CHAPTER THIRTEEN

Support for Avery

Recent investigations of the role of nucleic acids in biology have verified the opinion that
they are comparable in importance to the proteins, especially with respect to the problem
of the structure of the gene. The work of Avery on the relation of nucleic acids to the
change in type of pneumococci provides a further illustration of the fundamental
significance of these substances.

(Beadle, Pauling and Sturtevant, 1946, 30)

Here surely is a change to which, if we were dealing with higher organisms, we should
accord the status of a genetic variation; and the substance inducing it—the gene in
solution, one is tempted to call it—appears to be a nucleic acid of the desoxyribose type.
Whatever it be, it is something which should be capable of complete description in terms
of structural chemistry.

It has been a matter for rejoicing to his many admirers, friends and followers in many
countries that Avery, a veteran now among investigators, should thus, on the eve of his
retirement, have attained this new peak of discovery—a fitting climax to a devoted career
of such wide influence on the progress of science.

(Sir Henry Dale, 1946, 128)

None of the experiments or facts, from the very beautiful biochemical research on
transforming principle to the possibly equally informative work of cytologists and gene-
ticists, leads directly and unambiguously to the conclusion that transforming material or
genes are nucleic acids, or largely composed of nucleic acids. I would appreciate learning °
whether or not the decision, so widespread today, that nucleic acid is a transforming ~
principle has in fact been decided by an unequivocal experiment, or whether it is no more
than a voted agreement at the present time.
(Cooper, 1955, 19-20)
When a discovery is made that calls in question an established paradigm like
the Protein Version of the Central Dogma one might expect the community
of scientists directly involved to reject its claims and to fight a rearguard
action against it on the grounds that the evidence was inadequate and could
not bear an interpretation in harmony with established thought. One would
then witness the familiar sequence of neglect, rediscovery and final recogni-
tion. Although it is possible to find striking examples of individuals who
resisted the implications of Avery’s work (Cooper, 1955; Sevag, 1952) this
was far from being the only reaction to the discovery of the chemical identity
of the transforming principle. This discovery was not neglected, not rejected,
and not rediscovered. The Kuhnian blindness which we observed in the work
on TMV in Chapter 10 was not a general feature of the discussions of
Avery’s work. In this and the subsequent chapter we shall explore the several

195
196 BACTERIAL TRANSFORMATION, ITS NATURE AND IMPLICATIONS

ways in which Avery’s evidence was made more convincing and ways in
which the implications of his discovery were followed up.

Strengthening the Evidence

In 1943 the Rockefeller group had used the reaction with appropriate anti-
serum as a sensitive test (1:50 000) for the presence of protein in the trans-
forming principle. This was far more sensitive than the histochemical and
analytic (N/P ratio) evidence to which Mirsky objected. But one could still
assert that during extraction and purification protein in the transforming
principle was altered in such a way as to prevent it from reacting with
anti-serum.

MacLeod had left the Rockefeller in 1941 to take the chair of medicine at
New York University’s College of Medicine. There, with Austrian, he con-
tinued his study of transformation in which he demonstrated the transfer not
of just one hereditary character but of three, each of which behaved in-
dependently of the others. Directed mutation, therefore, seemed not to be
the mechanism behind transformation and they concluded that there must
exist a “multiplicity” of DNA molecules, each “specificity” being determined
by a different one (Austrian and MacLeod, 1948, 458).

