MACLYN MCCARTY

THE

TRANSFORMING
PRINCIPLE

Discoueeig that Genes Are Mai ofL?NA

A volume of

The Commonwealth Fund Book Program
   under the editorship of
   Lewis Thomas, M.D.

W.W. NORTON & COMPANY

NEW' YORK * LONDON


CONTENTS

   INTRODUCTION                        9

   PREFACE                            13
I THE PREPARATORY YEARS                 19

II THE MEDICAL SCENE                   32
III THE SUGARCOATED MICROBE              51

IV TRANSFORMATION                      72

V ENTER MACLEOD                 89

VI THE RENEWED ATTACK                        101

VII MY INITIATION                       117

VIII INTIMATION 0F SUCCESS                 134

IX THE HOME STRETCH                   150
X STRENGTHENING THE EVIDENCE            172

XI THE FINAL MONTHS                   193

XII AFTERMATH                         213

   BIBLIOGRAPHY                      237

    INDEX                            245


INTRODUCTION

  LTHOUGH EACH NEW CENTURY differs in fundamental
A ways from all preceding periods in history, the twen-
  tieth century seems unique for the overwhelming scale
and scope of the transformation of human life affecting people
everywhere. Some have turned out for the better (human health
and physical ease in the affluent societies, for example), some
for the worse (the fouling of our planetary environment and
the massively lethal machines of warfare, for example). One
way or another, most of the changes are generally believed to
have been the result of science, in this most scientific of all
centuries, and of the technologies that follow inevitably in the
wake of scientific advance. For better or worse, our lives and
those of our children's children are seen as hostages to this
relatively new way of looking at and into nature, a method of
thinking and working that had its beginnings only a few cen-
turies ago and now dominates all human commerce.
The scientific method, as it is commonly termed, seems to
many educated laymen an arcane, stereotyped set of rules for
intellectual behavior, so specialized as to lie beyond the com-
prehension of ordinary people. We are in the hands of the
scientists, so it goes, and we do not understand what they are
up to, nor how or why they do what they do, nor most


10                          introduction

unnerving of all, can we guess what they are likely to do next.
In this atmosphere, there is need for new sources of insight
into the mind of science, and into the minds of individual
scientists. What motivates them and drives them along
enchanted by what can in real life be the most frustrating of
human occupations ? How do they go about selecting the
problems they wish to study? As they work, do they move
from the facts at hand to hard truths, or do the facts come in
as astonishments after a truth has been guessed at? Is the
profession of science a self-limited endeavor, and will it, sooner
or later, come to an end with all the answers in hand? Or is
it, as I would guess and hope, a permanent fixture in human
endeavor, likely to go on forever, each puzzle solved raising
new, unpredictable puzzles.

The Commonwealth Fund, in its wisdom, has committed
resources for the sponsorship of a series of books to be written
by working scientists about their own work, for a general, lit-
erate readership. The books being planned (some of them
already being written) will deal with the broadest range of
research domains, ranging from cosmological physics and
planetary biology to molecular genetics and cell biology. The
writers are authorities in their various fields, caught up in the
excitement of their own investigations, and capable of clear
and (mostly) nontechnical prose.

This book, by Dr. Maclyn McCarty of Rockefeller Univer-
sity, is the first in The Commonwealth Fund Book Program
series. It deals with the discovery by Avery, MacLeod, and
McCarty in the 1940s that genes are made of deoxyribonu-
cleic acid (DNA). This single discovery opened the way into
the biological revolution which continues to transform our view
of nature in the most intimate details, and continues as well
to cast up, in its wake, one biotechnology after another for the
comprehension and, it can be hoped, the reversal of human
disease processes.

The selection of this book, and of those which will follow
in the years immediately ahead, has been the responsibility


Introduction                                         11

of the Advisory Committee of The Commonwealth Fund Book
Program: Alexander G. Bearn, M.D., Professor of Medicine
at Cornell University College of Medicine and Senior Vice
President for Medical and Scientific Affairs, Merck Sharp &
Dohme International; Donald S. Fredrickson, M.D., Presi-
dent, Howard Hughes Medical Institute; Lynn Margulis,
Ph.D., Professor of Biology, Biological Science Center, Bos-
ton University; David E. Rogers, M.D., President, The Rob-
ert Wood Johnson Foundation; Berton Rouech6, Writer;
Frederick Seitz, Ph.D., President Emeritus, The Rockefeller
University; Otto Westphal, M.D., Director Emeritus, Max-
Planck Institute for Immunobiology; and Edwin Barber, Vice
President, W. W. Norton & Company, Inc. The Managing
Editor is Helene Friedman.

The Editors and Advisory Committee are happy to ack-
nowledge the constant interest and intellectual support of
Margaret E. Mahoney, President of The Commonwealth
Fund.

LEWIS THOMAS, M.D.
Editor and Program Director
President Emeritus, Memorial
  Sloan-Kettering Cancer Center
University Professor, State University
of New York at Stony Brook


PREFACE

F ORTY YEARS HAVE PASSED since Oswald T. Avery, Colin
  M. MacLeod, and I published our paper identifying the
  substance responsible for the transformation of pneu-

mococcal types as deoxyribonucleic acid (DNA). Because of
the nature of pneumococcal transformation, this finding car-
ried with it the implication that DNA must be functioning as
a carrier of genetic information, and the paper thus presented
the first experimental evidence for the nature of genetic mate-
rial. We had presented the experimental data with a mini-
mum of interpretation and speculation, raising the question
in the minds of some whether we really understood the sig-
nificance of our findings. Many years went by, however, before
MacLeod and I even got around to discussing the possibility
of writing the story of the discovery in an attempt to clarify
the sequence of events and our interpretation of them. We
never got very far with this. I had too many other obligations
even to contemplate the job. On one occasion, in 1969, Colin
thought that he had enough free time to tackle it, and he asked
me to make the laboratory notes available to him in a room at
the Rockefeller Hospital. I was happy to comply with this
request, which was based on his conviction that the notes should
not be moved from the institution. However, he soon became


14                       Preface

involved in other activities that effectively nipped his literary
efforts in the bud. When he died in February 1972, he had
managed little more than a few preliminary notes. He wrote
me in late 1971 that he had found it necessary to put the whole
matter aside once again.
I don't believe that Avery had ever considered writing.such
a book. Any interest he might have had was lost long before
he finished his active work in the laboratory. On the other
hand, even before the DNA work had come to fruition, he
liked to talk about the book that he could write about that
"wonderful little bug," the pneumococcus, the object of most
of his investigative career. The story would center on devel-
opments that came from his earlier discovery that the impor-
tant capsule surrounding the pneumococcus is composed of
complex sugars, and he had selected a catchy title for his
imaginary book: "The Sugarcoated Microbe." I have chosen
to perpetuate this felicitous designation by using it as the title
of my Chapter III.
I was not able to get down to a serious effort in writing the
story until after I had reached emeritus status at Rockefeller
University. The question was: what kind of book should it be?
There was no doubt that it had to be my story, since I could
not speak directly for the inner feelings of my colleagues. At
the same time, I felt that it was important to write it in a way
intelligible to the general reader-that is, to anyone who had
any interest in reading about the discovery. Soon, however, I
began to have difficulties dealing in a simplified manner with
the technical aspects of the research. Since I am convinced
that some information about the pneumococcus (and about
the biochemical and immunological approaches used in the
research) is essential for an understanding of the events that
led to our discovery, I have persisted in the attempt to pro-
vide what I believe to be the necessary background. I realize
that there is some danger that the product of this effort will
not be satisfying either to the general reader or to the biolog-
ical scientist, too technical for one and too oversimplified for


Preface                                 15

the other. I can only hope that the general reader, condi-
tioned by the increased sophistication of science reporting in
the daily press and in the many popular science magazines,
will not be deterred by the technical detail that is included.
The young scientist is not often imbued with a sense of
history relating to his activities, and indeed it has often been
suggested that he should not be if he is to get on with creative
work in his field. Any effort, however, to recapture the details
of a path of research some forty years after it took place will
soon make one acutely aware of how valuable it would be to
have profuse letters, notes, and diaries of the time. I have
only a modicum of these materials and have therefore relied
heavily on laboratory notes and reports, which tend to be not
only impersonal but usually lacking in any description of the
rationale and motivation for the experiments undertaken. Any
success in reconstructing the events, therefore, without
resorting to guesswork or a shaky memory, has been the result
of a careful review of my various sources and an analytical
interpretation of the factual data and chronology. I have man-
aged to eliminate some errors and misconceptions, but any
that remain are entirely mine.
I am indebted to Miss Carolyn Kopp, Archivist, and Mrs.
Sonia Mirsky, Librarian, at Rockefeller University for making
available to me a complete set of the reports to the Board of
Scientific Directors of the Rockefeller Institute for Medical
Research from 1928 to 1948. Miss Kopp also generously pro-
vided me with a number of items from the archives relating
to Avery. I am grateful to the Tennessee State Library and
Archives in Nashville for giving me access to the Avery Papers
in their possession.
I am happy to acknowledge the support provided by the
Alfred P. Sloan Foundation in the early phase of writing this
book. Throughout the later phases I have enjoyed the encour-
agement and generous support of the Commonwealth Fund
Book Program. This has been an important factor in sustain-
ing my efforts, and I deeply appreciate the confidence shown


16                       Preface

by the Commonwealth Committee, under Lewis Thomas, that
reviewed the early drafts.

Finally, I owe a special debt to my wife, Marjorie. In addi-
tion to the encouragement and support she gave me during
the writing of the book, when I was often plagued by doubts,
she proved to be an extraordinarily sharp-eyed proofreader at
each stage of the process.

New York 1984


   THE
TRANSFORMING
PRINCIPLE


I

THE PREPARATORY
   YEARS

S URELY NO ONE is prepared to discover a faulty memory.
It comes as a shock to be presented with incontrovertible
evidence that one's recollection of a distant experience is

faulty at best. Recently my older brother showed me a pocket
diary-appointment book that my father kept in 1929, the year
I started college. Among the notes that he had jotted in this
book were the results of tennis and golf games with family
members during the spring and summer of that year in Port-
land, Oregon. My father, a keen competitor, indicated the
players, the winners, and often the scores of these matches,
and there were numerous entries recording my participation
with him in both games. The difficulty is that, while I remem-
ber the tennis clearly, I have no recollection whatever of hav-
ing played golf in Portland, and this unchallengeable reminder
has done nothing to rekindle the memory or to conjure up
tee, green, or clubhouse.

I have had enough additional indications of these memory
gaps to approach the matter of my early history and the events
that determined the path of my career with some caution. I
have been able to find little in the way of other diaries or


20              The Transforming Principle
documents that I can rely on to provide factual information.
However, I can be certain it was sometime in childhood that
I became set on the course that led me into medical science
and ultimately to Avery's laboratory at the Rockefeller Insti-
tute for Medical Research. It is apparent, also, that my deci-
sion to become a doctor came too early to have been based on
fully rational considerations. Although I have no personal rec-
ollection of the time that this idea became fixed, I have the
assurance of my mother that it was at least by the age of 10.
A few years later, when I was in junior high school, I can
recall not only that I had no doubts about being headed for a
career in medicine but also that in my mind this had already
come to mean medical research.
The origin of my precocious interest in medical science
remains obscure. I can identify nothing in my environment as
a child or any specific episodes that may have given rise to it.
It seems likely to me now that it came from something that I
had read, but I do not have a clue as to what that might have
been. Paul de Kruif's Microbe Hunters, a book that influ-
enced many of my generation, was published in 1926 when I
was already in high school and it thus came much too late to
have initiated the process. My copy of Microbe Hunters was
given to me by my parents for Christmas in 1929. (Actually, I
had read it earlier after obtaining it from the public library.)
At a minmum, the book served to reinforce my determination
to prepare myself for medical research and it also led to other
reading, such as Rene V. Radot's The Life of Pasteur.
There was little precedent in my family for a career in
medicine or science, or, for that matter, for advanced educa-
tion of any kind. The only exception that I know of was a
maternal aunt who attended a proprietary medical school in
Fort Wayne, Indiana, one of the kind that disappeared in the
first quarter of this century during the revolution in medical
education that followed publication of the famous Flexner
report, She died tragically, before receiving her medical degree,
from septicemia resulting from a cut suffered while perform-


The Preparatory Years                                21

ing an autopsy. The other members of the family on both sides
were forced by circumstances to curb any educational aspira-
tions they may have had. My mother and father were born in
small villages in northern Indiana, and both had to leave school
after the eighth grade to help support their families. They
made the most of their limited school experience and supple-
mented it with reading so that their fund of information was
much broader than one might have expected. My mother could
recite from memory more poetry than I have ever known and
she could also quote long passages from Shakespeare. She
transmitted her love of literature and knowledge to her sons,
and I can remember her reading regularly to my older brother
and me during our preschool years. This early introduction to
the world of books resulted in our becoming avid readers on
our own. Our reading ranged from a series of adventure sto-
ries for boys to considerably more substantial fare, such as the
books of Booth Tarkington, Mark Twain, James Fenimore
Cooper, and Alexandre Dumas p&re. Some clue as to the tim-
ing of our selection of this reading material comes from an
incident which occurred in 1920, when we were 11 and 9,
relating to the naming of our newly arrived next younger
brother. We were invited to suggest a name and came up with
"Raoul," the hero of The Vicomte de Bragelonne, which we
had encountered in reading this lengthy sequel to The Three
Musketeers and Twenty Years After. Fortunately, it became
obvious that we had no idea how the name was pronounced,
and "Raoul" was dropped as a possibility.
It seems apparent now that this home environment clearly
fostered the kind of aspirations that I later developed, even
though I cannot detect the origin of the stimuli that generated
the specific interest in medicine. My primary education was
more than adequate, but perhaps a little unusual. I attended
a total of five different schools in three cities before finishing
sixth grade, providing a diverse experience which I believe
was much more positive than negative in its impact. This view
is in contrast to the one widely held by the time my own


22             The Tran.sforming Principle
children attended school, when we frequently heard P.T. A.
members express the conviction that moving from school to
school was disastrously disruptive to the educational and psy-
chological development of the child. My mother's reaction on
learning of this view was to be glad that she did not know at
the time that our peripatetic education was supposed to be
bad for us. In retrospect, I don't believe that it was difficult
to make the necessary adjustments, and we had the advantage
of learning how to cope with change at an early age, as well
as that of the broadening effect of varied educational
approaches.
This itinerant schooling had to do with my father's occu-
pation. He had gone to work for the Studebaker Corporation
in South Bend in the early 1900s when its major activity was
the manufacture of horse-drawn vehicles. The company main-
tained a network of factory branches for the national distri-
bution of its products and, after he had worked his way up in
the sales division, my father was sent to Portland, Oregon,
when I was three years old, as the assistant branch manager.
Although he was greatly attracted to Portland and the Pacific
Northwest, he was also increasingly aware that the future of
Studebaker lay with the automobile and he requested transfer
from the horse-drawn vehicle division. As a result, in 1915 we
moved to Dallas, Texas, for his first assignment in automobile
sales, but in less than two years we were back in Portland
where he had been appointed manager of the automobile
branch.
It was in Portland on this second sojourn that I started
school in 1917. When my mother took me to be enrolled in
the neighborhood school it was her intention to place me in
kindergarten, since she had been conditioned by her experi-
ence with my older brother in Dallas to expect regular school
to begin at the age of seven rather than six. However, the
school had no kindergarten, and it took some persuasion on
the part of the teacher, as well as some pleading on my part,
before she allowed me to remain as a first-grader. The lack of


The Preparatory Years                       23

a kindergarten was symptomatic of the primitive stage of
development of this new neighborhood school, composed as
it was of temporary structures which for some obscure reason
were referred to as "portables." My first schoolroom had six
rows of desks, one for each of the ha&grades from one through
three, and one teacher managed the whole operation in a
manner reminiscent of that described in rural schools and
pioneer communities. It was almost impossible for an alert
pupil not to be aware of what was going on in the higher grades,
and it was an easy matter to skip a half-grade, as I did, simply
by sliding over to a seat in the next row. This move had rela-
tively little impact except to put me out of phase from then
on as a mid-termer. Nevertheless, despite the questionable
quality of this kind of compressed schooling by modern stan-
dards, it apparently provided me with a more than adequate
grounding in the traditional three R's.
Moves to new homes served by larger, better-established
schools brought me to third grade and a more drastic move
back to South Bend, Indiana, and still another school where I
remained through half of the sixth grade. At this point, in the
summer of 1922, my father left Studebaker and accepted a
new position with Nash Motors in Kenosha, Wisconsin, where
I completed sixth grade in my fifth grammar school. The next
stage of junior high school in Kenosha continued to provide a
more than adequate academic environment along with some
rather unusual special features, such as an imaginative pro-
gram in music appreciation and access to a fully equipped
printing shop. The latter was under the supervision of a full-
time teacher who, in addition to teaching the fundamental
skills of printing, directed interested students in producing
the magazine for the three city junior high schools. Learning
to set type, operate the press, and understand the elements
of typography are among my fondest memories of this period.
Toward the end of this junior high school experience, my
public school education was interrupted by a year at the Cul-
ver Military Academy, in 1925-1926. Situated in an area close


24              The Transforming Principle
to that in which my parents were raised, Culver was well known
in the northern Indiana community and enjoyed a reputation
for high academic standards as well as for character-building.
Influenced by this, my father obviously felt that it would greatly
benefit my brother and me to continue our educations in this
setting. The experiment was less than an unqualified success.
While I formed a poor impression of the school's vaunted aca-
demic excellence, I must confess that this view was influ-
enced by a distaste for the traditional military academy aspects
of the place, even though these were cushioned for my brother
and me. We were assigned to the band, which was a separate
unit at Culver, occupying its own barracks and replacing with
band practice the long afternoon hours of military drill of the
regular companies. My appreciation of this situation was tem-
pered by the fact that I was not particularly adept at my cho-
sen instrument, the trumpet. There were sixteen trumpets in
the band that year. I was relegated to the sixteenth chair play-
ing fourth-trumpet parts, which for the most part consisted of
counting innumerable measures of rest and coming in-almost
on time-with a single note.
There were other negative aspects to Culver, such as haz-
ing of the first-year "plebes," a practice borrowed from West
Point; but what bothered me most was the overall flavor of
the place, perhaps best illustrated by the way we were greeted
by fellow cadets upon arrival: "What did you do to get sent
here?" This attitude and the qualities it implied weakened
any appreciation I might have had for the school's merit's,
academic or otherwise. In the end, a series of events, includ-
ing a period when my brother went A.W.O.L., made it evi-
dent to our parents that we lacked enthusiasm for military
life. We were allowed to return to the familiar setting of the
public school the following year.
During my two and a half years in Kenosha High School I
began to plan more seriously for training in medicine. At this
time, in the late twenties, it was the perception of the lay
public that the medical school at The Johns Hopkins Univer-


The Preparatory Years                      25
sity was the place that medical research and researchers were
produced. I adopted the premise. This view had certainly once
been valid, since in the late nineteenth century the medical
school at Johns Hopkins was unique and the first in the United
States with a strong scientific and academic base. However,
by 1925 Hopkins had several rivals in the field. I was of course
unaware of this and never considered applying to any other
medical school.
Accordingly, my first move as a high school student intent
on planning ahead was to send for the Johns Hopkins cata-
logue. From this I learned that among the requirements for
admission to its medical school were a bachelor's degree and
a reading knowledge of both French and German. Kenosha
High School, while providing an admirable educational back-
ground in most respects, had certain limitations. It had, for
example, failed to reinstitute the teaching of German after
dropping it in a fit of patriotic fervor during World War I. I
was sufficiently anxious about this impediment to my progress
in fulfilling the Hopkins requirements that I arranged to take
private lessons in German for a year from the assistant prin-
cipal of the parochial German Lutheran school in Kenosha.
Clearly this was unnecessary, since I would have had no dif-
ficulty satisfying this requirement during my college years,
but I have had no occasion to regret the time spent in getting
this firm basis in German frotn a knowledgeable tutor. In a
somewhat similar vein, I was concerned about the mathemat-
ics curriculum at the high school, which did not go beyond
advanced algebra, so I was motivated to arrange for trigonom-
etry lessons during the summer from one of the teachers at
the school.
In retrospect this behavior strikes me as overzealous and
suggests that I may have had some of the attributes of an intol-
erable grind. However, this is an inaccurate picture, since I
had many other interests and found time for frequent tennis
and swimming, for playing in the high school band (with, alas,
no notable increase in skill over my efforts at Culver), and for


26              The Transforming Principle
dating, dances, and parties. In fact, from my present vantage
point over fifty years later, I find it difficult to believe that my
friends and I were able to pack all of this activity into our daily
lives, a reaction that no doubt merely reflects the usual lack
of comprehension on the part of the aging for the energy of
youth. I had also set up a chemistry laboratory in my base-
ment, and three of my classmates, each with his own home
lab, joined me in forming a club that we called the Amateur
Research Chemists. The key word here is "amateur," since
we were certainly inexperienced and generally incompetent
as chemists, creating some hazard to ourselves and others. As
a result of our access as alumni to that junior high school
printing press, we even had a letterhead, with a heading in
Gothic type proclaiming "The A.R.C. Club" and a definition
of the initials in parentheses below, but no address other than
"Kenosha, Wisconsin." We all had chemicals which we prob-
ably shouldn't have had-1 recall my bottles of both sodium
and potassium metal stored under kerosene-and one of my
friends managed by the use of this letterhead to acquire things
from J. T. Baker Chemical Co. that I doubt he could have
obtained without it. One of my memories of this period is of
spilling liquid bromine on his head while I was in the process
of trying to open his newly acquired bottle of this corrosive
element. This was quickly washed away without harm, and in
general we survived our inept excursions into laboratory sci-
ence, although I did sustain a rather severe burn of one hand
from hot sulfuric acid. These experiences contributed to my
learning-the hard way-that maintaining laboratory safety is
one of the first principles of research.
In contrast to the clear recollection of the reasons for the
early selection of Johns Hopkins for my medical training, I am
totally blank on the subject of what led me to choose Stanford
University for premedical education. It certainly had nothing
to do with the family move back to Portland, Oregon, for the
third time in March 1929, one month after my graduation from
high school. My application to Stanford-I overconfidently filed


no other-had gone in before I knew of the decision to move.
That decision on the part of my father to return to his beloved
Portland proved to be badly timed, and by the end of my first
year at Stanford we were on our way back to Kenosha again.
Portland had become economically depressed even before the
October 1929 stock market crash and, finding little in the way
of opportunity for his contemplated new business activity, my
father had become increasingly receptive to Nash's offer to
return as vice-president and general manager, with the clear
understanding that he would become president in the near
future.
Whatever considerations led me to Stanford, the result
was fully satisfactory. The school had not attained its current
national reputation and was populated principally by Califor-
nians. But it had high academic standards and a distinctive
flavor which set it apart from schools on the East Coast. The
unique architecture of its buildings, which covered only a small
segment of its extensive campus, together with the benign
climate and unusual vegetation, contributed to this flavor.
There was also, however, an informal air and a sense of per-
sonal freedom that reflected the university's German motto:
Die Luft da- Freiheit weht. All in all, it seemed a felicitous
environment for the next stage of my preparation for medical
science.
Within the limits imposed by the Stanford curriculum for
students in the "Lower Division"-that is, freshmen and
sophomores-I still kept my eye on those requirements for
admission to The Johns Hopkins Medical School, getting an
early start on more French and German as well as on mathe-
matics and the biological and physical sciences. From the point
of view of preparing for future research on the pneumococcal
transforming substance, the most important step was a sec-
ond-year decision to major in biochemistry. Biochemistry at
Stanford in those days bore little resemblance to the large and
diverse departments in universities today. It was a part of the
Chemistry Department, not a separate unit, and stalled by a


28              The Transforming Principle

single faculty member, Professor James Murray Luck. All of
the lectures in the general biochemistry course, which was
required for the first-year medical students who consituted
most of the class, were given by Luck, and he ran the associ-
ated laboratory course with the aid of one graduate assistant.
My additional activities as a biochemistry major included spe-
cial experiments in the laboratory, an evening seminar held
every week or two at Lucks home in Palo Alto, and finally a
full-time research project during the last quarter of my senior
year.
Dr. Luck at this period was launching the Annual Review
of Biochemistry. Its first volume appeared in 1932. This series
remains an important reference source in the field today, and
furthermore it spawned the development at Stanford of annual
reviews in more than twenty other fields of science. Thus, it
has become a major enterprise in scientific publishing. Early
on, Luck would carry galley proofs of the reviews in his pocket,
and more than once he gave me marked sections of the galley
to indicate the references that were to be my assignment for
reporting at the seminars. I have kept my copy of Volume I
of the Annual Reviews for its historical interest. In the context
of the DNA study, the most interesting feature of this seven-
hundred-page volume is the almost total absence of any dis-
cussion of the nucleic acids. The study of this component of
living tissues simply was not a popular field of biochemistry
fifty years ago.
My first real taste of laboratory research came toward the
end of my last year at Stanford. The project that Luck out-
lined for me had to do with liver proteins. Specifically, did
the considerable increase in the size of the liver in animals fed
on high-protein diets involve storage of specific proteins or
simply overall growth of the organ? The experimental animals
were rats maintained for a few weeks on either high- or low-
protein diets and then sacrificed so that the liver could be
removed, extracted, and separated into fractions for analysis


The Preparatory Years                         29
of protein components. I can't say that I was greatly intrigued
by the problem even at the time, but it did provide a consid-
erable breadth of experience in laboratory activity. I prepared
the special diets, tended the rats during the experimental
period, carried out the operative procedures that included
perfusion of the liver with salt solution to remove excess blood,
and then proceeded to the extraction, fractionation, and analysis
of the material. The poor definition of the separated liver pro-
tein fractions was probably the weakest aspect of the study,
depending as it did on differential solubility properties. The
most demanding part of the research was analysis of the pro-
tein content of each fraction by the Kjeldahl method. This
involved digesting the samples in strong acid to convert the
nitrogen of the protein to ammonia, followed by distillation of
the ammonia and its accurate quantitative measurement by a
titration procedure. My difficulties in setting up the array of
apparatus for these analyses left me with a strong distaste for
the Kjeldahl method which I have never lost.
This was my first experience with laboratory animals, and
the rats and I did not become completely comfortable with
one another in the course of the project. The cages were quite
deep, making it necessary to reach to the back rather blindly
at arms length in order to grab an animal with a gloved hand.
Naturally resenting this intrusion, the rats tended to counter
by biting a gloved finger. The gloves prevented any real dam-
age, but I generally emerged from these encounters so shaky
that it was difficult to get on with the operative procedures,
particularly the perfusion of the liver, which called for a steady
hand to get a needle into the small portal vein.
The outcome of this research indicated that all of the sev-
eral poorly defined protein fractions were increased in livers
of rats on the high-protein diet and thus suggested that growth
of the liver rather than simply storage of protein was involved.
However, it was obvious that in only ten weeks of that final
quarter at Stanford I had not completed the type of well-con-


30              The Transforming Principle

trolled experiments required for definitive answers. Dr. Luck
had departed before the end of the quarter for a summer at
Cambridge University, where he had received his early train-
ing. I was to mail him a report of the work when I was fin-
ished. I still have my copy of this report, and a thin and
amateurish document it is; but at least it does not go beyond
the limited data in reaching conclusions. Luck later returned
to this project in a more extensive and sophisticated study
that he published in The Journal of Biological Chemistry' in
1936. When I saw this paper I derived some comfort from the
trend of the overall results. They did not differ greatly from
those of my preliminary and incomplete efforts. The experi-
ence, despite its frustrations, had at least done nothing to shake
my determination to pursue the goal of medical research.
Having not lost sight of this goal, I completed my appli-
cation for admission to the medical school at Johns Hopkins
during the Christmas holidays in 1932 and received acknowl-
edgment of its receipt in early January. Dr. Luck tried to per-
suade me to alter my plans and apply to Stanford Medical
School, but I had encountered nothing that weakened my
determination with respect to Hopkins and ended by submit-
ting again only the single application. Late in January 1933 I
was asked in a letter from the assistant dean at Johns Hopkins,
Dr. E. Cowles Andrus, to "arrange for an interview with the
regional representative of the Committee on Admissions, Dr.
Emile F. Holman, Stanford University Hospital, San Fran-
cisco, California." Dr. Holman was professor of surgery and a
Johns Hopkins graduate who had trained under the great
Halsted, one of the "big four" of the early years of the Hop-
kins medical school. My appointment with Dr. Holman was
at 3:30 in the afternoon on February 8. Despite the hour, it
appeared to fall in the middle of his operating schedule since
he appeared in his office for the brief interview in a surgical
scrub suit. He was friendly enough to allay my mounting ner-
vousness, intensified by the sense of interrupting a busy
schedule, but I left with no idea whether I had made a favor-


The Preparatory Years                       31

able impression. Fortunately for my peace of mind, things
moved rapidly in the Hopkins admitting office in those days.
A letter dated February 21, 1933, from Dr. Andrus told of my
admission "to this Medical School contingent upon your com-
pleting the courses which you are now pursuing at Stanford
University." Having cleared this important hurdle, I faced the
final months at Stanford in a relaxed mood.


II

THE MEDICAL
  SCENE

  FTER A largely midwestern upbringing and four years
A at Stanford, arrival at the East Baltimore setting of The
   Johns Hopkins University School of Medicine gave rise
to something like culture shock. I had never seen anything
like it. In every direction from the school the streets pre-
sented a line of attached row houses. All boasted the same
simple design in red brick, built flush with the sidewalk and
unrelieved by the softening influence of lawns and trees. I
knew no one in Baltimore or in my incoming class at the med-
ical school with whom I could seek diversion during those first
few days to shake off the depressing effect of the strange envi-
ronment. There were no dormitories for medical students,
and my rental room on the third floor of a row house on North
Broadway did not ease the depression. An episode connected
with the renting of this room pointed up some of the more
parochial aspects of my early experience despite the moving
about that I had done in the West and Midwest. After I decided
to take the room on a late September afternoon, I tried to pay
my new landlady the agreed-upon monthly amount in advance.
She declined the cash, saying that she could not accept money


The Medical Scene                           33

on that day because it was Yom Kippur. I was totally mysti-
fied, having never heard of this or the other Jewish holy days
and knowing nothing of the rules for their observance. I was
clearly about to have my horizons broadened.
Eating was also a problem in East Baltimore, which offered
little attraction to the enterprising restauranteur. Although I
had arrived determined not to get involved with a Greek-let-
ter society as I had at Stanford, the blandishments of the med-
ical fraternities, for nothing else than to serve as an eating
club, became hard to resist. My doubts were sufficiently deep-
seated, however, that I consulted the dean of the school for
advice and reassurance before joining a fraternity. The activ-
ities of the fraternities in their quest for new members had
the salutary side effect of getting the new students acquainted
with one another, and in that manner I found a group of con-
genial colleagues who helped dispel my black view of East
Baltimore.
It was at one of the "rushing" affairs of a medical fraternity
that I got my first indication that Johns Hopkins was not quite
the ivory tower of medical research that I had fondly sup-
posed it to be. A graduate member of one of the fraternities,
then a resident in gynecology, who had written to me during
the preceding summer on behalf of his fraternity, engaged me
in conversation about my plans for the future. When I told
him that I planned to go into medical research, he laughed
and responded: "That's what they all say. You'll change your
mind before you finish. " Although I considered this a frivo-
lous and unreliable comment, there is no doubt that there was
more than a germ of truth in his implication that the emphasis
on research that I had anticipated no longer existed. Only two
or three members of my class of seventy have devoted their
careers to research.
The most effective antidote for my distaste for the new
environment in which I found myself was being immersed in
the demanding curriculum of a first-year medical student. Gross
anatomy, the dominant part of the beginner's course, soon


34              The Transforming Principle

presented a real challenge because of the inherent difficulty
of .sorting out the complex interrelationships between the
numerous structural components of the body, all with unfa-
miliar Latin names. One could not fully understand the course
and distribution of a nerve or blood vessel without at the same
time knowing something of the organs it served and the struc-
tures through which it passed. This dilemma sent the student
ranging through the anatomy textbook from one section to
another in a frantic attempt to get some kind of integrated
picture. It is not easy to find much in the way of intellectual
stimulation in the study of anatomy, but there is no doubt that
it supplies information essential for dealing with the more
dynamic problems of function.

My principal relief during this first term from activities
such as dissecting a cadaver and poring over anatomy text-
books and atlases came from the opportunity to resume the
study of biochemistry that I had begun at Stanford. At Hop-
kins the department and the course were called "Physiologi-
cal Chemistry," but this represents only the most trivial of
the several differences between the teaching of biochemistry
at the two schools. There were at least three full-time and
relatively senior faculty members in addition to the head of
the department, Dr. W. Mansfield Clark, as well as a number
of graduate students; and teaching was definitely not a one-
man show as at Stanford. Dr. Clark clearly put his stamp on
the character of the course, however. His emphasis on the
physical-chemical aspects of the subject resulted in the pre-
sentation of a picture of biochemistry which was completely
different from the one I had gotten at Stanford. Nevertheless,
the two courses complemented each other in a way that
increased the breadth of my exposure to the subject.

In recognition of my previous experience at Stanford, I
was not required to participate in the laboratory exercises in
physiological chemistry but was permitted instead to under-
take a special laboratory project under the direction of one of
the professors, Dr. Leslie Hellerman. This could hardly be


The Medical Scene                         35

called research, since the assignment that Dr. Hellerman gave
me was to try to repeat some experiments on the purification
of heparin, the blood anticoagulant, that had recently been
published in The Journal of Biological Chemistry.' Nonethe-
less, the techniques and procedures required in the work were
sufficiently diverse to expand my laboratory experience. The
experiment began with the extraction of crude heparin from
beef liver-liver seems to have been the dominant theme of
my early laboratory experience, but I have scarcely touched
it since, even as food-and the original workers dealt with
one-hundred-pound lots. Since we did not have the facilities
for working on this scale, I limited my efforts to tackling twenty
pounds of the organ at a time, which was quite enough. Some
weeks and numerous purification steps later, I wound up with
a small amount of white powder which still smelled remark-
ably like liver but had a fair amount of anticoagulant activity.
It did not, however, have the crystalline properties that the
original authors had described for their preparations. In later
years I labored under the inaccurate impression that they had
claimed in their papers to have crystallized heparin, and I
used this on occasion as an example of how skeptical one has
to be of published results, even when they appear in the best
scientific journals. Heparin has not yet been crystallized. Nor
is it likely to be, because it is now known to belong to a
class of substances with the technical name of sulfated
glycosaminoglycans, which are not amenable to crystalliza-
tion. On reexamining these papers almost fifty years later, I
find that the authors had carefully avoided this claim and cited
reasons to doubt that their crystals represented heparin itself.
The lesson I learned about scientific skepticism was thus sup-
planted by another: it is important to check one's facts before
drawing conclusions.

This heparin episode was my last fling at extracurricular
laboratory activity for some time to come. I did not seek
opportunities to engage in research projects during freetime
and summer vacations. Such opportunities were quite rare


36              The Transforming Principle

anyway in the pre-World War II medical school but also I
had made the decision to restrict my efforts to completing the
regular course work and to come back to research on a full-
time basis once this was done. The demands of the medical
curriculum were great enough to justify this as a realistic
approach. Hopkins had a long tradition of having no exami-
nations or quizzes during the first two years (and of supplying
no grades to the students at any time). During one week at
the end of the second year comprehensive written and oral
examinations were held in all of the preclinical sciences: anat-
omy, biochemistry, physiology, pharmacology, bacteriology,
and pathology. This struck me as an advanced and sensible
way of conducting the business of education, but no doubt it
imposed an intolerable stress on certain members of each class;
largely for this reason, I believe, the system was abandoned
the year after our class completed the exercise. Our clinical
courses during the next two years were also given without
formal examinations until the end of the last year, but this
seemed to create fewer problems for us, probably because the
subject matter was more pragmatic and less theoretical. A
record of our performance in each course, in lieu of grades,
was kept on file in the dean's office, closely guarded as confi-
dential data. This posed some difficulties for the active mem-
bers of the honorary medical society, Alpha Omega Alpha,
when they met each year to elect new members from the sen-
ior class. A senior member of the faculty had to attend with
copies of the necessary records. As each name was proposed
he would indicate without divulging any details whether the
candidate's academic record justified his being considered for
membership. My election to Alpha Omega Alpha was about
the only measure I had of my performance.

Since I had started Stanford less than a month before the
Black Tuesday debacle in 1929, essentially all of my premed-
ical and medical education came during the Great Depres-
sion. I was sheltered from its impact and never threatened
with interruption of my schooling through lack of financial


The Medical Scene                           37

support from my parents. Furthermore, I rarely read the
newspapers deeply or discussed economic or political topics
with my colleagues. As a result I was only vaguely aware of
the overwhelming impact of the economic collapse, and later
almost equally detached from reports of the growing clouds of
war in Europe. It was not that I was unconcerned, simply
poorly informed and preoccupied with other things.
The Hopkins students who did not have to work during
the summer holidays in the mid-thirties, or those who were
not lucky enough to find jobs, had the choice of relaxing to
recover from the rigors of the previous year or of seeking some
activity to supplement their medical education. I did a little
of both. I began the summer after the first year by getting
married. The event underscores the generosity of my parental
support and placed me in an unusual position with my fellow
students. Married medical students are commonplace today,
but there was only one other married member of my class at
the time. Aside from getting me out of East Baltimore, since
I had no intention of asking my wife to live in that area of the
city, I do not believe that my marriage changed the course of
my medical training. Being unaware that the authorities took
a dim view of early marriages, particularly at the postgraduate
level of internships and residencies, I had asked no one's per-
mission. Still later I found that there was even more explicit
disapproval at the Hospital of the Rockefeller Institute for
Medical Research. Both the original director and his succes-
sor, who held the post until 1955, subscribed to the view that
the aspiring medical scientist should defer marriage until he
was well established, being wedded in the meantime to the
research laboratory. However, this general attitude was
beginning to erode even before the war, and my marital status
never proved to be a handicap for me.
After a honeymoon trip by automobile that summer, I also
drove to Rochester, Minnesota, intending to find some med-
ical activity for vacation time the following year. I found that
the head of surgical pathology at the Mayo Clinic, Dr. Wil-


38              The Transforming Principle
liam Carpenter MacCarty (no relation, but a Johns Hopkins
graduate), had the custom of taking on a group of medical
students each summer for experience in his specialty. He
agreed to include me in the next group. Again I had done this
without consulting anyone at Hopkins, and I was shaken a
little by the reaction of my examiner in pathology during the
hectic week at the end of the second year. My oral examina-
tion was given by the head of the pathology department, Dr.
William G. MacCallum, a senior and highly respected mem-
ber of the faculty, who had been at the school since its early,
heroic days. In the course of quizzing me, he inquired about
my plans for the summer; after I had told him, he remained
silent for a few moments, contemplating the ceiling, and then
said, "Well . . . you will probably see a lot of material and
gain some experience. Just don't believe everything you hear."
I discovered later that the reason for this caveat was Mac-
Carty's unorthodox views about certain aspects of pathology.
Most notably he had claimed that it is possible to diagnose
cancer on the basis of the appearance of single cells in sections
of frozen tissue. MacCallum was right, however, about being
exposed to a large amount and a variety of material. Armed
with his warning I had an instructive summer at the Mayo
Clinic without becoming a disciple of MacCarty's views.
MacCarty was a warm and generous man, and he gained the
respect of all the members of the group of medical students
that he voluntarily provided with an opportunity for addi-
tional experience.
As I got into clinical studies the following year, I began to
believe that emphasis on pediatrics would be the best way to
promote my interest in the infectious diseases. This interest
had its roots in my earlier reading, such as The Life of Pasteur
and Microbe Hunters, but it had certainly not been enhanced
by the second-year course in bacteriology. Primarily a dry,
systematic presentation of the subject, dwelling on the clas-
sification and methods of identification of the principal classes
of pathogenic bacteria, the course did little to highlight the


The Medical Scene                         39
glamorous aspects of the subject. Having said this, I must also
concede that I first heard about the transformation of pneu-
mococcal types from one of the lectures of the professor of
bacteriology. His description of the phenomenon was so graphic
that I retained it until I came face to face with the reality in
the laboratory several years later.
In any event, I followed through on my notion by spend-
ing part of the summer after the third year as a substitute
intern in pediatrics. This kind of substitution is common and
satisfies both the needs of the medical student for some prac-
tical experience and the requirements for filling house staff
positions during vacations. In my case, it provided just the
exposure I needed to settle on pediatrics as the area to round
out my medical training. The most prestigious internship at
Johns Hopkins was on the Osler medical service, and the gen-
eral esteem in which it was held led me to apply for this as
well as for pediatrics. However, as the fourth year pro-
gressed, I realized that I was being influenced by irrelevant
considerations and withdrew my application for an intership
on the medical service, leaving myself as usual with all of my
eggs in one basket. It was a boost to my morale to have the
professor of medicine, Dr. Warfield T. Longcope, stop me in
the hospital corridor shortly thereafter to ask me why I had
withdrawn. I would not have guessed that he even knew who
I was.
It is legitimate to inquire why I bothered to take time for
hospital training in the first place, since I was planning a career
in laboratory research. This is an old question which has been
answered differently by different people. As a matter of fact
many successful medical researchers have opted to go directly
into the laboratory after receiving their medical degrees. In
my own case, I felt that the considerable body of theoretical
and systematic knowledge obtained during the medical school
years required supplementation with practical experience in
order to make it complete. In addition, I must confess that I
looked upon the clinical training as a hedge. I might not make


40              The Transforming Principle

a go of it as an independent investigator and I wished to be
ready for medical teaching as a fall-back position. Medical
practice was a poor third among the possible options. In any
event, I have never regretted the three years that I spent as
a pediatric house officer. I am still convinced that this kind of
postdoctoral clinical experience is an important part of the
training in human biology for anyone who expects to engage
in disease-oriented research.
The late 1930s were exciting years for a young student of
infectious diseases. The sulfonamide drugs, just introduced,
had ushered in an era of rapid change in our ability to deal
with bacterial infections. I had enough experience as a medi-
cal student with the pre-sulfonamide problems of treating
severe infections to fully appreciate the power of first the sul-
fonamides and later penicillin and a long series of antibiotics.
One memory lingers from that summer of 1936. As a substi-
tute intern in pediatrics I participated in futile efforts to save
a child with streptococcal meningitis, a disease that occurred
occasionally as a complication of middle ear and mastoid infec-
tion. It was uniformly fatal. Early in the period of my regular
internship the following year we were able to treat a similar
case with sulfanilamide. It is easy to understand the sense of
elation we all felt when the boy promptly began to improve
and ultimately recovered completely. In our concern today
about the misuse of antibiotics and the emergence of anti-
biotic-resistant strains of bacteria, we tend to forget that there
are a number of infections, like streptococcal meningitis, from
which no one had recovered prior to the discovery of effective
antibacterial agents.
There was probably no better place for clinical training in
pediatrics than the Harriet Lane Home for Invalid Children,
as the pediatric unit of The Johns Hopkins Hospital was then
known. All of the essential elements were there-a wide
selection of case material that posed the full range of disease
problems; a superb full-time faculty ably supported by a con-
scientious group of part-time practitioners; a house staff that


The Medical Scene                          41

was drawn from the top medical graduates at various schools
across the country; a nursing staff that worked in unison with
the physicians in the care of patients; and a social service unit
that was remarkable in its day for its breadth of coverage and
effectiveness. The moving spirit in the creation of the aura of
excellence and harmonious cooperation that pervaded the
Harriet Lane was the chief of pediatrics, Professor Edwards
A. Park. Dr. Park was a tall, Lincolnesque figure, soft-spoken
and gentle, whose considerable erudition was often obscured
by his self-effacement. His humility was real, and he seemed
unaware of his ability to bring out the best in his associates at
all levels or of his own major role in creating an illustrious
clinical setting. He was research-oriented himself, devoting
much of his active career to a study of rickets and scurvy.
Thus, he was most sympathetic and encouraging to those who
aspired toward research. He gave me a helping hand on
repeated occasions and continued his interest in my progress
well into his retirement years.
For those interested in infectious diseases, Harriet Lane
had another resource in the bacteriology laboratory under the
able supervision of Miss Helen Zepp. Zeppie, as we called
her, had little patience with ineptitude. In fact, she terrorized
some of the interns by her vocal criticism of their bumbling
efforts in handling bacterial cultures, but she was an excellent
teacher and guided those of us who persevered in the intra-
cacies of practical bacteriology. It was under her tutelage that
I got a more realistic grasp of the subject, and I spent many
of my "free" hours in that laboratory.
The bacteriological laboratory was the scene of my contri-
bution to a study of pneumococcal pneumonia that led to my
first published paper. This took place during my second year
at Harriet Lane when I was an assistant resident. The first
modified sulfa drug, sulfapyridine, had just been introduced
with the property-which sulfanilamide lacked-of being
effective against the pneumococcus. It seemed worthwhile to
carry out a test of its effectiveness in the treatment of pneu-


42              The Transforming Principle

monia in infants and children. The study was under the direc-
tion of Dr. Horace Hodes who had recently returned to
Baltimore after two years of training at the Rockefeller Insti-
tute to serve as director of the city's infectious disease hospital
and as a staff member at Harriet Lane. In addition to partici-
pating in the clinical management of the pneumonia cases, 1
did part of the bacteriological work involving isolation and
serological typing of the offending pneumococcus in each case.
The effectiveness of sulfapyridine was abundantly evident in
the seventy-one cases included in the study. My colleagues
and I reported the results in a paper published in the Journal
of Pediatrics2 for which I prepared the illustrative charts as
the amateur medical illustrator of the group. This clinical study
was an important episode in my training, since it gave me the
opportunity to become familiar with the properties and meth-
ods of handling of the microorganisms that would later play a
central role in my research.
My development as a pediatrician was certainly facilitated
by having our own young children to observe and learn from.
Our older son had been born just before I started the third
year of medical school, and his younger brother came along
toward the end of my intern year. Aside from the pleasure
and enrichment of our lives that the boys provided, they also
gave me a much better feeling for some of the problems pre-
sented by parents who brought their children to the Harriet
Lane clinic. Not that I was given much time to indulge in
simple enjoyment of my family. The clinical responsibilities
of the house staff were demanding, requiring long hours with
little scheduled time off, but the rewards were great. Dr. Park
gave the members of his resident staff a large measure of inde-
pendence, relying on their judgment and on peer interaction
to move them to seek assistance from the faculty and attend-
ing physicians when it was needed. The assistant residents
made decisions regarding admission to the hospital, an oner-
ous responsibility that at the same time provided a strong
stimulus for the development of clinical judgment and acu-


The Medical Scene                          43

men. I found my activities as assistant resident enjoyable and
absorbing so that I was happy to stay on in this capacity for a
second year, even though I was still looking ahead to the
adventure of laboratory research. I decided that this would be
enough time to devote to clinical training and began early in
the final year to look for an appropriate laboratory position.
There were limited opportunities for postdoctoral research
experience for M. D. s in those years just prior to World War
II. Only a handful of postdoctoral fellowships were offered,
and not many laboratories had the resources to accept and
support trainees on their own. An exception to this general
state of affairs was found in the Rockefeller Institute for Med-
ical Research where the individual laboratories had line items
in their budgets for the support of young hopefuls seeking
research training. Dr. Park seemed to have a good line of
communication on the situation at Rockefeller. He had man-
aged to place several of his research-oriented house officers
there in the past. In the fall of 1939 he told me of an opening
in the laboratory of Dr. Leslie T. Webster at Rockefeller and
suggested that I apply for it. It was thus that I made my first
visit to the Rockefeller Institute where I was greeted and shown
around by a former assistant resident at Harriet Lane who was
about to leave Webster's laboratory for the University of Chi-
cago. I had already been duly impressed by the reputation of
the Institute and now found myself somewhat awed by its out-
wardly austere atmosphere. Dr. Webster was friendly and
sympathetic during our interview, but in the end it was clear
that I did not fulfill his criteria for the position. He was plan-
ning to embark on a study of the effect of diet on infection and
was looking for someone trained in the science of nutrition.
Disappointed but not discouraged, I returned to Harriet
Lane for more help from Dr. Park. Not long afterward, he
had information on some other possibilities, one of which was
with Dr. William S. Tillett at New York University. Dr. Til-
lett had been on the Hopkins faculty when I was a medical
student, and I remembered him for his informative and stim-


44              The Transforming Principle

ulating lectures in the area of infectious disease. He had left
Hopkins in 1937 to become the professor of bacteriology at
New York University. The following year he became the first
full-time chairman of the department of medicine of that school.
Although I was unaware of the details of his scientific work, I
knew that he had an excellent reputation as an investigator.
The idea of working under him appealed to me, and I made
another trip to New York, this time with greater success. In a
letter sent January 15, 1940, Tillett wrote me as follows:

Dear Dr. McCarty:

Concerning the position here which we have discussed, I find
that I am able to offer you a position as a Fellow in Medicine for the
academic year beginning July 1, 1940, at a salary of $100 a month.
A desk in my laboratory, together with its facilities, will be available
for you. The exact nature of the problem we can decide on at lei-
sure.

