Avery, MacLeod, and McCarty:

Revolutionaries or Puzzle-Solvers?

Gordon C. F. Bearn
Williams College

December 1985

 
(A) Introduction: Griffith's Surprise ... .

(B) . The 19 44 Paper . @ e ° e e e e e e s e °. e

(Cc) The Lure of the Lore ......s +s ec «© « e

(D) Four Ways the Avery Result was Pursued ..

(E) Kuhnian Analysis: Revolutionaries or
Puzzle-Solvers? ° . ry e e e e e e e e e e
(F) The Invention of Theoretical Genetics: 1953

(G) Conclusion . . . «6 « «© «© «© © @ © ww @
The great names in the biology of the last hundred years are
Darwin, Mendel, and Avery.

--Erwin Chargaff, Heraclitean Fire, (1978), p. 105.

Part of the lore of molecular biology is that the discovery
which is its foundation went unrecognized for most of a decade.
The discovery was that genes are made of DNA. It was announced
in 1944, but according to the story, the profound biological
significance of that discovery was not fully appreciated until
the helical structure of DNA was discovered in 1953.

In the early 1970's when this story appeared in print, it
was denounced by some scientists and historians as a fairy tale.l
They pointed out that, in contrast to the case of Mendel, the
discovery that the genetic specificity of living organisms was
carried by molecules of DNA immediately commanded the attention
it deserved.

Although it is certainly true that this discovery was not
overlooked by the scientific community, it is also true that its
full elaboration did not evolve until many years had passed. In
this paper, I will describe the recognition that the 1944 results
received; this will lend support to those who denounce the lore
as a fairy tale. Nevertheless, I will not veil the limitations
of that recognition. In the dispute about the origins of
molecular biology, my intention is not simply to defend one side
against the other; rather my intention is to explain why each of

these opposing interpretations can claim some part of the truth.
(A) Introduction: Griffith's Surprise.

In February 1944 0.T. Avery, C.M. MacLeod and M. McCarty
published a paper entitled "Studies on the Chemical Nature of the
Substance Inducing Transformation of Pneumococcal Types.
Induction of Transformation by a Desoxyribonucleic Acid Fraction
Isolated from Pneumococcus Type III."2 the phenomenon they were
studying -- the transformation of pneumococcal types -- had been
reported in January 1928 by an English pathologist, Fred
Griffith.3

Pneumococci, the organisms which cause pneumonia, exist ina
number of true-breeding types which can be serologically
distinguished. If pneumococci of one type are grown in a medium
containing type-specific antisera, their descendents will have
lost their virulence, that is, their virulence will have become
attenuated. There is a visual test for whether or not a strain
has become attenuated: when grown on solid media, attenuated
strains look rough (R); virulent strains look smooth (S). Thus
any given type of pneumococci can come in an attenuated R form,
and a virulent S form.

Griffith found that if very large amounts (50 ml.) of
non-virulent (R) pneumococci were injected subcutaneously in
mice, the mice died and S pneumococci (of the same type as that
from which the injection was derived) could be recovered from the
dead mouse. He supposed that the pneumococci which were injected
had not completely lost the virulent S-antigen during
attenuation, and he reasoned that when the organisms injected
lyse they release this S-antigen which furnishes them with "a

pabulum which the viable R pneumococci can utilize to build their
rudimentary S structure."4 griffith further supposed that the
mice survived injection of smaller quantities of the non-virulent
R pneumococci; because only a small percentage of the R form of
any type will retain the virulent S-antigen. He reasoned that if
this explanation were correct, then he should be able to turn a
small, non-lethal injection of R cells into a lethal injection by
providing a non-lethal source of the S-antigen in the form of
heat-killed S pneumococci. Griffith:

It appeared possible that suitable conditions could be

arranged if the mass culture was derived from killed

virulent [S] pneumococci, while the living R culture was
reduced to an amount which, unaided, was invariably
infective. There would thus be provided a nidus and a high
concentration of S antigen to serve as a stimulus or a food,

as the case may be. 5
This hypothesis proved correct. The injection of dead (S)
pneumococci of a given type in conjunction with living,
attenuated (R) pneumococci of the same type proved lethal to the
mice. And living, virulent (S) pneumococci -- again of that type
-- could be recovered from the mouse.

Griffith's surprise was in his controls. To control his
experiment, he injected living non-virulent R cells of one
true-breeding pneumococcal type together with dead virulent S
cells of a different type. He expected that the R organisms of
one type would not be able to use the S antigen of a different
type as a "stimulus or food as the case may be." He expected the
mice to survive these particular injections. To his surprise the
mice died, and he recovered from the dead mice living pneumococci
not of the injected R type which had been alive, but of the

injected S type which had not been alive.

As we look back on Griffith's surprise, its significance for
molecular biology consists in its exhibiting the transformation
of one genetically pure population into a different genetically
pure population. But this could not have been what surprised
Griffith.
In 1928, bacteria were not known to possess nucleoid bodies,
and they were not thought about in genetical terms at all. R.
Dubos, sometime collaborator of O.T. Avery, has written of the
early response to the fluidity with which colonies of bacteria
changed their characteristics: "In most cases, the diversity and
complexity of the changes observed, the rapidity with which they
occurred, and the ease of their reversibility made it difficult
to believe that the chemical concepts of genetics sufficed to
explain the variability of bacteria."® Griffith's paper itself
exhibits this non-genetical approach to bacteria. To
contemporary eyes the phenomenon of S to R attenuation is a clear
illustration of natural selection operating on bacteria, but
Griffith speaks about attenuation in Lamarckian and teleological
terms which, today, have an odd sound:
By assuming the R form the pneumococcus has admitted defeat,
but has made such efforts as are possible to retain the
potentiality to develop afresh into a virulent organism.
The immune substances do not apparently continue to act on
the pneumococcus after it has reached the R stage, and it is
thus able to preserve remnants of its important S-antigens
and with them the capacity to revert to the virulent form.
While the R form may be the final stage in the struggle of
the bacterium to preserve its individuality, I look upon the
occurance of the various serological races as evidence of
similar efforts to contend against adverse circumstances. 7
In 1928, scientists were not thinking about bacteria
genetically but they were thinking about them in terms of types.

Griffith's result was surprising because it suggested that the

widespread belief that there were immunologically specific,
true-breeding types of pneumococci was mistaken. Coincidently,
Avery had played a major role in establishing this belief; thus
R.D. Hotchkiss comments:
Small wonder that [to Avery] the work of Griffith in
{1928]...seemed doubtful and contrary to all that had been
carefully established; for this young English microbiologist

described transformations that seemed to he conversions of
one true-breeding type into another.

(B) The 1944 Paper.

Soon after Griffith published his surprising result, Avery's
laboratory at the Rockefeller Institute in New York City
attempted first to reproduce and then to extend Griffith's work.
The history of these early investigations has been told by R.
Dubos and, in even more detail, by M. McCarty in his recently
published book, The Transforming Principle.? I will pick up the
story after Alloway, in 1932, had isolated a cell-free extract
which was capable of inducing transformation of pneumococcal
types. 10

At this point studies on the chemical nature of the

substance inducing transformation could begin. Such studies were
undertaken at the Rockefeller by Avery, first in collaboration
with C. M. MacLeod and then, after 1941 (when MacLeod moved from
the Rockefeller to NYU and McCarty moved from NYU to the
Rockefeller), in collaboration with M. McCarty. With one curious
three year hiatus from 1938 to 1940, these joint studies were
pursed continuously from 1934 to 1943, but Avery's lab did not
publish anything on transformation during this periog.il The

chemical identity of the transforming principle proved especially
difficult to discern. After all the hard work of its chemical
analysis had been accomplished, Avery wrote to his brother Roy in

May of 1943:

The crude extract (Type III) is full of capsular
polysaccharide, C (somatic) carbohydrate, nucleoproteins,
free nucleic acids of both the yeast [RNA] and thymus [DNA]
type, lipids and other cell constituents. Try to find in

that complex mixture the active principle!! 12
Of course this retrospective account makes the process of
chemical analysis sound too easy; because Avery and his
co-workers began by knowing nothing of what was in Alloway's
cell-free extract. Alloway described it as a “thick syrupy
precipitate."13

Avery, MacLeod, and McCarty faced three problems: (1) to
purify a substance X from this syrup which was still capable of
inducing transformation, (2) to identify the chemical nature of
this X, and (3) to give a biological explanation of the
transformation phenomenon.

The solution to (1) was rather difficult to find. The
method of purifying X and demonstrating that it retained the
ability to transform pneumococcal types proved to be very
delicate. According to McCarty the laboratory notes from as late
as 1940 and 1941 are ",..sprinkled with the description of
“experiments that failed because 'the system was off.' [And he
comments:] Sometimes this was due to a slip-up in the handling of
one of the known components, but more often the responsible
variable was never identified."14 Because the full story of the
solution to (1) is eloquently recounted in McCarty's book, I will

not discuss it further. Exciting as it was it was only the

discovery of a (usually) reliable procedure for isolating a
biologically active precipitate from the thick syrup obtained by
Alloway.