Avery, though he officially retired in 1943, continued to work at the
Rockefeller for several years, and collaborated with McCarty in devising an
improved procedure for extracting the transforming principle. This gave five
times the yield of the 1943 technique and could be used on Types II and VI
as well as on Type III (McCarty and Avery, 1946b). The pneumococcal cells
were allowed to autolyse, but in the presence of citrate. McCarty had dis-
covered the dependence of DNase upon magnesium icns (McCarty, 1946a).
Citrate removed these and thus prevented depolymerization of DNA.
McCarty himself had been trying since 1943 to strengthen the evidence for
the identity of the transforming principle by purifying DNase. This had been
available only as a crude extract of intestinal mucosa in 1943. By 1946 he
was able to demonstrate activity of DNase at very low concentrations, ten
thousand times weaker than the concentration at which proteolytic activity
could be demonstrated! The biochemist, Rollin Hotchkiss, who had come to
the Rockefeller in 1935 to work with Walther Goebel and Charles Hoagland,
took up the question of the chemical identity of the transforming principle
in 1947. A year later he was able to report to a conference in Paris, base
compositions for the transforming principle which differed from those for
thymus nucleic acid and for a tetranucleotide. He also reported inactivation
of the transforming principle by the crystalline DNase which Kunitz had
recently prepared (Hotchkiss, 1949; Kunitz, 1948). Next he showed that the
small quantity of amino acid that could be obtained from the transforming
principle was all accountable as glycine, which could be traced to the de-
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composition of adenine. This important find allowed him to conclude that
the maximum contamination of the transforming DNA with protein was
0.02 per cent.

Hotchkiss also sought for other markers which could, like the power to
produce a capsule, be transferred to recipient cells. If what was transferred
was genetic material then markers should behave independently. In the case
of penicillin resistance and capsule formation he was able to demonstrate
this (Hotchkiss, 1951). Later Julius Marmur worked under Hotchkiss on a
strain of pneumococcus which possessed an adaptive enzyme for utilization
of the sugar, mannitol. This gave the first case of linkage (with penicillin
resistance) (Hotchkiss and Marmur, 1954).

These findings allowed the Rockefeller scientists to express themselves less
cautiously. When McCarty addressed a symposium of the American Ghemi-
cal Society on “Biochemical and Biophysical Studies on Viruses’ he con-
cluded with the words:

It will be observed from the foregoing discussion that while the pneumococcal transform-
ing substance is virus-like in certain of its properties, there is some evidence inconsistent
with its classification with the viruses, despite the diversity of this group of agents. How-
ever, if one accepts the validity of the view that the biological specificity of the transform-
ing substance is the property of a desoxyribonucleic acid, the results of the present study
serve to focus attention on the nucleic acid component of virus nucleoproteins. In addition
to its probable role in the self-reproduction of the virus molecule, the nucleic acid moiety
may carry a specificity which is a determining factor in the ultimate structure of the virus.

(McCarty, 1946b)

A month later (May) McCarty gave the Eli Lilly Award lecture to the
Society of American Microbiologists. By this time he felt justified in con-
cluding ‘“‘that the accumulated evidence has established beyond reasonable
doubt that the active substance responsible for transformation is a specific
nucleic acid of the desoxyribose type.’’ And in the body of the lecture he
called for a “‘reconsideration of the possible role of nucleic acids in vital
phenomena ...” (1946c, 48), in the light of the “two cardinal effects’
associated with DNA, namely the induction of “predictable and heritable
modifications and the self-reproduction of the active agent in transformed
cells” (Ibid.). He went on to draw analogies between the biological properties
of the transforming substance and those of genes and viruses: transmissibility,
recovery in quantities far exceeding the original inoculum, and unitary be-
haviour. ‘Although the validity of these analogies may be questioned, they
serve to underline the possible implications of the phenomenon of trans-
formation in the field of genetics and in virus and cancer research”’ (Ibid.).
These were all carefully measured words, and Hotchkiss was equally
careful. He shied away from such crude statements as, the gene is DNA, or,
the transforming agent is DNA. There was always the possibility lurking in
198 BACTERIAL TRANSFORMATION, ITS NATURE AND IMPLICATIONS

the background that the agent was DNA-dependent but not itself composed
of DNA.