If you finally decide that you would like to take this position, I
will be delighted to have you and hope it will be an interesting and
pleasant experience.          Sincerely yours,
                      W. S. Tillett

I promptly accepted saying that "I believe the fellowship with
you offers me exactly what I wanted in the way of trying my
hand at laboratory work. . . ." The "$100 a month" was not
an unusual compensation for a scientific trainee in the pre-
war period. Since the resident staff at Johns Hopkins received
nothing but room and board (which as a married house officer
I didn't use), I was not dismayed by the figure. However, I
doubt that even a single person could have lived comfortably
on that amount in New York, even in 1940, and so I was des-
tined to continue to be dependent on the largess of my par-
ents.

Although I left Harriet Lane with some regrets, my depar-
ture from Baltimore itself in late June 1940 was most wel-
come. I had never developed any real fondness for the city,
and my duties as a pediatric house officer had required that I


The Medical Scene                         45

move back to East Baltimore in the immediate vicinity of the
hospital. In preparing for the move to New York we had found
a house with reasonable rent in an old residential area of
Flushing on Long Island. It was well enough endowed with
trees and a small lawn to satisfy the expectations generated
by my midwestern upbringing, and it provided a more
acceptable setting for raising our two young sons. We were
quickly settled in this new home and I was ready to join the
ranks of the subway commuters.

My official letter of appointment from the secretary of New
York University earlier that June had indicated that I was to
begin on September 1. I ignored this and presented myself at
Tillett's laboratory on July 1, only to find that he also was not
expecting me until September, despite the date given in his
letter offering me the position. He was about to leave for Maine
for the summer. Even so, I could use the laboratory during
that time, minus his supervision and the $100 a month. I was
too eager to start to let this opportunity go by, making use of
the time for preliminary experiments and a lot of necessary
reading in the library. His laboratory was on the same floor as
the department of bacteriology in an old building at the cor-
ner of First Avenue and Twenty-sixth Street, across from
Bellevue Hospital. The whole area was somewhat seedy and
there was little of that atmosphere of outward elegance that
had impressed me on my visit to the Rockefeller Institute.
However, the laboratory itself, located in the back of the
building next to the animal quarters, was more than adequate
for my needs.

As a rather natural outgrowth of my recent clinical expe-
rience, my initial laboratory efforts dealt with the sulfonamide
drugs. One of the developments that had caught my eye was
described in some recent reports from England. The rather
simple organic chemical p-aminobenzoic acid was apparently
capable of completely inhibiting the antibacterial effect of
sulfanilamide both in the test tube and in experimental infec-
tions. This provided a clue as to the mode of action of these


46              The Transforming Principle
new drugs. Nothing much came of my efforts to exploit this
finding except for a small paper showing that p-aminobenzoic
acid also nullified the curative effect of sulfapyridine in pneu-
mococcal infections of mice but did nothing to alleviate the
toxicity of the drug. 3
After Tillett returned in the fall, he suggested a project
involving the role of white blood cells (or leukocytes). Leu-
kocytes were of known importance in defense against bacte-
rial infection through their ability to engulf and destroy the
microorganisms, but were they essential for the curative action
of the sulfonamide drugs? The protocol called for the use of
rabbits which were to be rendered deficient in leukocytes by
the only method then available-the administration of ben-
zene. Once the animals had become sufficiently deficient in
leukocytes-a state referred to as leukopenia-they were to
be infected with pneumococci and then tested for the thera-
peutic efficacy of sulfapyridine in comparison with a group of
control animals with normal white blood cell counts. I carried
out all of the procedures, including the administration of the
drugs, the total and differential leukocyte counts, and the bac-
teriological work.
A number of difficulties arose that made it impossible to
achieve the original goal of this project. The most important
of them was the finding that sulfapyridine appeared to reverse
the leukopenic effect of benzene. As a matter of fact, we found
that if benzene and sulfapyridine were administered concur-
rently the fall in leukocyte count was totally prevented. The
work of toxicologists on the action of benzene, an industrial
poison, had indicated that the toxic effect was brought about
by some product of the oxidation of benzene in the body rather
than by benzene itself. This suggested that sulfapyridine might
be acting by interfering with the oxidation of benzene in the
tissues. I got a chance to try my hand at some biochemical
experiments again in showing that sulfapyridine did indeed
markedly suppress the amount of oxidation products (phenols)


The Medical Scene

47

excreted by animals receiving benzene. Dr. Tillett and I sub-
mitted this work for publication early the following summer."

As this work was getting started in October 1940, I wrote
to Dr. Park giving him an account of my progress and describ-
ing my activities in Tillett's laboratory. He replied with the
first of a series of invitations to return as chief resident physi-
cian at Harriet Lane. After the invitation, he added with char-
acteristic diffidence and honesty the following:

I cannot in all honesty advise you to be resident. What you really
ought to do in your own interest is to go on in bacteriology for at
least one more year and perhaps for two years. It would be splendid
if you could spend on year at the Rockefeller Institute. If I can help
you in furthering your plans for the continuation of your bacterio-
logical studies, please let me know and point out the way I ought to
proceed.

This advice agreed with my own inclinations, since I had no
intention of leaving laboratory work until I had given it a
thoroughgoing try and then only if I failed at it. On November
9 Dr. Park renewed his offer in a letter that crossed with mine
telling him of my decision to stay with Tillett. He more or less
reiterated his previous comment by saying:

I cannot urge you to be resident and believe that if you go on for
another year with Tillett or better at the Rockefeller Institute, it
would be the best plan for your future.

In our discussions of plans for a second year, Tillett had
suggested that I apply for a National Research Council Fel-
lowship in the Medical Sciences in the hope of obtaining a
somewhat more adequate stipend. I submitted the applica-
tion before Christmas in 1940, including Dr. Park among the
names of those who would serve as references. I gave little
further thought to this and was deeply immersed in the work
on sulfapyridine and benzene that I have just described when,
in March of 1941, I received a letter from Dr. Francis G.
Blake, the chairman of the Medical Fellowship Board, noti-


48              The Transforming Principle
lying me that I had been awarded a fellowship beginning Sep-
tember 1, 1941, "with a grant of $2,300." The letter then added
this bombshell in the next paragraph:
The Board would like to suggest that you give consideration to
the possibility of working in some other laboratory than that indi-
cated in your application; for example, with Dr. Colin M. MacLeod
at the Hospital of the Rockefeller Institute, with a view to broad-
ening your experience. I hope that this suggestion of the Board will
appeal to you as a desirable one. Will you kindly let me know as
soon as possible whether you are willing to accept this suggestion
and, if so, where and with whom you would like to work.
Because of Dr. Park's repeated emphasis in his letters to
me on the desirability of going to the Rockefeller Institute, I
have had occasion to.wonder whether he had written anything
in his letter of recommendation that had influenced the Board
to make this suggestion. I never found the answer to this. In
any event, when I showed Blake's letter to Dr. Tillett, after
an understandable first reaction when he said, "I wonder if
this is a crack at me?", he immediately began to take action
to make the necessary arrangements. He happened to know
that Cohn MacLeod had accepted the position of chairman of
the department of bacteriology at New York University and
on July 1 would be leaving Avery's laboratory at Rockefeller
and moving to the same floor of the building in which I was
then working. Tillett had maintained a close personal friend-
ship with Avery dating back to the 1920s when he had spent
several years at Rockefeller in his research group. He lost no
time in picking up the telephone to call Avery and asked him
if he would accept me as a fellow in his laboratory. Clearly
acting on the basis of Tillett's recommendation, since he hardly
knew me, Avery agreed. The approval of Dr. Thomas M. Riv-
ers, director of the Rockefeller Hospital, as well as approval
of the Fellowship Board were quickly obtained. I was set on
a course for Rockefeller.
I promptly wrote Dr. Park to convey the good news, and


The Medical Scene                        49
he replied with a congratulatory letter, including some of his
characteristic comments:

I am glad that you are going to work with Dr. Avery at the Rocke-
feller Institute. Everyone seems to think he represents the extreme
upper stratosphere. I hope that you do not develop "Bends" in mak-
ing the ascent.

Dr. Park knew Avery from his early years, having been his
medical school classmate at the College of Physicians and Sur-
geons of Columbia University. I learned from him later that
he had not considered Avery one of his more impressive class-
mates and had always been surprised by the outstanding rep-
utation he had acquired.

The role that chance plays in shaping one's career is clearly
evident in the course of events leading me to the Avery labo-
ratory at the right moment. The sequence that I have recounted
could have been altered at several points, resulting in a dif-
ferent outcome. If Dr. Webster had accepted me at Rockefel-
ler on that first attempt, if I had chosen one of Dr. Park's
suggested mentors for research training other than Dr. Til-
lett, or if my National Research Council fellowship had not
been timed to coincide with Colin MacLeod's departure from
Rockefeller, it is unlikely that I would have come to study the
substance responsible for the transformation of pneumococcal
types.

I had met Dr. Avery at a dinner in Tillett's home and found
him charming and a fascinating raconteur in this social set-
ting, but I was still not thoroughly acquainted with his scien-
tific contributions. When I visited him in the spring of 1941
to discuss plans for the coming year, he treated me to one of
his famous monologues describing the earlier work of his lab-
oratory on the pneumococcal polysaccharides. Nothing spe-
cific was mentioned about the project that I might undertake,
although he gave me a number of reprints of his scientific
papers and other reading material to peruse over the sum-


50               The Transforming Principle

mer. He did not touch upon the work on the transformation
of pneumococcal types. Since there had been no publication
on the subject from the laboratory since 1934, I remained
ignorant of his recent studies with MacLeod on transforma-
tion until I arrived to begin my fellowship in September.
Thus, I come to the point where my part in the story of
the discovery of the genetic role of DNA begins. However, in
order to provide a basis for comprehending the research and
its significance, it will be necessary first to introduce the reader
to the pneumococcus in a more intimate fashion and to describe
the investigations that paved the way for our later work. This
will be the object of the next three chapters.


III

THE SUGARCOATED
   MICROBE

T IS OFTEN POINTED OUT that research in the basic sci-
ences provides the base of new knowledge essential for
the development of the applied sciences, including med-

icine. We are less frequently reminded that the reverse can
also occur. Research directed against a specific medical prob-
lem has resulted in contributions to fundamental biological
knowledge. The most dramatic example of this is the discov-
ery that deoxyribonucleic acid (DNA) is the substance that
transmits genetic information. From the initial discovery of
the phenomenon known as "the transformation of pneumo-
coccal types" until the identification of the transforming sub-
stance as DNA, all of the researchers were medical
bacteriologists primarily interested in the cause and control
of human pneumonia. Admittedly, in the latter stages of the
search we came to see that our findings would not help to
eradicate pneumonia, but all of the earlier steps had emerged
from a study of the disease.

It is not surprising that pneumonia had preoccupied so
many bacteriologists shortly after birth of the science a little
over one hundred years ago. At the turn of the century, pneu-


52              The Transforming Principle

monia was the leading cause of death, ranking well ahead of
today's principal killers-heart disease and cancer-and it was
not limited to the aged and infirm. As the precision of the
techniques of bacteriological diagnosis improved, it became
evident that most of this devastating pneumonia was caused
by a single group of bacteria, referred to most commonly as
the pneumococci.
Pneumococci were first isolated from human sputum after
inoculation into laboratory animals in experiments reported
in 1881 independently by Louis Pasteur in France and George
M. Sternberg in the United States. The recognition of their
relationship to lobar pneumonia came from studies in several
laboratories over the next few years. The microorganism has
been called by a variety of names by bacteriologists since that
time, partly because of the difficulties inherent in defining the
relationships of bacterial species to one another so as to per-
mit accurate application of the Latin binomials customarily
used in biology. Today they are officially known as Strepto-
coccus pneumoniae, indicating their relationship to that large
family of bacteria that includes those responsible for strepto-
coccal sore throat and a number of other human ailments. I
will continue to refer to them as pneumococci, both for sim-
plicity's sake and for the historical dominance of this designa-
tion.
The pneumococcus is perhaps not especially remarkable
among the vast array of bacteria in nature. It does possess
certain attributes that make it recognizable to trained bacte-
riologists and set it apart from other microorganisms. It is about
average in size, being approximately 1 micrometer (or one-
millionth of a meter) in diameter. In nonmetric terminology,
it would require 25,000 pneumococci lined up in a row to
extend one inch. They tend to occur in pairs termed diplo-
cocci, which simply means that after dividing by the usual
bacterial process of binary fission the two daughter cells remain
associated. This post-divisional association extends even fur-
ther so that the organisms often appear as short chains, a con-


Type Ill pneumococci stained with gentian violet. Magnification approximately 2000x

(Reproduced with permissron from the Proceedings of the American Phllosophlcal
Society, 1984. 12827.)

Living type III pneumococci in the presence of India Ink. Particles of ink form the
dark background and reveal the capsule surrounding the orgamsms.


54

The Trunsforming Principle

figuration typical of streptococci in general. They are frequently
seen as pointed at one end and were thus referred to in the
early days as "lancet-shaped." These characteristics of the
organism are readily detected by examination of living bacte-
ria with an ordinary light microscope, but special staining
techniques have been applied to get additional information.
Insofar as the internal structure of the organism is concerned,
as in the case of other bacteria, not much was learned about
this until the modern procedures of electron microscopy were
used.

More relevant for us are the results of the application of
special stains. These stains revealed that virulent pneumo-
cocci with the appearance just described were in reality sur-
rounded by a structure we now call a capsule. The capsule
obviously has less substance than the organism itself. Its invis-
ibility under ordinary conditions is due to its being optically
indistinguishable from the surrounding medium. Procedures
other than staining can be used to confirm the presence of a
capsule. In one method a suspension of organisms is mixed
with a small amount of India ink so that the particles of ink
clearly delineate the capsule as separate from the body of the
organism. The size of the capsule varies among strains of
pneumococci, but it can be very large and exceed the diame-
ter of the coccus by three- or fourfold. As will be apparent
later, the capsule is an essential feature for the virulence of
the pneumococcus as an infectious agent. Furthermore, it plays
a central role in the story of transformation.

For growth of pneumococci in the laboratory, a bacterio-
logic medium that resembles beef broth is commonly used.
In fact, it is merely an extract or infusion of beef heart to
which has been added a material called peptone. Peptone is
a preparation of meat products that are partially broken down,
usually by treatment with digestive pancreatic enzymes. Also
present in the medium are some sugar and salts. After adjust-
ing the pH (a measure of the acidity or alkalinity of the soup)


The Sugarcouted MicrolIe                    55
to a value close to that occurring in blood, the completed
medium is sterilized by one of a variety of procedures. The
most common one, autoclaving, uses steam under pressure so
that the temperature is well above the boiling point of water
&I order to ensure the killing of heat-resistant spores. When
a good-quality medium of this kind is inoculated with pneu-
mococci and incubated at about normal body temperature,
the organisms will soon begin to divide, with a doubling time
of 20 to 25 minutes, so that a thousand organisms will increase
to several million in a matter of a few hours. A fully grown
culture in this medium after 8 to 12 hours will have a popu-

Electron microscopic picture of a thin section of a short chain of type Ill pneumo-
cocci. The organisms were embedded in the presence of India ink before section-
ing so that the capsule is made visible. Magnification approximately 25,000x.


S-3             The Transfornzing Principle
lation on the order of 500,000,000 diplococci or short chains
of pneumococci per cubic centimeter* of medium. As a point
of reference, it should be noted that a household teaspoon
holds about 5 cubic centimeters. In dealing with these large
numbers, bacteriologists have found it useful to emulate phy-
sicists and astronomers by using exponential figures. The usual
notation for the number just given would be 5 x lo8 organisms
per cubic centimeter, or simply 5 x 108/cc. The fully grown
culture has a visible turbidity imparted by the ability of the
dense collection of bacterial particles to interfere with the
transmission of light through the medium. However, this tur-
bidity depends on large populations of organisms, and there
can be as many as lO'/cc without any apparent change in the
clarity of the medium. The incidental information to be gained
from this fact is that a solution may be very clear and still
contain a great many bacteria.

The pneumococci in cultures of this kind can be harvested
by centrifugation, a process that involves transferring the fluid
to appropriate containers and placing them in a machine that
rotates at speeds of 1000 revolutions per minute or more. The
organisms by virtue of having greater density than the medium
are deposited at the bottom of the container and may then be
washed free of medium by suspension in salt solution, fol-
lowed by recentrifugation. A mass of pneumococci that has
been well packed by centrifugation is white or cream-colored
with the consistency and appearance of a yeast cake, which is
itself a collection of packed microorganisms. The yield is not
tremendous, however, and the dry weight of pneumococci
from a liter of culture (or approximately 1000 cc) ranges only
from 0.25 to 0.5 gram.

An alternative way of growing pneumococci and other bac-
teria, one useful for isolating, identifying, and counting the
number of viable organisms present in a liquid culture, is to

*The term milliliter (ml) is now generally used in place of cubic centimeter, but for
our purposes the two terms are essentially equivalent.


The Sugarcoated Microbe                     57

place them on solid media. The composition of the medium is
essentially the same as that of the fluid broth except that agar
is dissolved in the heated mixture so that it will form a firm
gel on cooling. In the case of the pneumococcus it is useful to
add also a small amount of blood in order to facilitate growth
of the organism on the surface of the gel. When pneumococci
are incorporated in a medium of this kind or spread on its
surface, each unit (diplococcus or short chain) will grow to
form a colony of many millions of cells that is readily visible
to the naked eye. The colonies assume a round configuration,
ranging in diameter from less than 1 to 2 or 3 millimeters, and
the appearance of their surface is variable from strain to strain
(as well as from one species of bacterium to another), although
pneumococcal colonies have certain common characteristics
that are useful in identification. If a fluid culture is accurately
and appropriately diluted before plating on solid medium, a
reasonably reliable estimate of the number of viable organ-
isms in the culture can be obtained by counting the number
of colonies formed. For example, a culture like that referred
to above with 5 x lOs/cc when diluted a millionfold would con-
tain only 5 x lo2 (or 500) colony-forming units per cubic cen-
timeter, a number within the range feasible for counting. In
practice, these high dilutions of a culture are obtained by a
stepwise process in which serial tenfold dilutions (e.g., 1.0 cc
of culture into 9.0 cc of diluent) are prepared and designated
by a negative exponential system: a lop2 dilution equals a
hundredfold dilution and 10P3 a thousandfold, etc. If 1.0 cc
of a lo-' dilution of a culture yields an average of 50 colonies
on solid medium, it is concluded that the undiluted culture
contained 5 x 10' colony-forming units per cubic centimeter.
The fact that the pneumococcus tends to occur in pairs or
short chains makes the figures only approximate horn the point
of view of the number of individual bacteria present and dic-
tates the use of the term "colony-forming unit. "
One of the attributes of the pneumococcus that sets it apart
from most other bacteria has to do with its pronounced suici-


58              The Transforming Principle

da1 tendencies. The organism is endowed with a mechanism
for self-destruction, composed of a set of enzymes which can
dissolve its protective cell wall and which are ordinarily kept
in an inactive state under favorable conditions, such as those
promoting rapid growth. However, under a variety of other
conditions these autolytic (self-dissolving) enzymes can be
triggered into action and an entire population of the organism
can be wiped out in a matter of minutes. It is not easy to see
how this self-destructive tendency provides any benefits to
the pneumococcus, but it was turned to the advantage of the
bacteriologist long before the explanation for it was known.
One of the early specialists in the field, Fred Neufeld in Ger-
many, discovered in 1900 that the addition of a little rabbit or
ox bile to a culture of pneumonococci resulted in complete
clearing of the suspension after a short period of incubation.
This property was called bile solubility and became widely
used as one of the diagnostic characteristics of the organism.
Pure bile salts and a number of modern detergents were sub-
sequently found to be highly active in solubilizing pneumo-
cocci, presumably by triggering the autolytic system, but this
result can also be brought about by nonchemical means, e.g.,
by repeated freezing and thawing of a suspension of pneu-
mococci.
Another property of the pneumococcus that was exploited
from the time of the earliest studies and one that proved of
great value in isolating the organism from sputum or other
body fluids is its striking virulence for the laboratory mouse.
On injection into the abdominal cavity, the organisms multi-
ply rapidly and usually result in the death of the mouse from
a widely disseminated infection within one or two days. Pure
strains of pneumococci isolated from pneumonia patients were
frequently so highly virulent that a single diplococcus would
cause a fatal infection, indicating that the mouse has little nat-
ural defense against these organisms when they are injected
by this route. The mouse model of pneumococcal infection


The Sugarcoated Microbe                     59

proved useful for many types of investigation, including stud-
ies of possible means of treating or controlling the disease.
Most of this information on the fundamental properties of
pneumococci was available by the turn of the century. An
increasing number of laboratories then began to seek an
explanation for the extraordinary disease-producing capacity
of these pathogens. Always in the picture was a possible
approach to the theory and prevention of pneumonia. Nowhere
was this research pursued more intensively than at the newly
established Hospital of the Rockefeller Institute for Medical
Research. This hospital, the first in the country to be devoted
solely to the investigation of human disease, had opened its
doors in 1910, a few years after the founding of the Institute.
The first director of the hospital, Rufus Cole, was a Hopkins-
trained physician with extensive experience in clinical bacte-
riology. Given this background, and the devastating impact of
lobar pneumonia at this time, a natural early project in the
new hospital was the study of this disease. That study was
destined to continue with unabated concentration for over thirty
years.
Bacteriological research had become progressively more
dependent on the application of the techniques of immunol-
ogy, a science that had its origins in bacteriology and had grown
along with it; intensification of the immunological approach
assumed a major role in pneumococcal studies. The early
attempts to protect animals against bacterial infection by vac-
cinating them with appropriately weakened or killed prepa-
rations of the organism had led ultimately to the recognition
that the sera of immunized animals contained substances that
reacted specifically with the bacteria. These substances came
to be known as antibodies and the bacterial components capa-
ble of inducing their formation as antigens. Antigens were
clearly not limited to the bacterial world. Foreign proteins,
such as the albumin of egg white, would also result in the
appearance of serum antibodies after injection into an animal.


60             The Transforming Principle
There was a remarkable degree of specificity in the antibody
response. Experiments showed that the antisera directed
against one bacterium had no reactivity with unrelated organ-
isms and that antibodies to one protein, such as albumin, would
not recognize other foreign proteins. There was no under-
standing of how animals managed to mount so specific a
response to a wide variety of different antigens. This puzzle
defied solution until the developments of modern immunol-
ogy in the last quarter-century, but the available knowledge
was applied with great vigor to the problems of infectious
disease.
In the case of the pneumococcus, it was Neufeld, discov-
erer of bile solubility, who obtained the first solid evidence
for the diversity of pneumococcal strains by using immunolog-
ical techniques. Neufeld observed that sera from rabbits and
horses that had been injected with pneumococci isolated from
one of his pneumonia patients would protect mice from infec-
tion not only with the same strain but also with pneumococci
from some of his other patients. He concluded that those strains
neutralized by the serum were all alike and designated them
as type I pneumococci. ' Later he found a second strain that
produced antisera against some of the remaining pneumonia
cultures but not against type I strains. These were referred to
as type II. Neufeld's findings by the mouse protection test
could be confirmed by a test-tube test known as the agglutin-
ation reaction. In the presence of type I antiserum, type I
organisms would clump together to form large masses while
the cocci of other strains remained separate from one another.
The results of mouse protection and agglutination experi-
ments matched each other perfectly.
Similar efforts to sort out the varied collection of pneu-
mococci obtained from pneumonia patients were among the
first studies to be pursued in Cole's laboratory at the Rocke-
feller Institute. Alphonse R. Dochez, a member of the initial
group of physician-scientists recruited by the research hospi-
tal, was able by Neufeld-like techniques to divide his collec-


The Sugarcoated Microbe                      61

tion into four groups. His group 1 and group 11 corresponded
to Neufeld's type I and type 11; group Ill was a smaller but
nonetheless important category that had at one time been
mistakenly thought to be separate from the pneumococci; and
group IV represented all other strains from pneumonia cases
that did not fall into one of the first three groups and for the
most part appeared also to differ from one another." Over the
succeeding decades group IV was shown, by the same kind of
serological analysis, to comprise a bewildering number of spe-
cific types, and some of the so-called "higher types"-that is,
those with higher numbers than the original I, 11, or lll-
were encountered with increasing frequency as causative agents
in pneumonia. However, types I, 11, and Ill (the designation
finally accepted as a combination of Neufeld's and Dochez's)
were responsible for fully three-foruths of the cases of pneu-
monia in 1910. Most of the intensified research of the period
dealt with these organisms.

In 1913 Rufus Cole made a move that was to have a pro-
found impact on the development of pneumonia studies at
Rockefeller. During a period when he was looking for a bac-
teriologist at the hospital, Cole had encountered a paper by
Oswald T. Avery on the subject of tuberculosis. The paper
influenced him to consider Avery seriously for the job. Avery,
then 35, was working in Brooklyn at the Hoagland Labora-
tory, a privately endowed laboratory associated with the Long
Island Medical College. In later years, he liked to tell the
story of Cole's visit to Hoagland to look over the unsuspecting
candidate. Avery was at the laboratory bench when Cole
arrived. On being asked what he was doing, Avery replied
that he was testing pneumococci for bile solubility using a
preparation of ox bile. Cole's comment, which Avery remem-
bered as something of a put-down, was: "At the Rockefeller
Institute we use buffered solutions of pure bile salts for this
purpose. "3 My personal postscript to this story is that when 1
arrived at Avery's laboratory at Rockefeller twenty-eight years
later, preparations of sterile ox bile were still kept on hand for


62             The Transforming Principle
testing bile solubility, although bile salts were certainly used
for chemical procedures with the organism.
Cole's overall impression must have been very favorable
nonetheless. He quickly followed up this visit by having Avery
come to Rockefeller to meet the director, Simon Flexner, who
soon thereafter arranged for Avery's appointment to start on
September 1, 1913. Avery came to his new job with a varied
background in bacteriology and immunology as well as an
established reputation as a skilled instructor in the intricacies
of his field of science, especially to small groups. He had already
acquired the nickname of "Professor," a title that he never
officially held. It was shortened to an affectionate "Fess" and
used by colleagues, friends, and family. I learned from one of
his stories, for example, that his young niece called him "Uncle
Fess." Quickly immersed in the world of pneumococci, Avery
quite naturally found himself associated with Dochez in col-
laborative studies. This led to a lifelong friendship and scien-
tific give-and-take between the two men which was only
temporarily interrupted when Dochez went to Johns Hopkins
from 1919 to I921 as associate professor of medicine. On
Dochez's return to New York as professor of medicine at
Columbia, they established "bachelor" quarters together, a
durable arrangement which lasted until Avery left New York
for Nashville in 1948. Their opportunities to stimulate one
another scientifically thus did not end even when they were
no longer together at Rockefeller. Many of their evenings at
home involved long discussions during which they would try
out their ideas on each other.
Dochez and Avery discovered in 1917 that culture fluids
of pneumococci, filtered to remove the bacteria, contained a
substance in solution that would form a precipitate when added
to antisera of the same kind that were used for mouse protec-
tion and agglutination. This precipitation reaction proved to
be type specific; that is, culture fluids in which type I pneu-
mococci had grown would precipitate only with type I anti-


The Sugarcoated Microbe                63

sera, type II cultures with type II antisera, and so forth.
Accordingly, they called this unidentified component of the
cultures the "soluble specific substance," or SSS for short.4
Reasoning that this substance was likely also to be released in
the body from the masses of pneumocci in the lungs of pneu-
monia patients and then to be excreted by the kidney, they
looked for it in patients' urine. Their hunch proved to be cor-
rect. It was frequently possible to diagnose the type of pneu-
mococcus causing an infection by a' simple test of the urine at
the time the patient was admitted to the hospital. The diag-
nosis was consistently confirmed by typing the offending orga-
nism once it had been isolated. On occasion, the SSS could
even be detected in the blood by the precipitation reaction.
Gradually it became apparent from a variety of clues that the
soluble specific substance must derive from the capsule of the
organism, that tenuous halo that surrounds each virulent
pneumococcus. More or less concurrently, compelling evi-
dence had accumulated that the presence of the capsule was
a sine qua non for the virulence of the pneumococcal cell. The
most dramatic proof of this came from the finding that pneu-
mococci, under appropriate cultural conditions, can lose their
ability to form capsules. The unencapsulated strains obtained
by this process, which was termed "bacterial dissociation,"
retained the other properties of the parent encapsulated
organisms but were totally avirulent for mice. Billions of these
unencapsulated cells could be injected without visibly affect-
ing the well-being of the mouse. This contrasted to the fatal
effect of a single diplococcus of the parent organism. Some
notion of what was going on inside the mouse to create this
remarkable result could be deduced from studies of the white
blood cells, the first line of defense of the body against bac-
terial infection. The white cells that serve this function had
been dubbed "phagocytes"-literally, cells that eat-and the
process by which they engulf and destroy bacteria is called
phagocytosis. Phagocytes have great difficulty ingesting


64               The Transforming Principle

encapsulated pneumococci. Something in the capsule clearly
interferes with the process, and as a result the organisms can
grow almost without restraint in blood or tissues of a suscep-
tible host. On the other hand, they will rapidly engorge them-
selves with unencapsulated organisms under the same
conditions, and a single white cell can accommodate hundreds
of pneumococci without indigestion.
Experiments with phagocytosis also did much to explain
the mouse protective effect of specific antisera. In the pres-
ence of type-specific antibodies, a virulent, encapsulated
pneumococcus becomes fully susceptible to prompt ingestion
by phagocytes. Thus, it began to appear that the antibodies
that protected mice against infection, those that agglutinated
the organisms, and those that precipitated with Avery and
Dochez's SSS were all the same and were directed against the
capsular material. Another manifestation of the interaction
between specific antibodies and the capsular material was
encountered by Neufeld when he observed that the usually
invisible capsule could easily be seen under the microscope
in the presence of type-specific antiserum. This striking effect,
which he called the Quellung--or capsular swelling-phe-
nomenon, even though it is not at all certain that "swelling"
by itself is enough to make the capsules visible, was widely
applied as a means of typing pneumococci in the clinical bac-
teriological laboratory. This was one of the first procedures
that I learned in Harriet Lane in the study of sulfapyridine
therapy of pneumococcal pneumonia in children.
  In addition to its effects on immune reactions and viru-
lence, the capsule also contributes a distinctive appearance to
colonies of pneumococci when they are grown on the surface
of agar medium. The colonies of encapsulated organisms have
a smooth surface, shiny or velvety in appearance, whereas the
smaller colonies of unencapsulated organisms have a rough,
rather pebbly surf&e (see the photograph on p. 166). The
terms "smooth" and "rough" derived from this colonial config-


The Sugarcoated Microbe                 65

uration came to be used as a shorthand equivalent for encap-
sulated and unencapsulated, or even for virulent and avirulent.
A further abbreviation to S and R was generally accepted as
the designation of these differences.
As this kind of information on the capsule and its interac-
tion with antibodies accumulated, the rationale for the use of
serum therapy in pneumonia was reinforced, and the efforts
to develop this approach were redoubled in the Avery labo-
ratory. At the same time, Avery was increasingly driven to
find the chemical nature of the specific soluble substances.
He was about to display two of the characteristics that were
responsible for his extraordinary success as an investigator: an
uncanny ability to ask the right questions and dogged persis-
tence in finding the answers, seeking expert help whenever
necessary. Some of his early observations with Dochez had
suggested that SSS might be a protein, a reasonable possibil-
ity in view of the fact that only proteins were thought to act
as antigens and to lead to the production of specific antibod-
ies, but subsequent examination of the properties of the mate-
rial made this uncertain. Avery continued to pursue the
problem along with his other studies, making concentrated
preparations of SSS which he was able to purify to some extent,
but he was frustrated in his attempts to learn the chemical
nature of the material. As he was looking about for help with-
his problem, his eye fell on Michael Heidelberger, a young
organic chemist who had spent several years in the Rockefel-
ler Institute laboratory of Dr. Walter Jacobs working on
chemotherapy and had recently moved to the hospital with
the group of clinical chemists under Donald D. Van Slyke.
Heidelberger was intrigued by the problem when Avery pre-
sented it to him but felt obligated to complete his work of
preparing crystalline hemoglobin for Van Slyke before taking
on another project. From time to time, on meeting Heidel-
berger in the corridor, Avery would remind him anew by
showing him "a small vial of brownish powder" and saying:


66               The Transforming Principle

"When can you work on this, Michael? The whole secret of
bacterial specificity is in this vial. "' Finally, some time in 1922,
they began the job together.
It was Avery's task to provide enough of the crude bacte-
rial product to satisfy the needs of the chemist. These needs
were considerably greater than anything he had been accus-
tomed to in his own analytical studies of the material. They
selected type II pneumococci for the initial efforts as the
organisms with the most favorable properties. Heidelberger
applied a variety of purification steps which they monitored
by the precipitation reaction with specific type II antiserum.
As this process went on, they obtained highly active material
that was totally devoid of protein and, according to Heidel-
berger, Avery at one point asked, "Could it be a carbohy-
drate?"" The answer, as it turned out, was yes. The soluble
specific substance belonged to a class of complex carbohy-
drates that are known as polysaccharides.
At this point it will probably be helpful to the reader with-
out much biochemical background for me to include a few
words about the polysaccharides. The term, which literally
means "many sugars," is applied to a common class of sub-
stances that represent large molecules formed chemically by
linking together the simple sugars, or monosaccharides. Since
there are numerous known monosaccharides, each of which
can be linked to others in a variey of ways, the potential for
diversity among polysaccharides is very great. The most com-
mon and best-known monosaccharide in nature is called glu-
cose, the sugar used by animal cells to provide their energy
requirement and the culprit in human "sugar diabetes. " When
glucose is appropriately linked with another simple sugar-
fructose, or fruit sugar-the product is a disaccharide, sucrose,
the familiar household sweetener obtained from sugarcane or
sugar beets. When living organisms form polysaccharides, this
linking together of simple sugars is continued until up to many
hundreds may be tied together in one very large molecule.
Starch is a relatively simple representative of the family of


The Sugarcoated Microbe                67

polysaccharides, since it is composed solely of glucose units
combined in one large structure. The polysaccharides that were
identified as the specific soluble substances of pneumococci
proved to be more complex, like most others found in nature,
because they have two or more monosaccharides built into
the structure.
The tools available to Heidelberger and Avery for the
analysis of pneumococcal polysaccharides in the early 1920s
did not permit them to work out the details of their composi-
tion immediately. They knew that the type II polysaccharide
contained some glucose but that there were other unidenti-
fied sugars present in larger amounts. Much later it was found
that the predominant sugar in the polysaccharide is one known
as rhamnose, one that occurs commonly in the plant and bac-
terial world but not in the animal world. The situation appeared
to be less complex in the case of the type III polysaccharide
in which they found only two components: glucose and glu-
curonic acid, the latter being an acid derivative of glucose that
is representative of the many modified monosaccharides that
are found in nature. Together with another chemist, Walther
Goebel, who joined the study in 1924, they were ultimately
able to show that the polysaccharide is composed of equal
amounts of the two sugars, occurring alternately along the lin-
ear molecule, so that the repeating unit is a glucose-glucu-
ronic acid disaccharidee7 The specificity of the type III
polysaccharide is inherent in the disaccharide structure, as
established elegantly by Goebel some years later when he
showed that the disaccharide when coupled chemically to a
protein yielded a synthetic antigen that would induce the for-
mation of antibodies reactive with the intact polysaccharide.'
The antibodies would even protect mice against type III
infection.
Avery had achieved his goal of finding out what the spe-
cific soluble substances were made of. At the same time he
had obtained the important corollary information that the pro-
tective capsule surrounding the pneumococcal cell consists


68              The Trunsfbrming Principle

primarily of a complex sugar. His private nickname for the
pneumococcus, "the sugarcoated microbe," had its somewhat
nostalgic roots in this heady period of discovery. The findings
had broader biological implications, going well beyond appli-
cation to problems of pneumococcal infection. They estab-
lished that polysaccharides can express biological specificity
and are able to act as antigenic substances.

Because of the revolutionary aspect of these implications,
the work was not immediately accepted universally. A pri-
mary objection was the view that only proteins have the nec-
essary diversity to display this kind of specificity and
antigenicity. It was held by some that the polysaccharide
preparations must be contaminated with a small amount of a
highly active protein. Scientists tend to be conservative. To
some extent their skepticism is justified, since many radical
new findings ultimately prove to be wrong. Avery's response
to this kind of skepticism was to search for some additional
type of experimental evidence that would dispel the doubts
about the polysaccharide nature of the specific soluble sub-
stance.

He reasoned that if he could destroy the polysaccharide
by some specific means that was unlikely to affect a contami-
nating protein, he could confirm that the biological activity
depended on the presence of the intact polysaccharide. How-
ever, the chemical procedures then available to him were not
selective enough in their action for this purpose. He thus
explored the possibility that there might exist enzymes that
were capable of degrading the pneumococcal polysaccharides.
Finding that none of the animal enzyme preparations that he
tried had a detectable effect on his material, he turned to a
number of plant and microbial sources-some of them rather
exotic, like the papaya-but without encountering anything
that altered in the slightest degree the reactivity of the poly-
saccharides with their specific antisera. His soluble specific
substances appeared to be extraordinarily resistant to destruc-
tion by any of the enzymes that occur in the plant or animal
world.


The Sugarcoated Microbe                69

As so often happens, chance played a large role in the ulti-
mate resolution of this problem. Sometime in the spring of
1927, a young French scientist, Rene Dubos, appeared on the
scene. Dubos, who was about to complete his studies for a
Ph.D. degree in soil microbiology at the New Jersey Agricul-
tural Experiment Station, paid a visit to the Rockefeller Insti-
tute to see his countryman, Dr. Alexis Carrel. In the course
ofthat visit, Dubos was introduced to Avery in the justly famous
dining room of the Institute where all of the members of the
scientific staff gathered for lunch. Avery asked Dubos about
the work he was doing and learned that he was engaged in a
study of soil microorganisms that are capable of decomposing
cellulose. Since cellulose, a major constituent of the cell wall
of plants, is a polysaccharide made up of glucose units, the
relationship of Dubos's thesis studies to the problem that had
been plaguing him was immediately apparent to Avery. He
invited Dubos to join him for further discussions in his office
where he related the story of the pneumococcal polysacchar-
ides and the importance of finding an enzyme that could destroy
them.
Dubos remembers Avery relating the importance of such
an enzyme to its potential value in learning more about pneu-
mococcal infections. The interpretation that I have given,
relating it rather to Avery's desire to eliminate the possibility
of some contaminating substance being responsible for the
activity of his polysaccharide preparations, is of course sec-
ondhand and comes from having heard repeatedly in later years
his recital of the events in one of his famous monologues.
However, I find that this interpretation is backed up by what
Avery wrote when he first reported the work on the enzyme
to the Board of Scientific Directors of the Rockefeller Insti-
tute in April 1930. He talks about the action of the enzyme
being "further proof that these polysaccharides, and not
impurities carried along with them, are really the substances
responsible for specificity. " Nonetheless, I have no doubt that
both motivations were behind Avery's continued interest in
the enzyme, and it is also true that by the time such an enzyme


70              The Transforming Principle

was finally obtained the doubts about the polysaccharide nature
of the capsular substance had been pretty well dispelled.
Dubos had indicated to Avery in that first conversation
that he considered it possible to find a soil organism capable
of producing the kind of enzyme he wanted. Showing again
his characteristic of seeking expert help when needed, Avery
made arrangements that same day for Dubos to meet both
Rufus Cole and Simon Flexner. Quietly he set in motion the
process of obtaining an appointment for Dubos at Rockefeller,
without making it obvious to Dubos. The upshot was that Dubos
became a member of his laboratory in September 1927.
On his first exposure to this new environment where the
emphasis was on the study of disease-producing microorga-
nisms, Dubos got interested in certain aspects of pneumococ-
cal biology that were unrelated to the capsular polysaccharide
and did not immediately initiate the search for a soil organism
that would produce the long-sought-for enzyme. No doubt he
was gently reminded of it from time to time by Avery, and he
began his attack on the problem in the summer of 1928, using
the type III capsular polysaccharide as the test substance.
Despite the very large number of different bacteria and other
microorganisms in the soil, it was soon obvious that those
capable of degrading the type III antigen must be very rare.
A variety of soil samples incubated with solutions of the poly-
saccharide for long periods of time resulted in no detectable
loss in its ability to precipitate with antisera Success finally
came with the use of a sample of soil from a cranberry bog in
New Jersey, from which he eventually isolated a bacterium in
pure culture that possessed the required properties.
While the soil bacterium clearly made an enzyme that split
the type III polysaccharide, it would only do so when the
polysaccharide was present in the medium and when simple
sugars that it could use as an energy source were absent. It
was thus one of the early examples of an enzyme whose syn-
thesis is "induced" by the substance it attacks. The soluble
enzyme released by the bacteria could be partially purified


The Sugarcoated hlicrobe                      71
and shown to progressively break down the polysaccharide
into small units made up of only two to four monosaccharides
that would no longer precipitate with specific antisera. It would
also rapidly remove the capsule from living type III pneumo-
cocci and, most remarkably, cure mice that had been infected
with a lethal dose of the organisms. It had no effect on the
capsular polysaccharides of other types of pneumococci, being
entirely specific for type III.'
Manifestly, this SIII enzyme, as it came to be known, had
all of the attributes that Avery wanted. It could verify the
polysaccharide nature of the specific soluble substance and at
the same time provide a valuable tool for the study of pneu-
mococcal infection. Dubos reports that when he wrote him of
the success of these experiments in the summer of 1929, Avery
took the most unusual step of returning from his customary
holiday in Maine to join in further experiments with the
enzyme. It is the only occasion that 1 know of on which he
interrupted his vacation to return to New York for laboratory
work, since this was a period that he liked to reserve for con-
templation and renewal. It serves to underscore his deep
interest in this development.
The SIII enzyme was later to be a significant factor in the
analysis and purification of the pneumococcal transforming
substance, but this recital of its discovery gets us slightly ahead
of our story. The enzyme was not yet known at the time that
Griffith carried out the first experiments on pneumococcal
transformation, which he reported in early 1928. However,
most of the other information on the pneumococcus so far
described, including the polysaccharide nature of the capsular
material, was available to Griffith. We will now change the
scene temporarily to London and describe the events in his
laboratory that marked the beginning of what was to become
a new era in biological science.


IV

TRANSFORMATION

F RED GRIFFITH was a medical officer in the Ministry of
  Health in London. Working in the pathological labora-
  tory of the Ministry in the period immediately following

the First World War, he had been caught up in the same
sense of urgency concerning the problem of pneumonia that
had motivated other workers, like Cole, Dochez, Avery, and
Neufeld. Local medical officers sent him specimens from
patients with lobar pneumonia from which he would isolate
and type the pneumococci. He accumulated a large number
of strains of pneumococci in this way and engaged in a variety
of experimental approaches in an attempt to learn more about
their behavior as pathogens.

One observation that intrigued Griffith a great deal was
that a single sputum sample from a pneumonia patient could
harbor as many as four or five different serological types of
pneumococci. His method of demonstrating this was ingen-
ious. A sample of the sputum specimen was injected into a
mouse and the organism isolated on the demise of the animal
would prove to be one of the common types of pneumococci,
for example, type I. He would then mix another sample of the
same sputum with a little type I antiserum, thus providing
protection against type I infection, and inject the mixture into


Transformation                            73

a second mouse. On this occasion the animal would succumb
to an infection that proved to be caused by one of the higher
types of pneumococci, a member of the so-called group IV.
The process could be repeated with another sample mixed
with antisera against both type I and the higher type, and still
another type of pneurnococcus would emerge. In this manner
he was able to show that many pneumonia patients harbored
two or more different types of pneumococci.
Griffith found it difficult to believe that these patients had
acquired each of these different bugs as a separate infection.
I am not sure why he was so resistant to this idea. The dissem-
ination of several serological types throughout the population
was common at times of high incidence of pneumonia. There
was thus a reasonable chance for the acquisition of two or more
of them. However, his skepticism proved to be a vital ele-
ment in the story of transformation by inspiring the direction
of his future research. He entertained as an alternative expla-
nation for the occurrence of multiple types in a single individ-
ual that the pneumococci in the tissues were undergoing a
change in serological type as a result of immune processes or
other environmental influences provided by the host. He
summarized this view in the following words:
On a balance of probabilities interchangeability of type seems a
no more unlikely hypothesis than multiple infection with four or five
different and unalterable serological varieties of pneumococci. '

His initial studies on the variability of pneumococci were
directed toward a reexamination of the conditions under which
the organisms would lose the ability to produce a capsule; that
is, to change from smooth (S) to rough (R) with concomitant
loss of virulence. He found again, as he and others had ear-
lier, that the most consistent means of bringing about the
change from S to R was to grow the S pneumococci in the
presence of specific antiserum directed against the capsular
polysaccharide. Similar unencapsulated R forms could be
obtained by other procedures, such as prolonged incubation


74              The Transforming Principle

of cultures on the surface of special agar media. The R forms
that were isolated by these procedures were all alike in that
they lacked capsules and were nonvirulent for mice, but they
differed greatly in the ease with which they could be reverted
to S forms of the original capsular type. While some R strains
seemed able to regain readily the capacity to produce capsular
material and to again become virulent for mice, others were
more fixed in the unencapsulated, avirulent state.
These stable R forms were of particular interest to Grif-
fith. He explored further their potential for reversion to the
fully encapsulated S form. Their lack of virulence was estab-
lished by the fact that injection into a mouse of 1 cc of fully
grown culture, containing the usual 5 x 10" organisms, caused
no obvious ill effects. He conceived the idea of using even
larger inocula by centrifuging 50-100 cc of culture and inject-
ing the total mass of bacteria recovered in this way under the
skin of a mouse. This procedure frequently gave rise to fatal
infections, and in each instance S organisms of the type from
which the R strain was originally derived were cultured from
the mouse on autopsy. Thus, if enough of the organisms were
used under the right conditions, even the stable R forms were
often able to revert.
The interpretation that Griffith placed on these results led
to his next experiments. He felt that such strains "may have
retained in their structure a remnant of the original S anti-
gen, " and he pursued the argument as follows:

When a strain of this character is inoculated in a considerable mass
under the skin, the majority of the cocci break up and the liberated
S antigen may furnish a pabuhlm which the viable R pneumococci
can utilise to build up their rudimentary S structure. The amount
of S antigen in an R strain, even one only partially attenuated, might
not be very large, and it might happen that such an R strain did not
liberate in sufficient concentration the stimulating or nutrient sub-
stances necessary to produce reversion. It appeared possible that
suitable conditions could be arranged if the mass of the culture was
derived from killed virulent pneumococci, while the living culture
was reduced to an amount which, unaided, was invariably ineffec-


Transformation                           75

tive. 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.'