In the 1944 paper, Avery, MacLeod, and McCarty argued that
the answer to (2) was that X was DNA. These arguments, presented
in a section called “Analysis of Purified transforming Material,"
were the heart of their paper. They presented seven
considerations which together suggested that X was very pure DNA.
I summarize those four considerations which were most relevant to
the controversy which followed publication.15

a. The transforming substance X exhibited "little or no

serological reactivity" with antisera to the
pneumococci type from which it was derived. This
suggested that X was not the sugar capsule of the S

pneumococcus or any part of its antigen. 16

b. They found that the Millon test, a qualitative test for
protein, was negative on X. The Dische reaction for
DNA was strongly positive. The Bial test for RNA was

“weakly positive," but so was that for other

preparations known to be DNA. These results suggested

that X was more likely to be a nucleic acid than a

protein.17

Cc. Various enzymes were tested for their ability to
inhibit transformation, i.e. their ability to digest xX.
In 1944, no pure DNase was available; but all those
enzymes capable of inhibiting transformation (and only

those) were also able to digest authentic samples of
DNA. These results suggested that of the nucleic

acids, X was more likely to be DNA than RNA.18

da. The transforming substance was very active in their
transformation system: 0.003 micrograms were capable of
inducing transformation at a concentration of one part
in 600,000,000. Thus it seemed unlikely that a trace

impurity was the source of X's biological activity. xX

seemed to be pure pna.19

This was the core of Avery, MacLeod and McCarty's evidence that X
= DNA. This was there answer to problem (2), the chemical nature
of the transforming material.

The authors of the 1944 paper did not explicitly endorse any
solution to problem (3); they did not explicitly offer any
biological explanation of the phenomenon of transformation. In
the discussion section of the 1944 paper, the authors merely
listed four possible hypotheses about "The Nature of the Changes
Induced" by the DNA fraction without deciding between them, and
apparently without even suggesting which hypothesis the authors
favored. The four hypotheses wereliue to Griffith, Dobzhansky,
Stanley, and Murphy. 29, The authors did not decide which of
these four hypotheses was the most plausible; the conclusion of
the 1944 paper said simply and safely:

The evidence presented supports the belief that a nucleic

acid of the desoxyribose type is the fundamental unit_of the
transforming principle of the Pneumococcus Type III.
(C) The Lure of the Lore

I have said that it is part of the lore of molecular biology
that the genetic significance of the 1944 results was not fully
appreciated until the early 1950's. As the story goes, this
delay was primarily the result of two hesitancies in the 1944
Paper: (a) the hesitancy with which Avery, Macleod and McCarty
reported their discovery that the transforming principle was DNA
and (b) the hesitancy with which they associated DNA with the
genetic material of the Pneumococcus. These supposed hesitancies
may be thought of as the lure of the lore.

It is sometimes thought that the great influence of Avery's
discovery is inconsistent with the claim that the 1944 paper was,
in these ways, hesitant. That is not true; the question of
hesitancy and the question of influence are two separate
questions: one concerns a printed text, the other concerns the
response to that text.

In this section I try to demonstrate that the 1944 text was
hesitant in both the ways I have mentioned, but I will also argue
that neither of these hesitancies is sufficient to account for
the delay between the discovery of the chemical nature of the

gene and the explosion of molecular genetics in the 1950's. The

lure is real, but it should be resisted.

(a) X = DNA.

In the discussion section of the 1944 paper we can find the
sentence: "If it is ultimately proved beyond a reasonable doubt
that the transforming activity of the material described is

actually an inherent property of the nucleic acid, one must still
10

account on a chemical basis for the biological specificity of its
action. "22 This sentence suggests that, in 1944, the authors did
not think they had proved, beyond a reasonable doubt, that X =
DNA. Wendell Stanley, whose hypothesis that transformation was a
viral phenomenon was mentioned in the 1944 paper, remarked in
1970 that the way the paper was written “...did not tend to imbue
the reader with confidence in their results."23

It is probably fair to attribute this hesitancy to Avery;
because during his summer vacation in Maine, he roughed out the
introduction and discussion sections of the paper. 24 That this
should have had a restraining effect on the interpretation
offered in that paper might be guessed from a passage in a letter
Avery sent to his brother Roy in May 1943: "It's hazardous to go
off half cocked -- and embarassing to have to retract later."25
MacLeod recalls that Avery was "...almost neurotic about
overstating the case" for their analysis of the chemical nature
of the transforming material. 26

Dubos has offered an intriguing psychological explanation
for what he also refers to as Avery's "...restraint and
self-criticism bordering on the neurotic...."2/ In 1916 and
again in 1917 Avery had published some premature specualtions
which were amply refuted soon after publication. It is true that
these early mistakes were embarrassing to Avery, and it is true
that at the end of his scientific carreer Avery was more hesitant
about taking risks in print than MacLeod thought reasonable. But
it is difficult to know how to evaluate Dubos' suggestion that
these two features of Avery's career were related as cause to

effect. Dubos may have discovered a psychological explanation
11

for why the 1944 paper only tentatively asserted that X = DNA;
however, even if that explanation is rejected, we can still ask:
does the tentativeness with which the 1944 paper claimed that X
was DNA explain why the genetic significance of the 1944 results
went unrecognized for ten years? The answer, I think, is no.
The simplest defense of this claim is that that early
hesitancy was short lived. In 1946, McCarty and Avery extended
their evidence, in two papers presented as Parts II and III of
their 1944 "Studies on the Chemical Nature of the Substance
Inducing Transformation of Pneumococcal Types. "28 A pure
preparation of DNase, which only depolymerized DNA, would have
been a valuable contribution to the 1944 analysis, but at that
time the only enzymatic systems containing DNase were impure;
they contained other enzymes not specific to DNA or even to
nucleic acids. It is against this background that McCarty and
Avery reported in 1946:
Since no purified preparation of desoxyribonuclease was
available, purification of the enzyme was undertaken in this
laboratory in order that enzymatic evidence concerning the
nature of the transforming substance could be made more
direct and conclusive. 29
The DNase they prepared did not give entirely unambiguous support
to the claim that X = DNA; because it did exhibit some
proteolytic activity. Nevertheless, as McCarty and Avery point
out:
The results of the present investigation show that in order
to detect proteolytic activity, it is necessary to use an
amount of purified desoxyribonuclease 100,000 times greater
than that required to cause rapid and complete destruction
of activity of the transforming substance. 30

Thus they concluded that there was "little doubt" that X = DNA. 32

If the scientific community harbored any doubts about the
12

conclusiveness of the 1944 evidence, the improved evidence of
1946 might have been expected to answer them. But it did not.
Part of the reason may have been that, as McCarty cautiously puts
it, "there is some evidence to suggest...that papers II and III
(which finally appeared in February 1946, just two years after
Paper I) were not very widely read. "32 However even those who
read them were not entirely convinced. Among these was A. E.
Mirsky who, like Avery, worked at the Rockefeller Institute.
Mirsky refused to be convinced that X was pure DNA, and McCarty
notes that "since he [Mirsky] was widely acquainted with
biologists and biochemists, [his]...dim view of the implications
of our work certainly reached many ears and undoubtedly had some
influence on its reception."33 Why did Mirsky's respond in this
way?

During the period I am discussing -- 1944 to 1953 --
Mirsky's own research was concerned with what was called
chromosin, a DNA-protein complex found in cell nuclei, and he
favored the hypothesis that X was just such a DNA-protein
complex. The lengths to which he went to defend the viability of
this hypothesis reached almost as far as a general inductive
skepticism. In 1947 he claimed that the enzymatic evidence was
not adequate to discriminate the possibility that the
transforming principle was DNA from the possibility that it was a

DNA-protein complex. 34

In 1950 Mirsky almost reached general
skepticism when he claimed that "it is difficult to eliminate the
possibility that minute quantities of protein that probably
remain attached to DNA, though undetectable by the tests applied,

are necessary [even if not sufficient] for activity...."°° AS
13

McCarty implies, Mirsky's stubborn refusal to let the evidence
convince him was significant because his position as an expert on
DNA chemistry made his doubts seem more than merely stubborn.
(It also exemplifies the philosophical truth that there is no
criterion for when reasonable doubts become unreasonable.)

It may come as a surprise to note that Mirsky's objections
to the claim that X = DNA actually made the genetic significance
of transformation more obvious not less obvious. In 1947, the
distinguished geneticist H.J. Muller published a genetic
interpretation of transformation which, at least in part, was
based on Mirsky's stubborn objections to the views of Avery,
MacLeod and McCarty. Muller thought that X was a gene; because
he thought that X was not DNA. Muller writes:

«+.0n 28 January [1946], Mirsky gave reasons for inferring

that in the Pneumococcus case the extracted "transforming

agent" may really have had its genetic proteins still

tightly bound to the polymerized nucleic acid; that is,

there were, in effect, still viable bacterial "chromosomes"
or parts of chromosomes floating free in the medium used.