We in the Avery laboratory were concerned throughout with the possibility that traces
of very active protein might account for transformation. My own respect for proteins owed
very much to long hours of fascinating learning from Alfred Mirsky during the thirties.
Quite on my own, then, I felt the same doubts he did: that the nitrogen—phosphorus atom
ratios of nucleic acid and protein could vary only as much as the phosphorus—that
DNase, purified, in fact all but discovered by McCarty out of a proteinase-rich pancreas
fraction, might still have mild proteinase action. Mirsky spoke about these objections, but
not very much to Avery’s group or he would have learned as I did how eager they were to
see the search for traces of protein continued.

(Hotchkiss, 1966, 189)

And so the “ifs”? and “seems probables” remained: “If this be true, it is of
especial interest that these determinants are available for chemical, physical,
and biological study in the form of the isolated, purified transforming
desoxyribonucleates of bacteria” (Hotchkiss, 1952, 436). “These analyses
seem to support the earlier inferences that the determinants being transferred

in the DNA transformation are the bacterial genes themselves” (Hotchkiss,
1955b, 5). Much later Hotchkiss wrote:

... people engaged in the sertous analysis of genetic mechanism were not ready themselves to
be stampeded into public generalization, or beguiled entirely by visions not necessarily
prophetic. The historian can later see where more emphasis, exaggeration, exposure,
boldness or cajolery, would have been “justified”. But do not historians also sometimes
observe the danger of the “bad guesses”, the places where overemphasis or persuasiveness
have given a generation viewpoints that had tediously to be unlearned ?

(Hotchkiss, 1972)

Confirmation from Paris

Results identical with those obtained by Avery, MacLeod and McCarty
were achieved with the colon bacillus Escherichia coli by André Boivin and his
collaborators Roger Vendrely and Yvonne Lehoult. Their work is of special
interest because, in addition to numbering among the first cases of trans-
formation outside pneumococcus, its significance was hailed by Boivin in
terms which, by comparison with Avery, McCarty and Hotchkiss, were
recklessly speculative.

Boivin’s contact with nucleic acids went back to the late 1920s when he
studied among other things the metabolism of purines and pyrimidines. In
the early 30s, as professor of medical chemistry in Bucharest, he collaborated
with the Mesrobeanus and the Magherus. At first he studied the nucleic acid
constituents of bacteria, then turned to immunochemistry and isolated the
important O antigen. 1936 saw him installed in the annex of the Pasteur
Institute in Garches where work continued throughout the war. There with
A. Delaunay and Miss Corre, Boivin did for the antigens of the colon bacillus
what Avery and Heidelberger had done for the pneumococcus. They found:
SUPPORT FOR AVERY 199

evidence of the extraordinary multiplicity of antigenic types among the colon bacilli, each
type possessing its own polysaccharide, characterized by a special chemical constitution
and by a particular serological specificity. Each type remains stable through successive
cultures; like the pneumococcus types, it can undergo antigenic degradation leading
from form S (smooth) to form R (rough) by losing its polysaccharide, and, like the pneu-
mococcus types again, it has the value of a true elementary species within the immense
species of Escherichia coli.

(Boivin, 1947, 7)