Accordingly, Griffith tried out the effect of a mass of dead S
pneumococci on the reversion of R organisms. Killing the bac-
teria did not present a problem, since pneumococci are quite
sensitive to heat and holding them at a temperature of 60oC
(140oF) for several minutes is more than enough to kill the
entire population of a fully grown culture. In the first experi-
ment that he reported, type II pneumococci were killed by
"steaming at 1OOC" and concentrated by centrifugation so that
the organisms from 50 cc of culture could be injected along
with a small inoculum of living type II R organisms. Each of
four mice given this mixture died within a few days of an
infection caused by virulent type II S pneumococci. His notion
about what was going on during the process of reversion from
R to S seemed to be borne out. A control experiment carried
out at the same time used steamed type I pneumococci along
with living type II R organisms, and in this case the mice all
survived. Thus, on the first occasion that he might have
observed the transformation of pneumococcal types, nothing
happened.

Griffith was well aware that steaming at 100oC was a pretty
rough way to treat biological material, and in the course of a
series of additional experiments he tried out a variety of other
procedures for heat killing the S pneumococci. The important
thing was to be sure that they were all dead. One of his favor-
ite procedures was to heat the culture at 60oC for 2 to 3 hours,
much longer than was actually needed, but insurance against
the possibility that a few living organisms might remain. It
was with material treated in this way that he obtained the first
results that appeared to involve a change in specific capsular
type. Eight mice were injected with heat-killed type I S
pneumococci from 50 cc of broth culture together with a small
inoculum of a live R strain derived from type II. All but two
of the animals survived, but both of those that succumbed


76              The Transforming Principle
yielded type I S pneumococci when cultured. In these two
mice the R cells had apparently been able to use something
provided by the dead S cells to start making the capsular
material characteristic of the dead cells-and to keep on doing
it! How does an investigator deal with a startling observation
like this? As a first reaction, he would think as Griffith must
have that he had made some foolish mistake and set about to
repeat the experiments with added care. In this case, the results
were reproducible, even though they remained spotty with
only part of the mice responding in any given experiment.
There would of course have been nothing remarkable about
these findings if the heat killing of the S organisms had not
been complete (99.99 percent was not enough), and Griffith
focused much of his effort on this point. For example, a large
number of control mice were injected with the heavy dose of
heat-killed S cells without the added living R organisms, and
in no instance did these animals succumb to infection or yield
living S pneumococci on culture. These and other experi-
ments, which he reported in some detail, convinced him that
neither escape from the killing process nor revival of dead S
organisms was a likely explanation for his remarkable find-
ings. He carried out a number of other experiments on trans-
formation with other strains of pneumococci. Type I R strains
could be transformed into either type II or type III S, and
similarly type II R strains could be transformed to type I or
type III S. He also found that his various R strains differed a
great deal from one another in their susceptibility to transfor-
mation just as they differed in the ease with which they would
revert to the original S type. Nevertheless, change of type
occurred with a high enough frequency in his repeated tests
to assure him that it was a general phenomenon and not one
limited to a narrow set of conditions.
Griffith wrote up these studies in a lengthy, detailed report
that he submitted to the Journal of Hygiene on August 26,
1927. It appeared in the January 1928 issue of that scientific


T!-U~fOrnUltiOfl                            77
journal as a paper of forty-six printed pages entitled "The Sig-
nificance of Pneumococcal Types. "3 The length of the paper
is largely attributable to the meticulous description of the
experimental procedures in each phase of his study, a reflec-
tion of Griffith's writing style that was probably exaggerated
in this case by the surprising nature of the experimental results.
His long discussion of these results makes it clear that his
primary concern was with their implications for the epide-
miology and disease patterns of pneumonia. With reference
to the possible mechanism of the transformation of type, he
held to a view similar to that which he advanced as the ratio-
nale for the use of a large mass of pneumococci in his initial
experiments on the reversion of R to S: "When the R form of
either type is furnished under suitable experimental condi-
tions with a mass of the S form of the other type, it appears to
use that antigen as a pabulum from which to build up a similar
antigen and thus to develop into an S strain of that type.""
There was no allusion to the remarkable f'act that the change
was permanent and that once an R form had begun to form a
capsule of a new S type it continued to do so indefinitely on
subculture through countless generations. Thus, something
had happened to perpetuate the change. But bacteriology had
developed as a science ahnost as if unrelated to the rest of
biology. It was too early in its history to expect genetic inter-
pretations of any phenomena encountered in the laboratory.
Other workers interested in pneumococci found Griffith's
results difficult to believe in view of their experience with the
stability of pneumococcal types. Their skepticism would no
doubt have been greater had not Griffith been so highly
respected as an investigator. However, his novel findings
received confirmatory support much more promptly than is
usually the case in scientific work. Fred Neufeld, whom we
met earlier as one of the leading investigators of pneumo-
cocci, had visited Griffith's laboratory in London while the
transformation work was in progress and had been given a


78              The Transforming Principle

preview of the essential findings. On return to his own labo-
ratory at the Robert Koch Institute in Berlin he set about to
try some transformation experiments himself. He was pretty
well prepared for this, since he had recently been carrying
out a series of studies on the interconvertability of R and S
forms of pneumococci, with the result that in a short time he
was able to repeat Griffith's findings. His paper describing his
work appeared in a German immunological journal just two
months after the publication of Griffith's original paper.5
There is a melancholy footnote to the story of these two
great pioneers of pneumococcal biology, Griffith and Neufeld.
Both of them became victims of World War II. Griffith was
killed in an air raid during the London blitz in 1941, and Neu-
feld died in war-ravaged Berlin in 1945, reportedly of starva-
tion. Griffith had some years earlier turned to a series of
important investigations of hemolytic streptococci, and Neu-
feld had presumably had little opportunity to carry on pro-
ductive experimental work after the rise of Hitler.
  I of course never knew either Griffith or Neufeld and can
contribute no first-hand information on either man. It is
somewhat surprising, however, that Avery and Griffith never
met. Neither of them seemed much interested in travel, par-
ticularly when it came to those time-consuming transatlantic
voyages. As far as I am aware, Avery made only one trip abroad,
in 1925, when he obtained a passport and visas for Austria,
the United Kingdom, Germany, Italy, and France. I believe
that he made this trip chiefly as a tourist with little in the way
of laboratory visits or other scientific contacts. He did not go
to Germany in 1933 when he was awarded the Paul Ehrlich
Gold Medal, probably because of the illness to which I will
refer later, but he submitted an address on the polysaccharide
story, carefully translated into German by a colleague, to be
read at the time of the award ceremony. Later he declined at
least two invitations to travel to England-to receive an hon-
orarydegree from Cambridge University and the Copley Medal
from the Royal Society.


Transformation                             79

When the copy of the Journal of Hygiene bearing Grif-
fith's article first arrived in the library at the Rockefeller Insti-
tute, probably not until March 1928 because of the pace of
transoceanic mail in those days, Avery and his colleagues were
greatly interested but not entirely convinced. By a curious
coincidence, one of Avery's young associates, Martin Daw-
son, had like Neufeld just completed a study of the intercon-
vertability of the R and S forms of pneumococci which he had
already submitted for publication in the Journal of Erperi-
mental Medicine." He was thus similarly equipped to get on
with the job of checking Griffith's results. Dawson was very
thorough in his analysis, raising a number of new points in
addition to the old one of how dead the heat-killed cells were,
but in the end his results confirmed Griffith in every detaiL7
A suitable R strain appeared to be convertible to any S type
he chose as long as the conditions of the mouse experiment
followed those described by Griffith.
Griffith had reported unsuccessful attempts to simplify the
transformation experiment by carrying out the procedure in a
test tube, thus eliminating the mouse as a silent partner in
the process. In his initial paper, Dawson described similar
attempts which proved to be equally futile. However, he
remained convinced that transformation in vitro-that is, out-
side the living body of the mouse-should be possible and
that achieving it would be an important step toward better
understanding the phenomenon. He acted on this conviction
after leaving the Rockefeller Institute to assume a position at
the College of Physicians and Surgeons of Columbia Univer-
sity where he resumed experimental work on the problem
with the assistance of a young Chinese associate, Richard Sia.
They tried, using test tubes, a variety of manipulations of the
conditions under which the suspension of heat-killed S organ-
isms (Dawson called this a vaccine for short) were brought
together with living R cells, including the addition of a num-
ber of substances like serum that were meant to help simulate
the conditions in the mouse. The key to success turned out to


80             The Transforming Principle
be very simple, as is so often the case in research of this kind.
It depended on controlling the numbers of living R cells that
were used as an inoculum. If they used a small volume of an
undiluted culture of R pneumococci, which still contained many
millions of organisms, the results were always negative. How-
ever, when the inoculum contained only a few thousand
organisms, as when a drop of a 10e4 dilution of the culture
was used, they began to see the emergence of transformed S
organisms almost as consistently as in the mouse.8
All that was needed was a little bacteriological medium
suitable for the growth of pneumococci, a dash of anti-R serum
(that is, a serum containing antibodies that agglutinated R
pneumococci), the heat-killed type III vaccine, and a small
number of living type II R organisms. After 48 hours of incu-
bation, living type III organisms could often be isolated from
the culture. After they had devised a means of obtaining pos-
itive results, they were surprised to find that they didn't really
need the large amounts of killed S cells that were apparently
necessary for Griffith's "nidus" in the mouse experiments.
Killed organisms from as little as 0.1 cc of culture were suffi-
cient on occasion to bring about transformation in the test
tube.
This last observation encouraged Sia and Dawson to see
whether they could do without the intact heat-killed cells.
They tried to replace them with such things as the superna-
tant fluid remaining after removing the killed cells by centrif-
ugation or with purified preparations of specific polysaccharide,
which they obtained from Heidelberger who was by this time
also at Columbia. When these attempts failed, they turned to
extracts of living S organisms prepared by repeated freezing
and thawing-as many as twenty-three times!-a heavy sus-
pension of the bugs. As pointed out in the last chapter, this
procedure triggers the autolytic enzymes of pneumococci and
leads to their complete disruption, but Sia and Dawson could
not know that among these enzymes were also ones that destroy


`Transformation                            81

the active substance they were after. They were unable to
report the transformation of pneumococci in the absence of a
whole-cell vaccine. In discussing the results of these experi-
ments, however, they made some interesting comments that
presaged some of the views about transformation that were to
he expressed at a later date:
In considering the nature of the mechanisms by which transforma-
tion of type is effected two possibilities present themselves: either a
latent attribute of the R cell may be stimulated by its association
with the S vaccine, or the organisms may acquire a new property
from the vaccine. The former conception involves the assumption
that all pneumococci possess the latent capacity of elaborating any
one of the known varieties of specific polysaccharide associated with
S organisms. The latter hypothesis suggests the possibility that, at
times, certain attributes of bacteria may be transferred from organ-
isms of one type to those of another type of the same species.g

I was surprised to discover recently that still another
member of the Avery laboratory was involved in work on
transformation during this early period. This was Thomas
Francis, Jr., who was a member of the laboratory from 1928
to 1936 and whom I got to know quite well in later years.
However, I cannot recall that either he or Avery ever men-
tioned his participation. This came to light as a result of a talk
that Francis gave at the First International Congress for Virol-
ogy in Helsinki, Finland, in 1968. His talk, which he entitled
"Moments in Medical Virology," included the following sec-
tion:

The second Moment of this revolution relates to the transformation
of pneumococcus. Just 40 years ago this month, I reported to the
Hospital of the Rockefeller Institute for Medical Research to work
on the pneumonia service under Cole as clinician and under Avery
as investigator. . . . Few of the staff were around and I had no patients.
Henry Dawson was there, however, working enthusiastically on the
transformation of pneumococcal types. I had read Griffith's reports
and knew a little about bacterial variation-particularly the rough-
smooth alteration. So I spent the mornings in the laboratory learn-


82             The Transforming Principle
ing of these phenomena and the afternoons in the library and on the
tennis court developing a model of the double fault. Being con-
vinced that the induced change of pneumococcus types in the ani-
mal host was a true bill, I began very primitive efforts to obtain
transformation in the test tube. But it seemed likely that what-
ever the transforming principle was, it needed special care and I
began making extracts by freezing and thawing the organisms in the
cold under relatively anaerobic conditions so as to avoid an enzy-
matic destruction of the principle. .
New lines of effort were freely allowed even if they were not
always enthusiastically supported. I found this when I studied trans-
formation of the rough Type III to virulent in rabbits; there was a
lot of specificity involved and much work, but it was never pub-
lished until later (by others). `" We called this Fess's pocket veto. In
any event, Alloway came to work with me in the clinical field and I
turned over to him the in vitro studies-which he successfully pur-
sued. In the meantime Dawson and Sia had also succeeded. l1
I am not sure about the total accuracy of Francis's recol-
lections, but there is no doubt that he worked actively in the
field for a time. The Alloway to whom he refers was J. Lionel
Alloway, who arrived in the lab the year after Dawson's
departure. He knew of Dawson and Sia's success with trans-
formation in the test tube from a preliminary report published
in 1930 and also possibly by word of mouth, since Dawson
maintained fairly regular contact with Avery for some years
after he left his laboratory. Armed with this information about
the experimental conditions that permitted transformation in
vitro, he concentrated on the next step of trying to prepare
active cell-free extracts of S pneumococci. His first paper on
the subject," which appeared in the Journal of Experimental
Medicine in January 1932, didn't tell anything of the false starts
and frustrations that he encountered in achieving this goal but
merely provided a brief description of a method that seemed
to work. Like Dawson and Sia, he used the procedure of
freezing and thawing but carried it out rapidly and repeated
it only as many times as was necessary to break up all of the
organisms-not more then seven or eight. He than promptly


Transformation                     83

heated the suspension of disrupted cells at 60oC for 30 min-
utes, followed by centrifugation to remove insoluble material.
His next step was an important one theoretically as a final
answer to those skeptics who continued to harbor a suspicion
that the supposed transformation represented nothing more
than the survival of an occasional viable S organism in the
vaccines. He diluted his extract and passed it through a bac-
terial filter of a type made of porous porcelain (called a Berkefeld
filter after its inventor) that had been shown to reliably hold
back bacteria while allowing the passage of soluble sub-
stances. The filtered extract was concentrated about tenfold
and tested in the transformation system.
A filtered extract of this kind prepared from type III S
organisms, when mixed with some pneumococcal broth and a
little anti-R serum and inoculated with a drop of diluted cul-
ture of a type II R strain, after incubation for 24 hours yielded
encapsulated, virulent type III pneumococci. With the same
type II R strain, a type I extract produced type I S organisms,
although somewhat less consistently. There was little doubt,
therefore, that Alloway had succeeded in getting the sub-
stance responsible for the transformation of pneumococcal types
into solution. Thus, in the historical development of the dis-
covery, Dawson gets credit for bringing the Griffith phenom-
enon out of the mouse and into the test tube, and Alloway for
eliminating the need for intact, heat-killed cells by preparing
active extracts. Dawson was obviously close to the latter result
also. In fact, Alloway notes in his first paper that Dawson had
told him personally of obtaining transformation with extracts
that had been exposed to fewer cycles of freezing and thaw-
ing, but he apparently chose not to pursue this further or to
publish his findings because of Alloway's priority.
Alloway, however, was not fully satisfied with the proce-
dures he had developed. In discussing his results, he gave
some hint of the difficulties he had encountered. Not all of his
extracts were active by any means, and many of the successful


84              The Transforming Principle

ones were so weak as to give positive results only part of the
time. This led him to continue the search for a better way of
preparing active extracts, and he reported his progress in these
efforts in a paper that was not completed until after he had
left the Rockefeller Institute and was published in February
1933.13 He described a number of improvements, the most
important being the preparation of the extract by lysing the
organisms with the bile salt sodium deoxycholate, rather than
by repeated freezing and thawing. In retrospect it is surpris-
ing that neither he nor Dawson had tried this earlier, since as
noted in the preceding chapter the so-called bile solubility of
pneumococci had long been known. When a heavy suspen-
sion of pneumococci, with a creamy consistency, is treated
with a small amount of bile salt it quickly becomes a thick,
viscous mess in which intact organisms can no longer be found
on microscopic examination. In an attempt to minimize the!
loss of transforming activity during this lytic process, Alloway
began the procedure in an ice bath and after 10 minutes brought
the suspension slowly to 60oC to stop the reaction and inacti-
vate the autolytic enzymes. The whole operation could be car-
ried out much more rapidly than the more cumbersome process
of freezing and thawing.
In the subsequent handling of the extract, Alloway then
introduced another new procedure that became an indispens-
able part of all work on the transforming substance from that
time forward. He added pure alcohol in a volume five times
that of the extract which resulted in precipitation of most of
the material that had been released from the pneumococci
and left behind the bile salt. The precipitated material could
be redissolved in salt solution and shown to contain the active
substance in transformation tests. Alcohol precipitation and
resolution could be repeated at will without loss of activity.
Alloway described the solutions of active material obtained by
these procedures as slightly turbid and opalescent, but he wa!
able to convert them into water-clear extracts by treatmen
with powdered wood charcoal.


Transformation                     8.5

Another Alloway innovation became a part of the routine
procedure of the transformation studies for many years to come.
He found that certain pathological fluids from human patients,
usually chest fluids, were more consistently effective in sup-
porting transformation than the rabbit or swine anti-R sera
that had been used previously. These fluids also contained
antibodies that agglutinated R pneumococci but appeared to
have other attributes that made them superior to the animal
sera. As material removed from patients for therapeutic pur-
poses, which would ordinarily simply be discarded, they had
the additional advantage of often being available in large
quantities. Hundreds of fluids of this kind were screened for
their effectiveness over the next decade in the Avery labora-
tory.
This description of Alloway's success in obtaining transfor-
mation with filtered, water-clear extracts of S pneumococci
suggests that by the time his work was completed and pub-
lished in 1933 all the necessary preparations had been made
to proceed with the business of identifying the active sub-
stance in the extracts responsible for transformation. It was
unfortunately not quite that simple. Even though the experi-
ments had demonstrated clearly that a soluble factor was
involved, transformation in the test tube remained an incon-
stant and maddeningly unreliable process. Sometimes it worked
and sometimes it didn't, and each time it failed it was neces-
sary to stop and try to find out why. The problem, as we shall
see later, could be with any one of the components of the
system so that correcting it was not necessarily easy. In short,
the transformation system had not yet been developed to a
point where it could serve as a dependable test in monitoring
the fractionation of extracts and purification of the active sub-
stance. There was obviously much work to be done before one
could hope to make significant progress toward the goal of
determining the nature of what had come to be known in the
Avery laboratory as the "transforming principle" and abbre-
viated as T. P.


86              The Transforming Principle

There is no doubt in my mind that Avery had already set
his sights on this goal while Alloway's studies were in prog-
ress. His name did not appear on the papers that either Daw-
son or Alloway published on the work carried out in his
laboratory, but he was almost certainly intimately involved
and closely followed the development of the experiments. A
case in point is the passage of the extracts through a Berkefeld
filter, a step that was looked upon as the final proof that intact
S organisms could not provide the source of the apparent type
transformation. In his recital of the early history of the sub-
ject, which I first heard on my arrival at Rockefeller several
years later, Avery implied that it was at his insistence that this
additional evidence was sought. When Alloway's first attempts
failed, with the loss of all activity after filtration, it was Avery
who suggested the successful device of making the extract
somewhat alkaline before passing it through the filter. As a
result of previous experience, he had known that many sub-
stances would stick to the filter if the solutions were even
slightly acid.
However, there was a matter relating to Avery's health
during this period that certainly must have curtailed his per-
sonal participation in the research and may have even pre-
vented him from keeping as close a watch on it as he would
have liked to. He had developed the symptoms of hyperthy-
roidism, or Grave's disease, and suffered from gradually
increasing disability brought about by this disorder. I do not
know the date of onset of these symptoms, but among the
papers of Simon Flexner there is a letter to Avery dated Octo-
ber 6, 1931, thanking him for a summary of his work and
including the following paragraph: "I am sorry to have imposed
the task on you, but I hope it did not cost you too much effort.
And let me add that I hope you will take proper care of your-
self, beginning immediately."14 His illness had apparently
progressed far enough by this time for it to have come to the
attention of the director. In addition to the physical disability
caused by the ailment, it also resulted in some mental anguish


Transformation                     87

and depression. Not the least of his difficulties came from the
tremor associated with hyperthyroidism which interfered with
his almost compulsively meticulous bacteriological technique.
His inability to carry out the customary bacteriological pro-
cedures without the risk of contamination was by itself a blow
to his self-confidence in the laboratory.

Although the precise date on which Avery finally came to
surgery for his disorder is not known, since the hospital rec-
ords have all been destroyed, the available evidence suggests
that it was in 1934. This was the only year of his long tenure
at the Rockefeller Institute for which the report submitted
each April to the Board of Scientific Directors did not include
a section written by Avery. His recovery to full health follow-
ing thyroid surgery was apparently slow, and it was more than
a year afterward that he regained his normal weight, which
was not much over a hundred pounds in the first place. There
was thus a long period in the early thirties, a crucial period in
the development of the research on transformation, when
Avery's work in his laboratory must have been much less
intensive than he would have liked.

The work on transformation had nonetheless continued.
On Alloway's departure in the summer of 1932 another young
physician, Edward S. Rogers, joined the pneumonia service
for laboratory training and decided to take up the struggle
where Alloway had left off. He had no great luck with the
project during his two years in the laboratory, turning up no
new information that was considered worthy of publication. I
do not have the laboratory notes from this period or from the
earlier work of Alloway, but the annual report to the Board of
Scientific Directors in April 1933 included a summary of
Rogers's investigations up to that time. He worked with extracts
of type III pneumococci prepared by the Alloway procedure
in attempts to purify further the active substance. None of the
several procedures that he tried during that first year had any
special promise. There are very few hints as to the nature of
his subsequent efforts, since the following .year was, as just


88              The Transforming Principlq

noted, the one in which no general report from the Aver9
laboratory was submitted. The frustrations that Rogers felt werd
but a harbinger of things to come in the search for the identity
of the transforming principle, a search that was taken up
immediately after his departure by a new recruit, Cohn
MacLeod.


V

ENTER MAcLEOD

c OLIN MUNRO MACLEOD had skipped so many grades
  during his early schooling in Canada that he was only 15
  years old when he first presented himself for admission

to McGill University. Forced by school regulations to defer
his start for another year until he was 16, he was still able to
complete both premedical and medical studies by the rela-
tively early age of 23. After two years of residency training at
the Montreal General Hospital, he joined the staff of the Hos-
pital of the Rockefeller Institute in the summer of 1934 as an
assistant resident physician and assistant in medicine, attached
to the pneumonia service of Cole and Avery.

MacLeod appears to have had little prior research experi-
ence, although I have no first-hand information on this point
and must rely on indirect evidence:There are no items in his
bibliography dating back to the pre-Rockefeller period. Nor
do I have any idea what influences directed his interests to
research and brought him to Rockefeller. These are among
the many questions that it never occurred to me to ask Cohn
while I still had the opportunity. Another such question relates
to how he coped with that period of his initial weeks in the
laboratory when his principal concern must have been the
selection of a research project. This could be a difficult pro-


90              The Transforming Principle
cess, since Avery never assigned a project to anyone, and after
some background reading and listening to Avery's discourses
on the past and present activities of the laboratory, the neo-
phyte was expected to come forward with his own research
ideas within the context of pneumonia. Whatever the situa-
tion may have been, MacLeod did not waste any time getting
down to work on the pneumococcus as demonstrated by his
laboratory notes, which date back to early August 1934 when
Avery was almost certainly away for the summer.
My collection of MacLeod's laboratory notes is not com-
plete, but the notes I do have give a good picture of his early
research activity at Rockefeller. They are nearly all carefully
dated, which is not always the case with the records of scien-
tists' experiments, and only occasionally did I have to guess
at the year in which a given set of data was obtained. It is
fortmlate that he was so precise, since the notes are not bound
together but are recorded on loose sheets that he had orga-
nized by subject and collected in manila folders. The notes
have the further happy quality of having been written in a
legible hand so that deciphering was never required.
MacLeod began by becoming intimately acquainted with
the pneumococcus in a series of experiments that were pretty
much a repetition of those of Griffith and Dawson on the con-
version of the S to the R form by growth in the presence of
type-specific antiserum. It is not evident that he was doing
this with the intention of finding an R strain that was more
suitable for transformation experiments, but this is the way it
turned out. In the course of a series of trials that involved
pneumococcal strains of different types, he isolated a rough
variant of a type II pneumococcus that had originally been
obtained in its virulent form by Avery from a fatal case of
pneumonia on the last day of 1916. MacLeod had selected this
particular R variant after thrity-six serial subcultures of the
parent type II strain in the presence of specific type II anti-
serum, and it thus came to be designated as strain R36. Because
of its favorable properties, descendants of R36 became the


Enter MacLeod                            91

organism of choice for all subsequent transformation experi-
ments and are still used today throughout the world for this
purpose.
The first recorded use of R36 by MacLeod in a transfor-
mation experiment-and one of his earliest attempts to carry
out transformation-occurred on October 19, 1934. He applied
the Dawson technique with a heat-killed type III vaccine as
the source of the transforming agent. In his comments on the
satisfactory quality of R36, he concluded that "transformation
occurred in 100% of cases. No homologous reversion occurred."
This later property proved to be characteristic of the strain. It
shows no tendency to revert to the production of the original
type II capsular material even when injected into mice in large
quantities by the Griffith technique. Only when given type II
transforming principle does it resume its original character.
This stable characteristic, together with the relative ease with
which it could be transformed to a number of other specific
types, set R36 apart from most of the other R strains that had
been isolated in various laboratories.
He soon sought to make extracts by Alloway's procedure,
so that by November 22 he was able to record successful
transformation of the same R strain to type I with a filtered
extract of type I pneumococci. In the course of the next few
weeks, he found that type III extracts gave more consistently
positive results than those of type I, which led him to focus
most of his attention on the former. This marked the begin-
ning of the application of a single model-that of type II R +
type III S-in the future analysis of transformation, an impor-
tant step for a number of reasons, not the least of which was
the availability of the Dubos SIII enzyme as an aid in sorting
out the part played by the capsular polysaccharide, which was
inevitably present in large amounts in the extracts.
Throughout this period there are no notes in Avery's hand
or other evidence of his personal participation in the experi-
mental work. However, a comment by MacLeod in the notes
describing his third type III extract, prepared from 4.8 liters


92             The Transforming Principle
of pneumococcal culture on January 4, 1935, indicates that
Avery was almost certainly beginning to get involved. After a
brief description of the procedures used in obtaining the extract
and a note on its potency, MacLeod added the following item:
"Disposition: 125 cc to Dr. Avery." His active participation is
also confirmed by the tone of the report that was submitted
that spring (April 20, 1935) to the Board of Scientific Direc-
tors. The lead item in the report from the Avery laboratory
dealt with transformation and, following an extensive review
of the earlier work on the problem, the renewed efforts were
introduced by this statement: "The work begun by Dr. Allo-
way and continued last year by Dr. Rogers is being actively
carried on at present in collaboration with Dr. MacLeod in an
attempt to ascertain the nature and properties of the trans-
forming principle present in active extracts of S cells." Most
of the properties of the transforming principle discussed in
the report came from observations that represented exten-
sions or refinements of the work of Alloway and Rogers and
they were not entirely new. There was, however, one finding
of major significance for future progress of the research in the
direct demonstration that the autolytic enzymes of the pneu-
mococcus could indeed readily destroy the activity of other-
wise quite stable transforming extracts, This not only provided
an explanation for the great variability experienced in obtain-
ing active extracts but also suggested a possible experimental
approach to improving the situation by inhibition of the
offending enzyme.
This 1935 report also contains some interesting discussion
indicating that Avery and MacLeod had yet to consider trans-
formation as a possible transfer of genetic information. They
wrote that "the results indicate that all R cells . . . possess a
potential but inactive system of enzymes capable of synthe-
sizing any of the type-specific polysaccharides, the particular
one being produced being determined by the specificity of
the activating stimulus. Once the capsular function has been
specifically activated, the newly transformed cells continue to


Enter MacLeod

93

synthesize the same capsular material and retain the same type-
specificity through innumerable transfers on artificial media
without the further addition of the activating substance ini-
tially employed to induce transformation." In other words,
they favored the first alternative mechanism proposed by Sia
and Dawson. Given the large number of pneumococcal types,
each with a chemically different capsular polysaccharide, this
concept would seem to burden the pneumococcal cell with an
inordinate amount of generally useless enzymatic material.
Nonetheless, this represented a more conservative view of
the situation at that time than the notion of genetic transfer,
and they were still left with the remarkable observation that
the "activating" transforming substance must continue to be
duplicated indefinitely by the transformed cells. This was dif-
ficult to explain in the light of the knowledge then available
about cellular mechanisms.

A final paragraph in this report reveals that the clinical
problem of pneumonia continued to be a motivating factor in
the work on transformation. They wrote that "the thought
suggests itself that were we in possession of knowledge per-
taining to the nature of the substances which serve as activa-
tors and inhibitors of the capsule-producing enzymes, the
knowledge gained might afford a new approach to a specific
attack directed toward the suppression of the capsular func-
tion upon the activity of which the pathogenicity of Pneumo-
coccus depends. " In other words, since only encapsulated
organisms are able to cause disease, an understanding of how
capsule production is controlled might lead to a mode of ther-
apy based on inhibition of this process.

Despite some obvious gaps in the laboratory notes, it is
evident that MacLeod's work over the next two years dealt
with various aspects of the problem. Progress was infuriat-
ingly slow, however, and they elected to include nothing on
the subject in the next report in 1936. He defined a number
of new properties of the transforming extracts, summarized in
the 1937 report, that served to guide future investigations.


94              The Transforming Principle

He found, for example, that transforming activity was highly
susceptible to inactivation by ultraviolet light, but the full sig-
nificance of this observation was not appreciated for some time.
A more immediate payoff came from his application to the
extracts of a procedure for removing proteins from solutions
of polysaccharides that had been devised by M. G. Sevag, a
worker in Neufeld's laboratory in Berlin. ' This involved shak-
ing the solution with chloroform together with a higher alco-
hol to prevent foaming, followed by centrifugation of the
mixture, after which a solid cake of denatured protein would
appear at the boundary between the heavy chloroform layer
and the lighter aqueous extract. By removing the extract and
resubmitting it several times to the chloroform process, prep-
arations could be obtained that contained no detectable pro-
tein by the available qualitative tests but which had lost none
of their transforming activity. This supported the notion that
the transforming principle was not protein in nature as had
been suggested earlier by the finding that trypsin, a protein-
splitting enzyme from mammalian pancreas that had recently
been obtained in crystalline form by Northrop at the Prince-
ton branch of the Rockefeller Institute, did not affect the activity
of transforming extracts. "Sevaging," as the chloroform pro-
cedure came to be known in the laboratory, was from then on
a part of the purification process applied to all transforming
extracts. Over the next decade large volumes of choloroform
and many hours of effort were devoted to it.

Another line of investigation that was prominent in the
shaping of future studies dealt with sources of enzymes other
than the pneumococcus itself that appeared to destroy the
transforming substance. Certain crude enzymes from mam-
malian sources, notably one that was designated as "bone
phosphatase," would consistently eliminate all transforming
activity after a brief exposure to the extracts. Perhaps of greater
immediate significance for the research was the finding that
all mammalian sera, including the chest fluids that were being
used in the culture medium in which the transformation


Enter MacLeod

experiments were carried out, contain small amounts of a sim-
ilar enzyme. Therein lay a clue to at least one of the uncon-
trolled factors that was responsible for the exasperating
variability in the success of transforming tests. MacLeod found
that heating the chest fluids at 60oC for 30 minutes seemed to
inactivate this enzyme and at the same time increased their
efficacy in the transforming system. It became routine to treat
the chest fluids in this manner in all future studies. He noted
that the enzyme in certain materials, such as rabbit serum and
pneumococcal autolysates, was not inactivated at this temper-
ature and required heating to 65oC for 30 minutes.

As a matter of fact, MacLeod had begun in 1936 to con-
centrate the lion's share of his attention on the serum factor
required in the transformation reaction. In the 1937 report,
he ended his brief comments on the properties of transform-
ing extracts with a statement that no selective means of isolat-
ing the active fraction had been discovered and then moved
on to a discussion of the "accessory factor present in serum,"
which he said had been more extensively studied. Most of the
remainder of the report deals with findings just described on
the presence in serum of an enzyme capable of inactivating
the transforming principle rather than with the positive attri-
butes of serum that made it essential in the transforming sys-
tem. On the other hand, the laboratory notes show that he
had carried out a large number of experiments applying a
variety of fractionation procedures to serous fluids in an attempt
to identify the "accessory factor." These experiments gener-
ally gave inconstant or nonreproducible results that proved to
be largely uninterpretable. In retrospect it would appear that
the procedures used in chemical fractionation of the serous
fluids tended to introduce modifications in the material that
interfered in one way or another with the complex process of
transformation. Years later, toward the end of my period in
Avery's laboratory, I wasted a good deal of time and effort on
similar experiments directed toward identification of the serum
factor. The problem was solved shortly thereafter by Rollin


96              The Transforming Principle

Hotchkiss, who joined the laboratory after my departure and
brought a fresh outlook and new approach to its solution. The
answer was embarrassingly simple. Serum albumin, the most
abundant single protein in serum, when added to culture media
in purified form, along with a little anti-R antibody, was able
to support transformation. Presumably it acted by virtue of an
ability to combine with and neutralize certain substances that
were toxic to pneumococci. However, since this refinement
came rather late in the game, all of the tests during the iden-
tification of the transforming principle were done with medium
containing heated chest fluids.
An assessment of the situation in the summer of 1937 sug-
gests that MacLeod and Avery were making some progress
and that they had succeeded in defining the conditions required
for transformation in the test tube more satisfactorily than had
previously been the case. To be sure, there were no break-
throughs in the search for the identity of the transforming
principle, their major goal, but one could hardly consider the
prospects for success in this venture hopeless. How can one
explain, then, that the project was suddenly dropped at this,
point, with little evidence of activity over the ensuing three
years? The topic of transformation was not referred to in the
spring reports of 1938, 1939, and 1940. The surviving labora-
tory notes contain no items that were dated during this entire
period, except for the records of one or two sporadic experi-
ments. It really looks as though the whole matter was put on
the shelf.
Some have interpreted this silent interval as evidence that
Avery and MacLeod were not sufficiently aware of the biolog-
ical importance of the problem. I believe the answer is con-
siderably more complex. Colin MacLeod had been working
for three years at Rockefeller and had as yet published almost1
nothing relating to his experimental laboratory studies. This/
would be disastrous for an aspiring young investigator today.`
Even in the 1930s it was a threat to MacLeod's career develi
opment. It is instructive to compare his early record with that


Enter MacLeod                           97

of his friend and colleague, Frank L. Horsfall, Jr,, who had
also come to the Avery laboratory from McGill University in
1934. By the end of 1937 Horsfall had more than a dozen full-
length scientific papers to his credit, most of them having
appeared in the Journal of Experimental Medicine. During
the same period, MacLeod's name had appeared as co-author
(with Horsfall, among others) on a few papers describing clin-
ical studies, chiefly on the use of rabbit anti-pneumococcal
serum in the treatment of pneumonia, and he had a prelimi-
nary note with Dubos on a topic unrelated to transformation.
The contrast was sure to be obvious to his superiors, espe-
cially to the new director of the hospital, Dr. Thomas M. Riv-
ers, who had succeeded Rufus Cole in July 1937. Avery himself
must have been sympathetic with MacLeod's predicament,
since he was well aware of the difficulties of research on trans-
formation and had a personal interest in seeing it go forward.
Cohn did try his hand at a paper on the transforming sub-
stance, probably in mid-1936, and indicated that he was plan-
ning a second one on the serum factor. This information comes
from a draft of the manuscript, handwritten in pencil, that was
found among his papers after his death. It was not complete
but certainly came close, since it included all of the experi-
mental part along with several tables. Avery had gone over
the draft, and there are pencilled comments by him sprinkled
throughout the twenty-one pages. At one point, for example,
in a section on the activity of the extracts, MacLeod had writ-
ten: "Thus an extract was considered of low potency if 0.1 cc
did not effect transformation," and Avery made the following
suggestion: "Define in positive terms-An ext considered
potent if 0.1 cc did effect. . . ." In the end, their enthusiasm
for this interim publication must have flagged because they
were still so far from the ultimate goal. There is no evidence
that it got beyond this initial stage.
There was an additional factor influencing a change in the
direction of MacLeod's research other than the need to find a
more immediately productive line of endeavor. The labora-


The Transforming Principle

tory had gradually worked out the details for the preparation
and use of type-specific rabbit pneumococcal antisera in the
treatment of pneumonia, and the accumulated experience with
this approach showed that it was highly effective in reducing
mortality from the disease. At this juncture, the sudden
appearance on the scene of the sulfonamide drugs as potential
chemotherapeutic agents in pneumonia changed the picture.
If these drugs lived up to their preliminary promise, they would
have the great advantage of acting on all pneumococci,
regardless of type, thus eliminating the need for typing the
offending organism before starting treatment. They would also
obviate one of the major disadvantages of serum therapy, the
frequent development of serum sickness from an immunolog-
ical reaction to foreign serum. It was clearly important for the
laboratory to have a look at the sulfonamides and to form its
own judgment about their potential. This is the task that
MacLeod undertook.

One might still ask whether it was really necessary to give
up the transformation studies so completely and why, for
example, Avery did not pursue these experiments on his own
after MacLeod had turned to other things. In point of fact,
Avery had never returned to the pattern of initiating his own
laboratory experiments after his illness. He loved to discuss
and participate in the devising of experimental protocols but
only rarely would he then proceed to the mechanics of setting
up the experiment. He would enthusiastically work with his
collaborators in this effort but would not initiate it on his own.
Even his nagging curiosity about the nature of the transform-
ing substance was not strong enough to break this pattern. He
no doubt followed closely MacLeod's successful experiments
on the sulfonamides, and together they even returned to some
experiments on another problem that had been set aside ear-
lier. The latter relates to a discovery that Tillett had made
when he was in the laboratory in 1930 on the appearance in
the blood of patients with acute infections of a substance not
present in normal subjects. Because of its implied relation-


Enter MacLeod                           99

ship to the host response to infection, this substance in Avery's
view clearly required better definition. Avery and MacLeod
showed that it was a protein, which they obtained in pure
form and characterized in some detail. This protein is still
known today as "C-reactive protein," denoting its original dis-
covery through its reactivity with fraction C (or the somatic C
poIysaccharide) of the pneumococcus, and studies of its func-
tion and significance are still in progress in many laboratories.
It may well emerge as the third major contribution of the Avery
studies on pneumonia to unrelated areas of biology and med-
icine, along with the discovery of the specificity of the poly-
saccharides and the uncovering of the genetic role of DNA.
This hiatus in the experiments on transformation raises still
another question. Weren't Avery and MacLeod afraid that
someone else would steal a march on them and seize the ini-
tiative in carrying out the search for the nature of the trans-
forming substance? As unbelievable as it may seem in today's
competitive scientific world, they had nothing to worry about
on this score, whether they knew it or not. All of the earlier
work, including that relating to transformation with cell-free
extracts, had been published for some time, but no one else
seemed motivated to pursue the transforming principle. The
full explanation for this can never be known, but Avery's lab-
oratory remained the only place that this line of research was
pursued. If any other investigators shared Avery's intuitive
guess about the significance of identifying the transforming
substance, they appeared not to have the will, or perhaps the
expertise, to become involved in so recalcitrant a research
project. It has been pointed out, in addition, that Rockefeller
was one of the few places where one could have continued
financial support for such a project for so long a period with-
out more substantial returns. In any event, except for the
publications from Avery's laboratory, it was difficult even to
find any mention of the desirability of learning the nature of
the active substance.
By the summer of 1940, MacLeod's productive work on


100              The Transforming Principle

the sulfonamides and C-reactive protein was well on the way
to repairing any deficiency he may have had in scientific puh-
lications. Having not for a moment lost their interest in the
transformation problem, he and Avery must have chafed at
the circumstances that had kept them from getting on with it.
They had no doubt discussed it frequently during this long
interval. It is my impression-perhaps gained from some-
thing Avery told me later-that at this point in 1940 they reas-
sessed the situation and agreed that after the summer holidays
they would join forces in a renewed attack on transformation,
making it their principal laboratory project. It was thus that
the sustained effort that led ultimately to the identification of
the transforming principle began in the fall of that year.


VI

THE RENEWED
  ATTACK

T HE PRIMARY GOAL of this rekindled activity, as Avery
  saw it, can be simply stated. Studiously avoiding pre-
  conceived notions, he wanted to determine what sub-

stance in the active extracts was responsible for transfor-
mation--or, at least, as he put it, "to what class of substan-
ces it belonged. " The difficulty lay in the great complexity
of the extracts that were made by dissolving the pneumo-
cocci with the bile salt, Presumably, the extracts contained in
solution essentially everything that had been present in the
living bacterial cell, and the tools so far' developed by bioche-
mists for separating individual components of this kind of mix-
ture were limited. They were tackling a tough problem.

It was October by the time MacLeod and Avery got down
to business on their proposed collaboration. Even though I
later became well acquainted with their laboratory setting and
got to know both of them intimately, I have difficulty visual-
izing just what kind of working arrangements they were able
to devise, since they were quite different in their experimen-
tal styles: Avery precise and methodical and MacLeod much
more impulsive and impatient. However, the record confirms


102              Th.e Transforming Principle

that they were cooperating closely on the project. While most
of the laboratory notes were kept by MacLeod, there are fre-
quent entries by Avery, often with both of them participating
in the write-up of a single experiment. The notes for this year,
extending into the summer of 1941, are all together in a single
loose-leaf binder and in some semblance of chronological order.
There are no significant omissions.
The first page of this notebook gives the description of an
experiment dated October 22, 1940, and written entirely in
MacLeod's hand except that at the top of the page, above the
title of the experiment, Avery had written "Exp. I (T.P.)."
This is a clear indication that Avery looked upon the resump-
tion of research on the nature of the transforming principle
(or T.P.) as a new beginning, but he was not wholly accurate
in designating this as "Exp. I." A little further into the book
there are two pages out of sequence indicating that a week
earlier MacLeod had prepared the first type III transforming
extract of the new series which he had labeled ExI / 40. The
focus of these initial experiments came from MacLeod's ear-
lier demonstration that the autolytic enzymes of the pneu-
mococcus could destroy the transforming substance and his
conclusion that it would be well to find some inhibitor of the
offending enzyme so that the active material could be pro-
tected during the extraction process. In the sole example I
have found of notes relating to work on this project during the
previous year, MacLeod had tested several substances as
inhibitors and found that sodium fluoride seemed to exert some
preventive effect on the inactivation of an extract by added
autolytic enzymes. Stimulated by this finding, which had been
set aside for many months, they returned to reexamination of
the fluoride effect and its possible usefulness in the prepara-
tion of transforming extracts.
The first extract prepared with the addition of sodium flu-
oride during the process of dissolution of the type III pneu-
mococci with deoxycholate was active, although not notably
more active than the extract prepared the previous week


The Renewed Attack                        103

without fluoride. Nevertheless, they were stimulated to use
this procedure in their first large-scale preparation made from
36 liters of a culture of type ,111 pneumococci. This was an
innovation, since earlier extracts had always come from rela-
tively small batches of culture (3 to 5 liters), and considerably
more effort was required in dealing with the larger volumes.
The results were a great disappointment. The extract showed
no transforming activity whatever on repeated test, and this
particular approach appears not to have been pursued further
even though fluoride was still looked upon as a potentially
useful inhibitor.
The introduction of the use of large-scale cultures in the
project requires further comment because of its importance
in the research and because it provides another indication that
MacLeod had been giving some attention to the problem before
the renewed effort began. As noted previously, the mass of
bacteria obtained from a liter of culture is not very great-not
more than a few tenths of a gram-so that the amount of mate-
rial available for extraction limited the progress of the exper-
iments. Clearly, the attempts to fractionate the extracts and
purify the active material would be aided by a larger mass of
the packed bacterial cells. The difficulty lay in recovering
pneumococci from the broth culture by centrifugation. The
ordinary centrifuges in the laboratory could handle about 1
liter of culture at a time, with an hour of centrifuging being
required to separate the cells adequately. This made it
impractical to deal with more than a few liters of culture at
one time.
An alternative device for the recovery of bacteria from large
volumes of culture had become available by modification of a
machine originally designed as a cream separator. The machine
consisted of a balanced metal cylinder about one and three-
quarters inches in diameter and ten inches long that was
mounted in a vertical position, connected to a turbine driven
by compressed air so that the cylinder could be. spun at speeds
of 30,000 rpm or higher. When whole milk was allowed to


104             The Trunsfortning Principle
flow in at the bottom of the rotating cylinder, the cream and
milk would be separated into layers in the centrifugal field as
they rose in the cylinder and could be collected from separate
outflow spouts at the top. The operation was even simpler as
applied to a bacterial culture, since the particulate bacteria
would stick to the wall of the cylinder and the depleted cul-
ture fluid would flow out at the top. It was feasible to pass
large volumes of culture through such a machine in a reason-
able period of time and leave all of the bacteria packed inside
the cylinder as a paste with about the consistency of a yeast
cake.
Obviously this cream separator-centrifuge was just the
thing for dealing with mass cultures of bacteria, but it had one
serious flaw when it came to applying it to pneumococci. In
the course of its operation at high speed, it emitted an invisi-
ble aerosol laden with bacteria, which dispersed into the
immediate environment. While this may have been tolerable
in dealing with various nonpathogenic bacteria, it was totally
unacceptable when one was centrifuging living, virulent type
III pneumococci. Sometime before the fall of 1940-I have no
record of the exact date-Colin MacLeod set about to find a
way to overcome this defect so that the machine could be
used with pneumococcal cultures. With the assistance of a
mechanically talented technician he designed an airtight, sealed
housing for the cream-separator-type centrifuge. This hous-
ing, constructed in the Institute's machine shop, was a metal
structure about 3 feet in diameter with access to the centri-
fuge through a gasket-equipped door which was fixed tightly
in place by a series of bolts like those used on automobile
tires. In fact, an ordinary tire wrench was used to remove and
tighten them. The turbine of the centrifuge was driven by
high-pressure steam rather than compressed air, and after
centrifugation of the pneumococci a short blast of the same
steam could be used to sterilize the chamber and the external
surface of the cylinder. The effectiveness of this protective
housing was thoroughly tested by running nonpathogenic


The Renewed Attack

1%

bacteria through the machine and placing exposed culture plates
in various locations throughout the room. There was no evi-
dence of leakage into the environment. It was a rather cum-
bersome gadget but served the purpose well.

The unsuccessful fluoride-treated extract of October 29,
1940, is the first record I have of this centrifuge-referred to
as "the Sharples," from the name of the manufacturer of the
cream separator unit-being used with the pneumococcus.
Over the next few years, thousands of liters of pneumococcal
culture were passed through the machine with only a few
mechanical difficulties and no mishaps resulting from dissem-
ination of live pneumococci. The increased yields of starting
material had a major impact on progress of the work; one could
now try a variety of fractionation and purification procedures
without being limited by the amount of crude active extract.