These might, in my opinion, have penetrated the capsuleless

[rough] bacteria and in part at least taken root there,

perhaps after having undergone a kind of crossing over with

the chromosomes of the host. 36 (my emphasis)
Thus, Mirsky's view of the chemical nature of X was actually part
of Muller's justification for claiming that X, whatever it was,
was the nearest anyone had come to putting a gene in a tube.

An explanation for this effect of Mirsky's objections and
indeed of Mirsky's objections themselves is at hand. The
chemical structure of nucleic acids was thought to be far too
repetitive to carry biological specificity. The reason was that

it was widely believed that the structure of nucleic acids was

ABCDABCDABCD where the four letters stand for the four
14

nucleotides. This was called the tetranucleotide hypothesis. As
Delbruck puts it, “...it was believed that DNA was a stupid
substance, a tetranucleotide which couldn't do anything
specific."37 such a repetitive structure, it was felt, could
play no more than a stabilizing role in the biological events of
cell division: perhaps the chromosomes consisted of a backbone of
nucleic acid around which the genetically active proteins were
wrapped. Surprisingly, for this very reason, the 1944 result
might have encouraged geneticists to attempt to isolate the
supposedly genetically active protein component as part of an
attempt to understand the biochemical activity of genes, but it
did not.

Summary. Avery, MacLeod and McCarty's reservations about
asserting X = DNA, cannot adequately explain the lack of
attention paid to the genetic significance of transformation in
the late 1940's and early 1950's. There are two probable reasons
for this. First, in 1946 new enzymatic evidence should have
quelled serious doubt about the nature of X. Second, even if,
following Mirsky, those enzymatic results were not believed this
might have made X look more like a gene, not less. Whether the
new enzymatic results of 1946 were taken as conclusive or not,
this gene in a tube seems not to have sparked the genetic

interest it warranted.

(b) X = Gene
It is difficult to find an unequivocal biological
explanation of the transformation phenomenon in the 1944 paper.

The reason for this is probably that Avery was not as interested
15

in how X functioned as he was interested in what X was. In his
May 1943 letter to his brother Roy, after indicating that, like a
gene, X was hetero- and auto-catalytic, Avery commented.

Sounds like a virus -- maybe a gene. But with mechanisms I
am not now concerned -- One step at a time -- and the first
is, what is the chemical nature of the transforming
principle? Someone else can work out the rest. Of course,
the problem bristles with implications. It touches the
biochemistry of the thymus type of nucleic acids [DNA] which
are known to constitute the major part of the chromosomes
but which have been thought to be alike regardless of origin
and species. It touches genetics, enzyme chemistry, cell
metabolism and carbohydrate synthesis, etc. [But] today it
takes a lot of well-documented evidence to convince anyone
that the salt of desoxyribose nucleic acid, protein-free,
could possibly be endowed with such biologically active and
specific properties and this evidence we are now trying to
get. It's lots of fun to blow bubbles -- but wiser to prick
them yourself before someone else tries to. So there's the
story Roy....Talk it over with Goodpasture but don't shout
it around -- until we are quite sure or at least as sure as
present method permits. It's hazardous to go off half
cocked -- and embarassing to have to retract later. 38

This well-known passage indicates that, as late as three
months before the 1944 paper was written, Avery was not fully
satisfied that X was pure DNA. As I have already argued, this
should have been clear from the final, published version.
Indeed, McCarty reports that even after that publication, in

1945, Avery "...continued to be plagued by nagging doubts about

whether we were right...."°9

More significantly the letter indicates that Avery was not
concerned to define the biological mechanism at work during
transformation. He was sure that the problem of transformation
bristled with biological significance, but he did not feel
inclined to work out the precise nature of this significance.
"Someone else can work out the rest." This may explain why, in

the discussion section of the 1944 paper, the authors merely
16

listed four possible hypotheses without deciding between them.
The four hypotheses were: (i) Griffith's: assimilating X to a
stimulus or pabulum required for the manufacture of the S
antigen; (ii) Dobzhansky's: assimilating transformation to the
induction of a genetic mutation; (iii) Stanley's: assimilating
transformation to infection by a virus; and (iv) Murphy's:
assimilating transformation to the stimulation of tumors in
healthy chickens by the injection of cell-free extract from
tumors in other chickens. 40 The authors did not decide which of
these four hypotheses was the most Plausible because, as Avery
wrote to his brother, that wasn't their primary concern and
because, as they wrote in the paper: "In the present state of
knowledge any interpretation of the mechanism involved in
transformation would be purely theoretical. "41

This last sentence, which represents a refusal to become
involved in theoretical interpretations of their solia
experimental results, was apparently typical of Avery's approach
to science. Dubos remembers that ",..Avery questioned the
validity of biological generalizations and was even reluctant to
use the word gene. He was virtually ignored by the theoreticians
of genetics, precisely because he made no effort to communicate
with them...."42 Theoretical biology was not to appear above
Avery'S name as it might above Delbruck's and Crick's -- not for
him, the Popperian conjecture, bold and improbable.

My next task is to determine whether this second hesitancy
of the 1944 paper might have been the cause of what McCarty
refers to as "...the apparently rather restrained acceptance of

the thesis advanced in the 1944 paper."43 One might reason: if
17

the 1944 paper only hesitantly claimed that X = gene, then one
can explain why the full recognition of the genetic significance
of Avery's work was retarded: Avery's conservatism was the cause
of this retarding. Nevertheless, I do not think this explanation
is entirely persuasive and for three principal reasons.

(1) One important consideration is that the same 1946 papers
that made up for the originally hesitant claim that X = DNA also
made up for the originally hesitant claim that X = gene. Thus
the factual basis for this explanation of the delay is not
secure. I will now briefly recount the evolution of the
Rockefeller group's interpretation of bacterial transformation.

In his May 1943 letter to his brother Roy, Avery discussed
the genetic significance of his investigations of transformation:

If we are proven right, and of course that's not yet proven,
then it means...that by means of a known chemical substance
it is possible to induce predictable and hereditary changes
in cells. This is something that has long been the dream of
geneticists. The mutations they induce by X ray and
ultraviolet light are always unpredictable, random and
chance changes. If we are proven right -- and of course
that's a big if -- then it means that both the chemical
nature of the inducing stimulus is known and the chemical
structure of the substance produced is also known.... 44

 

 

Nestled among his cautionary disclaimers is Avery's belief that
they had realized what he called the dream and what Muller called
the "Eldorado of geneticists": directed mutation. 4°

Not long after writing this letter, Avery went to Maine for
the summer. As I have already observed, while he was there he
wrote the first drafts of the opening and closing sections of the
1944 paper which was submitted for publication on November 1,

1943. It is not therefore surprising that some key words of

Avery's letter reappeared in the first sentences of that article.
18

These sentences also represent the closest that paper came to
giving a genetic interpretation of transformation:

Biologists have long attempted by chemical means to
induce in higher organisms predictable, and specific changes
which can thereafter be transmitted in series as hereditary
characters. Among microorganisms the most striking example
of inheritable and specific alterations in cell structure
and function that can be experimentally induced and are
reproducible under well defined and adequately controlled
conditions is the transformation of specific types of
Pneumococcus. 46

If we recall that Dobzhansky is quoted in that paper as believing
pneumococcal transformations to be “...authentic cases of
induction of specific mutations by specific treatments, "47 then
the thought occurs that in spite of their claims to the contrary,
the authors of the 1944 paper were not entirely agnostic about
the biological interpretation of transformation. Without being
explicit, they seem to have slipped an endorsement of
Dobzhansky's interpretation between the lines of their paper.

If I am right so to interpret the 1944 Paper, then it
becomes clear that, in 1946, McCarty and Avery changed their
explanation of the biological mechanisms underlying
transformation. The 1946 evidence was inconsistent with the
hypothesis that transformation was directed mutation: DNA
fractions from type III R cocci are indistinguishable from type
III S DNA fractions except that the former is not active in the
transforming system and the later is. If DNA were a mutagen then
these results would not be expected. A different interpretation
is suggested in 1946; to my mind it identifies DNA as carrying
the genetic specificity of bacteria, but curiously, it refrains

from saying so explicitly. Here is a full fledged genetic

interpretation which refuses to use the word "genetic":
19

It is possible that the nucleic acid of the R pneumococcus
is concerned with innumerable other functions of the
bacterial cell, in a way similar to that in which capsular
development is controlled by the transforming substance.

