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238  Reply to Gunther Stent, on the alleged "prematurity"
     of the work of Avery, MacLeod and McCarty in
     "Prematurity and Uniqueness in Scientific Discovery",
     Scientific American, December 1972.
     (submitted to Scientific American, but not published)

     In picturing Avery's work on DNA as an example of a "premature"
discovery, and coupling it with the neglect of Mendel between 1865 and
1900, Gunther Stent (December 1972) is augmenting a myth that deserves
to be corrected.  His statement is "that geneticists did not seem to be
able to do much with it or build on it ... had virtually no effect on
the general discourse of genetics."

     As evidence, he points to the published symposium "Genetics in
the 20th Century", in 1950.  Textual evidence in that volume is ample
to dispose of a parallel between Avery and Mendel; and I can add 
further history from my own experience of a kind that goes unrecorded in
the journals.

     However, this letter will be disservice if many omissions of
important contributors are taken later as evidence that they are not
in mind.  Some more relevant detail can be traced from a recent ex-
change of correspondence in Nature (Wyatt, H.V., Nature 235:86, 1972;
Lederberg, J., Nature 239:234, 1972; Olby, R., Nature 239:295, 1972;
Pirie, N.W., Nature 240:572, 1972).

     To focus first on Stent's remarks the 1950 volume: Mirsky's quarrel
in 1950 with the proof of the purity of transforming DNA has been
quieted by later evidence, but was consistent with the information
then available.  It reflected no lack of comprehension of Avery's
assertions.  Indeed it reflected the conceptual difficulty of thinking
of DNA as an informational molecule so long as chemist's perceptions
of its structure were dominated by the tetranucleotide model.  The
X-ray data of that era had contributed to the confusion.  For example,
Gulland (in 1947) cited Astbury's evidence that "a sodium thymonucleate
fiber is ... built to a regular pattern ... based on a sequence of
nucleotides that is a multiple of four."  But he too was troubled by
the evidence of specificity (citing Avery's work via Muller's review),
and pointed out that even small departures from statistical regularity
could be informationally important.  The structure of DNA was the 
subject of so much assiduous inquiry between 1944 and 1953 precisely 
because the biologists were trying to do more with it than the
chemical traditions seemed to permit.  (Chargaff's remarks at the
1947 Cold Spring Harbor Symposium are a notable example.)

     Indeed, Mirsky was right on the mark in his biological 
interpretation of the pneumococcus transformation, "considering the 
process to be essentially a hybridization".  This speculation, which 
Muller had articulated quite clearly in 1947, in his Pilgrim Lecture, 
"The Gene", actually went far beyond the existing evidence -- Avery 
himself was cautious about offering any biological interpretation 
whatever in 1944.  The first clearcut evidence that any factor other  
than the mucoid capsule could be determined by transferable DNA was 
published by Hotchkiss in 1951.  Meanwhile, other speculations that 
appeared in the 1950 volume were equally valid: for example, Caspersson 
and Schultz thought the DNA might be a non-specific regulatory factor, 
like hertero-chromatin, although other parts of their cytochemical 
study, e.g. on mitosis, clearly point to the identification of DNA with
gene as their working hypothesis.

     Beadle refers to "the new knowledge of transforming principles
[as] another chapter in genetics, and that promises to be among the
most exciting.  It has given chemists new incentive to learn about the
nucleic acids, compounds which everyone recognizes to be extremely
important biologically and about which so little is yet known."  
Evidently the pneumococcus work was so well known that it did not even
require an explicit bibliographic reference!

     In my own commentary, I followed Sonneborn in comparing both the
pneumococcus transformation and virus lysogenicity to cytoplasmic 
factors, a hazy forerunner of the episome concept.  Today we view the 
integration of virus genomes into the bacterial chromosome, as a 
meaningful parallel to the fate of transforming DNA.

     Darlington's discussion of chromosomes becoming protectively 
coated with nucleic acid is most nearly oblivious of the chemistry and 
specificities of DNA, in stark contrast to the clarity of his 
speculation about plasmagenes and viruses, and his bold efforts 
to think ofchromosomes as material, mechanical systems.

     More remarkable than the alleged prematurity of the pneumococcus
work is the short shrift evidently given to work on bacterial viruses
generally.  For the general discourse of genetics, this was at the
frontier of exploration; was it, therefore, also premature?

     Can one find such controversy, such teasing out of alternative
interpretations, such provocation of further investigation and   
hypothesis in the impact of Mendel on biological thought prior to 1900?

     Many other texts could be cited, but the mere fact that Avery,
McCarty and Taylor were invited to speak at the 1946 Cold Spring 
Harbor symposium, and that the 1947 symposium was devoted to nucleic
acids (with Boivin's participation) testifies to the ferment that
these studies had induced.  The original transcripts of the discussions
at those meetings would be richer sources for the intellectual
history of the subject than the sober, edited versions.