In 1942, after ten months spent in captivity in Germany, Roger Vendrely
returned to France and joined Boivin’s group. He found Boivin anxious to
establish the chemical basis of transformation which he believed must in-
volve nucleic acids. Already in 1941 Boivin had tried a variety of in vitro
arrangements to “‘discover whether, like the pneumococci, the colon bacilli
might not give way, by controlled mutation, to the process of type trans-
formation” (Jbid.). He had read the work of Griffith, Dawson, Sia and
Alloway and in 1941 he seemed to be thinking of type transformation as a
phasic development (Boivin, 1941, 799). Vendrely, as the biochemist, was
put on to the extraction of the transforming substance. The donor cells were
killed with chloroform and allowed to autolyse for two days at 37°C. Nucleo-
protein was then precipitated from the autolysate by acetic acid. The Paris
workers were then told about Avery’s 1944 paper revealing the role of DNA.
“Inspired by this work,” said Boivin, ‘‘we too have obtained evidence of the
intervention of desoxyribonucleic acid in directed mutations in bacteria. We
take pleasure in acknowledging the priority of the American authors in this
field” (1947, 9). All that Boivin and his colleagues had to do, it appeared,
was to treat their nucleoprotein extract with pepsin at pH 2, or better, to use
the Sevag-chloroform technique, to strip off the protein. At a meeting of the
Académie des Sciences, in November 1945, Boivin announced his success in
achieving transformation in £. coli. From the R form of Type S, they pro-
duced the S form of Type S, when cultured with a nucleic acid extract of the
latter. Likewise they achieved transformation of S, to S,. In December 1945
Experientia published these findings. The title of the paper contains the
phrase ‘Significance for the biochemistry of heredity”. The conclusion, in
which the donor type is referred to as C, and the recipient type as C,,
translates as follows:

It seems well established now that the bacterial cell possesses a small nucleus of thymo-
nucleic acid immersed in a cytoplasm of ribonucleic acid. Surely the principle derived
from C,, which demonstrated its ability to impose on C, a new molecular constitution for
its polysaccharide and a novel enzymatic equipment, results from a simple “solubiliza-
tion” of the rudimentary chromosomal apparatus of C,? The hypothesis seems likely. If
it corresponds to reality, it opens altogether novel horizons, and how promising these are
for the biochemistry of heredity. In particular, it is on the side of the nucleic acid and not
at all on that of the protein of the nucleoprotein macromolecule constituting a gene that
one must find the basis for the inductive properties belonging to the gene. That would
lead one to envisage the possibility of a “primary” or more likely “secondary” structure
200 BACTERIAL TRANSFORMATION, ITS NATURE AND IMPLICATIONS

able to differentiate between the various desoxyribonucleic acids within their natural
state of polyrnerization.
(Boivin, Delaunay, Vendrely and Lehoult, 1945, 335)

When Boivin attended the Cold Spring Harbor Symposium in June 1947, he
gave a remarkable paper in which he related the work on bacterial trans-
formation to Beadle and Tatum’s work on biochemical genetics, described
Tulasne’s confirmation of Robinow’s work on the bacterial nucleus (1947),
and the chemical mechanism involved (Vendrely and Lipardy, 1946), and
gave Tulasne’s and Vendrely’s cytochemical evidence, using RNase and
DNase, for the localization of RNA in the bacterial cytoplasm and DNA in
the nucleus of E. coli (1947).

When we look back over the mass of literature in the 1940s, it seems
scarcely possible that André Boivin could have so accurately predicted the
structure which the nascent subject of molecular genetics was to take. Con-
sider the following statements:

We may, at the most, catch a glimpse of a series of catalytic actions which set out from
primary directing centres (the desoxyribonucleic genes) proceed through secondary
directing centres (the ribonucleic microsomes—plasma~genes) and thence through tertiary
directing centres (the enzymes), to determine finally the nature of the metabolic chains
involved, and to condition by this very means, all the characters of the cell in con-
sideration.

Thus, this amazing fact of the organization of an infinite variety of cellular types and
living species is reduced, in the last analysis, to innumerable modifications within the
molecular structure of one single chemical substance, nucleic acid, substratum of heredity
as well as of acquired characters. This is the “working hypothesis” quite logically suggested
by our actual knowledge of the remarkable phenomenon of directed mutation in bacteria.

Thus there exist in the bacterial nucleus, as in the cell nucleus of higher organisms,
desoxyribonucleoprotein genes which serve as a substratum for the characters of the
species. It follows that whatever happens in the phenomenon of directed mutation can
hardly be interpreted otherwise than as a result of solution of the bacterial chromosome
apparatus without total destruction of its functional value.