The desoxyribonucleic acid from type III pneumococci would

then necessarily comprise not only molecules endowed with _

transforming activity, but in addition, a variety of others
which determine the structure and metabolic activities
possessed in common by both the encapsulated (S) and

unencapsulated (R) forms. 48
Thus, although the 1944 paper did indeed refrain from identifying
the transforming principle with the genetic material, this
hesitancy was gone by 1946. The hesitancy of the first paper is
therefore unable to explain the tepid reception given 1944 paper
by geneticists.

(2) It could be argued that even the 1946 paper was too
hesitant to have envigorated genetic interest in bacterial
transformation. However McCarty and Avery were not the only
scientists publishing genetic interpretations of transformation
and other scientists were not so circumspect as to avoid the word
"gene". In 1947, A. Boivin published a paper read at a Cold
Spring Harbor Symposium of the same year. Holding nothing back,
Boivin called the paper "Directed Mutation in Colon Bacilli, by
an Inducing Principle of Desoxyribonucleic Nature: Its Meaning
for the General Biochemistry of Heredity." And what was its

meaning for the biochemistry of heredity? Boivin:

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 revolutionary. 49

Unlike McCarty and Avery, Boivin does not seem to have
20

discriminated the posssibility that DNA was directing a mutation
from the possibility that it was the carrier of hereditary
character, but in this passage he offers an extremely explicit
account of the genetic significance of transformation. Thus by
1947, there had been published a remarkably theoretical paper
which asserted that genes were made of DNA with none of the
hesitancy concerning the word "gene" which characterized McCarty
and Avery's 1946 publications. Furthermore (although it is only
marginally relevant, since I am here surveying published
reports), we have it on McCarty's authority that the quotation
from Boivin above is "...certainly a fine statement of what we
believed but were too reticent to say.">0

It must be said that Boivin's paper was no more effective
than the papers of Avery and his colleagus at envigorating
genetic investigations of transformation or the transforming
principle. Part of the reason may have been that Boivin's
theoretical approach to genetics was at the time of this
publication, rather idiosyncratic. By 1960 it would not have
been.

(3) It is sometimes felt that both Avery's and Boivin's
genetic interpretations of transformation were unlikely to affect
practicing geneticists; because they weren't given by
card-carrying geneticists. However, this argument is inadequate
as an explanation for why the Avery results were not more
vigorously pursued; because at least three geneticists promptly
offered genetic interpretations of the phenomenon. I have
already mentioned Dobzhansky's which was published in 1941 and

Muller's which was published in 1947. Sewell Wright, the
21

distinguished biochemical and population geneticist, may be added
to the list, for in 1945 he wrote of pneumoccocal transformation;
"The results suggest chemical isolation and transfer of a gene
rather than induction of mutation."51 This is a succinct and
brilliantly clear statement.

Summary. The undeniable hesitancy of the 1944 paper with
respect to the genetic mechanisms underlying pneumococcal
transformation is unable to explain why this paper was not more
vigorously pursued in the decade following its publication.

There are three reasons for this. In 1946, McCarty and Avery did
publish an interpretation of transformation which is genetic in

everything but name. In 1947, Boivin followed McCarty and Avery
but added the name. Finally, the genetic interpretation was also
subscribed to -- in print -- by card-carying geneticists.

In this section I have supported the traditional view that
the 1944 paper did not unequivocally assert either that X = DNA
or that X = gene. Nevertheless I have rejected the traditional
view that these two hesitancies were the cause of the delay

between Avery's announcement and the explosion of molecular

genetics.
AL

(D) Four Ways the Avery Result was Pursued.

The discussion of the last section raises an issue which
puts the accepted lore of molecular biology in question. Is it
true that the Avery result was only tentatively accepted?

In recent discussions, this question has received
conflicting answers. On the one hand an examination of the
number of times the 1944 and 1946 papers were cited reveals that
they were not frequently given as references in papers by those
concerned with the genetics of microbes.-* This suggests that
Avery's papers were not considered very important. On the other
hand, it has been suggested that their importance was so obvious
that they would not have required citation any more than Mendel's
papers would have required citation. >>

If I had to choose sides in this debate I would
unhesitatingly report that the Avery result was widely known even
if it was not widely referred to. But I would rather not choose
Sides at all; because I think this particular debate masks what
is really interesting about this period of scientific
development.

The issue is not whether or not scientists knew about the

1944 paper. They did. Although The Journal of Experimental

 

Medicine had a "...fairly limited readership,"~4 the Avery result
was never lost to the scientific community in the way Mendel's
work was. What I want to discuss is not simply whether or not
the Avery result was known, but whether or not its profound
implications were fully comprehended. I am struck by the fact

that this failure to comprehend is even acknowledged in R. Olby's
23

attack on the lore of Avery's non-recognition. Olby: "Only with
the advantage of hindsight can we see the significance of the
1944 paper as obvious.">> The gestions are thus raised. What
gives us this advantage of hindsight? And what is it about the
way Avery's result was pursued that reveals its significance not
to have been fully grasped? Avery's work was not universally
ignored, but we must determine the particular ways it was
acknowledged. It was not immediately developed in the directions
which, with hindsight, appear obvious. Why?

It hardly needs pointing out that what gives us the
advantage of hindsight is that we know of the explosion of what
might be called theoretical genetics which followed the
publication of the April 25, 1953 issue of Nature. In that
issue, over the names J.D. Watson and F.H.C. Crick, there
appeared an article titled "Molecular Structure of Nucleic Acids.
A Structure for Deoxyribose Nucleic Acid." Hindsight gives us
this advantage: Avery's work initiated the biochemical
investigation of genetic phenomena which provided all of the most
exciting work in molecular biology for more than a decade
following 1953. With significant exceptions, what seems not to
have been recognized by those who pursued the Avery results
between '44 and '53, is that those results called for chemical
investigation with an eye to the way in which information was
encoded in DNA.

I should say that investigators at the time may have thought
that this was the direction in which the Avery result was
pointing. But these same investigators might either not have

known how to, or not cared to, move their research off in that
24

direction. Whatever the explanation should be, it is a fact that

chemical investigations were not an immediate consequence of the ULL .

1944 publication. gy
We may distinguish four different ways in which biologists

acknowledged the Avery result. Rather arbitrarily, I will
associate them with the names of one of the major contibutors to
each of these four ways of pursuing the results of Avery,
MacLeod, and McCarty: (i) in the manner of R.D. Hotchkiss, (ii)
in the manner of J. Lederberg, (iii) in the manner of M.
Delbruck, and (iv) in the manner of E. Chargaff. I hope to show
that only the last grants Avery the position granted him by
hindsight.

(i) In July 1946, McCarty left Avery's pneumococcal
research team to take command of the Rockefeller's streptococcal

laboratories. >°

In his memoirs, McCarty asks himself a question
that hindsight makes unavoidable: "how could one even consider
turning from the path of research opened up by the DNA
discovery"? His reply is that, perhaps because he was not
trained as a geneticist, he was "...little attracted to pursuing
the studies along genetic lines." His own inclination would have
been to attempt to purify from the active DNA fraction that
component whose sole function was to induce synthesis of the
type-specific capsular polysaccharide. For my purposes, what is
worth noting in McCarty's memoirs is that if he had continued
working on transformation he would not have left the field of
questions opened up by Griffith and pondered by Avery.

Already in 1938, before McCarty arrived at the Rockefeller,

Hotchkiss had asked Avery whether he might investigate some of
25

the questions raised by the phenomenon of transformation; Avery
said: not now. Finally as McCarty was leaving the pneumococcus,
Hotchkiss was permitted to participate. Hotchkiss represents the
line of research closest in spirit -- and in body -- to Avery
himself and farthest in spirit from what hindsight discloses as
the natural path of research. His concern was to demonstrate the
general genetic significance of the Avery result by showing that
DNA was able to induce transformation of characteristics other
than capsular synthesis.’ In this endeavor Hotchkiss was
successful. Hotchkiss also attempted to improve the evidence
that transformation by the DNA function was not being
accomplished by proteins contaminating that fraction. This again
was successful.°8 what distinguishes Hotchkiss’ manner of
pursuing the DNA discovery is the way in which Avery's own
questions and answers guided his research. Hotchkiss'
bacteriological investigations though elegant and original are
not on the path that, in hindsight, stretches between Avery, and
Watson and Crick.

(ii) J. Lederberg has argued powerfully that although the
Avery result suggested genes were bits of DNA, the evidence
",..was not yet conclusive for it was still controversial whether
bacteria could even be thought of as having a genetics."
Lederberg and his mentor F.J. Ryan therefore tried to produce the
transformation phenomenon in a non-bacterial system using the red
bread mold Neurospora. (Note the modulation required to give
significance to what we call the "repetition" of an experimental
result.) Their efforts were not successful, and to this day, .

