sometimes it can,such as if
a cylindrical object that is red in a working radio is black and
smells like burnt paint in the broken radio (Figure 2,inset,a
component indicated as a target).Replacing the burned object
with a red object will likely repair the radio.
The success of this approach explains the pharmaceutical
industry ’s mantra:“Give me a target!”This mantra reflects the
belief in a miracle drug and assumes that there is a miracle tar-
get whose malfunction is solely responsible for the disease that
needs to be cured.
However,if the radio has tunable components,such as those
found in my old radio and in all live cells and organisms,the outcome will not be
so promising.Indeed,the radio may not work because several
components are not tuned properly,which is not reflected in their
appearance or their connections.What is the probability that this
radio will be fixed by our biologists?I might be overly pessimistic,
but a textbook example of the monkey that can,in principle,type
a Burns poem comes to mind.In other words,the radio will not
play music unless that lucky chance meets a prepared mind.
Yet,we know with near certainty that an engineer,or even a
trained repairman could fix the radio.What makes the differ-
ence?I think it is the languages that these two groups use. Biologists summarize their results with the help of all-
too-well recognizable diagrams,in which a favorite protein is
placed in the middle and connected to everything else with two-
way arrows.Even if a diagram makes overall sense (Figure 3A),
it is usually useless for a quantitative analysis,which limits its
predictive or investigative value to a very narrow range.The lan-
guage used by biologists for verbal communications is not bet-
ter and is not unlike that used by stock market analysts.Both
are vague (e.g.,“a balance between pro-and antiapoptotic
Bcl-2 proteins appears to control the cell viability,and seems to
correlate in the long term with the ability to form tumors ”)and
avoid clear predictions.
These description and communication tools are in a glaring
contrast with the language that has been used by engineers
(compare Figures 3A and 3B).Because the language (Figure
3B)is standard (the elements and their connections are
described according to invariable rules),any engineer trained in
electronics would unambiguously understand a diagram
describing the radio or any other electronic device.As a conse-
quence,engineers can discuss the radio using terms that are
understood unambiguously by the parties involved.Moreover,
the commonality of the language allows engineers to identify
familiar patterns or modules (a trigger,an amplifier,etc.)in a
diagram of an unfamiliar device.Because the language is quan-
titative (a description of the radio includes the key parameters of
each component,such as the capacity of a capacitor,and not
necessarily its color,shape,or size),it is suitable for a quantita-
tive analysis,including modeling.
I would like to argue that the absence of such language is
the flaw of biological research that causes David ’s paradox.
Indeed,even though the impotence of purely experimental
approaches might be a bit exaggerated in my radio metaphor,it
is common knowledge that the human brain can keep track of
only so many variables.It is also common experience that once
the number of components in a system reaches a certain
threshold,understanding the system without formal analytical
tools requires geniuses,who are so rare even outside biology.In
engineering,the scarcity of geniuses is compensated,at least
in part,by a formal language that successfully unites the efforts
of many individuals,thus achieving a desired effect,be that
design of a new aircraft or of a computer program.In biology,we
use several arguments to convince ourselves that problems that
require calculus can be solved with arithmetic if one tries hard
enough and does another series of experiments.
One of these arguments postulates that the cell is too com-
plex to use engineering approaches.I disagree with this argu-
ment for two reasons.First,the radio analogy suggests that an
approach that is inefficient in analyzing a simple system is
unlikely to be more useful if the system is more complex.
Second,the complexity is a term that is inversely related to the
degree of understanding.Indeed,the insides of even my simple
radio would overwhelm an average biologist (this notion has
been proven experimentally),but would be an open book to an
engineer.The engineers seem to be undeterred by the complex-
ity of the problems they face and solve them by systematically
applying formal approaches that take advantage of the ever-
expanding computer power.As a result,such complex systems
as an aircraft can be designed and tested completely in silico,
and computer-simulated characters in movies and video games
can be made so eerily life-like.Perhaps,if the effort spent on for-
malizing description of biological processes would be close to
that spent on designing video games,the cells would appear
less complex and more accessible to therapeutic intervention.