In the course of their other experiments, Avery and
MacLeod had another look at the several components of the
transforming system, confirming the earlier findings and trying
to establish a reliable and consistent means of quantifying the
activity of the fractions of their transforming extracts. The type
II R strain, R36, had retained its favorable characteristics,
although they discovered that if it were not watched carefully
it would throw off mutants during subculture that were totally
resistant to transformation. They learned to recognize these
mutants by the appearance of the colonies they formed when
grown on blood agar plates, so that if the cultures were mon-
itored carefully they could avoid having the resistant mutants
dominate the population of R pneumococci. The transforma-
ble variants were redesignated R36A. Another component of
the system, the complex beef heart infusion broth that they
used as culture medium, was unpredictable in its ability to
support luxuriant growth of pneumococci and to provide the
right conditions for transformation. To achieve more uniform-
ity in this regard, they found it useful to apply a procedure
that MacLeod had introduced to remove sulfonamide inhibi-
tors from pneumococcal broth: adsorption of the broth with


106             The Transforming Principle

activated charcoal, yielding a pale yellow medium that was
much more reliable in the transforming system. When it came
to the serum factor that had to be present for transformation
to occur, they continued to find that the specimens of chest
fluid that they obtained for this purpose varied in their effec-
tiveness but that heating at 60oC for 30 minutes improved
even the best of them.
Attention to all of these points-the state of the R36 cul-
ture, charcoal adsorption of the broth, and careful selection
and heating of the chest fluid-helped to provide a better sys-
tem but by no means eliminated the annoying variability
encountered in the transforming tests. The notes are sprin-
kled with the description of experiments that failed because
"the system was off." Sometimes this was due to a slip-up in
handling one of the known components, but more often the
responsible variable was never identified.
It may be useful to have some picture of how the transfor-
mation tests were carried out at this time. Generally, one part
of heated chest fluid was added to three parts of charcoal-
adsorbed broth, and the mixture was placed in small test tubes
(called Wassermann tubes because they were originally intro-
duced by him for his serological test for syphilis) in ~-CC
amounts. Varying amounts of transforming extract were added
to a series of such tubes. All were then inoculated with one
drop (0.05 cc) of a lo-" dilution of a culture of R36A-roughly
about 2500 colony-forming units. After overnight incubation
at 37'C, a pretty good indication of the results of the test could
be gotten by simply inspecting the tubes. Because of the
anti-R antibody present in the chest fluid, the R organisms
would adhere to one another during growth and settle to the
bottom of the tube in clumps, leaving a clear supernatant fluid.
If transformation occurred, the newly formed encapsulated
type III cells would be unaffected by the anti-R antibody
(because of the presence of the capsule) and would grow dif-
fusely throughout the culture. Thus, a quick look at the tubes
was usually enough to determine which ones showed diffuse


The Renewed Attack                        107

growth indicating that the change had taken place. In prac-
tice, the contents of each of the tubes were subcultured by
plating on blood agar media in order to confirm that type III
organisms were actually present. When things went well, it
was a highly satisfying and conclusive test.

Nothing much can be gained by a chronological recital of
attempts that Avery and Macleod made to analyze and frac-
tionate transforming extracts during that year. It will be more
appropriate to highlight those efforts that represented signif-
icant advances in the project. It is not always easy to detect
the reasoning behind some of the approaches they used, since
the rationale of their experiments was not often discussed in
their protocols. I have made some deductions of my own on
these points, based on the internal evidence and what I was
told later by Avery of the manner in which the problem had
developed.

They usually started their fractionation attempts with type
III extracts rendered free of detectable protein by repeated
application of the Sevag procedure. Having removed one con-
stituent known not to affect transforming activity, they could
then concentrate on other components of the mixture. One of
the most promising, and frustrating, of the fractionation
methods that they tried involved the use of calcium salts. When
a solution of calcium chloride was added to a transforming
extract, sometimes a precipitate would form, sometimes not.
If a precipitate did form, it would often contain most of the
transforming activity of the whole extract. Furthermore, even
if no precipitate formed with calcium alone, the addition of
alcohol in amounts too small to have any effect in the absence
of calcium would bring down a voluminous precipitate. This
would also carry most of the transforming activity. They also
found that these precipitates contained most of what they called
the "nucleic acid" of the extract, based on a qualitative chem-
ical test called the Bial reaction. The Bial test was quite spe-
cific for ribonucleic acid-or RNA-which was often referred
to at that time as the yeast-type nucleic acid.


108              The Transforming Principle

Looking over these experiments today with the benefit of
hindsight, it is apparent that they were coming close to a means
of getting purified preparations of the transforming substance.
What obscured the results was the presence in their extracts
of large amounts of RNA and type III polysaccharide, both of
which were thrown out of solution under certain conditions
by the calcium-alcohol treatment. The presence of RNA in
the active calcium precipitates did lead them to retest the
effect of the enzyme, ribonuclease. They had tried this ear-
lier, but it was now available in essentially pure and highly
active form as a result of work at the Princeton laboratories of
the Rockefeller Institute by Moses Kunitz, who had recently
crystallized the enzyme from extracts of beef pancreas. Treat-
ment of a sample of one of the transforming extracts with this
enzyme broke down much of the RNA into molecules that
were small enough to be readily separable from the other
components. This separation was achieved by a process known
as dialysis in which the enzyme-treated extract was placed in
a cellophane bag and soaked in a large volume of salt solution.
The minute pores in the cellophane allowed the small mole-
cules to pass out of the bag while retaining the large ones. By
means of the Bial test it could be estimated that 75 percent of
the RNA had been removed by this process, and yet all of the
transforming activity had remained with the nondialyzable
material inside the bag.

In addition to making it unlikely that RNA had anything
to do with the transforming principle, these experiments car-
ried out in January 1941 introduced an important new ele-
ment into their analysis of the extracts. In the course of applying
the Bial test to the various fractions obtained, they tried an
additional test that they had not used previously: a test for
deoxyribose that depended on a reaction with the organic
chemical, diphenylamine. The diphenylamine test was not
particularly new but had apparently not come to their atten-
tion previously. What they now found was that the extract,
both before and after ribonuclease treatment and dialysis, gave


The Renewed Attack                        109

a definitely positive reaction characterized by the develop-
ment of a china blue color that was said to be typical of de-
oxyribose and thus also of DNA. In his comment on these
tests, carried out on January 28, MacLeod wrote: "Thus it
would appear as though these transforming extracts may con-
tain a little desoxyribonucleic acid* in addition to the large
amount of ribosenucleic acid present."

This first indication that the pneumococcus contained DNA
came as something of a surprise. Knowledge of the occur-
rence and distribution of the nucleic acids in nature had not
yet reached the point where one could assume that all living
cells contained both RNA and DNA. Indeed, the notion had
only recently been discarded that there were two general classes
of nucleic acid: plant nucleic acid, as typified by yeast prepa-
rations, and animal nucleic acids, as typified by thymus and
fish sperm preparations. A better picture had emerged with
respect to the situation in animal cells, assigning DNA to the
nucleus and RNA to the cytoplasm, but information about
bacterial nucleic acids was still rudimentary. While Mac-
Lead's further comments indicated some doubt about the
specificity of the diphenylamine test for DNA, they gradually
applied the test more frequently as these doubts were dis-
pelled.

Meanwhile things were not going all that well in the prep-
aration of extracts for fractionation. On February 13, for
example, Ex1/41 was prepared by the standard method from
35 liters of type III culture, and after testing its activity

*Some readers may find it confusing to encounter two different spellings for some of
the chemicals referred to in this book, especially those beginning with "desoxy" or
"deoxy." "Desoxy" was the standard spelling for compounds of this class through the
first half of this century, and it was changed to "deoxy" by an international nomen-
clature committee in the late 1950s. I have used the old spelling only when quoting
old documents and have adhered to the revised form elsewhere, even though I do
not believe that it was a necessary or inspired change. In either form the term merely
implies the removal of an oxygen atom from the molecule; and deoxycholate is a
modification of the bile salt, cholate, with one of its oxygens deleted. Deoxyribose is
related to ribose through elimination of the oxygen attached to its fifth carbon atom.


110             The Transforming Principle

MacLeod characterized it as "very weak." It was very weak,
indeed, transformation being obtained only with 0.5 cc of the
undiluted extract. In the end, these difficulties led to the rad-
ical step of abandoning the Alloway procedure altogether. On
March 11, Avery tried his hand at an alternative approach
with a small batch of type III pneumococci from 2 liters of
culture. I think that it is likely that MacLeod was away from
the laboratory at the time, since the experiment is one of the
very few recorded entirely in Avery's hand. What he did was
to heat kill the pneumococcal cells immediately after they had
been recovered by centrifugation, the idea being to inactivate
the T. P. -destroying enzyme before extraction began. The dif-
ficulty posed by this maneuver was that the heat-killed cells
were no longer susceptible to lysis by deoxycholate, thus
interfering with extraction of the cellular contents. Avery tried
to circumvent this by shaking the suspension of heat-killed
cells with a somewhat higher concentration of deoxycholate
than needed for lysis, relying on the detergent properties of
the bile salt to leach material from the cells. His tests for
transforming activity showed that active material could be
obtained in this way.

I suspect that there was some difference of opinion between
Avery and MacLeod about the promise of this approach.
MacLeod had inserted two pages in the notebook describing
experiments carried out in 1935 in which he had tried a simi-
lar procedure with rather indifherent results. This clue, together
with the evidence that Avery had taken the unusual step of
initiating the new trial on his own, suggests that MacLeod was
not very optimistic about solving their extraction problems
this way. They compromised by undertaking an experiment
on March 18 in which the pneumococci from 40 liters of cul-
ture were divided into two equal parts; Avery immediately
heat-killed his share at 65oC for 30 minutes to repeat his pilot
experiment and MacLeod processed the other portion by the
usual procedure. They kept separate notes on the preparation
of their extracts but then joined in testing them for activity.


The Renewed Attack

111

In reviewing the protocols, I cannot see that Avery's extract
of heat-killed cells was substantially more active than Mac-
Lead's preparation from lysed organisms, although the titra-
tions were not yet being carried out in a manner that would
allow precise quantitative comparisons. On the other hand,
Avery's extract obviously contained less total material and
showed strikingly less reactivity with pneumococcal antisera.
The implication was that one could obtain at least as much
active transforming principle from the heat-killed cells while
bringing along with it a smaller amount of the inert materials
that they would have to get rid of in the process of purifica-
tion. On March 25 they took the obvious next step of prepar-
ing an entire lot with heat-killed cells from 45 liters of culture.
This was a success, and the Alloway procedure was not used
again in the continuing drive to uncover the nature of the
transforming substance.

Even though the results of the comparison of the two
methods of extraction had not been dramatic, the laboratory
notes of this period began to reflect a remarkable change in
outlook of the research. Not only was the production of satis-
factory extracts much more consistent, but it gradually became
apparent that they were dealing with considerably more potent
material. Rather than obtaining extracts that were considered
potent if 0.1 cc was able to effect transformation, as defined
in their earlier work, they began to encounter material that
was active when 0.1 cc of a hundredfold dilution was tested.
Occasionally transformation occurred even when 1:lOOO dilu-
tions were used. It was apparent that much of the active mate-
rial must have been destroyed in the process of deoxycholate
lysis and that they now had in hand a procedure that was pro-
viding considerably more favorable starting material for puri-
fication.

This new development was still in its preliminary stages
when they had to prepare the annual spring scientific report
for the Board of Scientific Directors, and consequently this
change in approach to the extraction of the transforming prin-


112              The Transforming Principle

ciple was not described. In fact, their report in general was
somewhat reserved, as if they were holding back a bit. They
even gave their section of the report a rather cryptic title:
"Studies on Capsular Synthesis by Pneumococci." The omis-
sions in the report can only be explained by assuming that
they considered the work incomplete and in need of confir-
mation before it could be described in writing, even in an
internal document such as this. Thus, they say nothing about
finding DNA in the extracts, nor do they mention the cal-
cium-alcohol fractionation results. The failure to mention DNA
becomes more pointed in view of the following comment which
they made about the ribonuclease experiment during which
the diphenylamine test was first used: "Extracts prepared in
this manner [essentially the Alloway method] contain consid-
erable amounts of nucleic acid. The latter substance may be
almost completely removed by digestion with crystalline
ribonuclease without affecting the transforming potency."
Much of the report deals with a line of investigation, car-
ried on concurrently with the fractionation attempts, that
involved further study of the various crude enzyme prepara-
tions that were able to destroy the transforming substance.
The idea, of course, was to seek for clues as to the nature of
the active substance by determining what components these
enzyme preparations had in common; in other words, what
kind of an enzyme was causing the destruction. They had turned
up the information, more misleading than helpful in the long
run, that each of the effective enzyme mixtures contained an
esterase which they measured by its action on a low-molecu-
lar-weight ester (really in this case a simple fat, glycerol fully
esterified with butyric acid). Their interest in this component
was heightened by the fact that fluoride, a known esterase
inhibitor, exerted some inhibitory effect on the action of the
enzymes on the transforming substance. The following com-
ment was included in the report: "From the evidence obtained
by the use of various enzyme preparations it is not held that
the specific transforming principle is necessarily of the nature


The Renewed Attack                        113

of an ester, inasmuch as other enzymes may have been present.
However, the evidence obtained by the use of sodium fluo-
ride as an enzyme inhibitor when taken in conjunction with
other studies, suggests that the transforming principle may be
an esterified compound." It was never clear to me what kind
of esters they had in mind, and there is nothing to indicate
that they were considering the kind of phosphodiesters that
hold together the backbone of nucleic acids.
Sometime earlier that year MacLeod must have been
approached by New York University with an offer for him to
assume the chairmanship of the department of microbiology
at its college of medicine. I have no record of the date or the
details of negotiations, but it must have disrupted progress in
the laboratory work. The matter was settled by March 1941,
since Tillett knew of Cohn's impending move when the Fel-
lowship Board of the National Research Council suggested that
I go to Rockefeller to work with him. The prospect of this
move was inevitably a blow to Avery and, as I found later,
was not something that MacLeod anticipated with unalloyed
enthusiasm.
Colin talked about this matter at some length in a late
night conversation when we were sharing living quarters dur-
ing a meeting at Yale University in 1959. He had had no desire
to leave Rockefeller and, on the contrary, was hopeful of find-
ing a permanent place there. However, when he went to Dr.
Rivers, the director of the hospital, with the news of the New
York University offer, rather than generating some counter-
offer from Rockefeller, he was strongly urged to take the job.
The implication of this kind of advice from the director was
that the prospects were dim at Rockefeller and that he should
grab a good opportunity when he had it. My own reconstruc-
tion of the situation was that Rivers had already selected the
individual who would head a continuing pneumonia service
at the hospital after Avery's retirement two years hence. This
was Frank Horsfall, always a Rivers favorite, who had left the
Avery laboratory in 1937 to join the Rockefeller Foundation


114             The Transforming Principle

laboratories that were maintained on the Institute campus
where he was engaged in virus research. This fit in with Riv-
ers's interests and his idea that studies on pneumonia in the
future should focus on viral pneumonia. In any event, Hors-
fall was made a full member of the Rockefeller Institute as of
July 1941 and rejoined the Avery laboratory just as MacLeod
was leaving.

Thus, in a sense, Colin lost out to his old friend and col-
league. He was not the kind of person, however, to be immo-
bilized by disappointment, and he continued vigorous activity
in the laboratory while preparing himself for the move to
N.Y. U. and a rather different career. The research followed
the path that had already been started, with some more
experiments on the inactivating enzymes and their inhibition
and a number of attempts to sharpen up the results of frac-
tionation of the extracts with calcium and alcohol. A dozen
additional large batches of type III pneumococcal cells were
extracted during May and June to provide material for frac-
tionation, although the final four were precipitated by alcohol
and stored over the summer for future work. By and large,
the results were so variable as to be encouraging one day and
discouraging the next. The transforming activity might be
largely concentrated in a single fraction in one experiment
and then spread throughout a series of fractions when they
repeated it. A given procedure would give promise of sepa-
rating T.P. from other components, such as RNA and SSSIII,
but behave quite differently when they tried it again. Looking
back with the knowledge of subsequent events, I would guess
that their difficulties came from the complexity of the mixture
with its variable concentration of the several components, since
the sharpness of precipitation with both alcohol and calcium
depends on the relative concentration of these components.

It is not always easy to follow the details of the manipula-
tions used in the fractionation attempts, but one significant
new ingredient was introduced during this period. In an
experiment carried out on May 12, MacLeod commented as


The Renewed Attack                       115

follows: "It has been noticed previously that when alcohol is
added to an extract, the precipitates formed are of 2 kinds-
a. coming out at about i/2-3/4 volume of alcohol is stringy, veil-
like; b. flocculent at higher concentrations of alcohol. In this
expt., therefore, the attempt is made to obtain these 2 gross
fractions separately. " On this occasion most of the transform-
ing activity and most of the type III polysaccharide (or SSS)
appeared in the first type of precipitate and most of the RNA
in the flocculent fraction. However, the results on further trials
of this kind were inconsistent, and they obtained some sug-
gestion of separation of T.P. and SSS in this process.
The notes make it clear that they were equating the stringy
or fibrous alcohol precipitates with SSS and attributed the vis-
cosity of solutions of the extracts to this component. Scattered
throughout the descriptions of the procedures are comments
such as: "viscous-like SSS, " "precipitate stringy, fibrous-looks
like SSS," and "Ppt. is flocculent with very few strings of SSS."
They had a good reason for this assumption, since they had
earlier obtained a quite pure preparation of SSS with these
properties as a by-product of their fractionation efforts.
Nevertheless, this notion tended to obscure the possibility
that there might be another component of the extract with
similar properties.
Just as he was departing MacLeod wrote on July 7, as a
kind of distillate of the year's efforts on T.P., a detailed sum-
mary of the methods they had adopted for the preparation of
extracts, and he included a flow sheet describing procedures
for fractionation with calcium and alcohol. Since the latter was
based on a series of rather inconsistent experiments, he had
to hedge a little in defining what one could expect from the
individual steps. Then at the end of his outline of the method
he added two final sentences: "In this process of purification
there has been a great loss of activity. It may be necessary to
increase the concentration of SSS to improve the results." This
latter comment is rather cryptic, since there is little in the
notes to suggest that they had considered the type III poly-


116              The Transforming Principle

saccharide of importance in the transforming reaction. As a
matter of fact, it had long been assumed in the laboratory that
type III SSS had nothing to do with it. I later learned what
these second thoughts about the role of SSS in transformation
were all about.

It had recently been discovered that an enzyme capable
of synthesizing glycogen (a polysaccharide composed, like
starch, of only glucose molecules) would not work unless some
glycogen molecules were present in the reaction system. In
other words, the enzyme had to be primed by some of the
end product that it could build on during the synthesis. As an
explanation for the confusing results and loss of activity
encountered in their fractionation experiments, Avery atid
MacLeod had conceived the notion that something of the sort
might be involved in transformation. Without weakening their
conviction that the transforming principle was distinct from
the type III polysaccharide, it seemed possible that the enzymes
induced by T.P. in the process of transformation would not
be able to initiate the synthesis of the polysaccharide and form
a capsule unless there was an adequate supply of SSS in the
system to serve as a primer. They were not confident that
their tests of the role of the polysaccharide carried out years
earlier had eliminated this possibility. The need to resolve
this question provided me with my first project on transfor-
mation after I joined the laboratory that fall.

In essence, then, this was the state of the research on
transformation when I arrived on the scene in September 1941.


VII

MY INITIATION

ABOR DAY fell on September 1st in 1941, forcing me to
L delay my long anticipated appearance at the Hospital
  of the Rockefeller Institute until Tuesday the 2nd. When
I presented myself at the front desk, it was pretty obvious that
the receptionist was not expecting me. After her call to the
laboratory to confirm that I was a new postdoctoral fellow, it
was Frank Horsfall himself who came down to greet me. He
also seemed to be no more than vaguely aware that I was
scheduled to join the laboratory, but he received me cordially
and was most helpful in getting me settled and introduced to
the other members of the group. Although I knew that Avery
would not yet be back from Maine, I had seen no reason to
wait for his arrival to begin the fellowship. As it turned out, I
had an opportunity before his return to learn about the gen-
eral operations of the laboratory and to become familiar with
some of the Institute's other outstanding facilities: the superb
library and the fabulous lunch room. It was in the latter that
I was able to meet within a matter of weeks essentially all of
the members of the Institute's scientific staff.

Nothing about the Avery laboratory would impress those
who have depended on the movies for their idealized picture
of a laboratory. It had no elaborate or mysterious equipment,


The Rockefeller Hospital. The Avery laboratories were on the sixth floor at the left
(the east end of the building).  (From the ffockefe//er University Archives.)


My lnitiation

119

and of course no automated apparatus, electronic gadgets, or
computers. Even its structural features seemed anomalous,
since the area had originally been designed as a hospital ward
and was modified very little for its revised function. The orig-
inal planners of the hospital had overestimated the amount of
bed space that would be required in relation to research lab-
oratory space. The number of patients need not be too large
for intensive clinical research, and indeed if too many are
involved the investigators may be so overwhelmed by purely
clinical responsibilities that the research is shortchanged. In
order to correct the imbalance, the sixth floor of the hospital,
where the Avery laboratory was located, had been converted
in the early years to laboratory space without any significant
expenditure of funds. None of the partitions were changed,
and the wards, private rooms, kitchens, etc., were simply
adapted to their new function by moving in a different type of
furnishings. The basic unit for each investigator was the
microscope desk, a modification of the conventional knee-hole
desk that had a microscope cabinet on one side. The standard
accessories for bacteriological work at each desk were a Bun-
sen burner, a collection of bacteriological loops and needles
made of platinum wire attached to long rods, and receptacles
for the disposal of contaminated glassware.

The large room to which I was assigned had four of these
desks. Mine was placed in front of the marble mantel of a
fireplace, part of the embellishment of the original ward but
of course no longer functional. Aside from an incubator, a sink,
a fume hood, and a large square cabinet with a flat top surface
in the middle of the room, there was not much else in evi-
dence. The collection of centrifuges were all segregated in a
small room in another area where their noise could be con-
tained. Avery's private laboratory, in a small room adjoining
the main lab, had apparently originally been a ward kitchen
and was reached through a swinging door equipped with an
oval window. His desk stood against a bank of north-facing
windows but the view of the campus was usually obscured by


120              The Transforming Principle
a dark shade that was drawn to provide a better background
for the examination of various test tube reactions with the aid
of a green-shaded lamp that hung over the desk, suspended
from the ceiling. An electric refrigerator of the household
variety was the only item of equipment. On the other side of
his laboratory, through another swinging door, was a small
room modestly equipped for chemical work. Here I ulti-
mately carried out the experiments for preparation of an enzyme
that would break down DNA.
The stock-in-trade of the laboratory was sterile glassware,
and the collection was quite large and diverse. It included
flasks of different sizes, ranging from cumbersome ones of 4-
liter capactiy that were used for growing the mass cultures of
pneumococci, down to tiny flasks for analytical purposes; var-
ious kinds of test tubes, dominated by a large supply of Was-
sermann tubes for the transformation experiments; and
graduated pipettes of l-, 2-, 5, and lo-cc capacity, each of
which had been individually wrapped in brown paper before
sterilization. The fractionation of the extracts also required a
number of beakers, bottles, and other items for the "kitchen
chemistry"-as Avery called it. Then there were a number of
heavy glass centrifuge tubes and bottles, specially designed to
withstand breakage under the stress of centrifuging. All in all,
the place was set up in much the same way bacteriological
labs had been for a long time.
By the time Avery returned in the middle of September,
I was pretty well acclimated. Having read much more about
the pneumococcus and the earlier work of the laboratory, I
felt that I was prepared for his indoctrinating process. There
were two other young investigators in the laboratory, Dick
Mirick and Ed Curnen, who had been working with MacLeod
for two years on certain aspects of the sulfonamide problem
and were continuing their projects. They had given me some
idea of what I was to expect from Avery as my introduction to
the family and had warned me that I was not going to be
assigned a problem. The decision on my project would emerge


0. T. Avery in 1941 at about the time the author joined his laboratory.


122              The Transforming Principle

from talks with Avery and my reading and would be pretty
much up to me.

The heart of the Avery process of orientation was a series
of beautifully planned discourses that dealt with the major
lines of his pneumococcal research. These discourses had come
to be known by his young associates as Fess's "Red Seal Rec-
ords," a term that reflected their high quality and also the fact
that they tended to be repeated in much the same form on
each occasion that he delivered them. It is not that they were
memorized and repeated word for word, but certain phrases
and descriptive terms had caught his fancy so that he used
them consistently in the same way in telling a given story. He
had preselected th e most effective language and then stuck to
it. There is no doubt that the Red Seal Records were effec-
tive. They were used not only for new arrivals in the labora-
tory but also for visitors and for young members of other
research groups in the hospital. Many of the latter have vivid
memories of these discourses, usually given in the evening or
on a weekend when Fess was likely to be on hand and pleased
to find a willing listener.

None of Avery's former colleagues have been able to explain
his extraordinary success in training young scientists. Even
though his research group was never very large, a remarkable
number of those who passed through his laboratory emerged
as leaders in medical microbiology. Certainly more was involved
than the Red Seal Records, his philosophy of scientific research,
and notions about how a laboratory should be operated. Some
of his originality and creativity must have rubbed off on us as
we learned from his experimental genius. The objective evi-
dence for his success in turning out skilled investigators is
clear. At least a dozen of his former "students" were subse-
quently elected to membership in the National Academy of
Sciences, and this was at a time when the Academy had well
under a thousand members in all fields of science, only a small
fraction of whom were in the medical sciences. When I was
elected to membership in 1963, the Section on Pathology and


My Initiation                             123
Microbiology (which included most of those in medical sci-
ence) had only forty-six members, and ten of them were for-
mer associates of Avery. His influence was also reflected in
the composition of the staff of the Rockefeller Institute. In
1953, just as it was entering a period of rapid growth with the
addition of a program in graduate education, there were only
eighteen on the entire Institute staff with the top rank of
Member, and four of these had come from Avery.
It was from one of Fess's discourses, shortly after his return
from Maine, that I first heard the full story of the transfor-
mation phenomenon and learned what he and MacLeod had
been up to for the past year. It captured my imagination from
the beginning. I was soon certain that I wanted to work on
the problem, but I wasn't sure how matters stood and was
uncertain how to broach the subject. MacLeod had paid some
visits to the laboratory beginning in the first week after Avery's
return in order to join him in another crack at their fraction-
ation procedure, using the four extracts that they had stored
under alcohol over the summer. On one of these occasions, I
can recall the three of us standing around that high cabinet in
the center of the lab discussing possible research problems
for my fellowship year. MacLeod enthusiastically suggested
that I pursue further the work I had done with Tillett on the
prevention of benzene leukopenia by sulfapyridine. Nothing
could have been further from my thoughts.
I now realize that I was not sufficiently sensitive to
MacLeod's feelings about the transformation problem
throughout the early years of our association. I did not know
then that he had left Rockefeller most reluctantly, nor was I
yet aware of how large a stake he had in the development of
the research over several years. It is even possible that he
entertained some notion of taking the problem with him to
N.Y. U. There was every reason to suppose on the basis of past
performance that Fess would not pursue it on his own.
MacLeod could not have looked upon my untimely arrival in
the lab with other than mixed feelings. Yet he was always


124             The Transforming Principle

generous and helpful to me, and our friendship never appeared
to be poisoned with any taint of resentment. Many years later,
after his death, I received the first hint that he may have been
less than pleased with my participation in the research.
The efforts of MacLeod and Avery that September to
sharpen up the results of their fractionation procedure met
with the same kind of variability that they had encountered
earlier. MacLeod was clearly only present for short periods
during these experiments, but he wrote the notes for the frac-
tionation attempts. At the end of his summary, which repre-
sented a flow sheet for the procedure, he added the following
note: "most of the activity should be in Ppt. #4." Unfortu-!
nately, from the transformation tests carried out by Avery, it j
was evident that "Ppt. #4" had very little activity and that1
most of it was present in another fraction that was designated!
SSS. None of the fractions gave a diphenylamine test, pre-
sumably because they were too dilute. It was obvious that the
procedure was giving unpredictable results and still left them
with some apparent ambiguity concerning the part played by
sss.
Avery continued to carry out experiments with the extract
prepared that September, testing the various fractions and
trying to sort out the confusing results. Then one day late in
the month, while I was still undergoing my informal indoctri-
nation, he suggested that since I seemed interested in the
transformation problem I might like to join him in setting up
one of the tests and observe the phenomenon at first hand.
Discussion of this experiment and its implications led to my
participation in other tests, and without any explicit agree-'
ment about my role I quickly slipped into the position of his:
full-time collaborator in the research. From the second week
of October onward all of the laboratory notes are in my hand
with only occasional entries by Avery. Thus, the usual process
of selecting a research problem had been accelerated in my
case, stimulated by my obvious interest in the search for the


My lnitiation                            125

identity of the transforming principle and Avery's pressing
desire to get on with it.
Avery was an active participant in the laboratory work,
even though I soon found out for myself that he was not inclined
to initiate a new experiment. After we talked over what steps
to take next and agreed on a course of action, it was up to me
to set up the protocol and assemble the necessary materials.
However, he would then review the protocol and join me with
enthusiasm as we sat side by side to set up the experiment.
Often this involved a large number of test tubes to accom-
modate the several variables being tested, in addition to a
number of controls. It was in this manner that I was intro-
duced to Avery's extraordinarily rigorous bacteriological tech-
nique. He was fond of telling how he and Ben White, his
associate at the Hoagland Laboratory in his pre-Rockefeller
days, had agreed that they would treat all bacterial cultures
as though they contained the plague bacillus. They realized
that it was a common failing to become sloppy in handling
nonpathogenic organisms which in turn led to some relaxation
of acceptable techniques when dealing with more infectious
agents. Avery adhered for his entire career to this early reso-
lution to use maximum care in handling all bacteria.
In practice, his technique involved a series of rituals for
such procedures as unwrapping sterile pipettes, flaming the
bacteriological loop, or manipulating the cotton plugs of ster-
ile tubes or flasks. An experiment was not begun until the
required tubes, pipettes, reagents, and racks were systemat-
ically arranged on the desk for ready accessibility, and the
Bunsen burner properly positioned. He would then draw the
chair close so that the right hand, holding the pipette, could
be stabilized by placing the right elbow firmly on the desk.
The pipette, containing such material as the sterile medium
or bacterial culture, would then be held nearly stationary, with
the tip one or two inches from the flame of the Bunsen burner.
The left hand would be used to move tubes and flasks to the


126             The Transforming Principle

scene of the action, bringing them first to the fourth and fifth
fingers of the right hand for removal of the cotton plug, then
to the burner for flaming of the opening, to the pipette tip for
delivery of the sample, back to the burner for reflaming, and
then to the right hand to retrieve the plug. All this was done
with almost no movement of the pipette. A break in tech-
nique, such as touching the pipette to the outside of a tube or
brushing a hand against an exposed cotton plug, resulted in
immediate discarding of the possibly contaminated material.
As a result of these precautions, chance contamination during
the setting up of an experiment was virtually eliminated.

Although I soon began experiments directed toward the
major goal of the research on transformation, an important
prerequisite was to learn the procedures for preparing extracts
from the mass cultures of type III pneumococci. On October
21 Cohn MacLeod came to the laboratory to guide my hand
in my first attempt to cope with a batch of organisms from the
Sharples centrifuge. As was the custom, the cultures were
handled by Fred Kimmer, an elderly technician who had been
at the Institute for many years and at one time had worked
with Noguchi. He inoculated 51 liters of culture medium (sev-
enteen 4-liter flasks containing 3 liters of medium each) with
a heavy inoculum of type III pneumococci early in the morn-
ing so that they would be ready for harvesting by mid-morn-
ing. The culture was chilled as it ran into the Sharples by
passing it through copper tubing immersed in an ice-water
bath in order to terminate growth and protect it from possible
overheating during the final steam sterilization of the outer
centrifuge chamber. After completion of the centrifuge run,
the cylinder containing the packed organisms was removed,
wrapped in a Lysol-soaked towel, and delivered to the labo-
ratory. Then the fun began.

The problem was to get the bacterial cake out of the cy1-i
inder and into suspension in salt solution without spreadin
viable organisms all over the place. Teddy Nadeje, the same
technician who had aided MacLeod in devising the housing


My lnitiation                             127

for the centrifuge, had fashioned an instrument for scooping
the organisms out of the cylinder. It was a half-round, thin
metal plate machined to fit the inner surface of the cylinder
and attached to a long metal rod. The bacterial cake was trans-
ferred to a beaker on this gadget where it was scraped off with
the aid of a spatula. After several repetitions of this procedure
and some washing with salt solution, the material was all in
the beaker ready to be smoothly suspended in more salt solu-
tion and promptly heat killed. It was, however, a messy pro-
cedure. No matter how careful one tried to be in scooping the
bacterial cake from the cylinder, there were bound to be little
slips and sudden jerks. As a result, one would see small flecks
of white material fly in one direction or another with the dis-
concerting awareness that they were composed of millions of
viable pneumococci. Despite all precautions and the liberal
use of germicides, one could not complete the task without
the conviction that he had thoroughly contaminated himself
and the immediate environment.
Following my lesson from MacLeod on how it was done,
I processed a large batch of pneumococci on the average of
once a week for the next few months. Each of these was
extracted by shaking the suspension of heat-killed organisms
in the presence of deoxycholate and, after removing the
organisms by centrifugation, the extract was precipitated by
alcohol. The total precipitate was then redissolved in salt solu-
tion for removal of protein by repeated application of the Sevag
method. At this point, most of these early extracts that I pre-
pared were freeze-dried, a procedure that effectively pre-
served the activity of the crude extracts so that they could be
reconstituted as needed later for fractionation experiments.
Material from several hundred liters of culture had been
stockpiled in this way by the end of January 1942.
As I was handling these "Sharples runs," as we called them,
I gradually became aware that Fess was never present in the
laboratory while the organisms were being removed from the
Sharples cylinder and prepared for heat killing. If he hap-


128              The Transforming Principle

pened to be there when the cylinder was brought up from the
centrifuge room, he would quickly disappear. While I could
give no credence to Fred Kimmer's view that this behavior
was motivated by fear of possible infection, it took me some
time to realize what the answer really was. It was simply that
he could not bear to witness a procedure that deviated so far
from his standards of correct bacteriological practice. He
accepted its necessity for the research, but he could not be a
party to it. As soon as the bacterial suspension had been killed
by heating at 65oC for 30 minutes, he was ready to take part
in all of the subsequent steps.
Concurrently with the business of making transforming
extracts, I had begun analytical studies to reexamine the pos-
sible part played by the type III capsular polysaccharide in
transformation. Was it really necessary to have a little SSS
around as a template or primer in order for the transformed
cell to start synthesizing the polysaccharide so that it could
form a capsule? With the availability of the Dubos SIII enzyme
this would seem to be a simple question to answer, and indeed
the enzyme had been applied to the problem earlier, although
I was not aware of this at the time. Both Rogers in 1933 and
MacLeod in 1935 had tested the effect of the enzyme on their
transforming extracts and found that it did not seem to affect
transforming activity. The experience that MacLeod and Avery
had with their fractionation experiments in the spring of 1941
raised some doubts in their minds whether these early tests
had been sufficiently quantitative and complete enough to
answer the question. The idea was to be certain that the SIR
polysaccharide was completely eliminated by the enzyme and
that even the split products of the enzyme's action were
removed.
Dubos, who still had some of his original preparations stored
in the freeze-dried form, supplied the enzyme for my attempts
to deal with the problem. The activity of the enzyme could be
demonstrated quite simply by adding some of it to a solution
of the type III polysaccharide and then testing samples at


My lnitiation                             129

intervals for their ability to give a precipitate with type III
antiserum. A good enzyme preparation could destroy the pre-
cipitating reactivity of a dilute solution of the polysaccharide
in less than an hour. Since our type III antisera would form a
visible precipitate with solutions of polysaccharide at concen-
trations as low as 0.0002 milligram per cubic centimeter, the
test had a good degree of sensitivity. As I began experiments
on the effect of the enzyme on transforming extracts, I was
treated to a thorough indoctrination on the vagaries of the
transforming system. I encountered all of the difficulties of
the past and learned the methods of checking the medium,
the chest fluid, and the R strain as possible sources of the
trouble. After one experiment in which there was no growth
in any of the tubes, I inspected the test tubes for incomplete
removal of the detergent used in washing the glassware. It
was necessary to consider all possible sources of trouble and
to be persistent until the problem was solved. A great deal of
repetition of experiments was required.
At the end of November I finally completed a protocol
experiment that was satisfactory from all points of view. This
showed that if one treated a transforming extract with the
enzyme until it no longer had any serologically detectable type
III polysaccharide, and then thoroughly dialyzed away the split
products of the enzymatic reaction, there was no loss what-
ever of transforming activity. Although I did a few more
experiments of this kind to substantiate the finding, the results
were quite conclusive in establishing that SSS did not have to
be present for transformation to occur. It was time, therefore,
to get on with an effort to isolate and identify the transforming
substance.
One of the clear implications of the SIII enzyme results
was that the type III polysaccharide was something that we
should strive to get rid of in the process of purification of T. P.,
just as we did with protein. The enzyme was an obvious can-
didate for the job, but the supplies then available, while quite
adequate for the analytical studies, were not up to tackling


130              The Transforming Principle

the large amounts of polysaccharide contained in whole extracts.
This led us to consider other possible means of reducing the
amount of polysaccharide present in the extracts, to a point
where the residual remaining could be removed by the lim-
ited amounts of enzyme. One such possibility that suggested
itself was to modify the conditions under which we grew the
type III pneumococci for extraction. In the procedure we were
then using, Fred Kimmer would add a generous shot of glu-
cose to each flask to enhance growth during the last 2 hours
of incubation. This certainly achieved its purpose, but at the
same time the glucose, which the organisms used for the syn-
thesis of polysaccharide as well as for metabolic energy, greatly
increased the amount of capsular material produced. We
decided to try using a smaller initial inoculum of type III
pneumococci and incubating the cultures overnight without
the addition of excess glucose.

When the next extract was prepared after the successful
SIII enzyme experiment, on December 2, we adopted this
modified procedure. As expected, the bulk of packed cells
obtained after centrifugation was smaller than usual, and cor-
respondingly the amount of material extracted seemed to be
less, as indicated by the appearance of the alcohol precipitate.
Compensating for the reduced yield, serological analysis
showed that the extract had only a fraction-not more than
lo-15 percent-of the type III polysaccharide found in an
extract prepared two weeks earlier by the old method. The
real surprise came when we tested its transforming activity.
It was more potent than any previous extract. Transformation
occurred in tubes to which we had added as little as 0.3 cc of
a l:lO,OOO dilution, Two repetitions of this procedure con-
firmed that we could obtain highly active material containing
substantially less SSS in this way, and we abandoned the use
of extra glucose from then on.

I had driven into the laboratory on Sunday, December 7,
to read the agar plates from the transforming test of the prom-
ising extract prepared earlier that week and to set out some


My lnitiation                            13'
cultures for the next day. On the way home I heard news of
the Japanese attack on Pearl Harbor on the car radio. The
turbulent world situation, disturbing enough before this, was
now even closer to home. Not immune to the surge of patriotic
fervor, I found it difficult at first to concentrate on laboratory
work, Dr. Rivers had had the foresight to make some prepa-
rations for war as far as the Rockefeller Hospital was con-
cerned. A year or so earlier he had organized a U.S. Naval
Reserve unit for medical research to be based at the hospital.
If the unit were called to active duty, it was his intention to
use the hospital for special studies of medical problems that
arose among the navy personnel. He had recruited into the
naval reserve most of the younger men on the hospital staff,
including Horsfall, Mirick, and Curnen of the Avery labora-
tory. When I went to Rivers shortly after Pearl Harbor and
asked to join the reserve unit, he declined my request. His
reasoning was that I was married, with young children, and
thus unlikely to be drafted. He suggested that I carry on just
as I had been.
Without being wholly comfortable with his decision, I
managed to throw myself back into laboratory work. My efforts
during the succeeding weeks centered on trying a number of
different ways of separating the type III polysaccharide and
RNA from the active transforming principle in the hope of
finding methods that might be applied to the purification pro-
cess. Some of these had been tried before by MacLeod, and
I didn't have any more luck than he had in hitting upon a
selective method. It did occur to me, however, that in addi-
tion to limiting the amount of glucose available to the pneu-
mococci during growth it might be worthwhile to wash the
organisms before extracting them with deoxycholate. Since
the polysaccharide is on the surface of the bacterial cells,
washing the cells offered some promise of removing a large
part of it and possibly even some of the RNA. Up to that time
the routine procedure had been to add deoxycholate to the
bacterial suspension immediately after heat killing and to pro-


132              The Transforming Principle

teed directly with extraction. In pilot experiments with small
batches of pneumococci, I centrifuged the organisms after the
heat-killing step and washed them with more salt solution
before submitting them to deoxycholate extraction. Tests of
the individual fractions revealed rather unexpectedly that there
was readily detectable transforming activity both in the super-
natant of the heat-killed cells and in the saline wash. There
was much more in the deoxycholate extract, however, and
any losses encountered were more than compensated for by
the marked reduction in the amount of type III polysacchar-
ide and RNA present in comparison with that in the super-
natant of the heat-killed cells. Later experiments with large
batches and more quantitative titration methods showed that
more than 90 percent of the transforming activity could be
recovered in the deoxycholate fraction even after repeated
saline washing of the cells before extraction. We were on the
way to a more rational set of extraction procedures.
During the early weeks of 1942 I also pursued further the
possible use of the SIII enzyme in purification of the trans-
forming substance. While I had to come ultimately to the
preparation of my own enzyme for this purpose, I still had
enough from Dubos at this point for a number of trials. An
extract prepared on December 16 from cells grown without
extra glucose had been stored under alcohol after `deproteini-
zation rather than dried from the frozen state. This material
was redissolved and subjected to further purification attempts
using both the SIII enzyme and ribonuclease. After repeating
the Sevag process to remove the added enzyme protein and
dialyzing the solution to eliminate split products, it was pre-
cipitated with alcohol. To our surprise, before one volume of
alcohol had been added, a stringy mass of fibrous precipitate
separated out. Clearly it was not only the type III polysac-
charide in our extracts that could yield alcohol precipitates
with these properties. Furthermore, after crude separation of
this fibrous precipitate from the more flocculent precipitate
produced by higher concentrations of alcohol, transformation


My lnitiation                              133

tests showed that 99.9 percent of the activity was in the fibrous
fraction.

At the time these observations were made in January 1942,
there is no indication in the notes that we equated the fibrous
alcohol precipitate with DNA. Curiously, we did not even
record any diphenylamine tests for deoxyribose on the frac-
tions. The emphasis of our tests was solely on protein, RNA,
and SSSIII-the components of the extract that we were trying
to get rid of and thus needed evidence for success in elimi-
nating them. Nevertheless, this experiment marks the begin-
ning of a period when our attention was focused with increasing
sharpness on the possibility that the transforming principle
might indeed be DNA. I have tried as best I can to recon-
struct the sequence of events during this period in an attempt
to sort out the various factors that influenced us to direct our
primary attention to DNA.


VIII

INTIMATION OF
  SUCCESS

T HE PROCESS leading to our serious consideration of DNA
  as the bearer of transforming activity was surely grad-
  ual. Nothing in my memory or in the laboratory notes

suggests that there was a moment of sudden revelation, a sin-
gle experiment that resulted in a flash of insight and reorien-
tation of our thinking. On the contrary, the results of several
different experiments and the injection of some new infor-
mation from outside the laboratory were all involved in the
crystallization of the concept. Almost certainly the notion that
DNA might be the transforming principle had been enter-
tained from time to time after MacLeod and Avery had detected
the presence of DNA in their extracts a year earlier. It was an
attractive possible identity for a substance capable of causing
predictable and heritable changes in pneumococci in view of
the known localization of the DNA of higher organisms in the
chromosomes, the heart of the genetic apparatus. It had not
been possible to design experiments that would test this notion
directly, however, and none of the data obtained during the
previous year threw much light on the problem. By January
1942 we were aware that the transforming principle was usu-


Intimation of Success                      135

ally associated with material that gave a stringy, fibrous pre-
cipitate with alcohol-even when there was no type III
polysaccharide present-and before long we recognized that
most of the DNA in our extracts occurred in this same fibrous
fraction. At about this same time we had an opportunity to
learn more about the appearance and properties of pure DNA
as isolated by an improved technique from mammalian tis-
sues. This was new to us, since the sample of thymus nucleic
acid that we had obtained as a standard for the diphenylamine
test had been extracted with strong alkali, and it was a brown-
ish powder without any of the characteristics that we later
knew to be typical of native DNA. This sample had come from
a collection of chemicals that had accumulated in the labora-
tory of P. A. Levene, a Rockefeller biochemist who had car-
ried out much of the structural work on the nucleic acids.
Two floors above us, at the top of the hospital building,
the biochemist, Alfred E. Mirsky, had been for some time
carrying out basic studies on proteins. He was associated with
the laboratory of Alfred E. Cohn whose clinical studies were
concerned with heart disease, and as a result Mirsky's efforts
had been directed toward studies of myosin, the principal
protein constituent of muscle, including heart muscle. In the
spring of 1941, his findings with myosin led him to take a look
at another substance with similar properties that had been
described a few years earlier and given the name "plasmosin,"
indicating its supposed origin from the cytoplasm of liver cells.
In the course of purifying plasmosin, Mirsky found that it was
quite different from myosin, being composed of a complex of
nucleic acid and protein, with the nucleic acid component being
DNA. In collaboration with the cytologist, A. W. Pollister of
Columbia University, he showed that this nucleoprotein was
in reality derived from the nucleus of tissue cells, and they
ultimately gave it the name "chromosin."
Mirsky and Pollister refined the methods that had been
used in extracting material like plasmosin into an elegant pro-
cedure for obtaining pure preparations of DNA nucleoprotein


136             The Transfortvaing Principle

from any tissue. Simple and elegant, the method required
little more than the use of salt solutions of different strengths.
Organs like liver, spleen, or thymus were blended repeatedly
with physiological salt solution-so called because it is com-
patible with blood and tissues-which dissolved away most of
the soluble material of the cells and left behind an insoluble
residue composed largely of the cell nuclei. When this nuclear
residue was then placed in a much stronger salt solution that
contained about seven times the concentration of sodium
chloride used to make physiological salt solution, much of the
material began to dissolve immediately to form highly viscous
solutions of the nucleoprotein. The nucleoprotein could be
precipitated from this solution in the form of fibrous strands
simply by pouring it into several volumes of distilled water to
reduce the salt concentration. Repetition of this process of
solution in strong salt and reprecipitation by dilution led to
purified products from which essentially all of the cellular
constituents other than nucleoprotein had been removed.
The DNA and protein in these preparations are not linked
together by firm chemical bonds but are attracted to each other
by bearing opposite charges, the DNA being very acidic and
the protein (called histone) very basic. The attraction between
them is counteracted by high concentrations of sodium and
chloride ions, which is the reason that strong salt solutions are
able to dissolve the complex. To obtain pure DNA from this
mixture, Mirsky had only to apply the same chloroform
deproteinizing method of Sevag that we had been using on
the transforming extracts. It took some doing to achieve this
because the amount of protein was so great, but once it was
all removed there remained beautifully clear solutions of DNA
that no longer depended on high salt concentration for their
solubility. The DNA could be precipitated from solution by
alcohol to yield the same kind of fibrous mass that had become
so familiar to us with our pneumococcal material, and after
drying from pure alcohol and ether it appeared as a white


lntimutiofl of Success                       137

bundle of tangled fibers that bore some resemblance to as-
bestos.
Sometime in the late winter or early spring of 1942 Mirsky
gave us some preparations of his mammalian DNA. We were
thus able to look at the characteristics and properties of this
material in comparison with the fractions of our pneumococcal
extracts. He also told us of his finding that if, during the pro-
cess of precipitating his nucleoprotein by pouring the viscous
solution into water, he stirred the mixture, the fibrous precip-
itate would wind around the stirring rod so that it could be
simply lifted out as a single mass. It had been shown much
earlier by a Swedish worker, Hammarsten, that the same thing
would happen when pure DNA was precipitated by pouring
solutions into alcohol. On March 30, I did a small experiment
that I entitled: "The Nature of the Material in Transforming
Extracts Giving `Stringy' Precipitate in Alcohol." The notes of
this experiment begin with the following rationale: "A method
of preparing thymus-type nucleic acids depends upon the fact
that when a solution of the material is poured into alcohol in
a thin stream with constant stirring with a wooden rod, the
nucleic acid collects as a stringy mass around the rod. There
is apparently some thymus-type nucleic acid present in trans-
forming extracts, and there is also material which gives a stringy
precipitate with alcohol. The present experiment is carried
out to determine the relationship of the `stringy' material to
the thymus nucleic acid in the extracts and also to the trans-
forming activity. "
I used a solution of one of the freeze-dried preparations of
T.P. that had been stored away the previous fall. When the
solution of this crude material was poured into alcohol, how-
ever, the results were not so tidy as I would have liked. While
there was some fibrous precipitate that wrapped around the
stirring rod, similar fibers of precipitate could be seen floating
in the solution. The material was just a bit too crude to give a
sharply defined separation. Nevertheless, more than half of


138              The Transforming Principle

the DNA, as indicated by the diphenylamine test, and more
than half of the transforming activity were found in the frac-
tion that collected on the rod. Most of the RNA remained
with the material that had not adhered to the rod. The results
were clearly in the right direction and strengthened our grow-
ing suspicions that we might be dealing with DNA as the
transforming principle. The test also served as the model for
the technique that we later used in modified form in the final
purification of transforming DNA.
Much of our effort during the next month or two was
devoted to an entirely different approach that served to focus
our attention even more sharply on DNA. The ultracentrifuge
had recently been developed into a powerful tool for the analysis
of biological materials, based on the differential rate of sedi-
mentation of macromolecules of diBerent sizes. We were given
an opportunity to apply this kind of analysis to our transform-
ing extracts through the generous cooperation of Alexandre
Rothen, one of the physical chemists on the Institute staff.
Rothen's instrument, which had been designed and built at
the Institute, was housed in a basement laboratory and took
up most of the space in a medium-sized room. The centrifuge
itself required only a small corner, and the dominant feature
of the setup was the optical system used to visualize the rate
of sedimentation of components of the sample during centri-
fugation. With this device any macromolecular substance
present in adequate concentration could be detected as a
moving boundary while the sample was spinning at very high
speeds. The container in which the material was centrifuged
was tiny, holding only about one-half cubic centimeter, but
designed so that samples for chemical and biological analyses
could be accurately removed after completion of the centri-
fuge run.
We began our ultracentrifuge experiments in mid-April,
using one of the preparations of transforming substance that
had been purified by removal of both protein and SlII poly
saccharide. Very quickly we learned that the active substance


lfltimution of Success

139

must be an exceptionally large molecule and that it was not
present in very high concentration, since it was sedimented
more rapidly than the material that gave the fastest-moving
visible boundary. Even at the relatively moderate speed of
30,000 rpm, only 1 hour of centrifugation was required to con-
centrate 99 percent of the activity in the lower third of the
chamber. The only other known component of the extract that
was similarly concentrated under these conditions was DNA.
Here, then, was totally independent evidence to suggest that
transforming activity and DNA were somehow associated.