In bacteria—and, in all likelihood, in higher organisms as well—each gene has as its
specific constituent, not a protein but a particular desoxyribonucleic acid which, at least
under certain conditions (directed mutations of bacteria), is capable of functioning alone
as the carrier of hereditary character; therefore, in the last analysis, each gene can be
traced back to a macromolecule of a special desoxyribonucleic acid. . . . This is a point of
view which, in respect to the actual state of biochemistry appears to be frankly revo-
lutionary.

(Boivin, 1947, 12-13)

In the ensuing discussion, Brachet expressed surprise that Boivin’s autolysates
were active in transformation. Surely DNase was present and therefore the
activity must have been due to some substance other than DNA. All Boivin
could do was to assure Brachet that whereas colon bacilli contained a very
active RNase there was no evidence of a similarly active DNase, for Vendrely
had found the proportion of RNA to DNA to fall very markedly during
autolysis (Vendrely, 1947). Probably informally, Boivin was asked why he
had not used sodium desoxycholate, like Avery, or molar NaCl like Mirsky.
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So he added a footnote to his paper saying that colon bacilli resisted both
reagents so strongly that only very poor yields resulted from these extractive

procedures. Hotchkiss had this to say about Boivin and his evidence from
E. colt:

Boivin was respected for his identification of bacterial antigens far more complex than
those Avery had identified a couple of decades before. Boivin was I think also widely
considered an honest scientist, optimistic and given to simplistic logic. It is fitting that he
should appear in your lights as an early molecular biologist! But he lacked the quantitative
sense and self-critical attitude the best molecular biologists were to show. I doubt if we
will ever know whether he and his coworkers ever really achieved a DNA-caused trans-
formation since (I am told) his strains spontancously go through the same change. It
would have been outside his realm of inquiry to consider the role of selection in fostering the
conversions—so with Avery’s prior example just before him, I think he was overper-
suaded by his own scant observations.

Boivin called it “fifty per cent transformation” when (literally, when pursued) he
meant that transformation occurred in one half of the flasks treated with DNA under best
conditions. We asked, by 1951 and before, what per cent of treated cells are changed ? His
personal magnetism and enthusiasm were great, but these things are dangerous when
matters are in a qualitative stage.

(Hotchkiss, 1972)

Accordingly, we find another footnote in Boivin’s Cold Spring Harbor paper
which reads:

Despite apparently identical experimental conditions, the transformation of R, into 8,
through the action of the desoxyribonucleic acid of 5; is not regularly produced. In a
dozen tubes, containing the same volume of medium and the same dosage of desoxy-
ribonucleic acid, inoculated with the same number of bacteria, one frequently finds tubes
giving rise to transformation side by side with others where no transformation occurs, The
number of bacteria at the beginning and end of the culture and the concentration of the
desoxyribonucleic principle do not allow an explanation on statistical grounds of the
proportion of positive results obtained in the different experiments. All takes place as
though a factor, still unknown, were able to facilitate or to prevent transformation.

(Boivin, 1947, 8)

To make matters worse, other workers had difficulty in repeating Boivin’s
work, perhaps due to the difference in the competence of different strains
(Ravin, 1969, 65). Had Boivin’s strains 17 and 24 been available to other
workers, confirmation might have resulted, but these strains “were lost when
the tubes containing the parent strains were broken in a careless accident”
(Vendrely, 1972). Boivin was at the time in hospital following his first serious
attack of cancer, and Lederberg and Tatum, who received strains from
Boivin in 1947, “never confirmed his finding. In correspondence with Tatum,
Boivin admitted that these might have lost their competence in his own
hands, and he stated he would try to recover others on which he could verify
the transformation himself. His illness supervened” (Lederberg, 1972a).* At
Columbia, where “Avery’s work was very well known” (Lederberg, 1973).
Ryan and Lederberg had in June 1945 tried “‘to emulate Avery by trans-

