Reprinted from Nature, Vol. 324, No. 6098, pp. 627-628, 18 December 1986

© Macmillan Journals Ltd., 1986

Forty years of genetic
recombination in bacteria

 

Between April and June 1946, Joshua Lederberg and Edward L. Tatum carried out a series of
experiments that proved that bacteria can exchange their genes by sexual crossings. The experiments were
reported in Nature just 40 years ago'. In the following pair of articles, Joshua Lederberg first provides a
personal reminiscence of the circumstances of the discovery and then, together with Harriet Zuckerman,
considers it as a possible case of ‘postmature’ scientific discovery.

 

A fortieth anniversary reminiscence

Joshua Lederberg

In September 1941, when I started as an
undergraduate at Columbia University,
the genetics of bacteria was still a no-
man’s-land between the disciplines of
genetics and (medical) bacteriology. The
question whether “bacteria have genes,
like all other organisms” was still un-
answered, indeed rarely asked. My own
thoughts at that moment lay elsewhere. I
looked forward to a career in medical re-
search applying chemical analysis to prob-
lems like cancer and the malfunctions of
the brain. Cytotoxicology then appeared
to be the most promising approach to cell
biochemistry. It was Francis J. Ryan (d.
1963) who turned my attention to the shar-
per tools of genetics.

Ryan had spent 1941 —42 as a postdoct-
oral fellow at Stanford University, where
he had met G. W. Beadle and E. L. Tatum
(d. 1975), and had become fascinated with
their recent invention of nutritional muta-
tions in Neurospora as a tool for biochemi-
cal genetic analysis’. Although working on
a fungus like Neurospora did not go down
smoothly in a Department of Zoology as
at Columbia, where Ryan had accepted an
instructorship, he established a laboratory
to continue these studies. In January 1943
I was fortunate to get a job in his labora-
tory assisting in the preparation of media
and handling of Neurospora cultures.
Ryan’s personal qualities as a teacher and
the setting of serious research, discussion
with him, other faculty members and gra-
duate students in the department
nourished my education as a scientist. On
1 July 1943, I was called to active duty in
the United States Naval Reserve, and my
further months at Columbia College alter-
nated with spells of duty at the United
States Naval Hospital, St Albans, Long
Island. There, in the clinical parasitology
laboratory, I had abundant opportunity to
observe the life cycle of Plasmodium vivax.
This experience dramatized the sexual sta-
ges of the malaria parasite, which un-
doubtedly sensitized me to the possibility
of cryptic sexual stages in other microbes
(perhaps even bacteria). In October 1944,

  

>

Lederberg in 1945

I was reassigned to begin my studies at
Columbia Medical School; but I con-
tinued working with Ryan at the Morning-
side Heights campus.

Discovery

The important biological discovery of
that year, by Avery, MacLeod and
McCarty, was the identification of DNA
as the substance responsible for the
Pneumococcus transformation’. This phe-
nomenon could be viewed as the transmis-
sion of a gene from one bacterial cell to
another; but such an interpretation was
inevitably clouded by the obscure under-
standing of bacterial genetics at the time.
Avery’s work, at the Rockefeller Institute
in New York, was promptly communi-
cated to Columbia biologists by Theodo-
sius Dobzhansky (who visited Rockefel-
ler) and by Alfred Mirsky (of the Rock-
efeller faculty) who was a close collabor-
ator of Arthur Pollister in the Zoology
Department. The work was the focus of
widespread and critical discussion among
the faculty and students. Mirsky was a vo-
cal critic of the purported chemical identi-
fication of the transforming agent, while
applauding the central importance of the
work. For my own part, the transcendent
leap was simply the feasibility of knowing
the chemistry of the gene. Whether this
was DNA or protein would certainly be

clarified quickly, provided the Pneumo-
coccus transformation could be securely
retained within the conceptual domain of
gene transmission. I read the Avery, Mac-
Leod and McCarty paper on 20 January
1945, prompted by Harriett Taylor (later
Ephrussi- Taylor) a graduate student in
Zoology who planned to pursue her post-
doctoral studies with Avery. My excited
response is recorded as ... “unlimited in its
implications... Direct demonstration of
the multiplication of transforming fac-
tor... Viruses are gene-type compounds.”

Atonce, I thought of attempting similar
transformations by DNA in Neurospora.
This organism had a well understood life-
cycle and genetic structure. The biochemi-
cal mutants opened up by Beadle and
Tatum also allowed the efficient detection
of nutritionally self-sufficient (prototrophic)
forms, even if these were vanishingly rare.
This would facilitate the assay of transform-
ational events.