Neurospora have never been shown to exhibit transformation.
26

As Lederberg describes it, the work he did with E. Tatum at
Yale (and for which, in 1958, he received, with Tatum and Beadle,
a Nobel prize) was a direct result of those null results with
Neurospora. Lederberg: "One day I suggested that we [i.e. F.J.
Ryan and himself] ring the changes on our experimental approach.
Instead of trying to make Neurospora imitate a phenomenon
recently worked out in bacteria, we could use similar methods to
inquire whether bacteria had genetic mechanisms similar to
Neurospora. "60 Without wishing in any way to deny the brilliance
of the resulting discovery and investigation of microbial
genetics, this research is not part of what (in hindsight)
appears as the new wave, namely, chemical investigation of the
gene. Lederberg's line of research demonstrated that the
principles of Mendelian genetics -- thoroughly investigated in
the fruit fly -- could also be applied to bacterial systems. As
Lederberg put it in 1947, "...since we have been able to
demonstrate no appreciable point of difference between the
features of gene exchange in this strain of E. coli and in the
classical materials of Mendelian experimentation, the most
economical conclusion is that the mechanisms involved are also

similar."6l

Lederberg's investigations were not, any more than
Hotchkiss', in the biochemical lineage that ties Avery's work to
Watson and Crick.

(iii) The research interests of M. Delbruck, S. Luria, and
what came to be called the phage group evolved in complete
separation from the bacteriological investigations that made

transformation of central concern in Avery's laboratories. Thus

although the phage group was certainly aware of the DNA
27

discovery, they did not pursue it: their interests were
elsewhere.

The evidence that the phage group knew of Avery's results is
fascinating. In the early forties, Delbruck was at Vanderbilt;
so was Roy Avery, the recipient of Oswald's May 1943 letter which
included the uncharacteristically speculative suggestion that the
transforming principle might be the genetic material. According
to Delbruck, he met Roy Avery “...the day he received the letter

n62 Luria was

and he told me about it; and I read it then.
introduced to transformation by Dobzhansky's widely read book
Genetics and the Origin of Species (second edition, 1941). Since
Luria was in New York when he read that book, he immediately went
to the Rockefeller to talk to Avery about it. As Luria recalls
it: "This was sometime in the spring of 1943, or earlier, before
he published. And Avery told me the whole story, how it seemed
to be nucleic acids, and so on, "63 There can be no doubt; at
roughly the same time, Delbruck and Luria, from the same
unimpeachable source, learned of the DNA discovery.

Nevertheless, there is equally strong evidence that the
phage group was unwilling to investigate the phenomenon of
transformation. Delbruck's reaction to the Avery paper was less
than favorable. Recently recalling the debates in the forties
about whether DNA had sufficient chemical articulation to be able
to carry the specificity required of the genetic material,
Delbruck said:

I distinctly remember wading here [Cold Spring Harbor] at

low tide with Rollin Hotchkiss, every so often, and he

Plugging for the idea that DNA might contain enough

specificity...And even after people began to believe it
might be DNA, that wasn't really so fundamentally a new
28

story, because it just meant that genetic specificity was

carried by some goddamn other macromolecule, instead of

proteins. 64
This is a deeply revealing statement. It shows that Delbruck
considered chemical considerations to be alien to genetics.

For Delbruck, whether genes were made of this or that
macromolecule was tangential to what was behind his very entrance
into biology: understanding the process of genetic reproduction.
This being the goal, viral replication was an attractive system
to work with; because it presented the phenomenon of genetic
reproduction in what seemed to be it's purest form. Delbruck's
own inclination was to reach for understanding by combining
physical and genetical considerations: bypassing chemistry. ®°
His missionary zeal in promoting this particular research program
gave to the phage group, as a whole, an unconcern with chemical
considerations. In retrospect, Luria recognized this as a
deficiency in the way the phage group was thinking. Luria
recalls:

I had great admiration for him [Avery]. But he was

certainly working in something that seemed very different --

but then, I must admit, there was probably a weakness in
much of our thinking. ...we were blocked in biochemical
thinking. People like Delbruck and myself, not only were
not thinking biochemically, but we were somehow -- and
probably partly unconsciously -- reacting negatively to
biochemistry. And biochemists. As such. As a result, for
example, I don't think we attached great importance to
whether the gene was protein or nucleic acid. The important
thing for us was that the gene had the characteristics it
had to have. And that's why Watson and Crick were so
tremendously important to us, as genetic thinkers. Because
their structure had embedded in it -- one saw immediately --

the properties of the gene. 66
There was a possiblity that the phage group masked from itself.
It was the possiblity that the functional nature of the gene

might be manifest in its chemical structure.
29

I have yet to mention one result of the phage group which
will seem especially relevant to any discussion of the reception
of Avery's work by that research group. The announcement by
Hershey and Chase in 1952 that "...sulfur-containing protein has
no function in phage multiplication, and that DNA has some
function" is touted in textbooks and conversations as being the
crucial piece of evidence that converted microbial geneticists to
the view that genes were not made of protein but of pna.®? since
the evidence of 1952 in favor of the genetic role of (phage) DNA
was less clear than the evidence offered by Avery and his
descendents at the Rockefeller, if the 1952 evidence was the
decisive factor, there is reason to believe that this effect of
Hershey and Chase was not based solely on the quality of their
evidence. The phage data was much less decisive in ruling out
the possibility of protein contamination. Given the different
quality of the 1944 and the 1952 evidence, the different
receptions of the two experiments deserves explanation.

I am most tempted by sociological explanations. The
commitment of the phage group to phage (and to itself) resulted
in its members allowing themselves to be convinced by phage data
that DNA = gene, even when better pneumococcal evidence had not
been able to convince them of the same equation. The fact that
such an explanation gives a central role to an emotional
commitment to certain kinds of evidence may be sufficient reason
to look for another explanation. Olby, for example, denies that
"oo.it can be said that the phage group as a whole jumped on the
DNA trail in 1952."68 McCarty's view is that that although the

phage group did jump on the DNA trail after Hershey and Chase's
30

results, this would never have happened without the pneumococcal
evidence. ©?

For my purposes, what is significant about the phage groups
ignoring of Avery's work is this. They ignored it because they
were unconcerned with precisely those chemical questions whose
answers opened up the field we now know as molecular genetics.
From this point of view Hershey and Chase are not as significant
for their results, as they are for their questions. Indeed from
this point of view Luria's suggestion -- before Hershey and Chase
-- that phage results indicated that protein was the genetic
material is just as significant. 7°

(iv) Almost immediately after the 1944 publication, E.
Chargaff picked up those biochemical questions which make his
important work on the chemistry of nucleic acids the bridge
between Avery at the Rockefeller Institute and Watson and Crick
at the Cavendish Laboratory.

None of the three ways of responding to Avery's work which I
have already discussed involved chemists. Chargaff was a
chemist. In 1947, he wrote:

If, as we may take for granted on the basis of the very

convincing work of Avery and his associates, certain

bacterial nucleic acids of the desoxyribose type are endowed
with specific biological activity, a quest for the chemical
or physical causes of these specificities appears
appropriate, though it may remain completely speculative for

the time being. 71

Chargaff's acknowledgment that Avery had proved that DNA was
the genetic material posed his first question. If genes were DNA
then the chemical composition of DNA ought to vary from species

to species. He set out to determine the molar proportions of the

purine and pyrimidine components of DNA samples derived from
31

several species.72 ag he had suspected, there were species
specific differences between the molar proportions of purines and
pyrimidines in DNA derived from these three sources. Chargaff's
results revealed first that DNA was not composed of equal molar
amounts of all the nucleotides and second that the unequal
amounts varied from species to species. In a 1950 review of this
work, Chargaff claimed that these results "...serve to disprove
the tetranucleotide hypothesis."73

It is hard to underestimate the importance of this result.
It constituted a frontal assault on the main support of all those
who had doubted that DNA could possibly serve as the genetic
material. DNA was revealed not to be a repetitive, uniform
substance, and it was revealed to be species specific. However
these results were not the most significant ones to come out of
Chargaff's laboratory in the late 1940's and early 1950's.

Chargaff and his co-workers noticed that their evidence for
the species specificity of the chemical composition of DNA
exhibited some surprising regularities. The total molar quantity
of both purines (adenine and guanine) was always roughly the same
as the total molar quantity of both pyrimidines (thymine and
cytosine). Furthermore the molar amount of adenine was roughly
the same as that of thymine; and that of guanine was roughly the
same as that of cystosine. These three relationships are often
presented pictorially thus:

A+G=T+C

A =T
G=c

As is now well known, these three molar equalities were finally
32

given a chemical explanation by the Watson-Crick structure of DNA
which reveals that A is bonded to T and G to C. The
equimolarities discovered by Chargaff thus proved to be at the
heart both of the chemical structure of DNA's famous double helix
and of the mechanism of DNA transcription and replication.
Chargaff's manner of pursuing the Avery results is the one
highlighted by hindsight.
Summary. This last section presented a brief sketch of four
ways Avery's "Studies" were acknowledged. (i) The team at the
Rockefeller Institute, from which I have isolated Hotchkiss,
continued to address Avery's own questions: is transformation a
general phenomenon, and is there any protein contamination in the
DNA function? (ii) Lederberg saw the Avery result as suggesting
the existence of Mendelian Genetics at the bacterial level. rr
(iii) Delbruck, Luria, and the Phage group saw the Avery result a
as old-fashioned bacteriological research with perhaps the
significance of revealing that genes were made of this rather
than that macromolecule. (iv) Chargaff saw Avery's results not
as bound to Avery's own conservative questions, nor as linked to
Mendelian genetics, nor as a minor investigation of a rather odd

bacteriological phenomenon: in Chargaff's eyes Avery's results

gave chemistry wings.