The results of our several analytical centrifuge runs led
Rothen to suggest that it might be useful to apply the machine
to the purification of transforming extracts by using what he
called the "concentration head."This would hold a number of
plastic centrifuge tubes and allow much larger volumes to be
spun at speeds comparable to that used with the analytical
chamber. We had on hand many of the freeze-dried lots of
transforming extracts that we had stored away the previous
fall, so that it was a simple matter to redissolve and pool some
of these to try out Rothen's suggestion. I was really not pre-
pared for the results of this experimental approach. I was quite
accustomed to spinning down bacteria and various types of
precipitate, but it had never occurred to me that it was pos-
sible to spin dissolved substances out of solution. This was, in
effect, what we encountered. After centrifuging our solution
of deproteinized, but otherwise quite crude, transforming
extracts at 30,000 rpm for a few hours, we found at the bottom
of each of the centrifuge tubes a translucent, gelatinous pellet
that remained behind after pouring off the supernatant fluid.
The pellets could be readily redissolved in salt solution and
shown to contain essentially all of the transforming activity
and the DNA of the original solution. At the same time most
of the RNA, the SIII polysaccharide, and other pneumococcal
antigens remained in the supernatant fluid. While it seemed
impractical to use the ultracentrifuge as a tool for the routine
purification of T.P., the findings added an additional strong


140             The Transforming Principle
piece of evidence that we should focus our efforts on DNA.
The requirement for accurate estimates of the transform-
ing activity in the various fractions obtained in the ultracen-
trifuge experiments made me decide to try to beef up the
method of titration so that we could get more reliable quan-
titative data. My exposure to some of the work going on by
this time in Horsfall's virus laboratory suggested that I might
adapt the procedures used in measuring virus infectivity in
mice to our system. Because of the biological variability of the
response of even inbred mice to infection with an agent such
as the influenza virus, it was necessary to inoculate several
mice with each of a series of dilutions of the virus preparation.
It was then possible to calculate with the aid of a statistical
method the minimal amount of the virus that was able to infect
50 percent of the mice-a 50 percent endpoint for the titra-
tion. I felt that the tubes we used to carry out the transfor-
mation reaction, while clearly less complicated than the mouse,
were showing the same kind of variability. Thus, by using four
or more replicate tubes with each dilution of a solution of
transforming substance, I could also calculate 50 percent end-
points. This proved to be effective, and as long as the system
was working well I could get a good estimate of the relative
content of T.P. in each of the fractions that were recovered
from Rothen's centrifuge tubes. This became a routine method
of assay, and it was applied to a variety of other fractionation
experiments as well as to the measurement of the activity of
the final purified preparations.
All this was going on amidst some further distractions
occasioned by the war. In March, despite Dr. Rivers's assur-
ances to the contrary, I received my draft notice for induction
into the military service as a medical officer. When I brought
this to his attention, he immediately reversed his earlier deci-
sion and initiated the process of having me added to his naval
research unit, which had by that time been called to active
duty. On May 6, 1942, in the middle of the ultracentrifuge


lntimution of Success                        141
experiments, I was commissioned as a lieutenant, j.g., in the
U.S. Naval Reserve and assigned to active duty with the
research unit. There was a slight hitch at the end when my
orders came through assigning me to the Naval Hospital in
Annapolis, but Rivers had enough influence to get these orders
changed at the last minute.
For the next four years I worked on pneumococcal trans-
formation in navy uniform. This anomalous position caused
me a considerable amount of uneasiness and mental conflict.
On the one hand, the research had reached such an exciting
stage that it would have been extremely painful to give it up,
but on the other there was a persistent, nagging feeling that I
should be doing something more directly relevant to the war
effort. Shortly after I was commissioned I went to Rivers with
this problem, suggesting that it might be more appropriate if
I were assigned to another project, such as the one that Hors-
fall had begun on virus pneumonia, a disease that was already
a problem among military recruits. His reply was immediate
and unequivocal: "No, you keep on working with Fess. That
study is too important to drop. You don't have to worry about
it." I still did worry about it from time to time, although the
increasing tempo of the research and the excitement that was
building up as all roads seemed to lead to DNA tended to
keep my mind occupied with other matters. Later, after the
first phase of our work on transformation was nearly com-
pleted, I participated to a minor degree in the studies of virus
pneumonia and also took my regular turn "on call" as one of
the medical officers in the hospital. Nevertheless, most of my
time and effort during this whole period was devoted to one
aspect or another of the problem of pneumococcal transfor-
mation. The navy regularly received summary reports of these
studies, which must have mystified anyone who happened to
read them, but no comment or questions came back to us.
There is no indication that the navy ever recognized the role
that it played in this early chapter of the biological revolution.


142             The Transforming Principle
An unrelated outcome of my going on active duty in the navy
was that for the first time in my life I was financially indepen-
dent. One could support a family on the navy salary.
The time for preparing the annual spring report to the
Board of Scientific Directors came just as we were immersed
in the ultracentrifuge experiments. The results of these
experiments were obviously not ready yet for reporting. Avery
elected to avoid any discussion of our attempts at purifying
the transforming substance, since it seemed likely that the
situation was going to become much more definitive in the
near future. He wrote an eight-page mini-treatise on pneu-
mococcal virulence which included a description of three sep-
arate pieces of recent research on the subject: one carried out
by MacLeod during the previous year, one by Horsfall in the
period before he turned all of his efforts to virus pneumonia,
and one by me as a sort of sideline of research during the first
several months. Together they emphasized the complexity of
the property of virulence and showed that while the presence
of the capsule was essential for the expression of virulence it
was not by itself sufficient. Other properties of the pneumo-
coccus determine its ability to thrive in host tissues. One can
under certain conditions obtain, for example, fully encapsu-
lated type I organisms that are essentially nonvirulent. In
addition, capsules of di.fIerent serological types appear to allord
varying degrees of protection to the organism. Thus, in con-
trast to types I, II, and III, type XIV pneumococci display
little virulence for mice, even though they are commonly
associated with pneumonia in man. MacLeod's and my work
on virulence involved the application of the techniques of
transformation and was thus not totally separate from our main
line of endeavor. None of this was ever published except in
the form of a brief abstract,' but it illustrates the continuing
concern with the disease-producing aspects of the organism
in the course of the pursuit of the nature of the transforming
substance.
While we were mulling over the results of the ultracentri-


Intimation of Success                        143

fuge experiments, it occurred to us that there was an addi-
tional way in which we could test our suspicion that DNA was
involved in transformation. Since we knew of crude enzyme
preparations from several different sources that would destroy
transforming activity, why not examine the effect of these same
enzyme preparations on authentic DNA, such as the material
that Mirsky was making from mammalian tissues? Over the
next few months, I set up a series of experiments repeating
the studies of the action of the enzymes on T.P. and at the
same time comparing their ability to degrade calf thymus DNA.
The results were unequivocal; all of the preparations that
destroyed transforming activity were also able to degrade DNA.
Some additional pieces of information further strengthened
the correlation. We knew that the effect of dog and human
sera on the transforming substance could be eliminated by
heating at 60oC but that this was not sufficient for rabbit sera,
which required heating to 65oC. Tests of the DNA-splitting
activity of sera followed precisely the same pattern, and rabbit
sera could be inactivated only at 65oC or above while heating
at 60oC was sufficient to eliminate the activity of dog and human

sera.
The combination of these several lines of experimental
evidence that consistently pointed to DNA had by the sum-
mer of 1942 pretty much convinced us that in all probability
it was the transforming substance. We were not unaware that
this idea would be greeted with skepticism and that we would
need much more rigorous proof before we could consider
publishing anything about it. We had already been told by
more than one person, Alfred Mirsky being the first, that the
transforming principle could not possibly be deoxyribonucleic
acid because "nucleic acids are all alike." This point of view
was widely held, having been generated for the most part by
the work of P. A. Levene on the structure of the nucleic acids.
For large molecules they were certainly deceptively simple in
composition. The basic small molecular building block is called
a nucleotide and consists of a nitrogen-containing organic


144             The Transforming Principle
"base," combined with a sugar (ribose in RNA and deoxyri-
bose in DNA) and phosphate. Since there are only four differ-
ent bases in a given nucleic acid, and thus only four different
nucleotides, there appeared to be limited possibilities for
diversity. Furthermore, Levene had advanced a "tetranucleo-
tide theory," which proposed that the repeating structural unit
was represented by the four different nucleotides hooked
together in the same order, thus reducing drastically any chance
for diversity among macromolecules of nucleic acid. There
wasn't much solid chemical evidence for the tetranucleotide
theory but it had nonetheless gained a fair degree of accep-
tance among biochemists.
Even if one did not accept this restricted view of the struc-
ture of DNA, the composition of the other major macromo-
lecular constituent of chromosomes, protein, seemed much
more favorable for the task of expressing genetic information.
In the case of proteins, the small structural units are called
amino acids, and there are twenty chemically different amino
acids involved in the construction of a protein molecule. Since
a moderate-sized protein contains hundreds of these amino
acids linked together in a linear chain, the possibilities for
diversity are almost infinite. It is no surprise, therefore, that
in the minds of those who thought about the possible chemi-
cal nature of the gene, protein was the prime candidate. It
was easy to find comments like the following from even the
most eminent workers in the field: "If one assumes that the
genes consist of known substances, there are only the proteins
to be considered, because they are the only known substances
which are specific for the individual. "2
Not quite everyone jumped to this conclusion, however,
and we were able to find some comfort in the writings of a
few workers, even though they were unable to present any
experimental evidence for diversity of the nucleic acids, In
one of the few papers that directly addressed the problem of
the chemical nature of the gene, Jack Schultz had considered


lntimtiofl of Success                       145

the paucity of information on the "monotonous uniformity" of
nucleic acids and wrote in 1941: "When it is considered that
the highly polymerized thymonucleic acid has been studied
in detail from a single source, and only recently have the ribose
nucleic acids begun to be prepared in a comparably elegant
manner, it is evident that the earlier conclusion can be accepted
only as a first order approximation, and that much new data is
necessary before we can exclude the possibility of specificities
in the nucleic acids themselves."3 Though hardly the kind of
comment that could be cited as support for our growing belief
that the transforming substance might be DNA, it was still
something of a morale builder in the beginning stages of our
flirtation with this idea.
Perhaps my favorite among the handful of quotes we were
able to find expressing some optimism about the biological
role of the nucleic acids I encountered in an old biochemistry
textbook by R. A. Gortner. 4 I had come across this book while
browsing in a bookstore in Chicago during my Stanford years
and picked it up because it seemed to present the subject in
a different manner from the text that we were using. Gortner
had obviously been deeply impressed by a paper by the
biochemist J. B. Leathes, entitled "Function and Design,"
which had been published in Science in 1926.5 To the footnote
marking the first citation of the paper, Gortner had added the
comment: "Every biochemist or biologist interested in vital
phenomena should read this paper." He quoted at length the
calculations of Leathes that dramatized the vast diversity of
the proteins; but later at the end of his discussion of nucleo-
proteins, after noting that nucleic acids form approximately
40 percent of the chromosomes, he returned to another state-
ment of Leathes: if we consider that into these chromosomes
"are packed from the beginning all that preordains, if not our
fate and fortunes, at least our bodily characteristics down to
the color of our eyelashes, it becomes a question whether the
virtues of the nucleic acids may not rival those of amino acid


146              The Transforming Principle

chains in their importance." This was pure speculation, of
course, but put forward with enough verve to have a special
appeal for me.
As we were considering in the early summer of 1942 what
steps would be necessary to verify the identification of the
transforming substance as DNA, we became involved in a col-
laborative experiment with Mirsky that added some addi-
tional information on the subject but was probably more
important for the ultimate impact that it had on the general
acceptance of our work after it was published. Mirsky, having
established the general applicability of his procedure for the
extraction of nucleoproteins to a wide variety of mammalian
tissues and to fish sperm, was interested in trying it out on
some of our pneumococci. On July 7, I harvested a 75-liter
batch of type III pneumococci, heat killed them as usual at
65oC for 30 minutes, and then turned them over to Mirsky for
extraction by his procedure, with Avery and me closely fol-
lowing the process. Working in a cold-room at a temperature
just above freezing, he proceeded to wash the pneumococcal
cells three additional times with physiological salt solution and
then to stir them overnight with strong salt solution in an
attempt to extract the nucleoprotein. It was evident that the
cells had not yielded up an amount of material comparable to
that obtained from tissues, since the extract showed none of
the characteristic extreme viscosity of his usual preparations.
Testing a small sample by alcohol precipitation revealed that
a small amount of fibrous material was present, however, and
Mirsky reduced the salt concentration of the extract by dialyz-
ing it against physiological salt solution. This resulted in the
appearance of a visible precipitate, some of it in the form of
fibers, which could be recovered and dissolved in a small vol-
ume of strong salt solution. Under these conditions the amount
of material present was sufficient to give the typical viscosity,
and he was able to reprecipitate it by his usual procedure of
adding the solution to several volumes of distilled water.


Intimation of Success                        147

Mirsky obtained a purified product by repetition of the
process of redissolving and repreciptating the material and
found on chemical analysis that it was made up principally of
deoxyribonucleoprotein, similar to his mammalian chromo-
sins. The yield was minuscule, however, and two further
extractions of the pneumococcal cells with strong salt did not
produce a significant amount of additional material. The rela-
tive inefficiency of the salt extraction was underscored when
I took the residual pneumococcal cells after Mirsky was fin-
ished with them and applied our standard deoxycholate pro-
cedure. I recovered a substantial mass of fibrous DNA on
alcohol precipitation of my extract-many times the amount
that Mirsky had obtained-which after further purification
proved to have the expected biological activity.
I tested Mirsky's nucleoprotein preparation for transform-
ing activity, encountering some difficulties because of its sol-
ubility properties. Nevertheless, it proved to have quite
respectable activity and induced transformation when present
in concentrations as low as 0.2 microgram per cubic centime-
ter. Here, then, was a DNA-containing fraction of type III
pneumococci, isolated and purified by an entirely different
set of procedures, and it displayed the same biological activ-
ity. As far as I was concerned, this was a considerable boost
to the idea that the transforming principle was indeed DNA,
but neither Avery nor Mirsky apparently saw it that way.
Admittedly this new product contained a considerable amount
of protein, but I was not concerned about this, since I was
confident that one could get rid of it without affecting biolog-
ical activity just as we had with our own preparations. As a
matter of fact, I had had to eliminate some of the protein in
order to make the material soluble enough to test in the trans-
forming system. The important point to me was that this pu-
rified DNA-containing fraction had been isolated from
pneumococci by means that were totally independent from
ours but was still highly active in the transformation system.


148             The Transforming Principle

It was clear, however, that the Mirsky procedure leached too
little of this material out of the pneumococci to be of any use
to us in our attempts at further purification.
Not being intimately acquainted with the details of our
research on the transforming principle up to this point, Mir-
sky appears to have attributed greater influence to this collab-
orative experiment on our final results than actually existed.
When he and Pollister finally wrote up a complete description
of their work on chromosin some four years later, they included
an account of our combined pneumococcal experiment and
made the following comment about it: "Because of the effec-
tiveness of a preliminary removal of `cytoplasmic nucleopro-
teins' in the isolation of the pneumococcal desoxyribose
nucleoproteins by us, this procedure was subsequently used
in the isolation of the transforming principle by Avery,
MacLeod, and McCarty."6 This was clearly a misconception,
since it was several months prior to our collaboration that we
had hit upon the device of washing our pneumococci with salt
solution before extracting them with deoxycholate, and I had
been using this approach as already described to reduce the
amount of type III polysaccharide, ribonucleic acid, and pro-
tein in our initial extracts.
Any communication between the Avery and Mirsky labo-
ratories had long since come to an end by the time this paper
was published. I have never had a clear understanding of how
and why this estrangement came about, although the passage
just quoted suggests that Mirsky placed a much higher eval-
uation on his contribution to our work than we did. However,
this never seemed to me an adequate basis for the breach or
for his assuming the role, as he did, of the principal public
skeptic on the subject of the DNA nature of the transforming
substance. The lack of communication also caused some minor
inaccuracies in his report of pneumococcal chromosin. These
were not of great significance, although I did find them
annoying when the paper first appeared. He reported on the
transforming activity of the preparation, correctly attributing


lntimution of Success

149

the test to me, but assigning it a potency that was ten times
greater than I had actually found. I will return to consider the
impact of Mirsky's views on the acceptance of our findings in
discussing the aftermath of the first publication of our results.

This experiment with Mirsky that July had not deflected
us from our primary purpose-to formulate a course of research
that would solidify the evidence in favor of DNA. We now
had in hand methods of purification that would allow us to
eliminate to below the level of detectability all of the other
known components of the extracts. Accordingly, we could
proceed to the preparation of several lots of highly purified
DNA from type III pneumococci that could be subjected to
rigorous analysis by a variety of approaches. In addition to
assaying our final products for transforming activity, we could
appIy a number of different tests to assess the composition
and purity of the material. We had qualitative chemical tests
that were helpful in telling us how successful we had been in
getting rid of protein, carbohydrate, and ribonucleic acid. These
could in turn be supplemented by the much more sensitive
serological tests in the case of the antigenic proteins and poly-
saccharides of the pneumococcus. We could go a step further
and obtain an accurate elementary analysis from the microan-
alyst at the Rockefeller Institute. It was also contemplated
that once we had suitable preparations we would ask our
physical chemist friends to look at their homogeneity in the
ultracentrifuge and electrophoresis apparatus. If all of this was
reasonably successful, we felt that, along with data on enzy-
matic inactivation, we should have the kind of evidence
required.

This was not a small program. We wanted to secure ade-
quate material for analysis and thus we planned to use the
bacteria from 200 or more liters of bacteria-that is, at least
three Sharples runs-for each preparation. Beginning imme-
diately, by August I had enough washed type III pneumococ-
cal cells stored under alcohol for us to start the first preparation.
Set for the final drive, we awaited Avery's return from Maine.


IX

THE HOME STRETCH

  UR PLAN for the purification of pneumococcal DNA was
0 nothing more than a combination of all of the steps that
  had proved out over the previous two years. The pneu-
mococci were heat killed at 65oC immediately after they were
harvested and then washed two or three times in physiologi-
cal salt solution. We then extracted the washed cells in the
usual way with deoxycholate, repeating the process as long as
the extracts yielded significant amounts of fibrous precipitate
on the addition of alcohol. As a matter of fact, our attention
had focused sharply on these fibrous alcohol precipitates.
Because of the entrapment of air bubbles as the fibers were
formed during the addition of alcohol with stirring, the fibrous
mass would float to the top so that it could be simply lifted
out on a spatula, separating it in one step from much of the
other material present in the extract. The fibrous precipitates
were then redissolved in salt solution to give viscous solutions
that were shaken repeatedly with chloroform and amyl alco-
hol by the Sevag procedure for the removal of protein.

It was at this point that we applied the treatment with the
SIII enzyme, carrying out the reaction until the material no
longer gave a detectable precipitate with type III antiserum.
After repetition of the Sevag procedure for removal of the


The Home Stretch                         1s

enzyme protein that had been added, the preparation was ready
for the final stages of purification. Here we relied on the prop-
erty of the DNA that permitted it to wind around the stirring
rod during alcohol precipitation. The rationale was that, after
the removal of the type III polysaccharide, there was no known
component of the extract other than DNA that was capable of
separating out in the form of fibrous strands under these con-
ditions. Thus, by careful precipitation of the DNA at the min-
imal concentration of alcohol required, we should leave behind
any remnants of other substances-protein, carbohydrate, or
rihonucleic acid-that still remained in the preparation. When
we dropped alcohol slowly into our viscous solution with con-
stant stirring, the collection of fibers on the stirring rod began
when an amount of alcohol equal to 0.8 the volume of the
solution had been added and was usually complete by the time
we had reached 0.9 volume. We then simply removed the
precipitate on the rod, washed it in 50 percent alcohol, and
redissolved it in salt solution. After repeating this process a
few times, we were finished and ready to submit our product
to analysis.
I don't mean to imply that things always went smoothly as
we undertook to prepare several lots of this kind of material.
There were a number of hitches along the way, and some
modifications in the procedure were necessary as we found
that we still had a few things to learn about the properties of
the transforming substance. We even had some problems with
simple fundamental operations, like growing the type III
pneumococci for extraction. Early in the fall the central media
department supplied us with a few 75-liter lots of broth that
either sustained the growth of the organisms very poorly or
not at all. I spent some time trying to find the source of the
trouble and ended up participating in the preparation of our
next batches of media. The difficulty was never pinpointed,
but fortunately the difficulties disappeared with careful atten-
tion to the details of the cookbook-type recipe that had to be
followed.


1.52             The Transforming Principle

We were also plagued with unpredictable recurrences of
"trouble with the system" leading to unsatisfactory titrations
of transforming activity. On each such occasion we had to go
back to the drawing board and make sure that each of the
components of the system-the medium, the chest fluid, and
the type II R strain-was not in some way at fault. Because of
our inability to eliminate this variability entirely, we always
approached the reading of one of the transforming titrations
with trepidation, particularly in crucial experiments. Fess and
I had a tacit agreement that neither of us would obtain a sneak
preview of the results before the other had arrived in the
morning. It is during this period that I have my most vivid
recollection of his reaction as we converged on the incubator
each day to remove the racks of tubes for reading. I can still
see the expression on his face, a curious mixture of eager
anticipation and apprehension for fear something had gone
wrong with the complex biological system. At times like these
he used one of his often repeated sayings: "Disappointment is
my daily bread."
Things were not all black, however, and despite occasional
setbacks due to technical difficulties we made good progress.
The first of our purified preparations was ready for analysis by
November and the second about a month later. Each of these
had been made from the pooled organisms from three Shar-
ples runs, representing about 200 liters of culture, and the
yield of final product was less than 45 milligrams in each case.
In general, these preparations lived up to our expectations.
They had excellent transforming activity, and the chemical
and serological tests indicated that we had been successful in
our attempts to eliminate the known inactive components of
the original extracts The results of the elementary chemical
analysis were also encouraging, since the values for nitrogen
and phosphorus content were close to the theoretical figures
calculated for pure DNA.
In getting the material ready for elementary chemical
analysis, we had to eliminate the salt by dialyzing the solution


The Home Stretch                        153

thoroughly against distilled water. This led to the puzzling
and unexpected finding that the purified preparations pro-
gressively and rather rapidly lost their transforming activity
when retained in solution in the absence of salt, without any
apparent changes in physical properties. When dissolved in
physiological salt solution, the material showed no loss in bio-
logical activity after being stored for months in the refrigera-
tor, while a distilled water solution became inactive within a
few days. We were not able to explain this behavior, but once
having learned about it through bitter experience we could at
least avoid the problem by dialyzing only that portion of a
preparation that was to be subjected to chemical analysis. Up
to that point we had wasted some effort by attributing the
diminished activity of our dialyzed material to the recurring
troubles with the transforming system.

We encountered a second new property of the purified
transforming system when we tried to keep it in the dried
form. In contrast to the crude extracts, which we had been
able to preserve for long periods after drying from the frozen
state, the pure products lost transforming activity after drying
about as rapidly as the distilled water solutions. This was true
whether they were freeze-dried or dried from alcohol and ether.
If a sample of the dried material were redissolved immedi-
ately after drying, the solution would have full activity; but
subsequent samples on successive days showed progressively
diminishing activity, with total loss within a week or so. Here
again there were no detectable changes in the other proper-
ties of the pneumococcal DNA; it was still a fibrous, asbestos-
like material in the dry form and gave solutions of the expected
viscosity when dissolved. We were obliged, therefore, to keep
the final products in salt solution and stored either in the
refrigerator or, for more protracted periods, in a deep-freeze
maintained with solid CO2 (dry ice).

A large preparation, made from a total of 300 liters of
pneumococcal culture, completed in mid-February 1943, and
a smaller one completed a month later fully confirmed the


154              The Transforming Principle
previous findings on the quality and transforming activity of
the pneumococcal DNA. Thus, when the time came to write
our annual report to the Board of Scientific Directors, we were
in a position to be much more definite about the progress of
our attempts to determine the chemical nature of the trans-
forming substance. Our report went to the Board in mid-April.
It began with a statement on the historical background of the
subject that we used later, with only minor modifications, in
preparing our manuscript for the publication of this work. The
tone was set by the opening sentence, which read: "Biolo-
gists, especially the geneticists, have long attempted by
chemical means to induce in higher organisms predictable and
specific changes which thereafter could be transmitted in series
as hereditary characters." After the historical background, we
described the transforming system, the current methods of
purification of the active substance, and the nature of the evi-
dence suggesting that it was DNA. There then followed a bit
of interpretation and discussion of the implication of the results.

Assuming that the sodium desoxyribonucleic acid and the active
principle are one and the same substance, then the transformation
from R + SIII represents a change that is chemically induced and
specifically directed by a known chemical compound. Moreover,
this substance selectively determines a differentiation of cellular
function and structure corresponding in type to that of the S organ-
isms from which the agent was derived. The interaction between
the R cell and the transforming principle initiates a series of com-
plex reactions which culminate in the synthesis of the Type III cap-
sular polysaccharide. Thus, the transforming principle-a nucleic
acid-and the end product of the synthesis it evokes-the Type III
polysaccharide-are each chemically distinct and both are requisite
in the type specific differentiation of the cell of which they form a
part. The former has been likened to a gene, the latter to a gene
product, the accession of which is mediated through enzymatic syn-
thesis. The genetic interpretation of this phenomenon is supported
by the fact that once transformation is induced, thereafter without
further addition of the inciting agent both capsule formation and the
gene-like substance are reduplicated in the daughter cells. The


The Home Stretch                        55

changes induced are therefore not transient modifications but are
transmitted through innumerable transfers in ordinary culture media.

If the present studies are confirmed and the biologically active
substance isolated in highly puiified form as the sodium salt of
desoxyribonucleic acid actually proves to be the transforming prin-
ciple, as the available evidence now suggests, then nucleic acids of
this type must be regarded not merely as structurally important but
as functionally active in determining the biochemical activities and
specific characteristics of pneumococcal cells.

It is evident that Avery was quite willing at this juncture
to be explicit about the genetic implications of our findings,
at least to this audience. We have been faulted for not having
been more explicit on this point in our published work. Cer-
tainly, MacLeod and I were much less inclined to be cautious,
but Fess, in addition to his caution, held to the philosophy
that it was enough to present the facts and leave the interpre-
tations to others. It was not that he was indifferent to the
interpretations, since he enjoyed discussing them with his
associates in the laboratory and with a few other close friends,
but he was more than reluctant to put his speculations in writ-
ing for public consumption. His two younger colleagues were
not so inhibited but had to defer to his wishes in this matter.

Avery had passed his 65th birthday the previous October
and was scheduled to be transferred to emeritus status at the
end of the academic year on June 30. He had apparently not
intended to continue in the laboratory after his retirement but
planned to leave New York for Nashville, Tennessee, to join
his brother, Roy, who had been there for some years as pro-
fessor of bacteriology at Vanderbilt University. The develop-
m&nts in the laboratory had pretty well wiped out any
enthusiasm he may have had for leaving, and he decided that
he could not possibly break away until the promising work on
the transforming principle had been brought to some reason-
able conclusion. As far as the Rockefeller Institute was con-
cerned there was no reason for him to leave, since it had long


156             The Transforming Principle

been the policy to provide laboratory facilities and modest
support for Members Emeriti so that they could continue their
research. Both of the directors, Dr. Gasser (who succeeded
Dr. Flexner in 1935) and Dr. Rivers, had already urged him
to stay.
On the evening of May 13, Avery sat down in his apart-
ment to write a long letter to Roy explaining why he was not
going to be able to move to Nashville that summer as origi-
nally planned.' He ran into some kind of block on that first
evening, however, and did not finish the letter until late on
the night of the 26th. A clue to what may have bothered him
appears on page 3, just before the break, where he wrote: "If
this War wasn't on I tell you frankly I would liquidate my
affairs & start for Nashville this fall." In the interim he appar-
ently thought better of blaming the delay solely on the war,
and on resuming he launched into a detailed description of
the research as a fuller and more forthright explanation for
the delay. The tone of his description is less formal than in
the annual report, and it is apparent that he had not talked to
Roy about it previously. Everything is included: the historical
background, the details of our current efforts, the specula-
tions, and even the doubts. I did not know of this letter until
more than twenty years later. Shortly after he received it, Roy
had shown it to a colleague at Vanderbilt, Max DeJbriick, who
was well on his way to becoming the acknowledged leader of
the so-called "phage group, " which made remarkable contri-
butions to biological science through the study of bacterial
viruses, or bacteriophages. It was Delbriick, some time after
Fess had died, who was responsible for having Roy dig the
letter out of his stored memorabilia, and Roy became inter-
ested in making the letter more widely known because of his
conviction that Fess had never received due recognition for
his work. To my knowledge, the first publication of a portion
of the letter was in 1964 in a German textbook, Klassische und
molekdare Genetik, by C. Bresch.' Hotchkiss included a more
extensive reproduction of the letter in an essay that he wrote


The Home Stretch                         1.57
in 1966 for inclusion in a volume honoring Delbrtick,3 and
Dubos published the complete text-except for the introduc-
tory part that dealt only with family matters-in his scientific
biography of Avery which appeared in 1976."
I am guilty of having written that the letter represents the
first written record of the discovery of the role of DNA as the
carrier of genetic information, but it is of course antedated by
the annual report, which was completed at least a month ear-
lier. I have also noted that it served as a useful rebuttal for
the view espoused by some that we were unaware of the
implications of our findings. All in all, the letter is of sufficient
importance to repeat part of it here. It conveys some of the
special flavor of Avery's exposition under less formal condi-
tions. We will pick it up after the historical background has
been completed.
  For the past 2 years, first [with] MacLeod & now with Dr.
McCarty I have been trying to find out what is the chemical nature
of the substance in the bacterial extract which induces this specific
change. The crude extract (Type III) is full of capsular polysacchar-
ide, C (somatic) carbohydrate, nucleoproteins, free nucleic acids of
both the yeast & thymus type, lipids & other cell constituents. Try
to find in that complex mixture, the active principle!! Try to isolate
and chemically identify the particular substance that will by itself
when brought into contact with the R cell derived from Type II
cause it to elaborate Type III capsular polysaccharide, & to acquire
all the aristocratic distinctions of the same specific type of cells as
that from which the extract was prepared! Some job-full of heart-
aches & heart-breaks. But at last perhaps we have it. The active
substance is not digested by crystalline trypsin or chymotrypsin-It
does not lose activity when treated with crystalline Ribonuclease
which specifically breaks down yeast nucleic acid. The Type III cap-
sular polysaccharide can be removed by digestion with the specific
Type III enzyme without loss of transforming activity of a potent
extract. The lipids can be extracted from such extracts by alcohol &
ether at - 12oC without impairing biological activity. The extract
can be de-proteinized by the Sevag Method (shaking [with] chloro-
form & amyl alcohol) until protein free and biuret negative. When
extracts, treated & purified to this extent, but still containing traces
of protein, lots of C carbohydrate & nucleic acids of both the yeast


158              The Transforming Principle

& thymus types are further fractionated by the dropwise addition of
absolute ethyl alcohol, an interesting thing occurs. When alcohol
reaches a concentration of about 9110 volume there separates out a
fibrous substance which on stirring the mixture wraps itself around
the glass rod like thread on a spool-& the other impurities stay
behind as granular precipitate. The fibrous material is redissolved
& the process repeated several times-In short, this substance is
highly reactive & on elementary analysis conforms very closely to
the theoretical values of pure desoxyribose nucleic acid (thymus type).
Who could have guessed it? This type of nucleic acid has not to my
knowledge been recognized in pneumococcus before-though it has
been found in other bacteria.
Of a number of crude enzyme preparations from rabbit bone,
swine kidney, dog intestinal mucosa, & pneumococci, and fresh blood
serum of human, dog, and rabbit, only those containing active
depolymerase capable of breaking down known authentic samples
of desoxyribose nucleic acid have been found to destroy the activity
of our substance-indirect evidence but suggestive that the trans-
forming principle as isolated may belong to this class of chemical
substance. We have isolated highly purified substance of which as
little as 0.02 of a microgram is active in inducing transformation. In
the reaction mixture (culture medium) this represents a dilution of
1 part in a hundred million-potent stuff that-& highly specific.
This does not leave much room for impurities-but the evidence is
not good enough yet. In dilution of 1:lOOO the substance is highly
viscous as an authentic preparation of desoxyribose nucleic acid
derived from fish sperm. Preliminary studies with the ultracentri-
fuge indicate a molecular weight of approximately !500,000-a highly
polymerized substance.
We are now planning to prepare new batch & get further evi-,
dence of purity & homogeneity by use of ultracentrifuge & electro-
phoresis. This will keep me here for a while longer. If things go well
I hope to go up to Deer Isle, rest awhile-Come back refreshed &
try to pick up loose ends & write up the work. If we are right, & of
course that's not yet proven, then it means that nucleic acids are
not merely structurally important but functionally active substances
in determing the biochemical activities and specific characteristics
of cells-& that by means of a known chemical substance it is pos-
sible to induce predictable and hereditary changes in cells. This is
something that has long been the dream of geneticists. The muta-
tions they induce by X-ray and ultraviolet are always unpredictable,;
random, & chance changes. If we're proven to be right-and of course:


The Home Stretch                          `59
that's a big if-then it means that both the chemical nature of the
inducing stimulus is known & the chemical structure of the sub-
stance produced is also known-the former being thymus nucleic
acid-the latter Type III polysaccharide and both are thereafter
reduplicated in the daughter cells. And after innumerable transfers
and without further addition of the inducing agent, the same active
& specific transforming substance can be recovered far in excess of
the amount originally used to induce the reaction. Sounds like a
virus-may be a gene. But with mechanisms I am not now con-
cerned-one step at a time--& 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 which are known
to constitute the major part of the chromosomes but have been
thought to be alike regardless of origin & species. It touches genetics,
enzyme chemistry, cell metabolism & carbohydrate synthesis, etc.
But today it takes a lot of well documented evidence to convince
anyone that the sodium salt of desoxyribose nucleic acid, protein
free, could possibly be endowed with such biologically active & spe-
cific properties & this evidence we are now trying to get. It's a lot
of fun to blow bubbles-but it's wiser to prick them yourself before
someone else tries to.

So there's the story Roy-right or wrong it's been good fun &
lots of work. This supplemented by war work and general supervi-
sion of other important problems in the Lab has kept me busy, as
you can well understand. Talk it over with Goodpasture*but dont
shout it around-until we're quite sure or at least as sure as present
method permits. It's hazardous to go off half cocked-& embarrass-
ing to have to retract later.

In addition to its historical implications, this letter gives a
pretty good picture of the state of affairs in the laboratory in
May 1943. The "new batch" to which Avery referred was
already under way, having been started at the time the letter
was being written. The combined organisms from two 75liter
lots were used in a slightly modified method which consisted
of carrying out all of the procedures in the cold except those
that required higher temperature, like extraction with deoxy-

*Dr. Earnest Goodpasture, a professor at Vanderbilt and a good friend of both Avery.


160             The Transforming Principle
cholate and treatment with the SIII enzyme. Everything went
smoothly and by the end of the first week in June we had
completed the chemical and serological analyses that showed
the new preparation to be up to the standards of our previous
lots. Perhaps, not surprisingly, in view of the special care that
we had exercised in keeping the material cold throughout the
purification process, it was unusually high in biological activ-
ity. As little as 0.003 microgram (3 x lo-' gram) of the final
product was effective in producing transformation in 50 per-
cent of the tubes. This was the preparation with which we
then proceeded to "get further evidence of purity and homo-
geneity by use of the ultracentrifuge and electrophoresis."

Dr. Rothen made several ultracentrifuge runs first to
determine whether the optically visible boundary seen during
centrifugation coincided with the biological activity and sec-
ond to confirm his earlier estimate of the molecular weight.
Fortunately the quantitative titration of transforming activity
was working beautifully at this time so that we could accu-
rately measure the amount of T.P. in the fractions removed
from the centrifuge cell. The results were most encouraging.
The purified material had a single, exceedingly sharp bound-
ary as it sedimented in the ultracentrifugal field, and the
transforming activity clearly moved with this boundary. We
had similar good news from the electrophoretic studies car-
ried out by another physical chemist colleague, Theodore
Shedlovsky. From the application of optical techniques like
those used with the ultracentrifuge, it was shown that there
was only one moving boundary as the material moved in an

ON THE FACING PAGE: A page from the laboratory notebook recording a test of
transforming activity of the final preparation before writing up the work. The t
marks in the table refer to the presence of diffuse growth, presumptive evidence
for transformation. Sill indicates that type III pneumococci were recovered after
plating out the cultures for confirmation. R indicates that only rough organisms
were recovered. Not all of my laboratory notes were this tidy, although the principle
of preparing thorough, clearly legible records was adhered to throughout the
research.


t

i

__
d-

ew


162             The Transforming Principle
electric field and that again this was associated with the bio-
logical activity. Thus we had the added assurance that not
only was our purified pneumococcal DNA homogeneous by
two quite diflerent physical tests but also that it was extremely
unlikely that its transforming activity resided in some other,
undetected component.
Avery's doubts were still not altogether resolved. How could
we establish with certainty that transformation was not attrib-
utable to some unknown substance that was carried along in
our purification process and remained as a minor constituent
of the final product? This question led us to make a pilgrimage
to the Princeton laboratories of the Rockefeller Institute to
consult with two of our colleagues there, John Northrop and
Wendell Stanley. Both Northrop and Stanley were to win the
Nobel Prize in 194.6, Northrop for his crystallization of pep-
sin, the protein-splitting enzyme of the stomach, and Stanley
for crystallization of the tobacco mosaic virus. The work of
both men had been greeted with much skepticism when first
reported. The principal question was how did they know that
their crystals were not merely carrying along a small amount
of a contaminant that possessed the biological activity. It seemed
to us, therefore, that they had faced problems similar to ours.
We had seen less of Colin MacLeod during this period
because, in addition to his task of building up and running the
department of microbiology at New York University, he had
become heavily involved in activities related to the war effort,
serving as consultant to the secretary of war and director of
the Commission on Pneumonia of the Army Epidemiological
Board. He found time, however, to join Fess and me in our
trip to Princeton. Northrop and Stanley were certainly under-
standing and sympathetic, but they had no magic formula for
solving our problem and no specific procedures to suggest.
They seemed impressed with the data we had in hand, and
their only advice was that we should marshal all of the evi-
dence that we were able to obtain and proceed with publica-
tion.


The Home Stretch                    163

Even though the conference had ended on a distinctly

upbeat note, Fess remained hesitant. I can remember that as
we discussed the situation on the way home on the train, Colin
asked him with a certain amount of impatience: "What else
do you want, Fess? What more evidence can we get?" I don't
believe that he replied to this, but one answer that he had
was to seek still more advice. I can recall the session that Fess
and I had for this purpose with Van Slyke, a good friend and
colleague who had been at Rockefeller since 1907 and who
was a distinguished biochemist. He also offered no specific
advice, giving us the same sort of encouragement we had got-
ten at Princeton. Strangely, in another manifestation of those
memory gaps, I had completely forgotten a similar meeting
with Max Bergmann, another biochemist who had come to
the Institute from Germany in 1934. He had been one of the
early workers to be concerned with the structure of proteins,
and he developed at Rockefeller a remarkable research group
in this field. The evidence that this meeting actually took place
is a loose yellow sheet that I found among my notes on which
I had pencilled what was apparently a summary of his com-
ments in reply to our queries. It is unfortunately undated but
almost certainly relates to this same period, since Bergmann
died in 1944. What makes the lapse in memory all the more
inexplicable is the nature of his comments, which are more
emphatically supportive than anything we had heard from
others. I headed my notes, "Interview with Dr. Bergmann,"
and began with the following paragraph:

In the light of present knowledge, the statement that all nucleic
acids are the same regardless of the source from which they are
derived is nonsense. If they are large polymeric compounds, there
is an endless number of possible combinations all of which would
possess the same elementary composition but would differ in chem-
ical structure none the less. Nucleic acids hold too prominent a place
in biology to be completely non-specific substances. The lack of evi-
dence of any specificity associated with nucleic acids is only due to
the fact that they have not been investigated sufficiently.


164              The Transforming Principle

This is rather strong stuff for that particular period in the
history of nucleic acids, and I can't be sure how faithfully I
had paraphrased his comments without injecting some inter-
pretations of my own. I go on to a list of several suggestions
that Bergmann made for obtaining further evidence. Some of
these we had already tried, such as salt fractionation of the
extracts, and others (e.g., chromatography) we were not up to
tackling with the methodology then available. In any event,
my notes suggest that he was more responsive than the others
we consulted, and I have no explantion for the obliteration of
this episode from my memory.
I do not believe that Fess was greatly reassured by these
consultations, but in the end he yielded and agreed that it
was probably time to begin writing up the work. He would go
off to Maine for the summer and give it some further thought,
but at the same time would prepare drafts of the introduction
and the discussion. It was my job to write up the methods
section of the paper and to collect the experimental protocols
that we would use to document the results. I also had a few
odds and ends of experimental work to do in the laboratory in
order to tidy up some of the details. One of these had to do
with the statement about the transforming substance being
recoverable from the transformed cells in amounts far in excess
of that originally used to induce the transformation. In other
words, the R strain, after being induced to form the type III
capsular polysaccharide, continued to reproduce the inducing
agent as well as the polysaccharide. It seemed certain that this
must be so, but as far as I could tell no one had ever demon-
strated it experimentally-that is, isolated a colony of the
transformed cells, grown them up in a few liters of culture,
and shown that one could extract as much transforming prin-
ciple as one could from the original type III strain. I did the
experiment in July with the expected result-the transformed
cells were an excellent source of the active material-and wrote
Fess about it along with other bits of new information that he
might want to use in writing the discussion.


The Home Stretch                    1%

;  When Fess returned in the fall we got down to the job of
ipreparing the paper in earnest. In order to avoid the interrup-
,tions of the telephone and laboratory activity, we obtained a
`small room in the library and were cloistered together there
for a few hours each day. We began by going over the initial
drafts that each of us had prepared and trying to decide what
,else should be included. I remember being so bold as to sug-
!gest that we use some information from the experiment that
we had done with Mirsky, since as I said before I considered
ift to be supportive of our thesis, but Fess quickly vetoed this
.rdea. He was probably right, because it was a single experi-
-ment with such a minute yield of active material that com-
: plete analysis was not possible. He may have had other motives
`besides his view of the adequacy of the data and their bearing
on our conclusions, but I was not aware at the time that there
had yet been any cooling of the relationship between the two
laboratories.
The writing went slowly, as the casting of every phrase
had to be carefully scrutinized in the manner for which Fess
was famous. It turned out to be a rather long paper-twenty
printed pages-necessarily including a description of the results
of earlier work, largely by MacLeod, which had established a
more reliable transforming system, as well as examples of all
the recent data. As we neared completion of the final draft in
October, we suddenly realized the value of a photograph
showing the dramatic difference between colonies of the R
strain and those of the transformed type III organisms. We
had not bothered to stop along the way to get illustrative
material of this kind, and I had to scramble to have suitable
photographs taken in a hurry. On October 28, just three days
before we submitted the paper for publication in the Journal
of Experimental Medicine, I spent a few hours with the pho-
tographer in the illustration division of the Institute shooting
pictures of a blood agar plate with colonies of the inoculating
R strain, R36A, on one half and colonies of transformed type
III cells on the other. Finally, by trying a variety of lighting


Colonies of pneumococci on the surface of blood agar. This is the picture used in
the 1944 paper. The small colonies on the left are of R36A, the unencapsulated
strain derived from type II. The smooth, glistening colonies on the right are of the
same strain after transformation with DNA from type III. They have capsules of
type Ill polysaccharide.  (Reproduced from The Journal of Experimental Medicine, 1944,
79: 137-758, plate 7, by copyright permission of The Rockefeller University Press.)


The Home Stretch                    167

angles and cropping out areas that were out of focus, we came
up with an acceptable picture. By contrasting the small, rough-
surfaced R colonies with the much larger, juicy-appearing col-
onies of organisms that had been transformed to produce type
III capsules, it showed the magnitude of the change and turned
out to be a useful addition to the paper. It has since been
reprinted in many books to illustrate the phenomenon of
transformation.
An amusing episode occurred during this period when Fess
discussed with me his concerns about the order in which our
names should appear on the paper, a matter that causes more
trouble among scientists than the layman might imagine. He
said that he wasn't sure whether the names should appear in
the order of the length of association with the problem, on the
basis of age and seniority, or simply alphabetically. It was not
until after he had left me on that occasion that it suddenly
hit me that all of the alternatives came to the same result.
No matter how you sliced it, it was "Avery, MacLeod, and
McCarty." It was fine with me.
After the manuscript was put in final form and thoroughly
proofread, Avery delivered it by hand on November 1 to the
editor of theJournal of Experimental Medicine, Peyton Rous.
Rous was another longtime colleague, having joined the staff
of the Rockefeller Institute four years before Avery. He was a
gifted and versatile experimentalist in his own right (he found
in 1910, for example, the first virus that causes cancer in ani-
mals, a discovery for which he was awarded the Nobel Prize
more than fifty years later), and at the same time labored for
years building and sustaining the reputation of the Journal.
He was a skilled and strict editor, demanding clarity and cor-
rect English as well as scientific accuracy from his contribu-
tors. Avery told his old friend on submitting the manuscript
that he wanted him to go over it just as he would if it were a
paper submitted by an unknown outsider, and Rous took him
at his word.
Avery had me join him in his office when Rous personally


168              The Transforming Principle

delivered the edited manuscript to discuss his suggested
changes. He began by reminding Fess that he had been asked
to give it the full treatment and proceeded to bring up a long
series of points. The typescript was covered with many lightly
pencilled notations in Rous's fine handwriting. Most of these
dealt with minor queries or suggested changes in wording,
but there were a few more substantive comments. We had
included in the discussion that quotation from the paper by
Leathes in which he stated that "it becomes a question whether
the virtues of the nucleic acids may not rival those of the amino
acid chains in their importance," and ROW pointed out that
this was pure speculation and really helped very little to sup-
port our thesis. In the end, it was deleted. I have a vivid
recollection of his reaction to my use of the word "routinely"
at two or three places in describing the methods. He called
attention to the unacceptability of the word in a colorfully
phrased note-"Saving your presence, `routinely' is a louse
on the dictionary." I was amazed to find that he was correct
and that none of the standard dictionaries had yet caught up
with the fact that this adverbial form was in wide use. The
word was replaced with the phrase "as a routine" in the cor-
rected version of the paper.
I should not give the impression that our discussions with
Rous assumed a contentious quality, because all of the points
at issue were resolved amicably and rather quickly. It is a pity
that no copy of this edited manuscript still exists to illustrate
the Rous style and to remind me of some of the details of the
editing that I am sure I have forgotten. As a matter of fact,
due to Avery's rather ruthless cleaning out of his files on his
departure from Rockefeller in 1948, there is not even a copy
of the revised version of the paper. I cannot recall that Rous
at any time indicated what he thought about the work or how
he viewed its broader implications, but some indication of the
latter emerged after his death in 1970. Dr. Rous's extensive
collection of reprints of scientific articles had come into the
hands of Dr. Paul Cranefield at Rockefeller who discovered


The Home Stretch                    169

that Rous had written on his copy of a reprint of our paper, as
instructions to his secretary: "Please file under genetics."
The paper was ready for the printer by December, and all
we had to do was wait, somewhat impatiently, for it to appear
in the Journal. I was not immune to concerns about having
some of my experimental work published if I were to succeed
in establishing myself in a research career-a manifestation of
the "publish or perish" syndrome-and I had chafed a little
under the onus of having worked for well over two years with-
out a publication. Accordingly, my impatience was fed by this
attitude, as well as by the more substantial consideration based
on my conviction that our discovery had broad biological sig-
nificance and the sooner it appeared in print the better. There
was, however, plenty to do in the laboratory to keep us busy
in the meantime.
There was also the matter of reporting on our findings to
our colleagues in the other laboratories of the Institute. We
did not have the profusion of lectures, seminars, and other
meetings that exist today, but every Friday afternoon there
was a staff meeting, attended by essentially everyone, at which
recent work from one of the laboratories was presented. It
was an effective mechanism for keeping us up-to-date on the
activities of the other research groups at the Institute. Fess
had not presented any of the work from his laboratory before
this forum for many years, and Colin and I felt that he should
tell the transformation story there, now that we had the paper
in press. After initially expressing some reluctance, he finally
agreed that it was appropriate and the talk was scheduled for
December 10, 1943. It is listed in the records of the staff
meetings under the same title as the paper: "Studies on the
Chemical Nature of the Substance Inducing Transformation
of Pneumococcal Types, " with all three of our names.
The room in which these meetings were held was not large
but was adequate for the size of the staff, although on this
occasion there were enough visitors from the outside so that
a few of those attending had to stand at the back of the room.