* Transformation has since been achieved in EF, coli (see: Oishi and Cosloy, 1972; Wacker-
nagel, 1973).
202 BACTERIAL TRANSFORMATION, ITS NATURE AND IMPLICATIONS

forming Neurospora mutants with DNA extracts. This was unsuccessful, and
was therefore regarded as unworthy of report” (Lederberg, 1972b). It had
been carried out precisely to clarify “whether ‘transformation’ was a typical
gene transfer’? (Lederberg, !972a). Meanwhile, Boivin’s work found its way
into the literature as a confirmation of Avery’s discovery, and Arthur
Pollister, who had collaborated with Mirsky, was greatly impressed by the
French work, especially that of Boivin’s collaborator, Vendrely (see
Chapter 14).

The Debate over Bacterial Transformation

It has been urged that the famous Avery, MacLeod, McCarty paper was not
widely read because it was published in a journal normally found only in
medical libraries (Wyatt, 1972). It is true that Avery made no attempt to get
a short report of the work published in a widely circulated journal like
Science or Nature. On the other hand news does not have to be published in
order to travel! Quite apart from visits made by such scientists as Gulland
(1946) and Macfarlane Burnet (1943), transformation was discussed at three
unpublished symposia: The Mutation Conference, New York, January 1946.
Biophysical and Biochemical Studies on Viruses, Atlantic City, April 1946.
Conference with unknown title, Hershey (Penn.), October 1946.

The subject of the Cold Spring Harbor symposium of July 1946: “Heredity
and Variation in Micro-organisms”, had been chosen in the year Avery’s
paper appeared and the meeting would have been held in 1945 had not
travel restrictions made it impossible. When the participants met in 1946
Avery, McCarty and Harriet Taylor were present and reported on the pro-
gress they had made in identifying the environmental factors essential to
transformation. At yet another meeting in 1946—Society of American
Microbiologists at Detroit—McCarty read almost the same fine paper that
he had given in Atlantic City a month before. On this occasion he received
the Eli Lilly Award in Bacteriology and Immunology. Nor did this flush of
interest subside in 1947. The Cold Spring Harbor Symposium of June 1947
was devoted to nucleic acids and nucleoproteins. Boivin, Chargaff, Hotchkiss,
Mirsky, Pollister and Harriet Taylor were present.

These meetings gave adequate opportunities for geneticists, virologists and
biochemists to discuss transformation. In Europe the scene was less conducive
to the publicizing of Avery’s work. When the Society for Experimental
Biology held a meeting on nucleic acids in Cambridge (1946), no one was
invited to talk on transformation, and in his paper on bacterial nucleic acids
and nucleoproteins M. Stacey succeeded in submerging his account of Avery’s
work in a list of what everyone else had done. Enthusiastic though he was,

Stacey’s own interpretation was clearly in the nucleoprotein camp (Stacey,
1947, 96).
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There was one bright exception—the exciting colloquium held in Paris in
1948 by the Centre Nationale de la Recherche Scientifique (C.N.R.S.) with
support from the Rockefeller Foundation. But even this meeting failed to
have the wide impact which it most certainly deserved, perhaps because the
proceedings were published in French in a limited number of copies of the
C.N.R.S. colloquia.

This gathering had been planned by André Lwoff and Boris Ephrussi.
They entitled it: “Biological Units Endowed with Genetic Continuity”. “A
year later”, wrote Hotchkiss, “before I had realized that I almost never
would find anyone who had read the symposium article, I was distressed to
find that a tired abstractor for Chemical Abstracts had covered my own and
also Ephrussi’s conference papers in two short words, ‘a review’ ” (Hotchkiss,
1966, 190). But what a grand colloquium it had been! Hotchkiss had re-
ported his work with crystalline DNase and his quantitative chromatography
of the transforming DNA. Boivin later referred to this as “the first direct
argument of a chemical nature in support of the existence in nature of a
multiplicity of nucleic acids” (Boivin, 1948, 1258). Harriet Taylor had
described “intermediate” and “extreme” forms of pneumococci and had
provided evidence for the presence of at least two functionally distinct
DNAs in one and the same bacterial extract. Boivin, who by this time had
moved with Vendrely to Strasbourg and had been joined by the cyto-
chemist R. Tulasne, described their work on the localization of DNA and
RNA in the bacterial cell, and their measurement of the DNA content of
diploid and haploid cells.