A related argument is that engineering approaches are not
applicable to cells because these little wonders are fundamen-
tally different from objects studied by engineers.What is so spe-
cial about cells is not usually specified,but it is implied that real
biologists feel the difference.I consider this argument as a sign
of what I call the urea syndrome because of the shock that the
scientific community had two hundred years ago after learning
that urea can be synthesized by a chemist from inorganic mate-
rials.It was assumed that organic chemicals could only be pro-
duced by a vital force present in living organisms.Perhaps,
when we describe signal transduction pathways properly,we
would realize that their similarity to the radio is not superficial.In
fact,engineers already see deep similarities between the sys-
tems they design and live organisms (Csete and Doyle,2002).
Another argument is that we know too little to analyze cells
in the way engineers analyze their systems.But,the question is
whether we would be able to understand what we need to learn
if we do not use a formal description.The biochemists would
measure rates and concentrations to understand how biochem-
ical processes work.A discrepancy between the measured and
calculated values would indicate a missing link and lead to the
discovery of a new enzyme,and a better understanding of the
subject of investigation.Do we know what to measure to under-
stand a signal transduction pathway?Are we even convinced
that we need to measure something?As Sydney Brenner
noted,it seems that biochemistry disappeared in the same year
as communism (Brenner,1995).I think that a formal description
would make the need to measure a system ’s parameters obvi-
ous and would help to understand what these parameters are.
An argument that is usually raised privately is why to bother
with all these formal languages if one can make a living by con-
tinuing with purely experimental research that took years to
learn.There are at least two reasons.One is that formal
approaches would make our research more meaningful and
more productive,and might indeed lead to miracle drugs.A
more immediate reason is that formal approaches may
become a basic part of biology sooner than we,experimental
biologists,expect.This transition may be as rapid as that from
slides to PowerPoint presentations,a change that forced some
graphics designers to learn how to use a computer and put
others out of work.
Of course,a plea for a formal approach in biology is not
new.The general systems theory,developed by Ludwig von
Bertalanffy because of his fascination with the complexity of
live organisms,was formulated 60 years ago,as well as his
concept of organisms as physical systems (von Bertalanffy,
1969).Bertalanffy ’s fundamental studies have been followed
by several attempts to approach cells as systems,the latest of
which,systems biology,has been rapidly developing into an
active field (Bhalla and Iyengar,1999;Bhalla et al.,2002;Bray,
1995;Davidson et al.,2002;Guet et al.,2002;Hartwell et al.,
1999;Schoeberl et al.,2002).Available computer power and
advances in analysis of complex systems raise hope that this
time the system approach will change from an esoteric tool
that is considered useless by many experimental biologists,to
a basic and indispensable approach of biology.
The question is how to facilitate this change,which is not
exactly welcomed by many experimental biologists,to put it
mildly (Bray,2001).Learning computer programming was
greatly facilitated by BASIC,a language that was not very use-
ful to solve complex problems,but was very efficient in making
one comfortable with using a computer language and demon-
strating its analytical power.Similarly,a simple language that
experimental scientists can use to introduce themselves to for-
mal descriptions of biological processes would be very helpful
in overcoming a fear of long-forgotten mathematical symbols.
Several such languages have been suggested (Kohn,1999;
Pirson et al.,2000)but they are not quantitative,which limits
their value.Others are designed with modeling in mind but are
too new to judge as to whether they are user-friendly (Maimon
and Browning,2001).However,I hope that it is only a question
of time before a user-friendly and flexible formal language will
be taught to biology students,as it is taught to engineers,as a
basic requirement for their future studies.My advice to experi-
mental biologists is to be prepared.
Yuri Lazebnik
Cold Spring Harbor Laboratory
Cold Spring Harbor, New York 11724
E-mail: lazebnik@cshl.edu
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Publicado por MM às March 21, 2006 04:24 PM