170             The Transforming Principle

Avery's talk followed the same sequence and much of the
phraseology of the paper, and it closed, as I remember it,
with the same conclusion that we had used to end the paper:
"The evidence presented supports the belief that a nucleic
acid of the desoxyribose type is the fundamental unit of the
transforming principle of Pneumococcus Type III." He received
a resounding round of applause, but when the chairman called
for the customary questions or discussion, there was no
response. The regular chairman of the staff meetings that year,
Frank Horsfall, was absent because of illness, and the secre-
tary, Howard A. Schneider, was in the chair. He later recalled
the situation as follows: "At the conclusion of his polished and
long-worked-over address, I rose to call for discussions and
questions. No one rose to my call. No one spoke. There fol-
lowed one of those long silences that haunts me yet. Instinc-
tively I felt we were witnesses to something important, even
though I cannot say I fully appreciated just how important
that paper was to become as the years unrolled. And then,
one man arose. It was Dr. Michael Heidelberger, an old col-
league of Fess and then professor of immunology at Colum-
bia. I cannot remember all he said, although Dr. Heidelberger
was brief in his remarks. I do recall his describing the years
of thought and incubation that he personally knew, as a for-
mer colleague, lay behind the afternoon's paper. When Dr.
Heidelberger sat down another long silence ensued. At last,
when I could stand it no longer, I said, `This company, having
reached an unanimity of opinion, is now adjourned.' "5

My recollection is not too different from Schneider's, only
I don't believe that I considered the silence embarrassing or
strange. The applause had reflected the esteem and affection
which most of the staff held for Fess almost as much as it did
a response to the content of the talk. No one was prepared to
comment on the latter on the spur of the moment. A few have
mistakenly recalled that after the lecture Mirsky had come to
the podium at the front of the room and delivered his first
public rebuttal, indicating why he thought it was going beyond


The Home Stretch                           171

the evidence to conclude that the transforming substance was
DNA. This actually occurred much later in a quite different
situation. There were no expressions of doubt on the occasion
of Fess's valedictory.

The Journal of Experimental Medicine prided itself in
appearing promptly on the first of each month. On February
1, 1944, the issue bearing our paper was on the library table
with the other new accessions for the day.6 This marked the
end of what seemed to me to have been a very long search.
Recently my brother returned to me the copy of the reprint
of the paper that I had sent to my mother as soon as they were
available, and I find that I had expressed this sentiment by
writing on the reprint: "This is it, at long last."


X

STRENGTHENING
THE EVIDENCE

E VEN THOUGH we looked upon the publication of the paper
  as a milestone, we did not by any means consider that
  it marked the end of the job. We had already heard

enough about nucleic acids being all alike to know that there
were going to be doubts about our findings. The question was:
how could we get additional, compelling evidence that it was
the DNA itself and not some protein remaining in our puri-
fied preparations that was responsible for the biological activ-
ity?

I was not very optimistic about getting this kind of evi-
dence by further purification of our transforming DNA. My
lack of confidence in this approach was based on a bit of chem-
ical calculation. There is a physical constant called Avogadro's
number which states that a gram molecule of any substance-
that is, an amount equal to the molecular weight in grams-
contains 6.022 X 1O23 (or roughly 6 followed by 23 zeros) mol-
ecules, manifestly a very large number. This would apply as
well to large molecules and, if we assumed a molecular weight
of 1 million for our DNA, it would have that number of mol-
ecules in a million grams. However, even 1 milligram would


Strengthening the Evidence                   173

have 6 x 1014 molecules, and the smallest amount of our best
preparation that was able to induce transformation-O.OO3
microgram (3 x lo-' gram)-would still have more than a bil-
lion. This apparent excess didn't bother me, since we had no
idea how the DNA managed to get into the R pneumococcus
and become integrated into the cell's mechanisms in order to
initiate the production of type III capsular polysaccharide, and
it seemed unlikely that this could be a very efficient opera-
tion, Furthermore, if we were right, only a small portion of
the total DNA in our preparations could be specific for cap-
sular synthesis and the rest of it had to be concerned with
various other functions of the pneumococcal cell. One could
assume that there had to be an excess of DNA molecules in
the transforming system.
The implications of these numbers with respect to protein
contamination were more troublesome, however. If we made
the optimistic assumption that there was no more than 0.1
percent protein in our final product, the minimal transform-
ing dose of 0.003 microgram would still have millions of pro-
tein molecules in it. The available analytical methods were
not up to detecting contaminating protein at this level, and I
could see no prospect of devising methods of purification that
would assure us of having eliminated essentially all of the pro-
tein. We already knew that the hypothetical protein would
have to have rather special properties, since it resisted our
deproteinization procedures, was unaffected by several pro-
teolytic enzymes, and was carried along without loss through
all the steps in the purification of the DNA. We concluded
that we should look for an alternative approach in attempting
to validate the identification of the transforming substance as
DNA. The idea that appealed to me, and one that had cer-
tainly been fostered by my experience with Avery up to that
point, was to get a purified and well-characterized enzyme
that could digest DNA and to show that it would destroy the
transforming substance. This was pretty much in line with
Avery's thinking back in the 1920s when he was confronted


174             The Transforming Principle

with the necessity of convincing skeptics that his polysacchar-
ides themselves possessed serological specificity rather than
being dependent on contaminating protein. We needed
something like the SIII enzyme that he and Dubos had finally
come up with at that time. The enzymatic experiments included
in our paper, showing that all of the crude preparations capa-
ble of inactivating the transforming principle also acted on
purified mammalian DNA, were all right as far as they went,
but they were only correlations and thus not conclusive. What
we needed was a well-characterized deoxyribonuclease that
would be generally effective in splitting DNA in much the
same way that the crystalline proteolytic enzymes already
known at that time were able to attack most proteins.
I got very little help from a search of the biochemical lit-
erature. No one appeared to have made a serious effort to
obtain even a partially purified deoxyribonuclease. This was
another reflection of the rather poorly developed state of nucleic
acid biochemistry at the time this work was in progress. Kun-
itz had reported his isolation of crystalline ribonuclease in 1940,
and so this was also a relatively new product for application to
biological studies. About the most useful information that I
could glean from the earlier literature on DNA-splitting
enzymes was that the mammalian pancreas, the same source
used by Kunitz for his ribonuclease, was likely to be the rich-
est source of the DNA enzyme. Otherwise, there was not much
to be found about its properties or methods of preparation.
Our interest in having a bona fide deoxyribonuclease had
not waited for the completion of the first phase of the work
and publication of the paper. As early as the summer of 1942,
after we had accumulated the various kinds of evidence point-
ing to DNA as the transforming substance, we realized that
the availability of such an enzyme would be of great help. Our
little chemical laboratory was presided over by a biochemical
technician, William La Rosa, whom Avery had more or less
inherited from Alexis Carrel at the time that the latter had
closed his laboratory in 1940. La Rosa had been engaged in


Strengthening the Evidence                   175

some work related to the sulfonamide drugs with Colin
MacLeod and now seemed available for tackling exploratory
experiments on deoxyribonuclease. (Our laboratory short-
hand for the enzyme was for some years "dornase," but the
generally accepted abbreviation today is DNase, and for
ribonuclease, RNase.)
La Rosa was a good chemist, but he had been given a mea-
sure of independence in his previous work under Carrel that
made him resistant to carrying out faithfully the research pro-
tocols that I drew up for our attempts to purify DNase. He
tended to inject his own ideas into the research and rarely
managed to complete an experiment as I had outlined it. I
found this frustrating since the results never satisfied me, but
I was too heavily engaged in the work on the transforming
factor to carry out the experiments myself. As a result, there
was little progress toward obtaining a DNase during this period.
One important piece of information did come out of his efforts,
however, when he found that the enzyme present in pan-
creatic extracts seemed to require the presence of magnesium
ion (Mg"`) in order to exert its activity on DNA. This was in
contrast to Kunitz's RNase, which had no such requirement
for metal ions, but I was able later to confirm La Rosa's obser-
vations fully and to make some practical applications of this
information in the study of the enzyme's effect on transform-
ing DNA.
La Rosa left Rockefeller by the summer of 1943, freeing
the chemical laboratory for me to try my own hand at the
DNase experiments whenever there was a lull in the activities
relating to the preparation of the paper on the DNA nature of
the transforming substance. I used the same starting material
that I had had La Rosa use-a commercial preparation of a
dried extract of beef pancreas. This brownish powder was far
from being ideal for the purposes of chemical fractionation,
but it had the advantage of being readily available and it did
have potent DNase activity. Measurement ofenzyme activity
in the various fractions was something of a headache, since no


176             The Transforming Principle
simple chemical method was available. The most obvious
physical effect of the enzyme on a solution of DNA of the
Mirsky type was the loss of its characteristic viscosity, accom-
panied by a loss of its ability to give fibrous alcohol precipi-
tates, and I chose to measure the rate of fall of viscosity as an
index of DNase activity. This meant that the reaction had to
be carried out in a viscosimeter, with repeated readings being
taken over a period of time in order to determine the rate of
change. It was a cumbersome method, but at least it was sen-
sitive and also reliable in telling us what we wanted to know-
that is, it could be shown that the rate of fall of viscosity was
proportional to the concentration of enzyme present.
By applying standard salt fractionation procedures, I was
able to separate material from the pancreatin that had far more
DNase activity than the crude enzymes and sera that we had
used in making the experimental correlations we were about
to publish. These products were themselves still very crude
but good enough to permit initial studies on the optimal con-
ditions for measuring the enzyme's activity. Even at this early
stage I couldn't resist trying their effect on some of our trans-
forming DNA, and the results gave us some indication, even
before the paper was published, that a purified DNase was
going to back up our story. The data were too preliminary and
the purification attempts had not progressed far enough, how-
ever, for us to incorporate any of this information into the
paper.
Early in January 1944 we acquired a replacement for La
Rosa as a technician in the chemistry laboratory to help me
with these studies. Up to the onset of the war the technical
staff of the Rockefeller Institute had been nearly all male (in
our group there were La Rosa, Fred Kimmer, and Teddy
Nadeje), most of whom had come as youngsters and grown up
with the place. The war changed the situation rapidly, as all
of the replacements and the new technicians hired for the
special projects were young women, and they were in the
majority by the end of the war. Our representative of this new


Strengthening the Evidence                    177
wave was Jacqueline Jonkowske, who had previously been
working in a hospital clinical laboratory and was happy to escape
routine analyses by moving to a research lab. She was ideal
for the job: technically competent, able to follow directions,
and with enough patience to sit for hours in front of viscosi-
meters measuring the enzyme activity of different fractions.
As it turned out, I needed her help even more than I had
suspected. During that winter I began to develop the symp-
toms of arthritis, manifested at the outset principally by morning
stiffness. I can still recall the agony of trying to hobble down-
stairs on awakening to set up the thermostat and take some of
the chill off our underheated house-a victim of oil rationing.
My feet then began to bother me, and I found it difficult to
stay on them all day in the laboratory as I had been accus-
tomed to do. Subsequently, as other joints became inflamed
and swollen, my effectiveness in the laboratory was clearly
suffering, and in the middle of May I tossed in the towel and
entered our hospital as a patient. Whether or not it was ther-
apeutically wise to have my hospital bed in the same building
as my laboratory, it made it possible for me to keep some of
the work going. As far as therapy was concerned, I was fortu-
nate to be under the care of Dr. Robert F. Watson, who had
been the resident physician of the hospital when I arrived in
I941 and had continued in a similar capacity after the unit was
called to active duty. Watson was associated with the rheu-
matic fever service and thus had some expertise in dealing
with the problems of joint disease, but, more important, he
was a superb and judicious physician.
I had seen enough of the ravages of rheumatoid arthritis
to dread the possibility that I was suffering from it. When the
Normandy D-Day came along after I had been in the hospital
for three weeks, my morale was at a low ebb. Two of the
leading rheumatologists in New York City had been brought
to see me in consultation, and they agreed that rheumatoid
arthritis was the most likely diagnosis. Both recommended
that I be started on gold therapy. Fortunately, Watson wasn't


178             The Transforming Principle
any more enthusiastic about this recommendation than I was
and, with the support of a consultation by mail with a third
specialist, he held off any specific treatment while waiting to
see what further developments there were on simple bed rest.
To everyone's surprise, I began to show definite improve-
ment and was able to return home on July 7 with only a few
residual symptoms, which proceeded to disappear perma-
nently over the next few weeks. Had I received the gold treat-
ment, my case would have gone on the record as a remarkable
cure for that mode of therapy.
The laboratory notes suggest that, despite my illusions about
keeping the work going, not very much had really gone on
during this period. In February we had given up the use of
dried pancreatin as the source of the enzyme and had turned
to extraction of fresh beef pancreas, which Fred Kimmer was
able to pick up for us as we needed it by stopping off at the
slaughterhouse on his way to work. Nevertheless, we contin-
ued to have trouble in reproducibly separating out clean frac-
tions of the active enzyme, and we were troubled in addition
by the ability of the protein-splitting enzymes, which abounded
in the pancreatic extracts, to destroy the DNase. Our efforts
to circumvent these problems continued along with experi-
ments designed to define better the properties of the enzyme
and the conditions for its accurate measurement.
Things were still in this state when I returned to the lab-
oratory in August and decided that it was high time to consult
Kunitz about the approaches that he used in fractionating his
pancreatic extracts. He had not only obtained RNase from this
source but together with Northrop had earlier isolated crys-
talline preparations of the two major protein-splitting enzymes,
trypsin and chymotrypsin, and of their inactive precursors from
this same starting material. It is difficult to imagine now why
I was so slow about seeking his help, since I was certainly
aware of his work. It would seem that the search for a DNase
had too long been merely a sideline, relegated to a second
priority until the work on the purification of transforming DNA


Strengthening the Evidence                   179

was completed. When I called Kunitz, he suggested that I
come to his laboratory and observe his techniques. I quickly
arranged for my second visit to the Princeton laboratories of
the Rockefeller Institute.
Kunitz was an old-timer, having come to Rockefeller the
same year as Avery. He had initially held a technical position
but then gradually rose through the ranks of the scientific staff
until he finally became a full Member in 1949. In the course
of his association with Northrop in their early work on pro-
teins, he turned out to be an absolute genius at the business
of crystallizing proteins, and he tends to be remembered pri-
marily for this even though he also carried out extensive stud-
ies of the properties and biological significance of the proteins
that he isolated. He was a delighful little fellow, about as tall
as Avery, and with a heavy accent that he had carried over
from his native Russian. He could not have been more hospi-
table or more generous with his time in helping me with my
problem.
The Kunitz laboratory was beautifully equipped for the
large-scale preparation of enzymes from various sources, and
the standard procedures that he had devised were elaborately
worked out and systemized. The net effect was to make his
published methods highly reproducible if one faithfully fol-
lowed his directions, as I found out later in repeating some of
his preparations. The heart of his fractionation process was
the application of the time-honored technique of "salting out"
proteins, usually with ammonium sulfate. Ammonium sulfate
has a number of advantages for this kind of work, one of the
most important being its high solubility-it takes 760 grams
(about 1.67 pounds) of the salt to fully saturate 1 liter of water.
Kunitz had constructed a formula for calculating the amount
of ammonium sulfate required to bring a protein solution to
any desired level of saturation, or to bring it from one level to
another, and he had prepared tables of the data for quick
application in the laboratory. These data, together with hints
on filtration methods and a few other tricks of the trade. were


180              The Transforming Principle

to be of great help to me. The key to his success with pancreas
was the use of a dilute sulfuric acid (about 2.5 percent) instead
of water in the initial extraction of the ground organ. The acid
inhibited the activation of the proteolytic enzymes and at the
same time eliminated a problem with mucoid substances that
interfered with fractionation and filtration.
It did not take long after I returned to New York to get
together the necessary materials to apply the Kunitz tech-
nique to the isolation of DNase. The first step in his proce-
dure, after obtaining the acid extract of the pancreas, was to
bring it to 0.4 saturation with ammonium sulfate and to dis-
card the precipitate that was formed, since all of the several
enzymes in which he and Northrop were interested remained
in the filtrate at this point. My first experiments with his pro-
cedure revealed that the DNase was wholly contained in the
rejected 0.4-saturated precipitate. It was painful to realize that
during the processing of vast quantities of pancreas in the
Princeton laboratories over the previous years all of the DNase
had been tossed out with the garbage. This observation had
its compensations, however, since it suggested that it should
not be too difficult to separate the DNase from the bulk ofthe
trypsin, chymotrypsin, and ribonuclease, as well as the other
enzymes with which Northrop and Kunitz had been con-
cerned.
I modified the Kunitz procedure by bringing the acid pan-
creatic extract to only 0.2 saturation with ammonium sulfate
before filtering to obtain a clear solution and then increasing
the concentration of the salt to 0.4 saturation in order to pre-
cipitate the DNase. Very quickly I had preparations that were
much more potent than anything I had made previously, and
with some reworking of this fraction I obtained material that
seemed most promising for the purposes that Avery and I had
in mind. The purified product would cause a readily detect-
able fall in the viscosity of a DNA solution when used in con-
centrations as low as 0.01 microgram per cubic centimeter;
and it took 100,000 times as much material to demonstrate


Strengthening the Evidence                   181

any protein-splitting activity. When we tried it out on our
pneumococcal DNA preparations, the same low concentra-
tions totally destroyed transforming activity, and with even
smaller amounts of the enzyme (0.001 PgIcc) the activity was
clearly diminished. The enzymatic approach to verification of
the DNA nature of the transforming substance was living up
to our expectations.
We got some additional encouragement as a result of fur-
ther studies on the activation of DNase with metal ions. We
found first that, among a number of other metal ions, only
manganese ion (Mn'+) was as effective as magnesium ion
(Mg2+) in activating the enzyme. It had occurred to me that
sodium citrate (a salt of citric acid, the principal organic acid
of citrus fruits) should inhibit the magesium-activated DNase
by virtue of its well-known ability to tie up Mg2+ in a complex
so that it was no longer free. This turned out to be the case,
and citrate eliminated completely the fall in viscosity of a DNA
solution exposed to the Mg2+ -activated enzyme but had no
inhibitory effect whatever when Mn2+ was used as the acti-
vator. The same pattern held in experiments with pneumo-
coccal DNA: the destruction of transforming activity by Mg2+-
activated DNase was prevented by the presence of citrate but
the action of the Mn2+ -activated enzyme was unaffected. This
made it all the more certain that it was the DNase itself that
was acting on the transforming substance.
I made a number of attempts to crystallize the DNase,
since this seemed about the only feasible means of achieving
further purification to get rid of the residual proteolytic activ-
ity and other probable contaminants in my preparations. The
powerful modern methods for the separation and purification
of enzyme proteins were still a long way off. I had saved all of
the residues after removing the DNase from my pancreatic
extracts and I was thus able to use this material to get expe-
rience with protein crystallization by repeating the experi-
ments of Northrop and Kunitz. This is how I discovered the
precision and reproducibility of their published methods.


182             The Transforming Principle
Before long I had my own crystalline preparations of five of
their enzymes, but none of this experience was translated into
any success in crystallizing DNase. Kunitz is reported to have
remarked during a lecture that for success in work of this kind
"All you need is a barrel of ammonium sulphate and a drum
of concentrated sulphuric acid." Northrop added in discus-
sion, "One also needs a barrel of patience."l This, or some
more subtle ingredient, is what I seemed to lack.

While this work was in progress an event occurred that
revealed something of how the younger members of the hos-
pital staff viewed the work on pneumococcal transformation.
This was at a dinner of the staff, held at the Harvard Club on
November 2, 1944, that had a dual purpose: to give a send-off
for that part of our naval research unit that was about to depart
for the southwest Pacific and to honor Fess after his recent
retirement. (I made the error in an earlier publication" of giv-
ing the date of this dinner as April 1943, even though I was
vaguely aware that the southwest Pacific theme came at the
same time as the homage to Avery.) Part of the entertainment
at the dinner was a series of verses written by various mem-
bers of the staff to the tune of Gershwin's "It Ain't Necessarily
So" (beginning in verse 1 with "Little Avery is small, but oh
my!"). This collection of amateur poetry has been preserved
because one of Avery's longtime associates, Ernest Stillman,
undertook after the dinner to have it printed at a press he
owned. The pages were bound together with a front sheet
bearing the title that was given to this set of verses:

FORTUNE FAVORS THE PREPARED MIND

                 or
YOU'VE GOT TO HAVE IT IN YOUR GENES

Moral: Go change your genes!

  As work on the enzyme progressed during the fall, I
decided that I had aquired enough information to present it


Strengthening the Evidence               183

at one of the Friday afternoon staff meetings. My talk was on
December 15, 1944, just a year after Avery's presentation
before the same group, and I gave it the title: "Isolation and
Purification of Desoxyribonuclease and Its Action on the
Transforming Substance of Pneumococcus." I felt that I had
to write out my speech in detail, because I didn't trust myself
to keep the presentation clear and concise if I were to talk
with only an outline, and I still have the original of the triple-
spaced typescript that I used on this occasion. It was a rather
dry and technical talk, describing the purification and prop-
erties of the enzyme and then emphasizing its effects on the
pneumococcal transforming DNA. I ended this part of the
presentation with a fairly explicit statement on what I thought
the results implied: "Although ultimate purification of the
enzyme has not as yet been achieved by the use of crystalli-
zation methods, the purity and activity of the present prepa-
rations are sufficient to provide the conclusive confirmatory
evidence that was sought concerning the desoxyribonucleic
acid nature of the transforming substance."
I then tacked on a discussion of an aspect of our research
on the transforming substance that I have not previously men-
tioned in these pages. It was omitted primarily because it had
no direct bearing on the main body of the work directed toward
determining the chemical nature of T. P., but I have the addi-
tional excuse of having lost all of the laboratory notes on the
numerous experiments that we had carried out on this phase
of the problem. I had adopted MacLeod's procedure of seg-
regating notes in separate manila folders on the basis of sub-
ject matter, and this set got misplaced after I had used the
material while writing a paper on the subject, which I did
early in 1945. These notes were then irretrievably lost, and I
thus have no reminder of the details and timing of these stud-
ies, although I do remember that the first observations were
made during my first year with Avery and that the work was
carried out intermittently for the next few years. This line of
research began with the observation that the addition of ascorbic


184              The Transforming Principle

acid-vitamin C-to our pneumococcal extracts resulted in
complete loss of transforming activity. We explored this inac-
tivating effect further in the hope that it might be of help in
identifying the transforming substance or in determining the
chemical basis for its specificity. The work never paid off in
this respect.
We found that the inactivating effect of ascorbic acid was
dependent on its undergoing oxidation with the formation of
peroxides that served as the active agents, and a number of
organic compounds that undergo the same kind of autoxida-
tion were shown to be equally effective in inactivating T.P.
This action could be blocked by excluding oxygen from the
system or by incorporating a reducing agent, such as the amino
acid cysteine. A more tantalizing finding was that transform-
ing DNA which had been rendered totally inactive by treat-
ment with ascorbic acid could be restored to almost full
b lg' 1 ti t b
io o ma ac vi y y subsequent exposure to reducing agents.
It was apparent, therefore, that the oxidative inactivation was
reversible ifit had not progressed too far, and it was this aspect
that I stressed in the stalf meeting talk-contrasting the irre-
versibility of inactivation by DNase with the reversible inac-
tivation by ascorbic acid. My paper describing the latter aspect,
published in the Journal of Experimental Medicine in May
1945, was entitled "Reversible Inactivation of the Substance
Inducing Transformation of Pneumococcal Types."3 I was
unable to claim that these observations provided any support
for the thesis that the transforming substance was DNA.
My presentation of the DNase story at the staff meeting
before the work was completed and the paper written had
reversed the procedure we had followed a year earlier when
our paper had already been submitted for publication before
Avery gave his talk. I had decided that I would like to publish
my findings on the purification and properties of the enzyme
in the Journal of General Physiology (another Rockefeller
Institute journal) where all of the work of Northrop and Kun-


Strengthening the Evidence               185
itz had appeared, and I felt that this would require some fur-
ther strengthening of the quantitative and biochemical data.
In addition, I had not given up hope of being able to crystal-
lize the enzyme before writing up my results. Accordingly,
much of my effort in the laboratory through the summer of
1945 was devoted to making more preparations of DNase so
that I could bring the study to some reasonable stopping point.
I had also prepared a rabbit antibody to the purified DNase
and needed to do more experiments to show that it reacted
specifically with the enzyme and also that it would inhibit its
action in breaking down DNA.
When I finally got around to writing the paper in the fall,
I had an experience of a kind that must sooner or later happen
to nearly everyone engaged in scientific research-I discov-
ered that I had been scooped. In a review article on enzymes
I found a reference to a German paper, published in 1941 in
the Zeitschrijl fib- physiologisches Chemie, that seemed to deal
with the purification of DNase." Due to the interruption of
communications by the war, this paper was not available in
our library or other libraries in the New York area, but I found
on inquiry that I could obtain a photostatic copy from the office
of the Alien Property Custodian in Washington. I quickly did
this and discovered that the German workers, although they
called their enzyme by a different name (thymo-polynucleo-
tidase), had gone over much the same ground that I had. They
had also apparently begun with dried pancreatic extracts and
then turned to the use of fresh pancreas and acid extracts by
the Northop-Kunitz procedure. Our two studies had much in
common, including failure to crystallize the enzyme, although
the German workers touched upon some points that I had not
considered and conversely my work dealt with some matters
not included in their paper. Their method of measuring enzyme
activity was so different from mine that I was unable to make
any direct comparison of the relative activity of our final prod-
ucts. In the end I had to write an addendum to the manu-


186             The Transforming Principle

script, describing the results of the German study and noting
that in the light of their work part of my paper represented
independent confirmation of their results.5
This example of the impact of a breach in scientific com-
munication no doubt ranks among the more trivial of the
destructive consequences of World War II, but it caused us
some loss of time and a great deal of extra work. Had we had
access to the German paper at the time it first appeared, it
would have been a simple matter to have prepared some pur-
ified DNase and tested its action on transforming DNA before
writing the first paper in 1943. There can be little doubt that
this would have bolstered our evidence that transforming
activity resided in DNA. As matters now stood, Fess and I
decided to report our results on the action of our DNase on
the transforming substance in a short communication in the
Journal of Experimental Medicine, and it was ready for sub-
mission on October 10, 1945, just a few days after my paper
on the enzyme had been sent to the Journal of General Phys-
iology. It was given the same general title as our 1944 paper
("Studies on the Chemical Nature of the Substance Inducing
Transformation of Pneumococcal Types") and designated as
paper II, with the subtitle: "Effect of Desoxyribonuclease on
the Biological Activity of the Transforming Substance."' It gave
the details on the kind of experiments I have described on the
inactivation of the transforming substance by the enzyme,
including the differential effect of citrate on the Mg'+- and
Mn'+-activated enzyme and the fact that a half-hour exposure
to the purified preparation at concentrations of less than 0.01
microgram per cubic centimeter caused total destruction of
the T. P.
In the discussion we tried to emphasize our view that the
enzymatic evidence "leaves little doubt that the ability of a
pneumococcal extract to induce transformation depends upon
the presence of a highly polymerized and specific form of
desoxyribonucleic acid. " We then added a paragraph directed
at the kind of criticism that we had been told was being voiced


Strengthening the Evidence               187
by Mirsky (he had said nothing to us directly; in fact, there
was no longer any communication):
The objection can be raised that the nucleic acid may merely
serve as a "carrier" for some hypothetical substance, presumably
protein, which possesses the specific transforming activity. Depo-
lymerization of the nucleic acid would according to this hypothesis,
destroy the effectiveness of the essential carrier and thus result in a
loss of biological activity. There is no evidence in favor of such a
hypothesis, and it is supported chiefly by the traditional view that
nucleic acids are devoid of biological specificity. On the contrary,
there are indications that even minor disruptions on the long-chain
nucleic acid molecule have a profound effect on biological activity.
Thus, treatment of the transforming substance with concentrations
of desoxyribonuclease so small that only a slight fall in viscosity occurs
causes a marked loss of biological activity. It is suggested that the
initial stages of depolymerization which are reflected by only mini-
mal changes in the physical properties of the nucleate are sufficient
to bring about destruction of specific activity.
In essence, we felt that the burden of proof had been shifted
to those who suggested that the transforming substance was
not DNA. We agreed that the enzymatic studies did not throw
any light on the chemical basis for the specificity of the nucleic
acids but merely confirmed that such a basis must exist. We
recognized the importance of this by writing: "It remains
one of the challenging problems for future research to deter-
mine what sort of configurational or structural differences
can be demonstrated between desoxyribonucleates of separ-
ate specificities."
In this flurry of publication activity there was yet another
manuscript, submitted at the same time and designated as
paper III in the series on T.P. The subject dealt with another
dividend growing out of the work on DNase and represented
our other major area of laboratory activity during the preced-
ing months. It had occurred to me that since citrate was such
a powerful inhibitor of pancreatic DNase it might conceivably
have a similar effect on the pneumococcal enzyme that had
long created a problem because of its ability to destroy the


188             The Transforming Principle
transforming substance. I made a crude pneumococcal enzyme
preparation and determined that its action on DNA-like that
of the Mg2+-activated pancreatic enzymewas totally blocked
by citrate. This immediately suggested that in citrate we had
in hand the kind of inhibitor that MacLeod had sought when
he was trying fluoride at the time he and Avery had resumed
full-time studies on transformation in the fall of 1940. It seemed
to me that it ought to be possible to increase the yield of
pneumococcal DNA by returning to the old Alloway proce-
dure of lysing the living organisms with deoxycholate as long
as sufficient citrate was present in the suspension of organisms
at the time of lysis. This worked like a charm. Within less than
a half-hour after adding a dash of deoxycholate to a suspension
of type III pneumococci in citrate, the organisms had all dis-
solved to yield a highly viscous, translucent solution that could
immediately be subjected to the first stages of purification by
shaking with chloroform by the Sevag procedure. None of the
old problems of loss of biological activity was encountered,
and the yield of transforming DNA was several times as large
as that obtained after extraction of heat-killed cells.
It was necessary to modify the purification process a bit,
however, since the extract prepared by dissolving the organ-
isms was very different in character and contained practically
everything that had been present in the living cells. The amount
of RNA, for example, was greatly in excess of that in our extracts
of heat-killed cells, and I coped with this by using RNase at
the same time that I treated the material with SIII enzyme,
dialyzing the mixture during the digestion process so as to get
rid of the enzymatic split products. This seemed to work, and
after carrying out the fractionation steps that depended on the
fibrous nature of the alcohol precipitates of DNA, we had a
product with activity comparable to that of our best prepara-
tions obtained by the old method. The surprise came on analysis
of the material, when we found that it was heavily contami-
nated with the somatic C polysaccharide, a major constituent
of the cell wall of the pneumococcus. This had never been a


Strengthening the Evidence               189
problem before, presumably because the amount of this poly-
saccharide released from the heat-killed cells was very small
and in a different form from that found after lysis of the entire
organism.
The removal of the C polysaccharide from the transform-
ing DNA depended on rediscovery of the merits of calcium-
alcohol precipitation, with which Colin MacLeod had experi-
mented four years earlier when he had come close to hitting
upon a powerful method for separating out the transforming
substance. In the presence of excess calcium ion, the addition
of a very small amount of alcohol is sufficient to bring DNA
out of solution in the form of a tangled mass of fibers. This
precipitation is complete when an amount of alcohol equiva-
lent to one-fifth the volume of the solution containing the DNA
is added (for a final alcohol concentration of about 16 percent,
or less than that of a fortified wine), and the fraction thus
obtained has all of the transforming activity. However, the C
polysaccharide remains in solution under these conditions,
making its removal from the DNA a relatively simple process.
In this way, we could get from a single 50-liter batch of pneu-
mococci up to 80 milligrams of purified DNA (as opposed to
45 milligrams from 200 liters of heat-killed cells), which was
comparable on analysis to our products prepared by the lengthy
and less efficient method we had published previously. We
had already known that the extraction of DNA from heat-killed
cells was far from complete. I had saved the residual cells
from most of our preparations and reextracted them later at a
somewhat higher temperature, showing that one could still
get appreciable amounts of active transforming DNA from this
worked-over source.
The new method also allowed us to consider seriously the
extension of our findings to the isolation of transforming DNA
from pneumococcal types other than type III. We did not have
a reagent like the SIII enzyme for degrading the capsular
polysaccharides of the other pneumococcal types, and so we
had to be selective in picking suitable organisms. Types I and


190              The Transforming Principle

XIV, for example, proved to be like type III in having acidic
capsular polysaccharides that were not separable from DNA
even by the calcium-alcohol method. On the other hand, we
found that the polysaccharides of types II and VI behaved in
the same way as the C polysaccharide so that purified DNA
could be prepared from these types. These DNAs were active
in the transforming system, inducing our R strain to produce
type II and type VI capsules, respectively, and thus establish-
ing on a more general basis that the pneumococcal transform-
ing substance is DNA. The experiments with type II were
not, strictly speaking, an example of transformation, since the
R strain, R36A, had originally been derived from a type II
organism. However, the implications are the same, because
as noted earlier R36A had totally lost its capacity to revert and
could be induced to make type II capsules again only through
specific transformation.
The additional studies were brought together in paper III,
which bore the subtitle: "An Improved Method for the Isola-
tion of the Transforming Substance and Its Application to
Pneumococcus Types II, III, and VI."7 To my way of think-
ing, the findings described added further support to the thesis
that it was the DNA itself that carried the transforming activ-
ity. Armed with information about the properties of the enzyme
that degrades DNA, we had been able to return to the prob-
lem of loss of activity during extraction of the transforming
substance-a problem that had plagued workers in the field
since the initial observations of Griffith-and show that it was
readily solved by adding an inhibitor of DNase. When one
considered the combined data of our original paper, the direct
effect of purified DNase, and now the demonstration that
DNase inhibitor would protect the T.P. during lysis of the
organisms, there was not much room left for the skeptics to
advance sensible alternatives to the view that DNA was the
active substance in transformation. There is some evidence to
suggest, however, that papers II and III (which finally appeared
in February 1946, just two years after paper I) were not very


Strengthening the Evidence                   191

widely read. They were infrequently referred to in discus-
sions of the transformation work, and I found that it was com-
monly assumed that data on the action of a purified DNase on
the transforming substance had been included in the first paper.
I will explore more fully the general reaction to our results in
the last chapter.
A final note about the crystallization of DNase. My efforts
had come to naught and just before I left the Avery laboratory
in 1946 I approached Kunitz with the suggestion that he take
up the problem. I got the impression that he was eager to do
this, having held off up to this time because he considered it
my property. I took some comfort from the fact that he didn't
find it easy either, but in the end he succeeded and was able
to publish a preliminary report on the crystallization of deoxy-
ribonuclease in Science in 1948.8 Hotchkiss, who had come to
Avery's lab as I left and continued to work on transformation,
showed that the crystalline enzyme was more potent than my
partially purified DNase in destroying transforming activity.
When Kunitz published two full-length papers on crystalline
DNase in the Journal of General PhysioEogy in 1950,g he was
very generous about my role in this business when he wrote:
"The present studies, which led to the isolation of the enzyme
in crystalline form, should be considered as a continuation of
McCarty's work, since Dr. McCarty not only suggested to the
writer that he enter the field but also cooperated in the initial
stages of these studies." I had visited him on a couple of occa-
sions while the job was in progress and, in addition to the
vicarious enjoyment of seeing my baby come out in the form
of crystals, I had an opportunity to get some idea of how he
did it. Patience was hardly the word to characterize his approach
to the problem. Meticulously, and with a highly systematized
procedure, he tried the effect of a whole series of variables
(salt concentration, acidity, temperature, etc.), each of which
was changed independently in small increments. It was labo-
rious, but his sweeping approach just about assured him of
ultimate success.


192             The Transforming Principle
My consolation prize for having failed at crystallization of
DNase was to come up unexpectedly with crystals of another
substance of interest in the laboratory, C-reactive protein. We
always checked our chest fluids for their possible content of
C-reactive protein, and early in 1946 we received a large vol-
ume of fluid (from one of the navy patients with pneumonia
in our hospital) that proved to have a high concentration of
the substance. Since the fluid proved to be useless in the
transforming system, I decided to isolate the protein for pos-
sible future studies. It was in the course of this process that I
obtained it in crystalline form, more or less accidentally,
although I am sure that my experience with the pancreatic
enzymes had sensitized me so that I knew what to look for.
Having a protein from human serum in the form of beautiful
rhomboid plates" was an exhilarating event in itself, but it
also led to a renewed interest in this substance that fostered
future studies.


XI

THE FINAL MONTHS

  s THE WORK ON DNase and its application to the prob-
A lem of transformation neared an end, Fess and I had
   had a number of discussions about what line of research
we would tackle next. There were a number of unanswered
questions concerning what actually went on in the transform-
ing system when one added transforming DNA to the growing
culture of rough pneumococci, and there remained the chal-
lenge of whether there was anything useful we could do to
dispel any of the lingering doubts that DNA was itself the
transforming substance. Among the oldest of the unsolved
problems was that of the serum factor and why it was neces-
sary to add it to the transforming system. We still had no clue
as to the purpose it served. It seemed likely, however, that it
was involved in providing the right conditions for the inter-
action of the rough pneumococci with the transforming DNA
and that we might learn more about this interaction if we could
discover the nature of the serum factor. I was thus led into
some unproductive research, referred to earlier, in which I
repeated and extended the kind of experiments on the frac-
tionation of the serum factor that Colin MacLeod had been
involved in some ten years before. The reasons for the failure
of this approach are probably not worth discussing in detail.


194             The Transforming Principle

The elusive serum component was later shown by Hotchkiss
to be the single most abundant protein in serum-albumin-
which appeared to act by protecting the pneumococci from
certain toxic substances in the growth medium.
My frustration during this period was more than matched
by Fess's depressed state of mind, which created an uneasy
atmosphere in the laboratory. He had always been suscepti-
ble to swings in mood, but the periods of apparent discour-
agement and depression had in my experience been of short
duration. I was told by Horsfall, however, that prior to his
thyroidectomy in 1934 Avery's natural ebullience had been
quite understandably suppressed for a long period. I believe
that his difficulties in 1945 were much more complex in ori-
gin. In the first place, after the long and dedicated search for
the nature of the transforming substance, the completion and
publication of the DNA paper followed by the confirmation
with DNase gave an aura of anticlimax to our current activi-
ties. Furthermore, he continued to be plagued by nagging
doubts about whether we were right, doubts that were clearly
not ameliorated by the reservations expressed by others, such
as Mirsky, and the apparently rather restrained acceptance of
the thesis advanced in the 1944 paper. I suspect that he was
also suffering some mental conflict in relation to his commit-
ment to retire and move to Nashville to join his brother, Roy.
The reasons that he had advanced for not making the move in
1943 were no longer valid, but we were all convinced that he
had little enthusiasm for leaving Rockefeller and New York.
He was obsessed with the idea that he should leave, however,
and frequently reiterated his observation that "A man should
know when he's through, move on, and get out of the way of
the young."
On top of all this, much of the work going on in the labo-
ratory was not the kind that he felt comfortable about partici-
pating in personally. As a result, he had a great deal of free
time that he had difficulty in filling with other activities. He
frequently went off to visit some of his former associates-


The Final Months                         195

Rene Dubos, Frank Horsfall, or Rebecca Lancefield-in their
laboratories where he would be brought up-to-date on the
recent developments in their research. There was a limit to
the amount of time he could spend in this fashion with busy
people who were intent on their own activities and inevitably
there were many hours when he was at loose ends. He would
come and sit in the chair beside my desk, saying very little
but effectively holding me immobile to share his gloomy out-
look. If I made a move to get up to do something in the lab,
he would make a gesture with his hand, raising one finger as
though he were about to say something, a strategem that
worked very well to keep me at the desk even after I had
learned by experience that he was not likely to follow it up
with conversation.
As time went on I found it difficult to cope in this situation
with the necessary restraint and good humor, and I'm afraid
that I was not nearly as patient with Fess as I should have
been. It was particularly aggravating to see how quickly he
could turn off the gloom if the social circumstances required
it. On occasion, while sitting at my desk, he would receive a
telephone call from a friend like Shosho MacLeod, Colin's
wife, and immediately undergo a remarkable alteration. His
face would light up, become animated and smiling, and his
voice would acquire a new timbre, expressing interest and
enthusiasm-features of his personality that I had not seen or
heard for days. The reversal was just as sudden and when he
had finished the conversation and hung up the phone, his face
fell abruptly with the return of his apathetic expression, just
as if it had been triggered by breaking the connection. He
never gave any direct indication that he was aware of my irri-
tation, which must have been all too obvious at times, but he
did make a couple of peace offerings which suggested that he
had some insight into the problem and the stress that his par-
tial paralysis imposed on me. In April 1945 he presented me
with a copy of the recently published second edition of Karl
Landsteiner's famous book The Specijicity of Serological


196             The Transforming Principle

Reactions. Then, about two months later on my birthday, he
gave me a copy of Rem? Dubos's first book, The Bacterial Cell,
which had just appeared. He had never done anything like
this before, and I interpreted the gifts as tokens of apology,
although the brief inscriptions in the books-"To Mac from
Fess"-provided no suggestion of this.
Our relationship gradually improved without ever quite
reverting to the easy camaraderie that prevailed during the
heat of the search for the nature of the transforming sub-
stance. An event that almost certainly fostered the improve-
ment was the arrival of a new face in the laboratory early in
the summer of 1945. Harriett E. Taylor had just received her
Ph.D. in genetics from Columbia University and had been
awarded a postdoctoral fellowship from the National Research
Council to come for, training in the laboratory. A bright, tal-
ented, and personable young lady, Harriett was an asset to
the laboratory from the very beginning. In retrospect, I believe
that her joining our studies at this juncture also brought a
boost in morale through the implications of her having chosen
the lab for her first postdoctoral experience. Here was at least
one young biologist, trained in classical genetics and steeped
in its traditions, who clearly saw the significance of the studies
on pneumococcal transformation and accepted the evidence
that DNA was the carrier of genetic information. Indeed, she
looked upon transformation as the wave of the future in genetic
research.
Harriett was soon taking an active part in all of the exper-
imental work, including the unproductive attempts to identify
the serum factor by fractionating and purifying it, and at the
same time she initiated some studies of her own on more
genetic aspects of pneumococcal transformation. She was an
excellent worker and adapted quickly to her new environ-
ment, which must have been quite different from anything
she had known in the biology department at Columbia. Even
the frustrations of the serum factor problem did not serve to
dispel the new sense of harmony that had settled on the lab.


The Final Months                        197

Fortunately, some of our efforts were more successful and
rewarding. It had occurred to me that the purified DNase
might provide a means of finding out more about what was
going on during the process of transformation. Since one could
easily add the enzyme to the transforming system in amounts
that would destroy any free DNA in a matter of seconds, it
seemed possible to determine how long it took the rough
pneumococci to take up the DNA after they had been inocu-
lated into the system. Once the DNA had been taken up by
the pneumococci and the process of transformation initiated,
the addition of DNase could no longer have any deleterious
effect. To test this idea, I started out with a large group of
tubes of the transforming medium, each of which contained a
liberal dose of type III DNA and the usual inoculum of R36A.
On overnight incubation, transformation would have occurred
in 100 percent of these tubes, if they were not tampered with.
My tampering consisted of temporarily removing sets of four
tubes from the incubator at half-hour intervals and lacing them
with an amount of DNase that was capable of wiping out the
viscosity of a DNA solution in less than a minute. The incu-
bation of the whole collection of tubes, which had been sub-
jected to DNase treatment at different times, was then
continued overnight for the completion of the transformation
reaction.