     Indeed, the paper by Avery, MacLeod and McCarty, published in
1944, had already elicited a number of further investigations within
the first five years after its appearance.  (That this was perhaps not
true within the "phage group" is testimony to a policy that had a 
certain wisdom at the start -- of ignoring work on systems other than 
the T phages, and focussing on biometrical and biophysical to the 
exclusion of biochemical methodology.  These paradigms resulted in 
brilliant successes, and may have led Stent to identify "the general 
discourse of genetics" with the doctrines of an outstanding group.)

     By a similar principle of egocentricity, my own work looms very
large in my perceptions of the impact of the 1944 paper.  It was 
enthusiastically brought to my attention in January 1945 by Harriet 
Taylor (then a graduate student at Columbia, later to work as a 
postdoctoral fellow with Avery. She is better known by her married name,
Ephrussi-Taylor; her premature death by cancer in 1968, in the prime
of her career was bitterly lamented by many scientific colleagues as
well as her friends.)  At that time I had just returned to my under-
graduate studies after a brief tour of naval hospital service.  Every
biologist at Columbia was well aware of the work -- if only on account
of Dobzhansky's references to it in his monumental "Genetics and the 
Origin of Species"; and I soon appealed to Francis J. Ryan (then an 
assistant professor of zoology, recently returned from a postdoctoral
fellowship with the Neurospora group at Stanford) to work under his 
supervision on the genetic implications of transformation.  (Ryan's
early death in 1963 has deprived us another alert witness and an
extraordinarily fine human being.)  If the Griffith-Avery phenomenon
was indeed a gene transfer, we should try to corroborate this either
by demonstrating it in a "higher" (we would now say eukaryotic)
organism like Neurospora, or by looking for firmer evidence that 
bacteria have genes and a genetic structure like eukaryotes.

     By June 1945, having now started studies at Columbia Medical
School, I also began to work on "transforming" Neurospora.  We used
only the crudest extracts in our first experiments; but no matter, we
soon found that the control cultures were also showing spontaneous
reversions to the wild type, and this phenomenon needed to be cleared
up first.  Remarkably, this had not been analyzed previously -- perhaps
because reversions were nuisances to be avoided in nutritional
studies.  These experiments never were productive of the original goal
of emulating the pneumococcus transformation.  However, they showed
how well selective techniques could be applied to nutritionally 
deficient mutants for genetic analysis. Needless to say, we wrote little
of our negative results nor the original motives.

     As Medawar has pointed out, scientific papers sacrifice personal
truths for the sake of clear exposition of verifiable, public assertions
of scientific fact.  To that extent, intellectual historians must 
beware of relying on such documents; they already know how to be
skeptical of autobiographical rationalizations.

     My medical curriculum included a course in medical bacteriology
that taught the inherent absence of sexual reproduction among bacteria.
Perhaps for this reason, by early July I began to search for sexual
recombinants in E. coli with these selective methods.  The following
year, a fellowship with E.L. Tatum gave me the intellectual and
material environment, and the time, to pursue these studies -- and 
serendipitously the appropriate strain, E. coli K-12, to carry them to
a successful conclusion.

     In our first brief published reports, we referred to Avery only
in the cautionary sense of having tested the E. coli system for 
sensitivity to deoxyribonuclease, to verify that free DNA was not 
involved.  Subsequently, both before I left Yale in 1947 and later at 
Wisconsin, Tatum and I looked hard to find a DNA-transfer system in E.  
coli, especially among strains sent to us by A. Boivin.  However, these 
evidently lost their competence at Strasbourg as well as in the U.S. 
before we could confirm those results.

     The interpretation, if not the initial discovery, of viral 
transduction in Salmonella (with N. Zinder) was deeply influenced by the
pneumococcus precedent.  Indeed we coined the term transduction with
the intent of embracing both phenomena as examples of transfer of genes
by DNA fragments, whether or not encapsulated in a virus particle.

     The Rockefeller group's work was so well entrenched in the general
discourse of genetics that I used the 1944 paper throughout my own
teaching of genetics at Wisconsin.  In 1951, I incorporated it in a
reprint anthology published by the University of Wisconsin Press.
Needless to say, the 1944 work was also cited in many reviews; or else
a later updating article by one of Avery's colleagues might be a more
efficient reference.  The "pneumococcus transformation" was so well
known that it was often cited, or Avery's name used, without a 
specific reference.

     Neither the experimental data relating to the purity of 
transforming DNA, stated in the 1944 paper, nor the genetic concept of 
gene transfer which was perhaps implied by it, were immediately accepted
by the scientific community.  The fact that the critics were wrong in no
way demeans their essential function for the integrity of science.
The net result of skeptical and inquisitive engagement and valid 
controversy over those issues was to elevate the level of falsifiable
assertion that is the essence of scientific inquiry.  Mendel was
ignored until his work was rediscovered.  Avery was challenged on
several fronts, and this helped to spark a conflagration of scientific
effort -- to which many others also lent matches and fuel.  Popular
recognition of Avery's work was delayed, but not egregiously.  Had he
survived a few years longer, there would be little issue about that,
nor then about the alleged prematurity of his work.
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