Between January and May, 1945, I
shared this idea with Francis Ryan; in
June, he invited me to work on the subject
with him. To our dismay, we soon disco-
vered that the leucine-minus Neurospora
mutant would spontaneously revert to
prototrophy’, leaving us with no reliable
assay for the effect of DNA in mediating
genetic change in Neurospora. Questions
about the biology of transformation would
remain inaccessible to conventional gene-
tic analysis if bacteria lacked a sexual sta-
ge. But was it true that bacteria were asex-
ual? Rene Dubos’ monograph, The Bac-
terial Cell’, footnoted how inconclusive
the claims were for or against any morpho-
logical exhibition of sexual union between
bacterial cells.

My notes dated 8 July 1945 detail
hypothetical experiments both to search
for mating among Monilia (medically im-
portant yeast-like fungi) and to seek gene-
tic recombination in bacteria (by the pro-
tocol that later proved to be successful).
These notes coincide with the beginning of
my course in medical bacteriology. They
were provoked by the contrast of the tra-
ditional teaching that bacteria were Schi-
zomycetes, asexual primitive plants, with
an appreciation of sexuality in yeast’,
which was represented at Columbia by the
graduate research work of Sol Spiegelman
and Harriett Taylor.

Dubos* cited many unclear, and two
clear-cut negative results”* for sexuality in
bacteria using genetic exchange metho-
dology. But these two studies had no
selective method for the detection of re-
combination and so would have over-
looked the process had it occurred less
often than perhaps once per thousand
cells. With the use of a pair of nutritional
mutants, say A°B” and A B’, one could
plate out innumerable cells in a selective
medium and find a single A*B* recom-
binant. In early July, I began experiments
along these lines. In the first instance I
used a set of biochemical mutants in
Escherichia coli, which I began to accumu-
late in Ryan’s laboratory. To avoid the
difficulty that had arisen in our Neuros-
pora experiments, a spontaneous rever-
ston from A’B* to A‘B’, the strategy
would be to use a pair of double mutants:
AB C'D‘ and A*B*C’D’. Sexual cross-
ing should still generate A*B*C*D* pro-
totroph recombinants. These would be
unlikely to arise by spontaneous rever-
sions which, in theory, requires the coin-
cidence of two rare events; AT > A* and
B’ — B*. Much effort was devoted to
control experiments to show that double
reversions would follow this model, and so
occur at a negligible frequency in the cul-
tures handled separately. Thus the occur-
rence of prototrophs in the mixed cultures
would be presumptive evidence of genetic
recombination.

Long shot

Meanwhile at Stanford, Ed Tatum,
whose doctoral training at Wisconsin had
been in the biochemistry of bacteria, was
returning to bacteria as experimental sub-
jects, having published two papers on the
production of biochemical mutants in E.
coli’, including double mutants like those
described here. During the summer of
1945 Francis Ryan learned that Tatum was
leaving Stanford to set up a new program-
me in microbiology at Yale. He suggested
that, rather than merely ask Tatum to
share these new strains, I apply to work
with him and get the further benefit of his
detailed experience and general wisdom.
Tatum agreed and suggested that I arrive
in New Haven in late March, to give him
time to set up his laboratory. He hinted
that he had some similar ideas of his own,
but never elaborated them. The arrange-
ment suited him by leaving him free to
complete his work on the biochemistry of
Neurospora, perform the heavy adminis-
trative duties of his new programme, and
still participate in the long-shot gamble of
looking for bacterial sex.

Printed in Great Britain by Turnergraphic Limited. Basingstoke. Hampshire

 

Experimental luck

1. We have learned” that E. coli strain
K-12 itself was a remarkably lucky
choice of experimental material: only
about one in twenty randomly chosen
strains of E. coli would have given posi-
tive results in experiments designed
according to our protocols. In particu-
lar, strain B, which has become the
standard material for work on bacter-
iophage, would have been stubbornly
unfruitful. Tatum had acquired K-12
from the routine stock culture collec-
tion in Stanford’s microbiology depart-
ment when he sought an E. coli strain to
use as a source of tryptophanase in
work on tryptophan synthesis in
Neurospora”. The same strain was then
in hand when he set out to make single,

 

 

and then double mutants in E. coli’. |
In 1946, I was very much aware of strain
specificities and was speculating about
mating types (as in Neurospora). I have
no way to say how many other strains
would have been tried, or in how many
combinations, had the June 1946 ex-
periments not been successful.