The results of this kind of experiment were clear cut and
consistent. If DNase were added to the system at any time
during the first 3 to 3.5 hours, transformation was completely
blocked and only the R organisms from the original inoculum
were found on subculture. On the other hand, if the addition
of DNase were delayed until four hours or later, it had no
effect on the reaction and transformed type III cells were found
in all tubes in the usual numbers. This seemed to be telling
us that, in the transforming system we had been using for the
past several years, the presence of the T. P. was irrelevant for
the first few hours of growth. The transforming DNA simply
sat there passively, waiting for the rough pneumococci to get


198             The Transforming Principle

in the mood to receive it. We could check this by growing the
R organisms for 4 hours in the transforming medium without
DNA and then determining how quickly they could take it up
after it was added to the culture. Again using DNase to elim-
inate unreacted DNA, but at shorter time intervals, we found
that the R organisms in these 4-hour cultures were able to
complete the transaction and proceed with transformation after
exposure to T.P. for as short a time as 5 minutes. Obviously,
some change had taken place in the pneumococci during the
first few hours of growth that permitted them to interact rap-
idly with DNA in their environment.
This alteration in the R organism that seemed to be required
for transformation was transient in the sense that, if incuba-
tion of the culture in the absence of DNA were continued
beyond 4 hours, they gradually lost the ability to take it up
rapidly when it was added. On the other hand, Harriett Tay-
lor found that if a 4hour culture were quickly chilled and
then refrigerated overnight, the pneumococci retained the
property of rapid interaction with DNA. Whatever the modi-
fication of the organisms was, therefore, it could be preserved
for a considerable period of time if further growth and metab-
olism of the living cells were temporarily suspended by
reducing the temperature. We had little information as to what
was going on to bring about this alteration in the behavior of
the organisms, leading to a condition that came to be known
as "competence," but the work of others a decade or two later
threw some light on the matter and showed it to be a complex
biological phenomenon.
The one thing that we knew was going on, of course, was
that during the 4 hours of initial growth the population of
pneumococci was progressively increasing, from the few
thousand organisms of the inoculum to about one or two mil-
lion. It was easy to show, however, that population size had
little or nothing to do with competence. As a matter of fact,
in the course of establishing this we found that with our
improved transforming system and purified transforming sub-


The Final Months                          199

stance the success of transformation had none of the marked
dependence on inoculum size that Dawson and Sia had
described when they first succeeded in getting transformation
in the test tube, an advance that was achieved only after a
thousandfold reduction in the number of organisms inocu-
lated. In our system, inocula of millions of cells were com-
patible with transformation, but even with these large numbers
a few hours' growth in the transforming medium was required
before they became competent.
Although these experiments on the conditions required
for the uptake by the rough pneumococci were not under-
taken with the idea that they might have a bearing on the part
played by serum factor in the transforming system, it soon
became evident that this was the case. The organisms became
competent and capable of rapid DNA uptake only when the
4-hour growth took place in the complete medium, which
contained chest fluid to provide the serum factor and anti-R
antibody. Growth in blood broth or in medium containing only
anti-R, in which the organisms multiplied perfectly well, would
not do the trick. This implied that, whatever the nature of the
serum factor might be, one of its principal functions was to
provide the appropriate conditions that would allow the pneu-
mococci to undergo the changes necessary for the assimilation
of the transforming DNA. This served to sharpen the focus of
the studies on the troublesome serum component and changed
the orientation of subsequent experiments.
During this period we also looked at other aspects of the
transformation reaction. For example, we were interested in
getting information on the frequency of transformation-that
is, how many of the pneumococci exposed to transforming DNA
actually went on to produce type III capsular polysaccharide?
We looked at this by diluting out competent organisms after
they had been treated briefly with DNA and determining the
minimal number that would yield type III colonies after trans-
fer and outgrowth in complete medium. Our best results indi-
cated that from 0.5 to 1 percent of the organisms in a 4-hour


200             The Transforming Principle
culture were able to carry the reaction to completion. While
this was probably a minimal figure, since the manipulations
tended to decrease the efficiency of transformation, the data
gave us some further insight into what was going on in the
tubes of our test system.
I had gradually become involved in giving more and more
talks about our work, with the result that the laboratory
experiments were no longer the strictly full-time endeavor
that they had been. One of the motives for these talks was to
make our findings better known among groups that might not
ordinarily read the Journal of Experimental Medicine. With-
out having any record of the exact date, I can remember mak-
ing a trip to Cold Spring Harbor, New York, to give a
presentation to the members of what was then the depart-
ment of genetics of the Carnegie Institution. I also talked about
the DNase before the Enzyme Club of New York City, which
in those days met regularly at the Faculty Club of Columbia
University. These reports on our work were good training for
me, but I have little idea how effective they may have been
in spreading the word about DNA.
Contrary to my impression at the time, I discovered long
afterward that Avery had taken part on at least one occasion
in these missionary presentations. He was so secretive about
it that I had no inkling of his talk until I saw it referred to in
a paper by Wyatt in 1975. ' It was given on the occasion of the
meeting of the American Association for the Advancement of
Science held in Cleveland in September 1944. Avery was vice-
president of the Section on Medical Sciences of the Associa-
tion and presented a paper that, according to a report of the
meeting published later in Science,2 was entitled "Experi-
mental Induction of Specific and Heritable Changes in Pneu-
mococcal Cells." True to his pattern of behavior with talks of
this kind, Avery did not allow the paper to be published. The
brief summary, by the secretary of the section, that was
included in the report of the meeting made no mention of
nucleic acid and revealed a rather restricted view of the work


The Final Months                                    201

in its final sentence: "The far-reaching implications of these
findings in the field of microbic life were considered in detail."
I had not seen this report in Science at the time, and in check-
ing the reference recently I noted that I had also missed an
item two weeks earlier in the same periodical reporting on
the award of the Gold Medal of the New York Academy of
Medicine to Avery on October 5 of that yeare In his citation
the president of the Academy had come somewhat closer to
the mark than the A.A.A.S. section secretary: "You have . . .
isolated the `transforming principle' as a thymonucleic acid.
This discovery has very far-reaching implications for the gen-
eral science of biology."

My first participation in a more formal conference came
about because of Fess's proclivity for not answering letters. It
is not true, as sometimes stated, that he never answered let-
ters, but he did tend to procrastinate in replying to those that
wanted something from him or requested detailed informa-
tion. He had an old-fashioned, roll-top desk in his small office
on the floor above the laboratory, and when it became too full
of unanswered correspondence that he no longer wanted to
face he would simply cover it all up by leaving the roll-top
down. On more than one occasion I saw him standing at the
closed desk and working on the top rather than open it and
remind himself of his derelictions.

Sometime in the late spring of 1945, Fess received a letter
inviting him to participate in a conference on "Intracellular
Enzymes in Normal and Malignant Tissues." The conference
was to be held in October under the sponsorship of the Inter-
national Cancer Research Foundation and the Jane Coffin
Childs Memorial Fund for Medical Research. He had long
since given up participating in activities of this kind, and con-
sequently the letter was relegated to the stack of unanswered
mail and remained there when he went off to Maine for vaca-
tion. The organizer of the conference, forewarned about Avery's
reputation as a correspondent, was resourceful enough to write
a second letter in August in which he indicated that he had


202             The Transforming Principle

interpreted Avery's silence as meaning consent, and accord-
ingly he was providing additional information and instructions
with regard to the conference. This served to bring quick action
from Fess, whose immediate response was to telephone me
from Deer Isle and ask whether I would be willing to take his
place at the meeting. Since I did not yet have any of his inhi-
bitions and was still eager to spread the word about DNA, I
was only too happy to accept. Very soon thereafter I received
my official invitation to attend.
As indicated by the title, the conference was oriented
principally toward cancer research, but one of the sessions
was on "Intracellular Enzymes of Nucleic Acid Metabolism"
for which I was asked to contribute a paper on the biological
role of the nucleic acids. This suited me fine, since I would
be able to summarize the past views about the function of
nucleic acids and then emphasize the implications of our find-
ings with the pneumococcal transforming substance. The con-
ference was an interesting one, held in a rambling resort-type
hotel in Hershey, Pennsylvania, and attended by many of the
outstanding biochemists and cancer researchers of the day,
seven of whom were subsequently awarded the Nobel Prize.
It was a successful experience for me in that I learned a great
deal during the four days of the meeting, although again I was
not sure that I had managed to convince any skeptics about
the genetic role of DNA. The copy of my prepared remarks
shows that I tried to relate our work to the main topic of the
meeting by saying: "the fact that desoxyribonucleic acid seems
to play a specific role in inducing and maintaining a heritable
modification in pneumococci gives rise to speculation con-
cerning the role of nucleic acid in the transformation of a nor-
mal tissue cell into a malignant one. In some types of neoplasm,
at least, the basic change may be a modification in the chem-
ical configuration and specific action of certain nucleic acid
molecules with a resultant change in the metabolism and growth
properties of the cell." This bit of gratuitous speculation didn't
exactly create a sensation either.


The Final Months

203

Some months later I had an opportunity to present our
findings in a quite different context, this time before a group
interested in viral research. Wendell Stanley had invited Avery
to participate in a symposium on "Biochemical and Biophysi-
cal Studies on Viruses" to be held in April 1946. Avery of
course declined and again offered me as a substitute. It was
natural for Stanley to include a paper on transformation in a
meeting that dealt with viruses-he had considered the trans-
formation phenomenon to be "virus-like" since the mid-1930s,
and we had referred to his published statement of this view
in the discussion section of our 1944 paper. His symposium
was a one-day affair held as part of the annual meeting of the
American Chemical Society in Atlantic City, New Jersey.
Because the other papers on the program that day all dealt
with animal, plant, or bacterial viruses, I discussed the rela-
tionship of the transforming substance to viruses after sum-
marizing the evidence for its identification as DNA. I was
inclined to emphasize the differences rather than the similar-
ities.

The ease tiith which the transforming substance can be inactivated
by enzymatic action stands in direct contrast to most of the accu-
mulated experience with animal and plant viruses and bacterio-
phage, which have been shown to be highly resistant to inactivation
by nucleases, and in most instances by other enzymes as well. It
may be that this is an indication of a fundamental difference between
the transforming substance and the viruses, a difference that had
already been suggested by the apparent absence of protein and ser-
ological activity.

I then concluded my talk with the following statement:

It will be observed from the foregoing discussion that while the
pneumococcal transforming substance is virus-like in certain of its
properties, there is some evidence inconsistent with its classifica-
tion with the viruses, despite the diversity of this group of agents.
However, if one accepts the validity of the view that the biological
specificity of the transforming substance is the property of a desoxy-
ribonucleic acid, the results of the present study serve to focus
attention on the nucleic acid component of the virus nucleoproteins.


204             The Transforming Principle
In addition to its probable role in the self-reproduction of the virus
molecule, the nucleic acid may carry a specificity which is a deter-
mining factor in the ultimate structure of the virus.

It was clear that Stanley had not drawn this conclusion
from our work himself, and he was not receptive to my remarks
on this occasion. In a historical piece on our work, written in
1970, he said:

It is obvious that despite my 1938 writings, I was not impressed
with the significance of the 1944 discovery by Avery, MacLeod, and
McCarty or I would have prepared high molecular weight tobacco
mosaic virus-RNA once again and tested it for virus activity despite
the fact that RNA was not suspected to have genetic properties. It
remained for Fraenkel-Conrat to do this important experiment in
my laboratory I4 years later.4

By the time he made these remarks in 1970, the free nucleic
acids of several viruses had been shown to be infectious and
capable of leading to the production of complete virus by the
infected cells. This is essentially what I was trying to predict
in a vague way in the final sentence of my symposium paper.

The proceedings of neither of these meetings-the Her-
shey conference on cancer or the Atlantic City symposium on
viruses-were published, and the message of my summaries
of our work was not disseminated beyond the groups that
attended the sessions. My first opportunity to reach a larger
audience came about in a quite different and gratifying man-
ner. Some of my colleagues, and I believe that Avery and
Horsfall were the prime movers, had nominated me for the
Eli Lilly Award in Bacteriology and Immunology. This was
one of the very few research awards in the field, and only
young investigators under the age of 35 were eligible; since I
was in my 35th year, my nominators had no time to lose. In
submitting the necessary documentation they had to include
copies of the manuscripts of the DNase work, because these
papers were still in press at the time the nomination was ini-
tiated. They managed to keep the whole business a secret


The Final Months                         205

from me so that the letter announcing my selection for the
award came as a complete surprise.

The Lilly Award was administered by three national sci-
entific societies in the field and was presented at the annual
meeting of the largest of these, the Society of American Bac-
teriologists. The Society met that year in late May in Detroit,
Michigan, at the old Book-Cadillac Hotel. Although the sci-
entific sessions lasted for a full week, I didn't have to appear
until Thursday, May 23, the day of the annual dinner at which
the award was to be presented by the president of the Soci-
ety. I arrived on that day, still in navy uniform, only to find
that there was no room for me at the hotel. It seems that the
name of the award winner was a closely guarded secret, meant
to be a complete surprise until it was announced at the din-
ner, and the secretary of the Society, in a misguided effort to
assure confidentiality, had hit upon the device of making my
reservation in the name of Dr. L. A. Ward (L. for Lilly, of
course) instead of mine. Unfortunately, when the supply of
rooms had been exhausted earlier that week, some officious
person had volunteered that she knew Dr. Ward and was sure
that he was not coming to the meeting, with the result that
my room was reassigned. After a short period of confusion,
the secretary solved the problem by sharing his official suite
with me.

I made the required address on the award-winning work
before a plenary session on the morning after the dinner; that
is, on May 24, about two weeks before my 35th birthday. This
talk carried the title: "Chemical Nature and Biological Speci-
ficity of the Substance Inducing Transformation of Pneumo-
coccal Types." I was allotted enough time to give a reasonably
detailed review of all of the research that we had completed
up to that time and to indulge in a little discussion of the
implications of the findings. I did not, however, break away
from our earlier reserved approach by explicitly claiming that
our results established DNA to be the substance responsible
for carrying genetic information in all living organisms. Rather,


206             The Transforming Principle

my discussion tended to follow the pattern of our papers and
the recent symposium talks. For example, part of the com-
ments on the implications were phrased in the following terms:
Indeed, there are certain striking analogies between the biological
properties of the transforming substance and those of viruses and
genes. For example, as in the case of viruses, the transforming agent
acts only on susceptible living cells; it is transmissible in series and
can subsequently be recovered in amounts far in excess of that orig-
inally used as inoculum. As in the case of genes, the transforming
substance behaves as a heritable unit in that it produces predictable
and durable alterations in cellular structure and function and is
reduplicated in daughter cells through successive generations. It
intervenes in the metabolism of the R cell, giving rise to the synthe-
sis of a new capsular substance, which in turn endows the cells with
distinctive and biologically specific characters not possessed by the
parent strain. Although the validity of these analogies may be ques-
tioned, they serve to underline the possible implications of the phe-
nomenon of transformation in the field of genetics and in virus and
cancer research.

On the other hand, I tried to be fairly forthright about our
conclusion that the transforming substance was indeed DNA:
Certainly there can be little doubt that de$oxyribonucleic acid must
be present in its intact, highly polymerized form [for transformation
to occur], and when all of the evidence is considered it appears
extremely unlikely that small traces of some other specific sLb-
stance, such as a protein, could be responsible for the manifestation
of transforming activity.
This review was published by the Society in one of its
journals, Bacteriological Reuiews,5 with unusual speed. It
appeared that same summer, thus providing some additional
exposure of our results to a bacteriological audience. The Lilly
Award also provided me with a handsome silver medal and a
check for $1000. The medal I still have as a memento of this
exhilarating time, and the check was promptly used to buy
my wife a piano, a luxury that we had been unable to afford
during the early years of our marriage.
  Another source of distraction arose in the late winter of


The Final Months

207

1946 as all of us in the naval reserve unit were anticipating
the termination of our navy service and return to civilian life.
Most of us did not have regular appointments at the Rocke-
feller Institute and were uncertain as to what we would be
doing when it reverted to peacetime status. Earlier in the
war, Dr. Rivers had been asked to organize an advance naval
research unit for the South Pacific, made up of a few members
of the Rockefeller group and a number of other investigators
recruited for their specific area of expertise. He assumed
command of this unit and moved out to Guam when it was
established there, leaving Horsfall in charge of the group that
remained at the Rockefeller Hospital. He spent all of 1945 at
this outpost, and his extensive correspondence during this
period with Horsfall and the director of the Institute, Herbert
Gasser, indicated his concerns about the future of the hospital
and its need for reorganization after the war. On his return in
January 1946, these matters claimed his top priority.

One of the most urgent of Rivers's problems was the
imminent retirement of the remaining senior members of the
hospital staff. The first of these was Homer F. Swift, head of
a laboratory concerned with streptococcal infections and
rheumatic fever, who was scheduled to retire in June 1946.
Because of the organization of the Institute there was no
requirement for retaining a laboratory in a specific area of
investigation on the retirement of the chief; but in the case of
rheumatic fever, Rivers felt that the disease continued to be
of sufficient importance to make it desirable to do so. While
he must have considered a number of possible candidates for
a successor to Swift, I have never had any information on this
point. I was taken completely by surprise when he called me
to his office in March and asked if I would be interested in
taking over the Swift laboratory on July 1.

The proposal did not include promotion to the rank of ten-
ured Member of the Rockefeller Institute, but it was clearly
implied that this would be forthcoming if I proved myself in
this new area of research. I had no qualms about the prospect


208             The Transforming Principle
of probationary status, since the offer seemed to me to rep-
resent a real chance to get a permanent place at Rockefeller,
a goal that had seemed so unattainable that I could hardly
admit to myself how much I wanted it. A more important
question was whether the problem of streptococcal infections
and their relationship to rheumatic fever represented an area
in which I was interested in devoting my future research efforts.
I had few, if any, reservations about this. I had had extensive
experience with the care of young patients with rheumatic
fever during my pediatric residency at Johns Hopkins and had
considered the disease to be among the most challenging
problems in the realm of infectious diseases. In addition, Swift's
laboratories occupied the other half of our floor of the hospital
building, so that my interest in the problem had been con-
stantly reinforced through contact with members of his group
during my years with Avery. In essence, the unsolved puzzle
was how the common streptococcal sore throat managed to
lead to the delayed appearance in many patients of rheumatic
fever, with its frequent severe involvement of the heart. Most
of the serious heart disease of young adults at that time could
be traced to the occurrence of one or more attacks of rheu-
matic fever in childhood. It was evident that an essential line
of attack on the problem was to learn more about the causa-
tive streptococci, making it a problem in medical microbiol-
ogy that certainly appealed to me.
There was one difficulty. How could one even consider
turning from the path of research opened up by the DNA
discovery? No doubt the lure of being on my own and having
a chance at a permanent Rockefeller appointment were fac-
tors, but there were other considerations. I was not trained
as a geneticist and was little attracted to pursuing the studies
along genetic lines. We had talked about attempts to trans-
form characters other than capsule formation in order to extend
the significance of the phenomenon, and we had even dis-
cussed possible models for demonstrating DNA transforma-
tion in higher, nonbacterial species. However, we made no


The Final Months                          209

move in this direction, and the former approach was left to be
exploited successfully by Hotchkiss and others. (It was not
until recent years that DNA transformation has been accom-
plished in higher organisms.) My own preference was to con-
tinue with a biochemical attack. We knew that DNA could be
extracted from R pneumococci in the same amount and with
the same general properties as that obtained from the S
organisms, but it was without effect in our capsule transform-
ing system. Our interpretation of this finding was that most of
the DNA in our purified transforming substance was con-
cerned with innumerable other functions and properties of
the pneumococcal cell, like that from R pneumococci, and
that only a small fraction was involved in directing the synthe-
sis of capsular polysaccharide. I thought that it should be pos-
sible to prove this by fractionating the material in order to
obtain purified, or at least highly enriched, preparations of
the DNA molecules responsible for capsular transformation.
I made only tentative and completely unsuccessful attempts
to separate out the active fraction of DNA, and it is just as
well that I did not become committed to a more serious effort.
Even with today's knowledge and techniques it would be a
monumental task.
All in all, it seemed that I was coming to a good stopping
point in these studies, and I did not delay long in telling Dr.
Rivers that I would accept the position. He sent me to Dr.
Gasser for the purpose, I am sure, of getting his concurrence
with the appointment. This interview didn't seem to be going
particularly well until I volunteered the information that I was
very much interested in the problem of rheumatic fever and
eager to begin research in the area. His comment was, "That's
what I've been waiting to hear you say," and it turned out
that little more had to be added. Rivers had of course dis-
cussed the matter with Avery in advance, which paved the
way for me when I went to Fess to seek his advice in the
matter. Fess would never tell one what to do in these situa-
tions, but he was very good at analyzing the pros and cons,


210              The Transforming Principle

thus clarifying the basis for a decision. I got the impression
that he considered the offer a great opportunity for me and
that he was neither surprised nor disappointed when I accepted
it.
After it was settled-sometime in April, as I remember
it-that I would be moving to the other end of the laboratory
floor on July 1, new plans were made for continuation of the
studies on pneumococcal transformation. It was arranged that
Rollin Hotchkiss would join Fess and Harriett Taylor when I
departed. Hotchkiss, a skilled and experienced biochemist,
had long had an intense interest in the problem of transfor-
mation and had, in fact, asked Fess to let him participate in
the work in 1938. Fess had replied something in the nature
of "Not now," a response that may have been motivated by
the fact that this was during the period that the problem had
been temporarily set aside. In view of this history, which I
was not aware of until many years later, it seems likely that
Hotchkiss was not any more enthusiastic about my appear-
ance on the scene in 1941 than MacLeod was. Like MacLeod,
however, he never showed evidence of this in our personal
relations, and was always a helpful and cooperative colleague.
I had a few weeks to bring my experimental work on trans-
formation to some kind of reasonable conclusion and not leave
behind any untidy overlaps with the new regime. There was
one more conference still ahead of us. We had been invited
to participate in a Cold Spring Harbor Symposium on "Heredity
and Variation in Microorganisms" to be held that June, and
we had yet to prepare for it. Fess had as usual declined the
invitation and offered me as substitute, and I conceived the
idea of using this forum for the presentation of all of our recent
research in order to avoid leaving behind pieces of the prob-
lem in which I felt I still had a significant stake. Quite simply,
I thought it would be better if I could make a clean break.
The paper I put together was entitled "Biochemical Studies
of Environmental Factors Essential in Transformation of
Pneumococcal Types," with Harriett Taylor joining Avery and


The Final Months                                   211

me as co-author.6 I included all that I thought was salvageable
from the work on serum factor, together with the data on the
time of uptake of DNA by R pneumococci and some experi-
ments, which I have not described in these pages, that gave
some indication of what the R antibody was doing in the trans-
forming system. The paper was prefaced with a brief historical
introduction in which we reiterated our earlier view that our
work "had established beyond reasonable doubt that the active
substance responsible for transformation is a specific nucleic
acid of the desoxyribose type," and then tried to explain the
rationale for our interest in the "environmental factors. " It
may have been a tactical error to focus on these ancillary mat-
ters rather than presenting a detailed review of the evidence
for the DNA nature of the transforming substance as I had
done for the Lilly Award lecture. There were a number of
geneticists at the symposium, and I suspect that most of them
had not heard the facts on which we based our conclusion.

In any event, I did not get the impression that many of
the geneticists there wholeheartedly embraced the implica-
tions of our findings for their own genetic studies. Harriett
and I both attended the meeting, and I believe that she may
have been a more effective proponent of our views than I was,
although I have no record of specific successes in this regard.
At the end of the session at which I had presented the paper,
one of the geneticists actually came up to me and said: "Now
that you fellows have shown that nucleic acid is not responsi-
ble for transformation, why don't you get to work and find out
what really is?" I recovered quickly enough from this sally to
reply that I was under the impression that this was exactly
what we had done-shown that it was DNA, thus abruptly
ending the conversation. He was a hard case, however, and
his subsequent writings indicated to me that he didn't have a
clear understanding of the phenomenon of pneumococcal
transformation, let alone the work that we had done on the
transforming substance.

These Cold Spring Harbor Symposia were held annually


212             The Transforming Principle
on selected topics of what was called "quantitative biology,"
and the entire proceedings of the meeting were published
each year in a hard-cover volume. The delay in publication
was great enough in 1946 so that by the time we had galley
proof Hotchkiss already had some of his evidence that pure
preparations of serum albumin would effectively replace the
serum factor in the transforming system as long as a little R
antibody was supplied from some other source. This sug-
gested that what we had written about a globulin fraction (the
other major class of serum proteins) playing a role in serum
factor was simply wrong. He called this to the attention of
Avery who in turn let me know that we had a problem, As
Hotchkiss put it some years later, Avery "refused to borrow
our facts [Hotchkiss's and Harriett Taylor's] to decorate their
paper, but neatly protected the readers by changing every
`globulin fraction' in the manuscript to `protein fraction.' "7 It
was all the more clear to me, however, that I had made a
mistake in trying to push our unsatisfactory serum factor work
into print just in order to leave no loose ends of the problem
behind when I moved out of the laboratory.
That move occurred on July 1, 1946, without any signifi-
cant disruption of normal activity. It was also the first day that
the members of our naval reserve unit were eligible for dis-
charge from the service, and I found time to go through this
process as well. The assumption of my new responsibilities
and my return to civilian life thus occurred on the same day.


XII

AFTERMATH

M ANY DIFFERENT OPINIONS have been expressed about
   the reception in the scientific community of our
   reports on the biological activity of pneumococcal

DNA and about the extent to which the work was unappre-
ciated or ignored. Since we had our own views on the subject,
we were naturally interested in these opinions as they appeared
but never made any public comments on them. In discussing
the matter here, I have no hope of resolving the numerous
issues that have been raised. However, in reviewing this part
of the history, I can call attention to a number of factors that
certainly influenced the reception of the pneumococcal DNA
story and give my own personal assessment of the degree to
which its acceptance was retarded.

In the first place, there is little question that the date of
the appearance of our first paper in February 1944 sharply
limited the audience that it reached. Coming as it did near
the height of our involvement in World War II, the paper was
seen by only a fraction of the biomedical scientists who ordi-
narily would have been following this journal and by almost
none of those who were working abroad. The later papers on
the pancreatic DNase and its effect on the transforming factor
did not fare significantly better, since they appeared prior to


214              The Transforming Principle

the restoration of the normal channels of scientific commu-
nication after the war. As a matter of fact, these follow-up
studies did not seem to benefit from the subsequent renewed
interest in the first paper, which apparently resulted from fur-
ther dissemination of information about the pneumococcal
studies, chiefly from the written comments appearing in review
articles by biologists but also by word-of-mouth. We had orig-
inally ordered three hundred reprints of the first paper, but
these were quickly depleted in the postwar period so that we
had to obtain an additional three hundred copies by photo-
offset to satisfy the renewed demand. On the other hand, papers
II and III were rarely cited in publications dealing with the
subject, even though the authors always referred to paper I.
In many cases it was not clear whether the writer was even
aware of the additional evidence that had come from the use
of DNase.

A second factor relates to the readership of the journal in
which the work was published. To be sure, all of the earlier
papers from the Avery laboratory on the subject of pneumo-
coccal transformation-that is, those of Dawson and Allo-
way-had appeared in the Journal of Experimental Medicine,
but the Journal was not one that was read by geneticists and
general biologists. Thus, those scientists who were most likely
to be interested in the broader implications of the findings
became aware of the work only if someone specifically called
it to their attention. Under these conditions, the manner in
which they heard the facts assumes considerable importance,
and this has a bearing on the impact of the reservations
expressed by Mirsky, as I will discuss shortly.

In addition to these immediate and specific factors that
influenced full dissemination of the pneumococcal DNA story,
there were elements in the general scientific climate that con-
tributed to slow acceptance of the results. As noted in an ear-
lier chapter, the science of bacteriology had developed almost
as if it were not an integral part of biology. Those bacteriolo-
gists who dealt with variation in microorganisms had adopted


Aftermath                              215

their own terminology instead of that of the geneticists,
speaking, for example, of bacterial dissociation rather than
mutation. On the other hand, the geneticists, who had made
their great strides in the understanding of genetic mecha-
nisms through the analysis of multicellular organisms that
undergo sexual reproduction, did not consider the bacteria,
with their simple life cycles, presumably devoid of any ele-
ment of sexual reproduction, as suitable for genetic study. The
techniques of mating and crosses, for example, could not be
used to establish genetic information as they were with the
fruit fly or maize. New information on bacterial systems was
just beginning to break down this rather artificial barrier
between genetics and bacteriology in the mid-1940s but many
of the classical geneticists were still influenced by the tradi-
tional view.
Thus, the majority of geneticists were not prepared to accept
information emerging from studies of the pneumococcus as
having any bearing on the genetics of higher organisms, just
as the majority of biochemists were still influenced by the
notion that nucleic acids were monotonously alike and there-
fore not likely candidates for the possession of biological spec-
ificity. As pointed out previously, even though the scientific
evidence on the concept of a uniform structure of all nucleic
acids was neither very rigorous nor convincing, the idea had
not been seriously challenged by recent chemical research and
its survival was fostered by the growing emphasis on proteins
as the bearers of biological specificity. The proteins were
obviously tremendously diverse and it was becoming increas-
ingly clear that they were responsible for the specificity of a
vast array of biologically important molecules, such as enzymes
and antibodies.
Alfred hlirsky had taken the point of view that we did not
have adequate evidence to claim that the transforming sub-
stance was DNA, and he had prepared a detailed assessment
of the evidence to support this contention. He did not discuss
the matter with us, but we had heard by the grapevine that


216             The Transforming Principle

he was expressing his opinion frequently in personal conver-
sations with interested individuals. Since he was widely
acquainted with biologists and biochemists, this dim view of
the implications of our work certainly reached many ears and
undoubtedly had some influence on its reception. As far as I
know, Mirsky's first public presentation at the Rockefeller
Institute of his opinions on this matter was on April 12, 1946,
when he gave a lecture at one of the Friday afternoon staff
meetings on "Some Aspects of the Chemistry of Chromo-
somes." Even then he did not incorporate the topic in his
lecture but summarized his views in response to a question
from the floor during the discussion period. I was not present
at the lecture, since this was the day that I had to be in Atlan-
tic City to participate in Wendell Stanley's American Chemi-
cal Society symposium on viruses. Fess had sat through the
whole talk without, of course, making any comment, and when
he told me about it on my return the following Monday he
said: "I'm glad you weren't there, Mac. You would have felt
that you had to answer him." He was still happy to let the
evidence speak for itself.

Because of my absence I had only secondhand information
on the precise line that Mirsky followed in making his com-
ments on the transforming substance. I knew his point of view
in general, however, and I assume that what he said at the
meeting was pretty much in the same vein as what he wrote
later in the year when he and Pollister published their first
full-length papers on their nucleoprotein studies in which he
also described our single collaborative experiment. The key
paragraph reads as follows:

Avery and his colleagues have shown decisively by inactivation
experiments that desoxyribose nucleic acid is an essential part of the
transforming agent, and if there is actually no protein in their prep-
aration, it would be obvious that the agent consists of nothing but
nucleic acid. This is a conclusion of the greatest interest in the study
of the chemical basis of biological specificity, and it should therefore
be scrutinized carefully. There can be little doubt in the mind of


Aftermath                               217

anyone who has prepared nucleic acid that traces of protein proba-
bly remain in even the best preparations. With the tests now avail-
able for detecting how much protein is present in a nucleic acid
preparation, it is probable that as much as 1 or 2 per cent of protein
could be present in a preparation of "pure, protein-free" nucleic
acid. . . . No experiment has yet been done which permits one to
decide whether this much protein actually is present in the purified
transforming agent and, if so, whether it is essential for its activity;
in other words, it is not yet known which the transforming agent
is-a nucleic acid or a nucleoprotein. To claim more, would be going
beyond the experimental evidence.'
Taken at face value, this analysis appears quite reasonable and
persuasive, but it seemed to us to ignore some of the impli-
cations of our experimental work. Our initial crude extracts
contained substantial amounts of protein, but as we removed
it during purification to a point where it was no longer detect-
able there was no loss of transforming activity. As a matter of
fact, the specific activity--that is, the activity per unit weight-
actually increased. Therefore, any remaining protein in the
final preparations, in addition to being totally resistant to pro-
tein-splitting enzymes (even after it had been subjected to the
denaturing effect of deoxycholate and the process of shaking
with chloroform), had to be completely insensitive to the pro-
cedures we used for deproteinization. This all stood in sharp
contrast to the exquisite sensitivity of the transforming activ-
ity to DNase. Moreover, we had the evidence that transform-
ing activity moved with the DNA in both the ultracentrifugal
and electrophoretic fields, which put further constraints on
the notion that a protein present in small amounts could be
responsible for the specificity.
Mirsky had an opportunity to summarize his views before
a different audience at the Cold Spring Harbor Symposium
that was held in June 1947 on the subject of "Nucleic Acids
and Nucleoproteins." This summary came in discussion of a
paper presented by Andre Boivin of Strasbourg, France, who
described his recent findings on transformation of another
microorganism, the common colon bacillus. The data appeared


218             The Trunsfonning Principle
to be fully confirmatory of our pneumococcal work, although
Boivin's studies later suffered some loss of credibility when
other laboratories were unable to reproduce his results. It must
be said for Boivin, however, that he was much less restrained
in discussing the genetic implications of his findings than we
had been. At his Cold Spring Harbor meeting, he made sev-
eral explicit statements like the following: "In bacteria-and,
in all likelihood, in higher organisms as well-each gene has
as its specific constituent not a protein but a particular desoxy-
ribonucleic 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."2 This was certainly a fine
statement of what we believed but had been too reticent to
say. Comments of this kind must have galvanized Mirsky into
action, and he rose during the discussion period to give a
detailed analysis, ticking off the several points of evidence for
the specificity of DNA and then rebutting each of them at
length. He then reiterated his conclusion that "it would be
going beyond the experimental facts to assert that the specific
agent in transforming bacterial types is a desoxyribonucleic
acid." Boivin in reply acknowledged that one could not say
this with absolute certainty but again echoed my opinion by
saying that "it seems to us that the burden of the proof rests
upon those who would postulate the existence of an active
protein lodged in an inactive nucleic acid."
I believe that Mirsky's views must have influenced a num-
ber of people, especially the classical biologists and geneti-
cists, but there is no way of accurately assessing the effect of
this. I have been told by Swedish friends that they feel it was
an important factor in the deliberations of the Nobel Prize
committee in those early years after publication of our papers
when Avery was still alive. The official line on this point as
expressed in the Nobel Foundation's volume, Nobel: The Man
G His Prizes, tends to support that interpretation. The dis-


Aftermath                              219

cussion of our work states in part: "The discovery, because of
its far-reaching implications, aroused much interest, and Avery
was proposed for a Nobel Prize. But doubts were also
expressed, and the Nobel Committee found it desirable to
postpone an award. Actually, Avery's finding was not accepted
in all quarters until A. D. Hershey . . . and M. Chase, in
1952, demonstrated that bacteriophage-DNA carries the viral
genetic information from parent to progeny."3 They do not
comment on the fact that Avery lived for three years after
1952.
I do not know precisely when or on what basis Mirsky
himself finally accepted that DNA was almost certain to be
the carrier of genetic information. It is not likely, however,
that it depended very heavily on the Hershey-Chase experi-
ment mentioned in the Nobel book, since by its nature this
was not likely to be any more convincing to him than our work
was. Another line of investigation that had a bearing on the
DNA thesis had been undertaken by Boivin, Vendrely, and
Vendrely in France shortly after they reported their results
on Escherichia coli transformation. They measured the amount
of DNA per cell in various organs of the animal body and
found it to be a constant value, the same for all somatic cells,
but just twice the amount present in the germ cells of the
same species4 This is just what one would expect if DNA
were the genetic material, because germ cells have only half
the complement of chromosomes of somatic cells. With his
colleague, Hans Ris, Mirsky carried out similar studies, pub-
lished in 1949, that in general supported the French results.
From this they were at least willing to conclude that DNA "is
part of the genie material. This does not mean, however, that
the gene consists of nothing but nucleic acid."5 This was not
a major change from the Mirsky assessment of the pneumo-
coccal transforming evidence. In the end, it must have been
a combination of various pieces of evidence that persuaded
him. In 1968 he wrote a piece on "The Discovery of DNA"
for Scientijk American that was chiefly a report of the early


220             The Transforming Principle
history following the original description of DNA by Miescher
in 1869. He indicated in his introductory paragraph that he
would "tell something of the investigative history of DNA until,
some 25 years ago, it was conclusively shown to be the genetic
material. " That would be 1943! In the final paragraph he comes
back to this point, writing that "investigators at the Rockefel-
ler Institute-following a line of investigation with a different
historical background-found that hereditary traits could be
transmitted from one strain of bacteria to another by the transfer
of DNA. Nucleic acid was thus shown to be the genetic mate-
rial."`j This would appear to be a substantial revision of his
earlier views.

Some of Fess's old friends found it difficult to forgive Mir-
sky for what they conceived as his role in retarding recogni-
tion of the DNA work. I can recall an occasion when one of
them would have happily prevented Mirsky from being given
the honor of being selected as a Harvey Lecturer if he had
been able, despite the fact that the high quality of his research
clearly justified his selection. Colin MacLeod was not quite
so vindictive, although he obviously was not happy about the
situation. He wrote me as follows on September 16, 1958:

Dear Mac

I suppose you saw the DNA article in the Times of Sunday, Sep-
tember 7, which by and large was very good. I could not refrain
from a snort, however, when in the second to the last paragraph
Drs. Mirsky and Ris are credited with demonstrating that DNA
determines the transmission of heredity. I suppose this is called
poetic justice or injustice. . . . See you soon.
                            Colin

As far as I was concerned, I was in the position of being on
the same faculty with Mirsky for the remainder of his life, and
it made no sense to continue to behave as though we did not
know each other. In the end, we arrived at a congenial rela-
tionship, even though one could hardly say that we were close
friends.


Aftermath                                          221

In the course of 1945 and 1946 there were enough indica-
tions from a variety of sources of acceptance of the implica-
tions of the 1944 paper to give us some encouragement. For
example, in the January 1945 issue of American Scientist
G. Evelyn Hutchinson of Yale University included a review
of our work in his "Marginalia, " a section that he contributed
regularly to the publication. In commenting on the signifi-
cance of the findings, he noted that the transforming sub-
stance "seems to be at least a fragment of a genetic system"
and concluded that "It is at any rate certain that Avery and
his co-workers have made an extremely fundamental contri-
bution not only to bacteriology and immunology, but to all
the biological sciences. "7 Among the comments of bacteriol-
ogists, those of J. Howard Mueller of Harvard were especially
noteworthy. After describing our findings in a 1945 review,
he went on to say: "The importance of these observations can
scarcely be over estimated and stimulates speculation con-
cerning such matters as the chemical basis for specificity in
nucleic acids, and the genetic implications presented by the
ability to induce permanent mutation in a cell by the intro-
duction of a chemical substance."s
In a similar vein, the great geneticist Sewall Wright, in a
review on the "Physiological Aspects of Genetics," inter-
preted our work as indicating that DNA might be a chromo-
somal fraction acting a genetic role." Sir Henry Dale went
even further in his citation of Avery for the Copley Medal,
which was presented by the Royal Society in 1946. He stated
that pneumococcal transformation should be given "the status
of genetic variation; and the substance inducing it-the gene
in solution, one is tempted to call it-appears to be nucleic
acid of the desoxyribose type. "lo Items of this kind certainly
told us that many in biological science were interpreting our
results in much the same way that we were.
At the same time that we were getting these indications
that many biologists accepted our evidence, while others
remained skeptical, there were also suggestions that many


222             The Transforming Principle

simply ignored it. A notable example comes from a confer-
ence on "Gene Action in Micro-organisms" that was held just
one year after the publication of the 1944 paper. Not one of
the several participants who presented papers on this topic
mentioned pneumococcal transformation, and no discussion
of the work appears in the published record of the meeting. l1
Evidence that workers in microbial genetics had not promptly
incorporated the possible genetic role of DNA into their
thinking was also apparent at the Cold Spring Harbor Sym-
posium in 1946, where I gave the paper on our later work as
discussed in the previous chapter. David Bonner, an impor-
tant contributor to the work on the biochemical genetics of
Neurosporu, included the following comment in the summary
of his paper: "There is quite general agreement at present
that genes contain nucleoprotein as an essential component of
their structure. One should expect, therefore, that genes, like
other proteins, have specific configurations [italics mine].""
In effect, it is possible to find a wide range of responses during
these early years to our claim that the pneumococcal trans-
forming substance was DNA. The obvious conclusion is that
there was no general consensus.
The most convincing evidence of acceptance of our thesis
came from those scientists who based their own research on
the assumption that it must be correct, even though we were
of course not aware of this until somewhat later. Preeminent
among these was Erwin Chargaff of Columbia University, who
has acknowledged on more than one occasion that it was the
1944 paper that led him to change the course of his laboratory
work and turn all of his efforts to the study of nucleic acids.13
He began with the view that our deduction that DNA carried
biological specificity meant that DNAs must differ chemically
from one another, and proceeded to carry out a series of
experiments showing that DNA from different species had
widely varying compositions as reflected by the proportions
of the four bases present in the molecule, laying to rest for-
ever the notion that nucleic acids are all alike. As he pursued


Aftermath                              223
these studies further, he discovered a phenomenon that is
referred to as "base complementarity": in all of the DNA sam-
ples examined, regardless of differences in overall composi-
tion, the number of molecules of the base, adenine, was equal
to that of the base, thymine; and the other two bases, guanine
and cytosine, were also present in equal amounts. This dis-
covery of the base pairing of adenine-thymine and guanine-
cytosine was of prime importance for understanding the struc-
ture of DNA, and it proved to be a decisive factor in the for-
mulation of the Watson-Crick model.
There is also little reason to doubt that the work of Watson
and Crick was directly influenced by the findings with pneu-
mococcal transforming DNA, although our studies were not
referred to in their papers. Watson makes this clear in The
Double Helix in his description of the basis for Francis Crick's
interest in DNA. He wrote:

Given the fact that DNA was known to occur in the chromosomes
of all cells, Avery's experiments strongly suggested that future
experiments would show that all genes were composed of DNA. If
true, this meant to Francis that proteins would not be the Rosetta
Stoue for unraveling the true secret of life. Instead, DNA would
have to provide the key to enable us to find out how the genes
determined, among other characteristics, the color of our hair, our
eyes, most likely our comparative intelligence, and maybe even our
potential to amuse others.
Of course there were scientists who thought the evidence favor-
ing DNA was inconclusive and preferred to believe that genes were
protein molecules. Francis, however, did not worry about these
skeptics." "
When they started their work on the structure of DNA in
1951, there was very little else on the record that could have
turned their attention in this direction. They certainly could
not have been influenced by the experiments of Hershey and
Chase with bacteriophage, referred to in Nobel: The Man 6
His Prizes as providing the evidence that finally convinced all
skeptics of the genetic role of DNA, since this work did not
appear until 1952.


224             The Transforming Principle

The Hershey-Chase experiments were ingenious and
interesting, but there has been some debate as to whether
they were responsible for the kind of impact implied in the
Nobel volume. As a matter of fact, it seems likely that the
reverse may have been true to some extent and that their
work might not have been so readily accepted had not the
information on pneumococcal DNA already existed. They
obtained evidence that DNA is the genetic material using an
entirely different system and different methodology, thus
complementing our work very effectively. The experiments
were done with bacteriophages (bacterial viruses) that were
composed of roughly equal parts of protein and DNA, and
each component was labeled during production of the phage
with a radioactive isotope-sulfur for the protein and phos-
phorus for the DNA. Using these labeled phages, they obtained
data which indicated that only the DNA entered the bacterial
cell at the time of infection; the protein coat was left outside. l5
Thus, they provided the first clear evidence that the nucleic
acid of virus carries its genetic message, a conclusion that was
inescapable if one accepted the general implications of the
pneumococcal work, as I had tried to point out in 1945.
Despite my change in laboratory and research activity in
1946, I did not immediately cease my attempts to serve as a
missionary for the DNA story. Among the talks that I gave
during the next few years, I have particularly vivid recollec-
tions of one included in a one-day "Symposium on Cancer" at
the University of Illinois College of Medicine in Chicago in
December 1948. This was held in honor of Professor Otto
Warburg, one of the giants of German biochemistry, and was
designed in part to present to him some of the recent scien-
tific developments that he may not have been familiar with
because of the information blackout during the war. I used
the same title as on several previous occasions-for example,
in the Lilly Award lecture-but talked principally from notes,
writing out only a brief introduction and summary. The rea-


Aftemmth                                22s

son that I remember this occasion so well is that Warburg
seemed to be barely listening to my talk and it was clear that
it made no impression on him whatsoever. Again, I came away
with the feeling that I had accomplished little or nothing in
the way of spreading the word.
The most amusing episode in connection with these later
talks occurred at my alma mater, Johns Hopkins, where I had
been invited to speak at the regular evening meeting of the
Johns Hopkins Medical Society in February 1949. I prepared
a new manuscript, rather than warming over previous reviews
of the story of pneumococcal transformation, and included some
of the recent data that had been published by others. On the
day of the talk, in order to have time for a visit to my old
haunts at the Harriet Lane Home, I took the train to Balti-
more at about noon. In the more than eight years since I had
left Hopkins, there had been many changes at Harriet Lane
and I found very few of my old colleagues on the scene. As a
result, the visit was brief and not very conducive to relighting
my nostalgic memories of the place. Through a mix-up, I had
not been notified that there was a dinner for the speakers at
the Faculty Club on the Homewood campus of the university,
and I repaired to a restaurant across from the hospital for an
early dinner.
In order to stretch out the dinner hour, I bought a copy of
a Baltimore evening paper to peruse at the table. Prominently
displayed on the front page, with banner headlines, was a news
release from the U.S. Army announcing the discovery of a
new drug for the treatment of sea sickness. This dealt with
Dramamine, which had originally been introduced as an
antihistamine. Dr. Leslie N. Gay, the head of the allergy clinic
at the Hopkins hospital, had noted its effect on motion sick-
ness and engaged in extensive tests of its effectiveness on sea
sickness on the ships returning our troops from Europe after
the war. The newspaper article ended with the information
that the work would be presented that evening at 8:15 at the


226             The Transforming Principle

meeting of the Johns Hopkins Medical Society in the Hurd
Memorial Hall of the Johns Hopkins Hospital.

Hurd Hall was a large amphitheater, which one entered
at the rear and then moved down the steps to reach the seats
that stretched on both sides of the aisle in descending tiers.
There was, in addition, an ample balcony at the rear and along
both sides where extra seats could be placed. By the time I
reached the hall, it was thoroughly packed with people; all
the seats were filled, many of the steps had been occupied,
and there were numerous standees all around the balcony. In
my seven years at Hopkins, I had never seen Hurd Hall so
overfilled. There were only two papers on the program, the
first being Dr. Gay's presentation of the impressive data on
the prevention of motion sickness with Dramamine. After a
short period of questions and discussion following his paper,
the president of the Society got up to introduce me as the
second speaker. Very little that he said could be heard because
of the noise created by people streaming out of the hall. When
the exodus was complete, after I had given the first few min-
utes of my talk, I counted approximately thirty-five hardy souls
who remained in the audience because they wanted to hear
about pneumococcal transformation or because they felt they
had to remain out of courtesy. It is obvious that in 1949 DNA
was no match for sea sickness in attracting a medical audi-
ence.