These important contributions were summed up by André Lwoff in the
following words:

The transforming principle of pneumococcus is deprived of proteins and appears to consist
exclusively of desoxyribonucleic acid. This is probably the case also for Escherichia coli. The
importance of DNA is indicated by the fact that diploid nuclei have twice the DNA of
haploid nuclei. The study of the transforming principle of pneumococcus has led to the
conclusion that the purine and pyrimidine bases are not present in equimolar proportions.
This gives an inkling of a possible explanation for the specincity of nucleic acids. Once the
transforming principle of pneumococcus is introduced into a bacterium it confers on it
permanently a given specificity. But this principle is susceptible of modification and even
at the present time we know of two varieties of specific nucleic acid of type III pneu-
mococcus. They have been compared to allelomorphic genes. In fact, they exclude each
other reciprocally as if in competition for the same receptor.

This fact thus throws light on the idea that the specific nucleic acids normally could and
should be combined with another constituent, probably a protein.

(Lwoff, 1948, 202)

The Influence of Studies in Transformation

There is no doubt whatever that the Avery paper of 1944 had a profound
effect on biochemists. “These wonderful discoveries”, said Mirsky, “have
caused chemists to consider critically the evidence for uniformity among
204 BACTERIAL TRANSFORMATION, ITS NATURE AND IMPLICATIONS

nucleic acids, and the generally accepted conclusion is that the available
chemical evidence does not permit us to suppose that nucleic acids do not
vary” (Mirsky, 1947, 15). I fear that his criticism of the evidence for DNA
as the transforming substance did incline influential geneticists like Muller to
retain the nucleoprotein conception of the gene rather than to go over to the
DNA conception. But within the ranks of biochemistry Mirsky’s criticism
may well have served to stimulate further work. We have already referred to
the genetic studies by Harriet Taylor and Rollin Hotchkiss. Two further
lines of research naturally suggested themselves: studies of DNA content of
cells and analysis of the base constitution of DNAs from different species.
In short, Avery’s work on bacterial transformation was not neglected. It did
lead directly to further chemical and genetic studies, the outcome of which
was crucial for Watson and Crick. This is not to say that those micro-
biologists and histochemists who supported the new view rapidly dominated
the entire scene; conservatism lingered on as seen in Kenneth Cooper’s out-
burst of 1955. Nor was the new view influential in England, where the old
school of geneticists and plant virologists complacently carried on with the
nucleoprotein gene. Perhaps it was Gulland’s death in 1947 which left the
British scientists to all intents and purposes blissfully unaware of the new
developments in nucleic acid chemistry across the Atlantic and in Paris.

The Significance of Bacterial Transformation
With the passage of time the work of Avery, MacLeod and McCarty looks, if
anything, more significant than in 1958; perhaps it was the most important
event in undermining the pre-eminence of the protein, the culmination of
a series of achievements which established the chemical basis to enzyme
action, antigenicity and finally transformation. It marked the beginning of
a new era in which a search for the chemical basis of nucleic acid “specifici-
ties” was undertaken, Muller admitted that if DNA was the transforming sub-
stance as Avery, MacLeod and McCarty concluded “their finding is revolu-
tionary” (Muller, 1947a, 22). Boivin likewise felt that in the state of bio-
chemistry at that time the postulation of many different DNAs “appears to
be frankly revolutionary” (Boivin, 1947, 12). One does not find scientists
describing a discovery as “revolutionary” every day of the week. This discov-
ery was special. It demanded a re-examination of the Protein Version of the
Central Dogma and of the tetranucleotide hypothesis. It suggested there
must be hidden in the molecules of nucleic acids chemical specificities as
rich as those of proteins. The debate over bacterial transformation there-
fore marks as Kuhnian a revolution as did the debate over macromolecules.
When we enquire into the reception Avery was given in the Rockefeller
itself we find that on the surface at least there was enthusiasm. P. A. Levene,
who died in 1940, was of course aware of the work on transformation in its
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earlier stages. “He was sceptical about the possible role of DNA in the
transformation reactions and when Dr. Avery and I [MacLeod] described
the system to him . . .—what the results were—and the properties we then
knew about the active material, he was highly sceptical that it could be
DNA” (MacLeod, 1968).