2. An equally important piece of luck
was that, the selected markers Thr
(threonine) and Leu (leucine) are found
almost at the origin of the E. coli chro-
mosome map". The cognoscenti will
recognize that in a cross BM T’L*F*
x B’M’T LF, the configuration used
in June 1946, these chromosome locali-
zations offer almost a maximum yield of
selectible recombinants. We were
therefore led stepwise into the complex-
ities of mapping.

 

 

It took about six weeks, from the first
senous efforts at crossing in mid-April
1946, to establish well-controlled, positive
results. These experiments could be done
overnight, so the month of June allowed
over a dozen repetitions, and the recruit-
ment of almost a dozen genetic markers in
different crosses. Besides the appearance
of A*B*C*D* prototrophs, it was impor-
tant to show that additional unselected
markers in the parent stocks would segre-
gate and recombine freely in the protot-
rophic progeny. This result left little doubt
as to the interpretation of the experiments.

An immediate opportunity for public
announcement presented itself at the in-
ternational Cold Spring Harbor Sympo-
sium in July. This was dedicated to the
genetics of microorganisms, signalling the
postwar resumption of major research ina
field that had been invigorated by the new
discoveries with Neurospora, phage, and
the role of DNA in the Pneumococcus
transformation. Tatum was already sche-
duled to talk about his work on Neuros-
pora. We were granted a last-minute im-
provisation in the schedule to permit a
brief discussion of our new results.

The discussion was lively. The most
principled criticism came from Andre
Lwoff who worried about cross-feeding of
nutrients between the two strains without
their having in fact exchanged genetic in-
formation. Having taken great pains to
control this possibility, I felt that the in-
direct genetic evidence was quite conclu-
sive. Fortunately, Max Zelle mediated the
debate. and generously offered to advise
and assist me in the direct isolation of sing-
le cells under the microscope. These sub-
sequent observations did quiet remaining
concerns of the group that Lwoff had
assembled at the Pasteur Institute, includ-
ing Jacques Monod, Francois Jacob and
Elie Wollman, who were to make the most
extraordinary contributions to the further
development of the field. The single cell

methods were also useful in later investi-
gations in several fields. A direct result of
the Cold Spring Harbor meeting was the
prompt ventilation of all the controversial
issues. With a few understandable, but
minor points of resistance, genetic recom-
bination in bacteria was soon incorpo-
rated into the mainstream of the burgeon-
ing research in molecular biology, and
after another decade or so into the standard
texts of bacteriology. It still took some
years to work out the intimate details of
crossing in E. coli; some, including the
crucial question of the physical mechan-
ism of DNA transfer between mating
cells, are still obscure.

The public image of the scientific frater-
nity today has seldom been so problematic
and the system cannot avoid putting a high
premium on competition and_ self-
assertion. We can recall with gratification
how the personalities of Ryan" and
Tatum" exemplified norms of nurture,
dignity, respect for others, and above alla
regard for the advance of knowledge.

 

Joshua Lederberg is at the Rockefeller Uni-
versity, New York, New York 10021. The
research summarized in this article was sup-
ported in 1946 by a fellowship of the Jane
Coffin Childs Fund for Medical Research.

. Lederberg, J. & Tatum, E.L. Nanere 188, 558 (1946).
. Beadle. G.W. & Tatum, E.L. Proc. natn. Acad. Sci.
U.S.A. 27, 499 — 506 (1941).
. Avery. O.T.. MacLeod. C.M. & McCarty, M. J. exp. Med,
79, 137 ~ 158 (1944),
. Ryan. F.J. & Lederberg. J. Proc. natn. Acad. Sci. U.S.A.
32, 163-173 (1946).
- Dubos. R. The Bacterial Cell (Harvard, Cambridge, 1945).
Winge & Lausten. O. C.R. Lab. Carlsberg, Ser. physiol.
22, 99-119, (1937).
7, Sherman, 1M. & Wing. H.U. J. Bact. 33, 315 — 321
(1937).
8. Gowen. J.W. & Lincoln. R.E. J. Bact. 44. 551 — 854
(1942).
9. Gray C.H. & Tatum, E.L. Proc. natn. Acad. Sci, U.S.A.
3, 404-410 (1944).
Lederberg. J. in University on the Heights, (ed. First. W.)
105 - 109. (Doubleday. Garden City, New York, 1969).
IL. Lederberg, J. A. Rev. Gener. 13, 1-5 (1979),
12. Lederberg J. Science 114. 68 - 69 (1951).
13. Tatum. E.L. & Bonner. D.M. Proc. natn. Acad. Sci.
U.S.A. 30. 30 — 37 (1944).
i4. Bachmann. BJ. Microb. Revs. 47, 180 ~ 230 (1983).

tw

ony

s

aw

10,