(E) Kuhnian Analysis: Revolutionaries or Puzzle-Solvers?
I am not about to launch a full scale interpretation and
defense of what Kuhn would call a scientific revolution; because

there is much in Kuhn's picture of discontinuous scientific
33

change that cannot be adequately defended. For my purposes, we
may say that a Kuhnian revolution consists in the change of
paradigm; and I will restrict the meaning of that notoriously
abused word to the definition given by Kuhn in the preface to The
Structure of Scientific Revolutions: "...paradigms. These I take
‘to be universally recognized scientific achievements that for a

time provide model problems and solutions to a community of

practitioners."/4

Paradigms -- concrete scientific achievements
-- are paradigmatic in a number of ways, two of which are
especially relevant here. They provide examples of what a
scientific problem is like, and they provide examples of what a
solution to that kind of problem ought to look like. Paradigms
function in this way by providing examples of judgments which
young scientists learn directly. When paradigms change, it is
clear that this may or may not cause a change in the collective
judgment that this is what a fruitful scientific question looks
like and that is what an acceptable scientific answer looks like.
Nevertheless, such changes are not, on Kuhn's account,
impossible: "...when paradigms change, there are usually
significant shifts in the criteria determining the legitimacy
both of problems and proposed solutions."/°

Thus in order to determine whether the Avery result was
revolutionary, it will be sufficient to determine whether the
three "Studies on the Chemical Nature of the Substance Inducing
Transformation of Pneumoccal Types" published in 1944 and 1946
guided future research by being used as paradigmatic examples of

a new style of asking and answering scientific questions.

However, one consequence of Kuhn's analysis of paradigm change is
34

that this is no longer a simple question. We must consider each
of the four different research traditions into which those
"Studies..." were incorporated, and then ask, of each tradition,
whether Avery's "Studies..." were functioning as paradigmatic
examples of the type of question to ask and of the kind of answer
to look for. Of course, we are especially interested in whether
genetical investigations were being modeled on Avery's
"Studies...;" because the central task of this paper is to decide
whether that work was immediately acknowledged as showing how to
raise genetic questions biochemically.

I do not doubt that the self-image of Avery, MacLeod and

McCarty was that they were first of all puzzle-solvers, not pan
9
d
revolutionaries. As the 1944 title makes clear, the puzzle was wn’
to determine "...the chemical nature of the substance inducing Js

transformation of pneumococcal types," and it was the peculiar
good fortune of this group that the solution to their puzzle had
broad biological implications. Furthermore, Hotchkiss and
Avery's other successors at the Rockefeller Institute seem to
have understood their own research as filling in the details of
the picture of transformation, just as Avery had seen himself as
filling in the details of Griffith's picture. If there is a
paradigm in the neighborhood -- a concrete scientific achievement
which provided model problems and solutions for a community of
scientists -- it is Griffith's original paper of 1928: not
Avery's of 1944. Avery's paper is an elegant solution to a
question arising naturally from Griffith's work. It is not,
first of all, a beginning; it is an end.

One surprising result of this analysis is that Delbruck's
35

and Hotchkiss' very different investigations can be seen as
having acknowledged Avery's work in the same way. Although the
former chose to ignore and the latter chose to pursue the
questions raised in Avery's "Studies...," their different
research activities showed that they both understood Avery's work
as the culmination of an investigation of a question originally
raised by Griffith in 1928. Hotchkiss continued to care about
that question, Delbruck did not. Nevertheless, they both placed
that work within the same space of possible questions.

On the other hand, Lederberg and Chargaff seem to have used
Avery's papers as the occasion for elaborating their own
questions on the basis of Avery's results. Whereas Hotchkiss may
be said to have pursued questions raised in Avery's "Studies...,"
these two scientists may be said to have pursued questions raised
by those "Studies...." Rather than refining Avery's solutions to
the gestions he raised, and rather than ignoring those questions,
they allowed Avery's discovery to direct their inquiries towards
questions which -- however much they were causally dependent on
Avery's result -- were not raised or addressed by Avery's
"Studies...." Neither Lederberg nor Chargaff can be said to have
modeled their questions and techniques on the questions and
techniques used with such skill by Avery, MacLeod, McCarty, and
their descendents. In each case, they raised new questions which
they pursued in new ways, and from these two perspectives Avery's
work must again seem to be the work of puzzle-solvers, not
revolutionaries.

In evaluating the scientific response to Avery's "Studies on

the Chemical Nature of the Substance Inducing Transformation of
36

Pneumococcal Types" we should discriminate two types of favorable
response. First there is the response of those who were
continuing questions raised in those "Studies...." These
scientists may be said to have used the Avery work (and, once
removed, Griffith's work) as a paradigm in planning their own
investigations. We might say their work is internally related to
Avery's; it feeds of the questions Avery addressed and the way he
addressed them. Second there is the response of those whose
questions take Avery's work for granted and build on it, but do
not model their own work on Avery's. Avery's DNA discovery was
instrumental in turning the attention of geneticists to bacteria
and of chemists to DNA, but the founders of molecular biology did
not model their investigations on Avery's. We might say their
work is externally related to Avery's "Studies..."; it builds on
Avery's results without building on the way Avery arrived at
those results. /6

Some may believe that because Avery's discovery was
instrumental in getting the likes of Chargaff and Watson to
investigate DNA, it was therefore revolutionary. I am not
tempted by this account; because it appears to be the start of an
infinite regress; because it looks as though similar reasoning
could make George III the revolutionary source of the American
Revolution; and because I think it hides from us the true nature
of the change in biological practice which occurred in the middle
of this century.

Thus in the narrow Kuhnian sense sketched at the start of

this section Avery, MacLeod and McCarty were not revolutionaries.
37

(F} The Invention of Theoretical Genetics: 1953.

If Avery's work was not paradigmatic for molecular biology,
what was? My discussion in sections (D) and (E) may seem to have
arrived at the point of giving that role to Chargaff. But I will
not.

In 1953, Watson and Crick did provide a universally
recognized scientific achievement that for a time provided model
problems and solutions to a community of practitioners (roughly N
molecular biologists). Theirs is the revolutionary example of
how to ask biologically significant questions at the molecular
level. Putting it this way, what is significant is not the of
chemical structure of DNA, but what they did with it: not their x
first paper of 1953 but the second which was called, "Genetical A
Implications of the Structure of Deoxyribonucleic Acia."77

This is not the place to launch an investigation of whether
my hypothesis that the significant change in biological practice
was the invention of theoretical genetics; and I would never
claim that no one but Watson and Crick could have seen the
genetical implications of the structure they built to account for
the Franklin's and Wilkins' pictures. However I am struck by
Chargaff's description of what made molecular genetics so new.
His ungenerous reaction to the fame of Watson, Crick, and their
descendants defines what was revolutionary about their work.
Chargaff described that work as part of "... the new science
which grew out of the fusion of chemistry, physics, and genetics,

i.e., molecular biology...."/8 Recalling a meeting he had with

Watson and Crick in May 1952, Chargaff writes:
38

What I did not then realize was that we were on the
threshold of a new kind of science: a normative biology in
which reality only serves to corroborate predictions; and if
it fails to do so, it is replaced by another reality...

What is currently considered as the structure of
deoxyribonucleic acid was established by people who required
no recourse to actual DNA preparations....It was clear to me
that I was faced with a novelty: enormous ambition and
aggressiveness, coupled with an almost complete ignorance
of, and a contempt for chemistry, that most real of exact
sciences -- a contempt that was later to have a nefarious
influence on the development of "molecular biology." 79

I want to emphasize Chargaff's disgust at the unrepentant
ignorance of Watson and Crick: “If they had heard before [1952]
about the pairing rules [first reported in 1950], they concealed
it. But as they did not seem to know much about anything, I was

not unduly surprised. "80

Perhaps more than anyone else, Chargaff
who was at the threshold of this new science, recognized its
differences from what he had thought of as biology and
biochemistry. Thinking back on that 1952 meeting with Watson and
Crick he comments: "I am sure that, had I had more contact with,
for instance, theoretical physicists, my astonishment would have
been less great."8l It is striking that the explosion of
molecular biology after 1953 drew physicists such as Gamow into
biology.

