Bruce Alberts
One of my most important formativeexperiences as a scientist was verytraumatic at the time. In the spring
of 1965, I had finished writing my PhD
thesis at Harvard University, in Cambridge,
Massachusetts, and had purchased aeroplane
tickets to take my wife Betty and our one-
year-old daughter with me for a postdoctoral
year in Geneva, Switzerland. Only one step
remained — a meeting of my thesis commit-
tee to approve the granting of my PhD degree
in biophysics. No one in recent memory had
failed at this late stage. But to my great
surprise, the committee failed me, specifying
the need for more experiments that eventu-
ally required six more months of research.
This was,of course,a great embarrassment
and a shock to my ego.There were the practi-
cal problems of having to remain at Harvard
— our apartment had already been rented to
the next tenant and my small family had
nowhere to live. But most importantly, I was
to spend the next few months struggling to
answer two questions that would be critical
for my future.What had gone wrong,and did
I really have what it takes to be a scientist?
As an undergraduate working with
Jacques Fresco in Paul Doty’s laboratory at
Harvard,I was handed a research project that
proved to be very successful. My undergrad-
uate thesis was quickly converted into two
important papers in 1960.This largely unde-
served success gave me a false image of how
easy it would be to do science. It also enabled
me to persuade Paul Doty to allow me to test
my own theoretical model for the initiation
of chromosome replication as the centre-
piece of my PhD research.
According to my model, the sites at which
DNA replication begins (now called replica-
tion origins) should be located at the two
ends of each DNA helix in a chromosome.
If this model was correct, the enzyme DNA
polymerase should create a transient cova-
lent linkage between the two complemen-
tary DNA strands at the tip of a chromosome
(a ‘DNA crosslink’). I began an extensive
search in DNA genomes for crosslinks that
were located near the sites where replication
begins. None of the tests supported my
particular model, but I did find other
crosslinks in all of the chromosomes that I
tested. I spent several years characterizing
these mysterious and unexpected ‘naturally
occurring crosslinks’, but even 40 years later,
their structure and origin are still not under-
stood (J. Mol. Biol. 32, 405–421; 1968).
In retrospect, the shock of having my
PhD thesis rejected in 1965 proved to be a
critical step in shaping me as a scientist,
because it forced me to recognize the central
importance of the strategy that underlies any
major scientific quest.
I had witnessed the frustration of scien-
tists who were pursuing obvious experi-
ments that were simultaneously being
carried out in other laboratories. These
scientists were constantly in a race. It had
always seemed to me that, even if they were
able to publish their results six months
before a competing laboratory, they were
unlikely to make truly unique contributions.
I had used a different strategy. My
approach had been that of predicting how
a particular biological process might work
and then taking years to test whether my
guess might be right. This was enormously
risky. The good news was that I was carrying
out experiments that were different from
those being done by everyone else. The
problem was that these tests could produce
only a ‘yes’ or ‘no’ answer. If ‘yes’, I might be
able to add something unique to the world’s
store of scientific knowledge. But if ‘no’, I
would learn nothing of real value — in this
case, I could eliminate just one of the many
possible ways in which DNA replication
might begin.
I wanted to continue to focus on how
DNA is replicated for my postdoctoral work
in Geneva. But what strategy should I
essay turning points
NATURE | VOL 431 | 28 OCTOBER 2004 | www.nature.com/nature 1041
choose? The months of analysis triggered by
the wake-up call of my PhD failure finally
produced an answer. I would look for a
unique experimental approach, but one that
would have a high probability of increasing
our knowledge of the natural world, regard-
less of the experimental results obtained.
After a great deal of soul-searching, I
decided that I would begin by developing a
new method — one that would allow me to
isolate proteins required for DNA replica-
tion that had thus far escaped detection. I
knew that the enzyme RNA polymerase,
which reads out the genetic information in
DNA, binds weakly to any DNA sequence —
even though this protein’s biologically
relevant binding sites are specific DNA
sequences. If the proteins that cause DNA to
replicate have a similar weak affinity for any
DNA molecule, I would be able to isolate
them by passing crude cell extracts through a
column matrix containing immobilized
DNA molecules.
Arriving in Geneva in late 1965 with my
PhD degree finally in hand, I found that by
drying an aqueous solution of DNA onto
plain cellulose powder, I could construct
a durable and effective ‘DNA cellulose’
matrix. A large number of different proteins
in a crude, DNA-depleted extract of the
bacterium Escherichia coli bound to a
column containing this matrix. Moreover,
these DNA-binding proteins could be readily
purified by elution with an aqueous salt
solution.Using this new biochemical tool
and a large library of mutant T4 bacterio-
phages obtained from Dick Epstein in
Geneva, I discovered the T4 gene 32 protein
after moving to Princeton a year later as an
assistant professor.This proved to be the first
example of a single-strand DNA-binding
(SSB) protein, a structural protein that plays
an important role in DNA processes in all
organisms (see Nature 227,1313–1318;1970).
The strategy of investing in method
development and then using this new
method for a major series of experiments
would be employed over and over again
during the next 25 years of my career as a
research scientist. As a result, my laboratory
almost never felt that it was in a race with
other laboratories, and our successes were
sufficient to satisfy both me and many of the
graduate students and postdoctoral fellows
who would join my laboratory. It seems
strange to recall that we may owe all it all to
one very unhappy PhD thesis committee at
Harvard,nearly 40 years ago. ■
Bruce Alberts is the president of the National
Academy of Sciences, 500 5th Street, NW,
Washington DC 20001, USA.
A wake-up call
How failing a PhD led to a strategy for a successful scientific career.
Bruce Alberts: ‘failure’ was a blessing in disguise.
28.10 turning points 1041 MH 22/10/04 5:31 pm Page 1041
© 2004 Nature Publishing Group