By 1943, when Avery read the great paper at the formal after-tea meeting
in the Rockefeller, ‘there was next to no discussion ... because it was a
standing ovation afterwards. There was obvious recognition and a terrifically
warm reception. Nobody mentioned any objection” (McCarty, 1968), The
story that Avery was vehemently attacked in a discussion following the lecture
and as a result dared not show his face in the Rockefeller for several weeks
thereafter is clearly untrue.

There was, of course, opposition from Mirsky which was expressed publicly
at meetings outside the Rockefeller. We have already examined the scientific
grounds for this opposition. But such opposition can rarely be considered in
isolation from other less objective grounds. We have noted that all three men
—Avery, Macleod and McCarty—were trained in medicine, not in bio-
chemistry. True, they differed from men like Griffith, whose interests in
epidemiology did not spill over into biochemistry. But medical research was
messy, the systems used in experimentation were complex to the point where
the results obtained from them were unreliable, and the transformation
system was far from being an exception. No doubt, therefore, there was that
feeling of professionalism on the part of biochemists in the Institute, like
Mirsky, which predisposed them to question the contribution of “doctors”, .
like Avery, MacLeod and McCarty, in the Institute’s hospital. The same
attitude exists to this day on the part of many a ‘‘pure” science department
towards an ‘‘applied’’ science department.

Not only did the transformation story involve this conflict between bio-
chemist and medic but in Sir Macfarlane Burnet’s view it signalled a change
from applied to pure research.

Looking back I fancy that it was only in the 1930s that medical scientists began to be
really interested in “pure” research ...

What swung microbiology perhaps for ever away from a primary desire to prevent and
cure infectious disease to its current preoccupation with molecular biology, was probably
Avery’s discovery ...

(Burnet, 1968, 59)

Burnet visited Avery in 1943 and wrote home to his wife telling her tnat
Avery:

“has just made an extremely exciting discovery which, put rather crudely, is nothing less
than the isolation of a pure gene in the form of desoxyribonucleic acid.” I think that must
be almost the last time I ever wrote DNA in full. Nothing since has diminished the
significance or importance of Avery’s work, Neither he nor I knew it at the time but in
206 BACTERIAL TRANSFORMATION, ITS NATURE AND IMPLICATIONS

retrospect the discovery that DNA could transfer genetic information from one pneu-
mococcus to another almost spelt the end of one field of scholarly investigation, medical
bacteriology, and heralded the opening of the field of molecular biology which has
dominated scholarly thought in biology ever since.

(Ibid., 81)
Parallel with this change, the introduction of new drugs like penicillin and
the sulphonamides made further attempts to develop immunological aids of
the sort the Rockefeller bacteriologists had been working on superfluous.
Men like Hotchkiss who had started out contributing to a problem in im-
munochemistry found themselves drawn into the genetics of bacterial
transformation.

Thus it came about that work begun by Griffith, a civil servant in the
Ministry of Health, was taken up by a medical institute, and was there de-
veloped to answer the question: “On what compound does the specificity of
the gene depend?” The Rockefeller’s administrators, who had shown so
little interest in genetics in the early days, now became very definitely
committed to it.