My hypothesis that Watson and Crick's papers of 1953 were
revolutionary because they provided paradigm examples of a new
type of question, and a new way of finding answers was

corroborated by Delbruck in a conversation with Judson, who o
reports: (

---1 asked [whether] what the Watson-Crick structure did was
define the problems next to be solved? Delbruck said,
Slowly, “Yes. Yes. Yes -- it gave a marvelous fixed point
from which to start on both these problems. Replication and
Readout. Marvelous in that it was so concrete...I mean that
it gave the hope that the whole solution will be possible in
39

terms of concrete three-dimensional chemistry.

Stereochemistry. Enzyme chemistry. Which before was not
clear. 82

(G) Conclusion

Having completed my defense of the claim that Avery, MacLeod
and McCarty were not revolutionaries, and an outline of why
Watson and Crick might have played that role, I am struck by the
uncontentiousness of these claims and set to wondering why there
have been such excited exchanges concerning the acceptance or
recognition of Avery's DNA discovery.

One explanation is that those exchanges have focussed on
whether Avery, MacLeod and McCarty on the one hand or biologists
in general on the other, recognized the full significance of the
1944 results. In this paper I have sided with those, such as
Lederberg, who assert that the full significance of this
discovery was recognized both by its discoverers and by most
biologists. Nevertheless resolving this question leaves behind
the issue I have been addressing in this paper: explaining the
delay between the recognition that DNA = gene and the scientific
investigation of that equation.

G.S. Stent has explained this delay with reference to what
he calls the prematurity of Avery's work. Stent writes that "a
discovery is premature if its implications cannot be connected by
a series of simple logical steps to cannonical or generally
accepted knowledge. "83 I have a suspicion that every surprising
result would count as premature by this criterion. Perhaps Stent

would say that only those surprising results which are not
40

fruitfully pursued soon after their publication are premature,
but this threatens to become the tautology that some surprising
results are not fruitfully pursued because they are not
fruitfully pursued.

Even if Stent's account of prematurity can be saved from
tautology, his particular account of Avery's work is inadequate.
He claims that the longevity of the tetranucleotide hypothesis
made it impossible for geneticists to think of DNA as the carrier
of genetic specificity. If this means that geneticists could not
believe that transformation consisted in the transfer of genetic
material from one pneumococcus to another, then Stent's claim is
false. We have seen that a number of geneticists believed just
that. This is not news, the attack on Stent by those who have
investigated these matters has been virtually unanimous, but my
investigation suggests that in a different sense Avery's DNA
discovery was indeed ahead of its time.

Stent's emphasis is on the "...conceptual difficulty of
assigning the genetic role to DNA...."84 However the problem was
not conceptual; it was PRACTICAL. The elaboration of the 1944
paper in 1946 by McCarty and Avery, and later by Hotchkiss,
successfully answered the conceptual point. But they did not
address the practical problem of what to do next. For those many
scientists who were able to accept that genes were made of DNA,
it was still not clear what to do. Since the chemical structure
of DNA wears its biological function on its sleeve, we cannot
resist thinking that the obvious thing would have been to try to
determine that chemical structure. But as Crick observes, this

is a distortion of hindsight: "Nowadays everyone swears they had
41

powers of prediction, and knew from the outset [1944?] that the
DNA structure would turn out to be significant. But this is
arrant nonsense. Nobody knew.... This part is luck."85 Avery's
work was ahead of its time, not in being unable to be conceived
genetically, but in being unable to be investigated genetically.

I am struck by the fact that, even as he argues that the DNA
discovery was not conceptually premature in Stent's sense,
McCarty appears to concede that it was premature in a practical
Sense. McCarty: "I would argue that the discovery was not
"premature' but rather required further biological, chemical, and
Structural development before it could be manipulated by the
geneticists, "86 Avery's work was not conceptually ahead of its
time, but since we now know of the explosion of biochemical
genetics after 1953, it cannot but seem to have been practically
ahead of its time.8?

Since I have discussed various ways Avery's work was pursued
in the forties, my view cannot be that it was impossible to
pursue Avery's work in 1944. My view is rather that what
hindsight reveals as the most significant way to pursue the DNA
discovery was not possible until Watson, Crick, and their
descendents provide examples of how to investigate genetic
questions at the level of biochemistry. You Might say it was not
possible until the invention of molecular biology, but that is
another story. A story involving, in addition to theoretical
innovations, innovations as concrete as the end of World War II,
the creation and generous funding of several National Institutes
of Health, and the ready availability of the familiar machinery

of modern biological laboratories.
42

What I have attempted to do in this paper is to place Avery,
MacLeod, and McCarty's discovery not in the history of scientific
awards, but in the history of science. It is beyond dispute that
Avery's identification of the chemical nature of the genetic
material was a sine gua non of the development of molecular
genetics. But I have argued that Avery's work did not function
as a model for how to pursue molecular genetics, and hence that

it was not a revolutionary discovery in Kuhn's sense. °8
10.

ll.

12.

43

FOOTNOTES

The dispute is well represented by:

H.V. Wyatt, “When does information become
knowledge?" Nature vol. 235 (January 14, 1972), pp.
86-89.

J. Lederberg "Reply to Wyatt" Nature vol. 239
(September 22, 1972), p. 234.

R. Olby "Avery in Retrospect" Nature vol. 239
(September 29, 1972), pp. 295-296.

O.T Avery, C.M. MacLeod, and M. McCarty, "Studies on the
Chemical Nature of the Substance Inducing Transformation
of Pneumococcal Types. Induction of Transformation by a
Desoxyribonucleic Acid Fraction Isolated From
Pneumococcus Type III" J. Exp. Med. v. 79 n. 2 (1944),
pp. 137-158.

F. Griffith, "The Significance of Pneumococcal Types" J.

Ibid., p. 130.
Ibid., p. 130.
R.J. Dubos, The Professor, The Institute, and DNA (New

York: The Rockefeller University Press, 1976), pp. 130-
131.

 

Griffith, "The Significance...", pp. 156-157. Ina
conversation with H. F. Judson, S. Luria "...damned
bacteriology as the last stronghold of Lamarckism." See:
H.F. Judson, The Eighth Day of Creation (New York: Simon
and Schuster, 1979), p. 55.

R.D. Hotchkiss, "Oswald T. Avery 1877-1955," Genetics v.
51 (January 1965), p. 4.

Dubos, The Professor..., pp. 137-141. Also see: M.
McCarty, The Transforming Principle: Discovering That
Genes Are Made of DNA (New York: W. W. Norton & Company,
1985), pp. 79-100.

 

J.-L. Alloway, "The Transformation In Vitro of R
Pneumococci Into S Forms of Different Specific Types by

the use of Filtered Pneumococcus Extract" J. Exp. Med. v.
55 (1932), pp. 91-99.

For an account of the possible cause of the hiatus, see
McCarty, The Transforming Principle, pp. 96-100.

 

O.T. Avery, Letter to his Brother Roy, May 26, 1943. A
long extract from this letter is printed in Dubos, The
Professor..., pp. 217-220; the passage cited above is on
p. 218. A shorter extract, which in a few trivial
13.

14.

15.

16.

17.
18.
19.

20.

21.

22.

23.

24.

25.

26.

27.

28.

44

matters does not agree with that of Dubos, was printed in

McCarty, The Transforming Principle, pp. 157-159. I have
not checked the original.

J.L. Alloway, (1932), cited in Dubos, The Professor...,
p. 138.

McCarty, The Transforming Principle, p. 106.

I have not summarized the general properties of X, nor
the ratio of nitrogen to phosphorus in X, nor the
behavior of X in electrical and centrifugal fields.

Avery, MacLeod and McCarty, "Studies..." I (1944), p.
150.

Ibid., pp. 144-145.

Ibid., pp. 145-150.

Ibid., p. 151.

Avery, MacLeod, and McCarty, "Studies..." I (1944), p.
155.

Avery, MacLeod, and McCarty, "Studies..." 1(1944), p.
156.

Avery, MacLeod, and McCarty, "Studies..." I (1944), p.
153.

W.M. Stanley, "The 'Undiscovered' Discovery" Arch. Env.
Health v. 21 (1970), p. 259.

McCarty, The Transforming Principle, p. 164.

Avery's letter to his brother Roy, May 1943, published in
Dubos, The Professor..., Dp. 220.

C. MacLeod in conversation with R. Olby September 1968
cited in R. Olby, The Path to the Double Helix (Seattle:
University of Washington Press, 1974), p. 188.

 

Dubos, The Professor..., p. 159, also see p. 95.

M. McCarty and 0O.T. Avery, "Studies on the Chemical
Nature of the Substance Inducing Transformation of
Pneumococcal Types. II. Effect of Desoxyribonuclease on
the Biological Activity of the Transforming Substance" J.

Exp. Med. v. 83 (1946a), pp. 89-96.

M. McCarty and O.T. Avery, "Studies on the Chemical
Nature of the Substance Inducing Transformation of
Pneumococcal Types. III. An Improved Method for the
Isolation of the Transforming Substance and its
Application to Pneumococcus Types II, III, and VI" J.
29.
30.
31.
32.
33.
34.

35.

36.

37.

38.

39.
40.

41.

42.
43.

44.

45.
46.

45

Exp. Med. v. 83 (1946b), pp. 97-104.

McCarty and Avery, "Studies..." II (1946a), p. 90.
Ibid., p. 94.

Ibid., p. 94.

McCarty, The Transforming Principle, p. 190-1.
Ibid., p. 216.

A.E. Mirsky, published contribution to discussion of
Boivin's paper Cold Spring Harbor Symp. Quant. Biol. v.
12, (1947), p. 16.

A.E. Mirsky, "Some Aspects of the Cell Nucleus" in
Genetics in the Twentieth Century: Essays on the Progress
of Genetics During its First Fifty Years, ed. L.C. Dunn
(New York: 1951), p. 132.

H.J. Muller, “The Gene. Pilgrim Trust Lecture” Proc. Roy.
Soc. London B. v. 134 (1947), p. 23n, footnote added in
January 1946 to a lecture originally delivered November
1945. By this time, Jan. 1946, Mirsky would have known
of McCarty and Avery's DNase evidence; see: McCarty, The
Transforming Principle, p. 183.

M. Delbruck, in conversation with Judson in Judson, The
Eighth Day..., p. 59.

Avery's letter to his brother Roy, May 26, 1943,
published in Dubos, The Professor..., p. 219-220.

McCarty, The Transforming Principle, p. 194.
Avery, MacLeod, and McCarty, "Studies..." I (1944), p.

155; Dobzhansky's interpretation was published in the
1941 edition of his Genetics and the Origin of the

Species, p. 47.

Avery, MacLeod, and McCarty, "Studies..." I (1944), p.
154.

Dubos, The Professor..., p. 155.

McCarty, The Transforming Principle, p. 194.

O.T. Avery's letter to Roy Avery in Dubos, The
Professor..., p. 219.

Muller, "The Gene," p. 23, first read November 1945.

Avery, MacLeod, and McCarty, "Studies..." I (1944), p.
137.
47.
48.

49.

50.
51.

52.

53.

54.

55.

56.

57.

58.

59.

60.

61.

62.

46

T. Dobzhansky, cited in Ibid., p. 155.
McCarty, and Avery, "Studies..." II (1946a), p. 95.

A. Boivin, “Directed Mutation in Colon Bacilli, By an
Inducing Principle of Desoxyribonucleic Nature: Its

Meaning for the General Biochemistry of Heredity" Cold
Spring Harbor Symp. Quant. Biol. v. 12, (1947), p.- 12.

 

McCarty, The Transforming Principle, p. 218.

S. Wright, "Physiological Aspects of Genetics" Ann. Rev.
Physiol. v. 7 (1945), 83.

See: H.V. Wyatt, "When Does Information Become
Knowledge?" Nature v. 235 (Jan. 14, 1972), pp.86-89.

See: J. Lederberg, "Reply to H.V. Wyatt" Nature v. 239
(Sept. 22, 1972), p. 234.

R. Olby, "Avery in Retrospect" Nature v. 239 (Sept. 29,
1972), p. 295.

Ibid., p. 296.

The biographical information in this paragraph and the
next is derived from McCarty, The Transforming Principle,
Chapter XI.

The idea of extending transformation to other markers
first occured to Hotchkiss around 1943. (See: R.D.
Hotchkiss, “Gene, Transforming Principle, and DNA" in
Phage and the Origins of Molecular Biology, J. Cairns,
G.S. Stent, and J.D. Watson, eds., (Cold Spring Harbor,
New York, 1966), p. 187.) One of his successes is marked
in his "Transfer of Penicillan Resistance in Pneumococci
by the Desoxyribonucleate Derived from Resistant
Cultures" Cold Spring Harbor Symp. Quant. Biol. v. 16
(1951), pp. 457-461.

 

Hotchkiss, “Gene, Transforming Principle, and DNA," p.
189.

J. Lederberg, "Francis J. Ryan" in University on the
Heights, W. First, ed., (New York: Doubleday, 1969), pp.
106-107.

 

Ibid., pp. 107-108.

J. Lederberg, "Gene Recombination and Linked Segregations
in Escherichia Coli" Genetics v. 32 (1947), p. 521.

M. Delbruck, in conversation with Judson in Judson, The

Eighth Day..., p. 59.
63.
64.
65.

66.

67.

68.

69.

70.

71.

72.

73.

74.

75.

76.

77.

47

S. Luria, in conversation with Judson in Ibid., p. 63.
Delbruck, in conversation with Judson in Ibid., p. 60.
Olby, The Path to the Double Helix, p. 238.

Luria, in conversation with Judson in Judson, The Eighth
Day..., p. 62-63.

A.D. Hershey and M. Chase, “Independent Functions of
Viral Protein and Nucleic Acid in the Growth of

Bacteriophage" J. Gen. Physiol. v. 36 (1952), p. 54.

Olby, The Path to the Double Helix, pp. 319-320. Also
see: McCarty, The Transforming Principle, p. 224.

McCarty, The Transforming Principle, p. 224.

Luria, in conversation with Judson in Ibid., p. 63, my
emphasis.

E. Chargaff, “Nucleic Acids and Nucleo Proteins of
Micro-Organisms" Cold Spring Harbor Symp. Quant. Biol. v.
12 (1947), p. 30.

E. Chargaff, Heraclitean Fire (New York: Warner Books,
Inc., 1980), p. 92. This book was first published in New
York by The Rockefeller University Press in 1978.

E. Chargaff, “Chemical Specificity of Nucleic Acids..."

Experientia v. 6 (1950) cited in Chargaff, Heraclitean
Fire, Pp. e

T.S. Kuhn, The Structure of Scientific Revolutions
(Chicago: University of Chicago Press, 1970), p. viii.
This book was first published in 1962.

Ibid., p. 109.

This distinction between internal and external dependence
on Avery's “Studies...” might heplfully be elaborated on
analogy with J.L. Austin's distinction between the
illocutionary act performed IN saying something and the
perlocutionary act performed BY saying something. See:
J.L. Austin, How To Do Things With Words The William
James Lectures of 1955. (London: Oxford University
Press, 1975), Chapters VIII and Ix.

J.D. Watson and F.H.C. Crick, "“Genetical Implications of
the Structure of Deoxyribonucleic Acid," Nature v. 171
(1953), pp. 964-969. (Olby tells us that this paper was
written "chiefly by Crick...." Daedalus Fall 1970, p.
963.)
78.

79.

80.

81.

82.

83.

84.

85.

86.

87.

88.

48

Chargaff, Heraclitean Fire, p. 106.
Ibid., p. 100.
Ibid., p. 102.
Ibid., p. 102.

Delbruck, in conversation with Judson in Judson, The
Eighth Day..., p. 61.

G.S. Stent, "Prematurity and Uniqueness in Scientific
Discovery" Sci. Am., v. 227 (December 1972), p. 84.

Ibid., p. 86.

F.H.C. Crick, in conversation with Anne Sayre in A.
Sayre, Rosalind Franklin And DNA (New York: W. W. Norton,
1975), p. 214n.

McCarty, The Transforming Principle, p. 227.

My interpretation is closest to that of H.V. Wyatt,
according to whom "...we may extend Stent's use of
‘premature’ and my use of ‘knowledge and information' if
we include a new concept: discovery can be premature if
it is not capable of being extended experimentally
because of technical reasons. Griffith's discovery of
transformation was extended because this was technically
feasible, and in the next 10 years steady progress was
made by Avery's associates at the Rockefeller Institute.
Each step brought Avery nearer to the identity of the
transforming principle. It was only when a new paradigm
was desirable in 1944 that the story seemed less clear."
See: H.V. Wyatt, "Knowledge and Prematurity: The Journey
from Transformation to DNA" Persp. Biol. & Med., v. 18
(Winter 1975), pp. 149-156, esp. pp. 149-150.

For reasons which are not entirely clear to me,
McCarty disagrees with Wyatt. Perhaps he is thinking
that in 1944 it was not impossible to pursue the DNA work
experimentally. This is true. But, as McCarty himself
admits, further work was required before the discovery
could be "...manipulated by the geneticists." See:
McCarty, The Transforming Principle, pp. 227-8.

 

My analysis of the events discussed in this paper was
immeasurably improved by conversations with M. McCarty
and J. Lederberg. Earlier versions of the present paper
profitted from the constructive criticism of M. Grene,
A.G. Bearn, and G.L. Vankin. Detailed suggestions of P.
Choppin proved especially helpful in preparing this final
version.