Although this episode was a source of embarrassment for
some of the members of the Hopkins Medical Society, I
remember being amused by it and taking the whole affair with
equanimity. By that time, I no longer hoped for any immedi-
ate and dramatic signs of universal recognition of the impli-
cations of the DNA work. On the other hand, I was convinced
that there was continuing progress in this direction and that
the ultimate acceptance of the genetic role of DNA was only
a matter of time. Perhaps this came more slowly than it might
have, but I have never been attracted to the notion that our


Aftermath                               227

discovery was "premature. " This idea was advanced by Gunther
Stent in 1972 in an article in Scientijk American entitled,
"Prematurity and Uniqueness in Scientific Discovery." He
introduced his thesis in the following way:
Five years ago I published a brief retrospective essay on molecular
genetics, with particular emphasis on its origins. In that historical
account I mentioned neither Avery nor DNA-mediated bacterial
transformation. My essay elicited a letter to the editors by a micro-
biologist, who complained: "It is a sad and surprising omission that
. . . Stent makes no mention of the definitive proof of DNA as the
basic hereditary substance by 0. T. Avery, C. M. MacLeod and
Maclyn McCarty. The growth of [molecular genetics] rests upon
this experimental proof . . . I am old enough to remember the
excitement and enthusiasm induced by the publication of the paper
by Avery, MacLeod and McCarty. Avery, an effective bacteriolo-
gist, was a quiet, self-effacing, non-disputatious gentleman. These
characteristics of personality should not [cause] the general scien-
tific public . . . to let his cause go unrecognized."
I was taken aback by this letter and replied that I should indeed
have mentioned Avery's 1944 proof that DNA is the hereditary sub-
stance. I went on to say, however, that it is not true that the growth
of molecular genetics rests on Avery's proof. For many years that
proof actually had little impact on geneticists. The reason for the
delay was not that Avery's work was unknown to or mistrusted by
geneticists but that it was "premature."16
I would agree that geneticists found no immediate way to
apply the information on DNA to their own experimental work,
but it is hardly irrelevant that this information was directly
responsible for the work of Hotchkiss (who had soon, by fur-
ther purification and analytical studies on transforming DNA,
convinced most biochemists, at least, that the notion of a con-
taminating protein was a myth), Chargaff, Watson and Crick,
as well as others, which bridged the gap and made possible
the development of molecular genetics. I would argue that
the discovery was not "premature" but rather required fur-
ther biological, chemical, and structural development before
it could be manipulated by the geneticists. Since these next


228             The Transforming Principle

steps stemmed directly from the proof that DNA is the hered-
itary substance, the emergence of molecular genetics still has
its origins in that discovery.
I cannot say that I am any more enamored of the point of
view set forth by H. V. Wyatt in an article entitled, "When
Does Information Become Knowledge?", l7 in which he uses
our 1944 paper and its recognition as the text for his discus-
sion. His essential point is that the information in our paper,
with its low-key presentation, could not be readily fitted into
accepted ideas at the time it was published and was therefore
not transformed into "knowledge." Wyatt's analysis appeared
before Stent's, but he returned to the topic later in a second
article that considers both points of view and some of the
objections that had been raised to their theses. He brings their
ideas together by stating that "Thus 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."ls While this is almost certainly true, I
don't believe that he establishes that it applies to the work on
pneumococcal DNA.
At the outset of his discussion, Wyatt poses the question:
"Why was it that Griffith's discovery of transformation led
eventually to DNA, whereas Avery's demonstration of DNA
as the genetic material did not lead immediately to a new
paradigm?" He proceeds by suggesting that the answer to this
assumed paradox involved technical problems: "Griffith's dis-
covery of transformation was extended because this was tech-
nically feasible, and in the next 10 years steady progress was
made by Avery's associates at the Rockefeller Institute." I would
hope that I have made it clear in these pages that this state-
ment does not very accurately reflect the state of the research
during this period and that one cannot assume, as Wyatt does,
that "each step brought Avery nearer to the identity of trans-
forming principle." In contrast to this view of the research
between 1928 and 1944, Wyatt felt that difficulty in following


Aftermath                              229

up on the 1944 paper "lay in translating the information into
a form which could lead to further experiments and could be
assimilated into a meaningful scientific paradigm." He sums
up with the comment: "Thus Avery's discovery was prema-
ture because the technical means were not yet available to
extend the work into other systems and confirm the universal
nature of the phenomenon. "
As I see it, the major flaw in this kind of analysis is that it
assumes some sort of parallelism between the scientific
approaches required to determine the chemical nature of the
transforming substance on the one hand and to capitalize on
the information that DNA was the carrier of genetic informa-
tion on the other. One obvious next step, as we recognized
early in the game, was to learn something of the chemical
basis for the biological specificity of the nucleic acids. It cer-
tainly must count as an "extension" of the information on
pneumococcal DNA that Chargaff began his work on the
chemical composition of DNA as a result of reading our paper
and that the information was also the basis for Watson and
Crick's focus on the structure of the molecule. Thus, along
one of the most important lines of research to be pursued, the
response was prompt and effective. Wyatt also takes a differ-
ent view than I do about what he calls the "extension of bac-
terial transformation to other systems." He notes that this did
not happen until almost twenty years after the publication of
Griffith's paper, but it is equally true that during this period
very few labs had even been concerned with the confirmation
of Griffith's results and only one with the nature of the trans-
forming substance. On the other hand, the publication of our
results on DNA soon stimulated a clear expansion of the field.
Boivin's work followed shortly upon ours, and by 1950 Hattie
Alexander had succeeded in obtaining DNA-mediated trans-
formation with another bacterial species, Hemophilus influ-
enzae." In addition, several pieces of work soon came along
demonstrating the DNA transformation of genetic characters
other than capsule formation (Harriett Taylor on colony var-


230             The Transforming Principle
iants " Robert Austrian on a type-specific protein,`l Rollin
Hot&kiss on penicillin resistance,22 and Hattie Alexander on
streptomycin resistance23), making it clear that the phenom-
enon was not restricted in some way to control of the synthe-
sis of capsular polysaccharides. Within ten years after the
publication of the 1944 paper, there was thus a great deal to
show for the follow-up on the original suggestion that DNA is
the carrier of genetic information. Progress only seems slow
when compared to current developments in molecular genetics,
but it has taken a vast amount of research in hundreds of lab-
oratories across the world to bring us to our present capacity
to manipulate genes almost at will. The earlier studies show-
ing that the transforming principle was DNA and those that
led to general recognition of the genetic role of DNA were by
contrast carried out by a mere handful of investigators.
By 1970 molecular biology was flourishing and just about
to be expanded fantastically by the technical developments
that made possible the powerful approaches classed in the cat-
egory of recombinant DNA. In the 1970s a number of books
began to appear that dealt with the history of DNA and the
recognition of its role as the genetic material. One of the first
and perhaps most scholarly of these was written by Robert
Olby, an English historian of science, who called his book The
Path to the Double Helix. The London edition of this volume
first appeared in 1973, but the edition that was available in
the United States, published by the University of Washington
Press, did not appear until a year later."' Olby had been work-
ing on the book for some years, however, and he was thus
able to interview Colin MacLeod personally in the early stages
of the writing and to have further correspondence with him
prior to Colin's death in 1972. Olby also interviewed me at
about the same time that he did Cohn in 1968, and we later
exchanged several letters. As a result of his contacts with the
two of us, he was able to present an authoritative treatment
of the pneumococcal DNA work, including a few vignettes
that were not extractable from the published work. His book


Aftermath                               231

is an extensive history that spans the period from the first
discovery of nucleic acids through the establishment of the
structure of DNA by Watson and Crick.
Another of these historical volumes wirtten by Franklin
H. Portugal and Jack S. Cohen, appeared in 1977. Their book,
A Century of DNA: A History of the Discovery of the Struc-
ture and Function of the Genetic Material,25 carries the sub-
ject through the solving of the genetic code. The authors had
reviewed the annual reports to the Scientific Board of Direc-
tors in the Rockefeller University archives, and they were the
first to point out that there was a hiatus in the work on trans-
formation in the Avery laboratory between 1937 and 1940, a
fact that I discovered independently in reviewing this mate-
rial. They also rejected Stent's categorization of the pneumo-
coccal DNA discovery as "premature" for much the same reason
that I have above.
The most recent of these assessments of the biological rev-
olution is Horace F. Judson's massive tome, The Eighth Day
of Creation,26 which is broader because it includes sections
on RNA and protein in addition to the primary one on DNA.
The latter section had the unusual distinction for a piece of
science history of appearing first in the Neuj Yorker. Judson,
like Olby, had spent several years collecting material for his
book, and in the course of this time interviewed most of the
major scientists who figured prominently in the development
of molecular biology. For reasons that are not entirely clear,
he never made any effort to see MacLeod, who was still alive
in the early stages of his research for the book, or to contact
me. Inevitably, therefore, his treatment of the pneumococcal
DNA portion of the story has a more second-hand quality and
does not incorporate the view of those that were involved
directly in the research. He is one of those who focuses almost
entirely on the 1944 paper, and there is no reference to the
subsequent work on DNase and its influence on the final proof.
As a matter of fact, the book is almost devoid of reference to
DNase in any connection.


232             The Transforming Principle

It was from Olby's book that I got the first intimation that
Colin MacLeod had views about my participation in the work
that he had never expressed to me. Olby quotes from a letter
wirtten to him by MacLeod in 1967 as follows:
By the time McCarty joined us we were virtually certain of what we
were dealing with, both on the basis of the methods of preparation,
the physical-chemical properties, and the elementary analysis.
Moreover, we had pretty good evidence that the enzyme which
destroyed activity was DNase from a variety of lines of approach.
. Maclyn McCarty was a great help in tying things down and in
getting further evidence that the enzyme was indeed DNase through
purification of the enzyme from pancreas.27
I have to confess that I was upset when I first read this in
1975, three years afer Colin's death. It certainly doesn't jibe
with my perception of what went on during those early years,
and nothing that I encountered subsequently on reviewing
the notes and other materials tends to support it. I can con-
ceive of Fess and Colin keeping from me at the outset their
conviction that they were dealing with DNA so as not to start
me off with preconceived notions, but there would have been
little reason to persist in this deception for the next several
months. The data in the laboratory notes suggest that Colin's
view resulted from a trick of memory in which he merged the
recollection of early events with those that occurred after I
had begun to work with Avery in the fall of 1941.
First, there was no preparation of purified pneumococcal
DNA, separated from the bulk of RNA and SSSIII, that would
have been useful for elementary analysis and physical-chemi-
cal studies until the fall of 1942. One elementary analysis is to
be found recorded in the notes before this time, on May 26,
1941, and it serves to make my point that the material then
available was not suitable for this kind of analysis. The sample
contained more carbon but less than half the amount of phos-
phorus and nitrogen found in our later preparations or in
authentic DNA, suggesting that a large component of SSSIII
was present. With respect to the evidence that the enzymes


Aftermath                             233
that destroyed transforming activity were DNase, I have been
able to find no record of these enzymes being tested on DNA
until I did it in the summer of 1942. In fact, no method for
measuring DNase activity had been available in the lab.
I feel, therefore, that I must stick with the interpretation
of the events as I have unfolded them in these pages. My
conclusion that MacLeod's memory was playing tricks on him
receives some support from another Olby quote, this time
from his recorded interview with Colin. In reporting on a visit
that he and Avery made to P. A. Levene to discuss transfor-
mation, Colin says: "He [Levene] was skeptical about the pos-
sible role of DNA in transformation reactions." The difficulty
here is that Levene died in September 1940, and it was not
mltil late January 1941 that Avery and MacLeod had discov-
ered, rather to their surprise, that their extracts contained a
small amomlt of DNA. They could not have raised the issue
of DNA with Levene on the basis of any specific information
about the pneumococcal material.
It has been my purpose to tell the story of the discovery
of the genetic role of DNA, along with what I feel to be the
necessary background, and I will not dwell further on the
aftermath. Certainly this is no place to attempt an assessment
of the current status of the explosive developments in DNA
science. Because my research has followed a different path
since those early years, I have not been personally involved
in any of these developments since the late 194Os, even though
I have followed them with interest. It has been an exciting
time for biologists in all branches of the field, including med-
icine.
The stimulus for finally getting down to the business of
writing this story came from the celebration of the thirty-fifth
anniversary of the publication of the 1944 paper. The talk that
I prepared on this occasion sent me back to the old laboratory
notes and archives, and I realized that a more serious job of
researching the available material would have to be carried
out in order to piece together the different phases of the


234             The Transforming Principle

investigation. Joshua Lederberg originated the idea for this
anniversary celebration. After he had accepted the appoint-
ment as the new President of the Rockefeller University, but
before arriving on the scene from Stanford, he sent me a
handwritten memo dated February 1, 1978:

Dear Mac-

A 35th Anniversary coming

I was just noticing the date and reflecting that it was the 34'
birthday of the DNA paper.

211144 was an important day in my life, and it would disappoint
me to let 2/l/79 go by without notice. I really would look forward to
having a convocation planned around that theme-perhaps a sup-
plement to J. Exp. Med., or whatever, as well. . . . And it's time
you brought your own reminiscences out of the closet! I'll ask you
what you've thought about it in March (visit). . . .
                   Yours, Josh

I had known Lederberg since the Cold Spring Harbor Sym-
posium in 1946, which he had attended as a very active and
articulate graduate student. He gives the 1944 paper credit
for changing the course of his career, moving him out of med-
ical school into the graduate study of genetics; and he was one
of those who had quite soon applied the information in the
paper to his own laboratory work in an unsuccessful attempt with
F. J. Ryan to cause mutations in the mold Neurospora with
DNA. I was quite sympathetic with his idea of celebrating the
thirty-fifth anniversary but did not think it was appropriate
for me to take a leading role in arranging it. The matter was
not forgotten, however, and plans were put in operation that
f'all for a special colloquium at the University on February 2,
1979. Lederberg, Dubos, Hotchkiss, and I all spoke, and each
member of the audience was provided with a reprint of the
original paper which had been reproduced, together with a
foreword by Josh, in the February issue of the Journal of
Experimental Medicine.

I gave my talk at the anniversary meeting the title: "The


Aftermuth                             235
Identification of the Pneumococcal Transforming Substance
as DNA: A Retrospective Look at How We Got There." It
was not published, but I used it extensively in preparing an
invited historical paper for the Annual Review of Genetics on
"Reminiscences of the Early Days of Transformation.""8 These
efforts moved me to think in terms of doing a more thorough
and complete job, which now, for better or worse, is finished.


BIBLIOGRAPHY

T HE MANY REFERENCES throughout the text to the Annual
  Scientific Reports to the Board of Scientific Directors
   of the Rockefeller Institute for Medical Research are

indicated by the date on which the reports were submitted
and they are not cited in this section. In addition, the material
drawn from the laboratory notes is also identified by date. The
annual reports are to be found in the Rockefeller University
Archives, and it is my intention to deposit the laboratory notes
in this same resource as soon as I have finished working with
them. The present section is designed primarily to provide
the specific reference citations for the published work to which
I have referred.

A comprehensive treatment of all of the research on pneu-
tnococci through the mid-1930s was provided in a volume
prepared by Avery's old friend and colleague at the Hoagland
Laboratory, Benjamin White (The biology of plaeumococcus.
1938. New York: The Commonwealth Fund). This book was
recently reprinted (1979) by H arvard University Press so that
it remains available to modern students of the subject.

           I. THE PREPARATORY YEARS
1. Luck, J.M. 1936. Liver proteins. I. The question of protein storage.
Jourfld ofBiological Chemistry 115:491-510.


238

Bibliography

11. THE MEDICAL SCENE

1. Scott, D.A., and A.F. Charles. 1933. Studies on heparin. Ill. The
purification of heparin. ]ournaZ of Biologicnl Chemistry 102:437-448.
2. Hodes, H.L., W.C. Stifler, Jr., E. Walker, M. McCarty, and R.G.
Shirley. 1939. The use of sulfapyridine in primary pneumococcic pneu-
monia and in pneumococcic pneumonia associated with measles. Pediatrics
14:417-446.

3. McCarty, M. 1941. Effect of p-aminobenzoic acid on therapeutic and
toxic action of sulfapyridine. Proceedings of the Society for Experimental
Biology and Medicine 46:133-136.

4. McCarty, hl,, and W.S. Tillett. 1941. The inactivating effect of sul-
fapyridine on the leukotoxic action of benzene. /o~lrnaE of Experimental
hfedicine 74:53I-544.

Ill. THE SUGARCOATED
     MICROBE

1. Neufeld, F., and L. Hgndel. 1910. Weitere Untersuchungen tiber
Pneumokokken-Heilsera. Ill. Mitteilung. Uber Vorkommen und Bedeu-
tung atypischer Varietgten des Pneumokokkus. Arbeiten aus dem kaiser-
/i&en Gesundheitsamte 34293-304.
2. Do&z, A.R., and L.J. Gillespie. 1913. A biologic classification of
pneumococci by means of immunity reactions. Journal of the American
Medical Association 61:727.

3. This story, which 1 heard from Avery on more than one occasion, is
also told by Dubos in his scientific biography of Avery (Dubos, R. J. 1976.
The Professor, the Institute, and DNA, 63. New York: The Rockefeller Uni-
versity Press).

4. Dochez, A.R., and O.T. Avery. 1917. The elaboration of a specific
soluble substance by pneumococcus during growth. ]ournul of Experimen-
tul Medicine 26:477-493.

5. Heidelberger, M. 1977. A "pure" organic chemist's downward path.
Annual Reoiew ofMicrobiology 31:1-12 (quote on p.9).
6. Ibid., 10.
7. Heidelberger, M., and W. F. Goebel. 1926. The soluble specific sub-
stance of pneumococcus. IV. On the nature of the specific polysaccharide
of Type Ill pneumococcus. Journal of Biological Chemistry 70:613-624.
8. Goebel, W.F. 1939. Studies on antibacterial immumity induced by
artificial antigens. I. Immunity to experimental pneumococcal infection with
an antigen containing cellobiuronic acid. Journal of Experimented Medicine
693353-364.

9. Avery, O.T., and R. Dubos. 1931. The protective action of a specific
enzyme against type Ill pneumococcus infection in mice. Journal of Exper-
imental Medicine 54:73-89.


Bibliography

IV. TRANSFORMATION

1. GriI%th, F. 1928. The significance of pneumococcal types. ]ournd of
Hygiene 27:113-159 (quote on p. 117).
2. Ibid., 129-130.
3. Ibid.
4. Ibid., 153.
5. Neufeld, F., and W'. Levinthal. 1928. Beitrage zur Variabilitat der
Pneumokokken. Zeitschrift fiir lmmunitiitsforschung 55:324-340.
6. Dawson, M. H. 1928. The interconvertibility of "R" and "S" forms of
pneumococcus. Journal of Experimental Medicine 47:577-591.
7. Dawson, M.H. 1930. The transformation of pneumococcal types. II.
The interconvertibility of type-specific pneumococci. Journal of Experi-
tnental Medicine 51:123-147.

8. Dawson, M.H., and R.H.P. Sia. 1931. In vitro transformations of
pneumococcal types. I. A technique for inducing transformation of pneu-
mococcal types in vitro. Journal of Experimental Medicine 54:681-700.
9. Sia, R.H.P., and M.H. Dawson. 1931. In vitro transformations of
pneumococcal types. II. The nature of the factor responsible for the trans-
formation of pneumococcal types. Journal of Experimental Medicine 54:701-
710.

IO. I do not know what publication Francis is referring to here.
11. This talk was published in international Virology 1. Proceedings of
the First International Congress of Virology, 1969, pp. 224-228. Basel: S.
Karger.

12. Alloway, J.L. 1932. The transformation in vitro of R pneumococci
into S forms of different specific types by the use of filtered pneumococcus
extracts. ]ournal of Experimental Medicine 55:91-99.
13. Alloway, J. L. 1933. Further observations on the use of pneumococ-
cus extracts in effecting transformation of type in vitro. Journal of Experi-
mental Medicine 57:265-278.

14. Letter to O.T. Avery from Simon Flexner 6 October 1931. From
the Papers of Simon Flexner in the archives of the American Philosophical
Society.

              V. ENTER MACLEOD

1. Sevag, M.G. 1934. Eine neue physikalische Enteiweissungsmethode
zur Darstellung biologisch wirksamer Substanzen. Isolierung von Kohlen-
hydraten aus Hiihnereiweiss und Pneumokokken. Biochemische Zeitschrifi
27.3:419.

VIII. INTIMATION OF SUCCESS

1. MacLeod, C.M., and M. McCarty. 1942. The relation of a somatic
factor to virulence of pneumococci [Abstract]. Journal of Clinical Inwsti-
gotion 21:647.


240                    Bibliography

2. Caspersson, T., E. Hammarsten, and H. Hammarsten. 1935. Inter-
actions of proteins and nucleic acids. Transactions of the Fnraday Society
31:367-389.

3. Schultz, J. 1941. The evidence of the nucleoprotein nature of the
gene. Cold Spring Harbor Symposia on Quantitatice Biology 9:56-65.
4. Gortner, R.A. 1929. Outlines of Biochemistq, 358, 3%). New York:
John Wiley & Sons.

5. Leathes, J, B. 1926. Function and design. Science 64:387-394.
6. Mirsky, A.E., and A.W. Pollister. 1946. Chromosin, a desoxyribose
nucleoprotcin complex of the cell nucleus. Journal of General Physiology
30:121.

IX. THE HOME STRETCH

1. The original of this historic letter is now among the O.T. Avery Papers
in the Tennessee State Library and Archives, Nashville, Tennessee. The
complete text is available, including the first three pages which were com-
pleted before Avery decided to undertake the description of his current
work in the laboratory.

2. Bresch, C. 1964. Klassische und molekulare Genetik, 130. Berlin:
Springer-Verlag.

3. Hotchkiss, R. D. 19fi6. "Gene, transforming principle, and DKA." In
Phage and the Origins of Molecular Biology, edited by J. Cairns, G.S. Stent,
and J.D. Watson, pp. 185-187. New York: Cold Spring Harbor Laboratory
of Quantitative Biology.

4. Dubos, R. J. 1976. The Professor, the Institute, and DNA, Appendix
I, pp. 217-220. New York: The Rockefeller Press.
5. Letter from H.A. Schneider to President Detlev W. Bronk of Rocke-
feller University written on September 22, 1965, with reference to the ded-
ication of the Avery Memorial Gateway, which took place at the University
on September 29. The letter is from the Detlev Bronk Papers in the Rock-
efeller University Archives.

6. Avery, O.T., C. M. MacLeod, and M. McCarty. 1944. Studies on the
chemical nature of the substance inducing transformation of pneumococcal
types. Induction of transformation by a desoxyribonucleic acid fraction iso-
lated from pneumococrus type III. Journal ofExperimmtal Medicine 79:137-
158.

X. STRENGTHENING THE EVIDENCE

1. Reported in G.W. Corner. 1964. A History of the Rockefeller Insti-
tute, 1901-1953: Origins and Growth, 430. New York: The Rockefeller
Institute Press.

2. McCarty, M. 1980. Reminiscences of the early days of transforma-
tion. Annual Reciew of Genetics 14:1-15.
3. McCarty, M. 1945. Reversible inactivation of the substance inducing


Bibliography

241

tnlns~~rmatio~~ of pneumococcal types. Journul of Esperiruentnl Medicine
81:501-514.

4. Fischer, F.G., I. Biittger, and H. Lehmann-Echternacht. 1941. fiber
die Thymo-polynucleotidase aus Pankreas. NucleinsHure. V. Zeitschrift fiir
pl'!l,siolofii.sches Chemie 271:246-264.

5. McCarty, M. 1946. Purification and properties of desoxyribonuclease
isolated from beef pancreas. Journal ofGeneru1 Physiology 29:123-139.
6. McCarty, M., and O.T. Avery. 1946. Studies on the chemical nature
of the substance inducing transformation of pneumococcal types. II. Effect
of dcsoxyribonuclease on the biological activity of the transforming sub-
stallce. Journal of Esperimentul Medicine 83:89-96.
7. McCarty, M., and O.T. Avery. 1946. 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, Ill, and VI. lournnl ofExperi?nenta~
Medicine 83:97-104.

8. Kunitz, M. 1948. Isolation of crystalline desoxyribonuclease. Science
108:19-20.

S. Kunitz, M. 1950. Crystalline desoxyribonuclease. I. Isolation and
general properties. Spectrophotometric method for the measurement of
desoxyribonuclease activity. II. Digestion of thymus nucleic acid (desoxy-
ribonucleic acid). The kinetics of the reaction. Journal of General Physiol-
ogy 33:349-x7.

10. McCarty, M. 1947. The occurrence during acute infections of a pro-
tein not normally present in the blood. IV. Crystallization of the C-reactive
protein. Journcd of Experimental Medicine 85:491-498.

XI. THE FINAL MONTHS

1. Wyatt, H.V. 1975. Knowledge and prematurity: The journey from
transformation to DNA. Perspectives in Biology und Medicine 18:149-156.
2. Science October 27, 1944, 100:375.
3. Science October 13, 1944, 100:328-329.
4. Stanley, W.M. 1970. The "undiscovered" discovery. Archives of
Envirmmentcd Health 21:256-262.

5. McCarty, M. 1946. Chemical nature and biological specificity of the
substance inducing transformation of pneumococcal types. Bacteriological
Reviews 10:63-71.

6. McCarty, M., H.E. Taylor, and O.T. Avery. 1946. Biochemical stud-
ies of environmental factors essential in transformation of pneumococcal
types. Cold Spring Harbor Symposia on Quantitative Biology 11:177-183.
7. Hotchkiss, R.D. 1966. "Gene, transforming principle, and DNA." In
Phage and the Origins of Moleculur Biology, edited by J. Cairns, G. S. Stent,
and J.D. Watson, p. 188. New York: Cold Spring Harbor Laboratory of
Quantitative Biology.


242

Bibliography

XII. AFTERMATH

1. Mirsky, A. E., and A. W. Pollister. 1946. Chromosin, a desoxyribose
nucleoprotein complex of the cell nucleus. Journal of General Physiology
30 (quote on pp. 134-135).

2. Boivin, A. 1947. Directed mutation in colon bacilli, by an inducing
principle of desoxyribonucleic nature: Its meaning for the general biochem-
istry of heredity. Cold Spring Harbor Symposia on Quantitative Biology
12:7-17.

3. Nobel: The Man 6 His Prizes, 3rd edition, 1972 (quote on p. 201).
Edited by the Nobel Foundation and W. Odelberg. New York: American
Elsevier.

4. Boivin, A., R. Vendrely, and C. Vendrely. 1948. L'acide desoxyri-
bonucleique due noyau cellulaire, depositaire des caracteres hereditaires;
argmnents d'ordre analytique. Comptes rendus hebdomadaires des SCunces
de I'Acaddmie des Sciences, Paris 226:1061-1063.
5. Mirsky, A.E., and H. Ris. 1949. Variable and constant components
of chromosomes. Nature (London) 163:666-667.
6. Mirsky, A.E. 1968. The discovery of DNA. Scientijic American 218:78-
88.

7. Hutchinson, G.E. 1945. The biochemical genetics of Pneumococcus.
American Scientist 33~56-57.

8. Mueller, J. H. 1945. The chemistry and metabolism of bacteria. Annual
Review of Biochemistry 14:734.

9. Wright, S. 1945. Physiological aspects of genetics. Annual Review of
Physiology 7:75-106.

10. Dale, Sir H. 1946. Address of the president. Proceedings of the
Royal Society (London) 185A:128.
11. AJ`nals of the Missouri Botanical Garden, 1945. Special Number,
Conference on "Gene Action in Micro-organisms," 32:107-263.
12. Bonner, 1). 1946. Biochemical mutations in Neurospora. Cold Spring
Harbor Symposia on Quantitative Biology 11:21.
13. Chargaff, E. 1963. Essays on Nucleic Acids. New York: Elsevier.
Chargaff, E. 1978. Heraclitean Fire, pp. 82-84. New York: The Rockefeller
University Press.

14. Watson, J.D. 1968. The Double Helix (quote on p. 14). New York:
Atheneum.

15. Hershey, A., and M. Chase. 1952. Independent functions of viral
proteins and nucleic acid in growth of bacteriophage. Journal of General
Physiology 36:39-56.

16. Stent, G.S. 1972. Prematurity and uniqueness in scientific discov-
ery. Scienti$c American 227:84.

17. Wyatt, H.V. 1972. When does information become knowledge?
Nature 23586-89.

18. Wyatt, H.V. 1975. Knowledge and prematurity: The journey from
transformation to DNA. Perspectives in Biology and Medicine 18:149-156.


Bibliography                             243

19. Alexander, H.E., and G. Leidy. 1951. Determination of inherited
traits of H. in$uensae by desoxyribonucleic acid fractions isolated from type-
specific cells. Journal of Experimental Medicine 93:345-359.
20. Taylor, H.E. 1949. Additive effects of certain transforming agents
from some variants of pneumococcus. Journal of Experimental Medicine
89:399-424.
21. Austrian, R., and C. M. MacLeod. 1949. Acquisition of M protein
by pneumococci through transformation reactions. Journal of Experimental
Medicine 89:451-460.
22. Hotchkiss, R.D. 1951. Transfer of penicillin resistance in pneumo-
cocci by the desoxyribonucleate fractions from resistant cultures. Cold Spring
Harbor Symposia on Quantitative Biology 16:457-461.
23. Alexander, H., and G. Leidy. 1953. Induction of streptomycin
resistance in sensitive Hemophilus infuenzae by extracts containing
desoxyribonucleic acid from resistant Hemophilus infuenzae. ]ournal of
Experimental Medicine 97:17-31.
24. Olby, R. 1975. The Path to the Double Helix. Seattle: University of
Washington Press.
25. Portugal, F.H., and J. S. Cohen. 1977. A Century of DNA. Cam-
bridge, Mass.: MIT Press.
26. Judson, H. F. 1979. The Eighth Day of Creation. New York: Simon
and Schuster.
27. Olby, R. The Path to the Double Helix, p. 185.
28. McCarty, M. 1980. Reminiscences of the early days of transforma-
tion. Annual Review of Genetics 14:1-25.


INDEX

activated charcoal, 106
agglutination experiments, 60, 62
albumin, see serum albumin
alcohol precipitation:
of DNA, 136-37, 146, 150-51, 188-
  89

of transforming extracts, 84, 107,
112, 114-15, 132-33, 135

Alexander, Hattie, 229
alkali, DNA extraction with, 135
Alloway, J. Lionel, 82-85, 91, 92,

   110-11
Alpha Omega Alpha, 36
Amateur Research Chemists, 26
American Association for the Advance-
  ment of Science, 200
American Chemical Society, 203, 216
American Scientist, 221
amino acids, 144
ammonium sulfate, 179-80
amyl alcohol, 150
Andrus, E. Cowles, 30-31
Annual Review of Biochemistry, 28
Annual Reuiew of Genetics, 235
antibiotics, value of, 40
antibodies, 59-60, 185, 215
pneumococeal virulence and, 64
antigens, 59
antisera, type-specific pneumococcal,
   98
arthritis, 177-78
asbestos, 137

ascorbic acid, 184
Austrian, Robert, 230
Avery, Oswald Theodore (Fess), 72,
  78, 121, 147, 204
awards to, 78, 201
cautiousness of, 155, 163
competition of, 99
correspondence of, 156-59, 201
discxxuses by, 122-23
Dochez's friendship with, 62
health of, 86-87, 194
laboratory facilities of, 117-20
laboratory technique of, 125-26, 128
McCarty's relationship with, 49-50,
   194-96
pneumococcal serotypes research of,
   62-63
retirement of, 155-59, 182, 194
Rockefeller Institute's appointment
  of, 61-62
seminars by, 169-70, 200-201
specific soluble substance research
  of, 63-71
as teacher, 122-23
Avery, Roy, 155-59, 194
Avogadro's number, 172

Bacterial Cell, The (Dubos), 196
bacterial cultures, for transforming

  extracts, 103-4, 120, 126, 130, 151
Bacteriological Reviews, 206
bacteriology, genetics vs., 214-15


246

Ino!ex

base-pairing, in DNA, 223
beef heart infusion broth, 54, 105
benzene, leukopenic effect of, 46, 123
Bergmann, Max, 16364
Berkefeld filter, 83, 86
Bial reaction, 107-B
bile salts, solubility of pneumococci in,
  58, 84, 101, 110

"Biochemical Studies of Environmental
  Factors Essential in Transforma-
tion of Pneumococcal Types"
(McCarty, Taylor and Avery),
  210-11
Blake, Francis G., 47
Board of Scientific Directors, annual
  reports to, 111, 142, 152-53, 231
Boivin, Andre, 217-18, 229
bone phosphatase, 94
Bonner, David, 222

calcium, DNA precipitation by, 107-8,
  112, 114, 189

cancer, DNA and, 202
capsular swelling test, 64
Carnegie Institution, 200
Carrel, Alexis, 69, 174
C carbohydrate, 157
centrifuges, 103-5, 119, 126-27, 149
see also ultracentrifuges
Century of DNA: A History of the Dis-
covey of the Structure and Func-
tion of the Genetic Material, A
  (Portugal and Cohen), 231
Chargaff, Erwin, 222, 227, 229
Chase, M., 219, 223-24
"Chemical Nature and Biological Speci-
ficity of the Substance Inducing
  Transformation of Pneumococcal
  Types" (McCarty), 205-6
chest fluids, 85, 106, 129, 152, 192,
   199

Cranefield, Paul, 168
C-reactive protein, 99, 100, 192
cream separators, 103-4
Crick, Francis, 223, 227, 229, 231
cubic centimeters, 56
Curnen, Ed, 120, 131
cysteine, 184

Dale, Sir Henry, 221
Dawson, Martin H., 79-82, 83, 90, 93,
  199

de Kruif, Paul, 20, 38
Delbrtick, Max, 156-57
deoxycholate, 84, 110-11, 127, 132,
  146, 188

chloroform extraction, of proteins, see
  Sevag procedure
chromatography, 164
chromosin, 135, 148
chromosomes, 134, 144, 158
chymotrypsin, 157, 178
citrate, 181, 186, 187-88
Clark, W. Mansfield, 34
Cohen, Jack S., 231
Cohn, Alfred E., 135

deoxyribonuclease (DNase):
activation of. 175. 181. 186
antibodies against, 185
assay for, 176
crystallization of, 181, 185, 191
need for, 173-74
purification of, 180-83, 185
in transformation systems, 197-98
transforming principle affected by,
   181

deoxyribonucleic acid (DNA), 51
alcohol precipitation of, 13637, 146,
  150-51, 188-89
biological specificity of, 163, 187,
  215

calcium precipitation of, 107-8, 112,
114, 189

cancer and, 202

Cold Spring Harbor Symposia, 210-12,
  217-18, 222, 234
Cole, Rufus, 59, 60-62, 70, 72, 81, 89,
  97

colony-forming units, 57
Columbia University, 135, 170, 196,
  200, 222

Columbia University College of Physi-
cians and Surgeons, 79, 80
Commission on Pneumonia of the
Army Epidemiological Board, 162
competence, of pneumococcus:
population size and, 198-99
serum factor and, 199
Cooper, James Fenimore, 21
Copley Medal, 78, 221
C polysaccharide, DNA contamination
  by, 188-89


Index

247

in chromosin, 135
diphenylamine test for, 108-9, 112,
124

enzymatic degradation of, 143, 158
evidence against transforming princi-
ple as, 216-19

evidence for transforming principle
as, 138-39, 146-47, 154-55, 187,
190, 216-17

as genetic material, 143-46, 154-55,
157, 206, 211, 218, 219, 221, 223,
224

natural distribution of, 109, 134
pneumococcal uptake of, 197-99
purification of, 136, 146
structural diversity of, 143-46, 159,
163, 215, 222

structure of, 143-44, 223
in transforming extracts, 108-9, 112,
133, 134

see also deoxyribonucleic acid; pneu-
  mococcal; transforming principle
deoxyribonucleic acid (DNA), pneumo-
  coccal:

C polysaccharide contamination of,
188-89

molecular weight of, 158, 160, 172
protein contamination of, 173, 217
purification of, 146-47, 150-53,
  160-61, 188-89
storage of, 153
transforming activity of, 158, 160
yield of, 152, 188
see also deoxyribonucleic acid; trans-
forming principle
deoxyribose sugar, 144
desoxyribonucleic acid, 109, 10%
see also deoxyribonucleic acid
dialysis, 108, 132, 146, 152, 188
diphenylamine, as test for DNA, 10%
  9, 112, 124

disaccharides, 66
"Discovery of DNA, The" (Mirsky),
  219-20
DNA, see deoxyribonucleic acid
DNase, see deoxyribonuclease
Dochez, Alphonse R., 72
Avery's friendship with, 62
pneumococcus research of, 60-61,
  62-65
Double Helix, The (Watson), 223
Dramamine, 225-26

Dubos, Rend, 69-71, 91, 128, 132,
  157, 174, 195, 196, 234
Dumas, Alexandre (p&e), 21

Eighth Day of Creation, The (Judson),
  2.31

electrophoresis, 149, 160, 217
Eli Lilly Award in Bacteriology and
  Immunology, 204-6

         I_
encapsulated (S) pneumococci:
production from unencapsulated (R)

forms, 74-75

production of unencapsulated (R)
  forms from, 73-74, SO
S and R forms and, 64-65
virulence and, 54, 63-64
Enzyme Club (New York City), 200
esterases, 112
"Experimental Induction of Specific
  and Heritable Changes in Pneu-
mococcal Cells" (Avery), 200

First International Congress for Virol-

ogy, 81-82

Flexner, Simon, 62, 70, 86
Flexner report, 20
fluoride, 102, 112-13, 188
Fraenkel-Conrat, Heinz, 204
Francis, Thomas, Jr., 81-82
freeze-drying:

of pneumococcal DNA, 153
of transforming extracts, 127
freeze-thawing, of pneumococcus, 80,
  82

"Function and Design" (Leathes), 145

Gasser, Herbert, 207, 209
Gay, Leslie N., 225-26
genes, DNA and, 206, 218, 221, 223
genetic material, proteins vs. nucleic

  acids as, 143-46, 222
genetics, bacteriology vs., 214-15
glucose, 130
glycogen, 116
Goebel, Wafther, 67
Gold Medal of the New York Academy
  of Medicine, 201
Goodpasture, Earnest, 159
Gortner, R. A., 145
Grave's disease. 86-87
Griffith, Fred, 71, 81, SO
life of, 78


248

Znakx

GrifIith, Fred (continued)
transformation research by, 72-77,
  190, 228

Hammarsten, E., 137
Harriet Lane Home for Invalid Chil-
  dren, 40-44, 225
Harvard Club, 182
Harvard University, 221
heart disease, rheumatic fever and, 208
heat killing, of pneumococcus, 75-76,
  110, 127, 128, 150, 189
Heidelberger, Michael, 65-67, 80, 170
Hellerman, Leslie, 34-35
Hemophilus influenzae, 229
heparin, 35
Hershey, A. D., 219, 223-24
histones, 136
Hoagland Laboratory, 61, 125
Hades, Horace, 42
Holman, Emile F., 30
Horsfall, Frank L., Jr., 117, 194-95,
  204

appointments of, 97, 113-14, 131,
170, 207

research of, 140, 142
Hotchkiss, Rollin, 156, 210, 234
research of, 95-96, 191, 209, 227,
  230

Hutchinson, G. Evelyn, 221
hyperthyroidism, 86-87

"Identification of the Pneumococcal
  Transforming Substance as DNA:
  A Retrospective Look at How We
Got There, The" (McCarty), 234-
  35

Illinois University College of Medicine,
  224

International Cancer Research Founda-
  tion, 201

"Isolation and Purification of Desoxyri-
  bonuclease and Its Action on the
  Transforming Substance of Pneu-
mococcus" (McCarty), 183-84
"It Ain't Necessarily So" (Gershwin),
  182

Jacobs, Walter, 65
Jane Coffin Childs Memorial Fund for
  Medical Research, 201

Johns Hopkins Medical Society, 225-
  26

Johns Hopkins University, 225
McCarty's education at, 32-44
McCarty's preparations for, 24-25,
  27, 30-31

McCarty's research at, 34-35, 42
Jonkowske, Jacqueline, 177
journal of Biological Chemistry, The,
  30, 35

Journal of Experimental Medicine, 79,
  82. 97. 165. 167. 169. 171. 184.
186, 200, 2i4, 234
journal of General Physiology, 184-86,
   191

Journal of Hygiene, 76-77, 79
Journal of Pediatrics, 42
Judson, Horace F., 231

Kimmer, Fred, 126, 128, 130, 176, 178
Kjeldahl method, 29
Klassische und molekulare Genetik
  (Bresch), 156

Kunitz, Moses, 108, 174, 178-82, 184,
  191

laboratory equipment, 103-5, 117-20,
  125-27, 138

Lancefield, Rebecca, 195
Landsteiner, Karl, 195
La Rosa, William, 174-75, 176
Leathes, J. B., 145, 168
Lederberg, Joshua, 234
leukopenia, 46, 123
Levene, P. A., 135, 143, 233
Life of Pasteur, The (Radot), 20, 38
lipids, 157
liver, 136
Longcope, Warfield T., 39
Luck, James Murray, 28, 30

MacCallum, William G., 38
McCarty, Maclyn:
Avery's relationship with, 194-96
awards to, 204-6
childhood hobbies of, 26
childhood medical interests of, 20
children of, 42
clinical training of, 39-42
early research of, 28-30, 34-35, 38,
  41-42
health of, 177-78


Index

249

at Johns Hopkins University, 32-44
MacLeod's opinion of, 232
marriage of, 37
Naval service of, 131, 140-42
parents of, 21, 22
pre-college education of, 21-25, 26
publications of, 164-71, 184-87,
190, 213-14

Rockefeller Institute appointments
of, 48-49, 113, 117, 207-10
seminars by, 183, 200, 201-6, 211-
12, 224-25

at Stanford University, 27-30
MacCarty, William Carpenter, 37-38
McGill University, 97
MacLeod, Colin Munro, 48-50, 126,
  154, 210, 220, 230, 231
competition of, 99
early research of, 89-92
education of, 89
publications of, 96-97, 100, 112,
  164-71

sulfonamide research of, 98, 100, 175
World War II activities of. 162

MacLeod, Shosho, 195
magnesium, 175, 181, 186
manganese, 181, 186
Mayo Clinic, 37-38
medical fraternities, 33
Microbe Hunters (de Kruif), 20, 38
Miescher, F., 220
Mirick, Dick, 120, 131
Mirskv, Alfred E.:

Avery and McCarty's collaboration
  with, 135-37, 143, 146-49, 165
Avery and McCarty's disagreement
  with, 170-71, 187, 214, 215-20
monosaccharides, 66
mouse protection experiments, 60, 62,
  72-73

Mueller, J. Howard, 221
myosin, 135

Nadeje, Teddy, 126-27, 176
National Academy of Sciences, 123
National Research Council Fellow-
  ships, 47-48, 113, 196
Neufeld, Fred, 72, 78, 94
pneumococcus research of, 58, 60,
  64, 77-78

Neurospora, 222, 234
New Yorker, 2.31

New York University, 45-48, 113-14
Nobel Prize, 162, 167, 202
Avery and, 218-19
Nobel: The Man and His Prizes (Nobel

  Foundation), 218-19, 223
Noeuchi, Hidevo. 126
Noythrup, John, 94, 162, 178, 180,
  181, 184
nucleic acids:

natural distribution of, 109
structure of, 113
see also deoxyribonucleic acid; ribo-
nucleic acid

nucleoproteins, 135-36, 148
nucleotides, 143-44

Olby, Robert, 230-31, 232-33
oxidation, transforming principle

affected by, 184

p-aminobenzoic acid, sulfapyridine

  inhibition by, 45-46
pancreas, 94, 108, 174, 175, 178, 180
pancreatin, 176, 178
Park. Edwards A.. 41, 42. 43, 47, 49
Pasteur, Louis, 52
Path to the Double Helix. The (Olbv)

230-31, 232 ' ' "'
Paul Erlich Gold Medal, 78
Pearl Harbor, attack on, 131
pediatrics, McCarty's interest in, 38-
  39

penicillin resistance, 2.30
pepsin, 162
peptone, 54
peroxides, 184
phagocytosis, pneumococcus virulence
  and, 63-64
phosphodiesters, 113
"Physiological Aspects of Genetics"
  (Wright), 221
plasmosin, 135
pneumococcal deoxyribonucleic acid,
  see deoxyribonucleic acid, pneu-
  mococcal
pneumococcal pneumonia, see pneu-
  monia, pneumococcal
pneumococcal serotypes:
discovery of, 60
in pneumonia, 72-73
soluble specific substances of, 62-63,
  6.568


250

pneumococcal serotypes (continued)
transformation of, see transformation
  of pneumococcal serotypes
virulence and, 142
pneumococcus:
bile salt solubility of, 58, 84, 101,
   110

competence of, 198-99
DNA uptake by, 197-99
encapsulation of, 54, 63-64, 142
heat killing of, 75-76, 110, 127, 128,
150, 189

laboratory growth of, 51-57, 120,
126, 130, 151

physical properties of, 52-55
in pneumonia, 52, 61
S and R forms of, 64-65, 73-77, 166
serotypes of, see pneumococcal sero-
types

suicidal tendencies of, 58
virulence in mice of, 58-59, 63-64,
142

see also encapsulated (S) pneumo-
  cocci
pneumonia, pneumococcal:
epidemiology of, 51-52
multiple serotypes in, 72-73
sulfapyridine treatment of, 41-42
pneumonia, viral, 114, 141
Polhster, A. W., 135-36, 148, 216
polysaccharides, 66, 116
serological specificity of, 68, 174
specific soluble substances as, 67
in transforming extracts, 108, 115,
   130

population size, competence and, 198-
  99

Portugal, Franklin H., 231
"Prematurity and Uniqueness in Scien-
tific Discovery" (Stent), 227
proteins, 135

ammonium sulfate precipitation of,
179-80

DNA contamination by, 173, 217
as genetic material, 144, 222
structural diversity of, 144, 215
structure of, 144
in transforming extracts, 94, 129,

147, 157

Index

Radot, Rene V., 20, 38
Red Seal Records, 122
reducing agents, 184
"Reminiscences of the Early Days of
Transformation" (McCarty), 235
"Reversible Inactivation of the Sub-
stance Inducing Transformation of
  Pneumococcal Types" (McCarty),
  184
rhamnose, 67
rheumatic fever, 207-B
ribonuclease (RNase), 175
crystallization of, 108, 174, 178
in purification methods, 108, 132,
  188

transforming principle affected by,
  112, 157
ribonucleic acid (RNA), 107
calcium precipitation of, 107
natural distribution of, 109
in transforming extracts, 107-8, 157,
  188

ribose sugar, 144
Ris, Hans, 219, 220
transforming principle separation

Rivers, Thomas M., 48, 97, 113-14,
  from, 131, 139

  131, 140-41, 207, 209
Robert Koch Institute. 78
Rockefeller Foundation, 113-14
Rockefeller Institute for Medical
  Research. 37. 43. 123. 163. 167.
207
early pneumococcus research at, 59,
  60-61, 79-84

Horsfall's appointments to, 97, 113-
  14, 131, 170, 207
hospital of, 119
McCarty's appointments to, 48-49,
  113, 117, 207-10
Rogers, Edward S., 87-88, 92, 128
Rothen, Alexandre, 138-39, 160
rough (R) pneumococci, 64-65
Rous, Peyton, 167
Royal Society, 78, 221
R36 strain of pneumococcus, 197
derivation of, 90
mutants of, 105

Ryan, F. J., 234

properties of, 91
use of, 91, 106

Quellung phenomenon, 64


Z?d?X

251

salting out, of proteins, 179
Schneider, Howard A., 170
Schultz, Jack 144-45
Science, 145, 191, 200-201
Schtijc American, 219-20, 227
scientific notation, 56-57
scientific skepticism, 35, 68, 73, 142,
  162

serial dilutions, 57
serotypes, see pneumoeoccal serotypes
serum albumin, 96, 194, 212
serum factor, 211, 212
competence and, 199
transformation dependence on, 95-
  96

Sevag, M. C., 94

Sevag procedure, 94, 107, 127, 132,
  136, 150-51, 157, 188
Shakespeare, William, 21
Sharples centrifuge, 105, 126-27, 149
Shedlovsky, Theodore, 160
Sia, Richard, 79-81, 82, 93, 199
"Significance of Pneumococcal Types,
  The" (Griffith). 76-77

smooth (S) pneumoeci, see encapsu-
  lated (S) pneumococci
Society of American Bacteriologists, 205
sodium citrate, see citrate
sodium deoxycholate, see deoxycholate
sodium fluoride, see fluoride
"Some Aspects of the Chemistry of
  Chromosomes" (Mirsky), 216
Specificity of Serological Reactions,
  The (Landsteiner), 195-96
specific soluble substance (SSS):
chemical nature of, 65-68
discovery of, 63

enzyme degradative for, 70-71
properties of, 115
transformation and, 115-16, 124,
  128-29, 173

in transforming extracts, 91, 115
transforming principle separation
from. 115. 131. 139

spleen, 136
Stanford University, McCarty's educa-

tion at, 27-30

Stanley, Wendell, 162, 203, 216
Stent, Gunther, 227, 228, 231
Stemberg, George M., 52
SIII enzyme, 91, 128, 157, 174

assay for, 128-29

availability of, 129-30
discovery of, 70-71
in purification methods, 132, 150,
188

transformation affected by, 129
Stillman, Ernest, 182
strep&o& infections, McCarty's
  interest in, 208

Streptococcus pneumoniue, 52
see also pneumococcus
streptomycin resistance, 230
"Studies on Capsular Synthesis by
  Pneumococci" (Avery and Mac-
  Leod), 112

"Studies on the Chemical Nature of
  the Substance Inducing Transfor-
mation of Pneumoeoccal Types. I"
  (Avery, MacLeod and McCarty):
acceptance of, 221-24
citations of, 214
influence on other researchers of,

  222-24, 227, 229-30, 234
limited audience for, 213-14
"prematurity" of, 227-29, 231
preparation of, 164-67
revision of, 167-68
seminar on, 169-70
skepticism about, 215-19
"Studies on the Chemical Nature of

  the Substance Inducing Transfbr-
  mation of Pneumococcal Types. II"
  (McCarty and Avery), 186-87
citations of, 214
"Studies on the Chemical Nature of
  the Substance Inducing Transfor-
  mation of Pneumococcal Types. III"
(McCarty and Avery), 190
citations of, 214
sucrose, 66
sulfanilamide, 40, 41, 45-46
sulfapyridine, 41
inhibition of, 45-46
leukopenia and, 46, 123
sulfonamides, 120
as anti-pneumonia drugs, 98
McCarty's research on, 45-47
MacLeod's research on, 98, 100, 175
medical impact of, 40
sulfuric acid, 180
Swift, Homer F., 207


252

Index

Tarkington, Booth, 21
Taylor, Harriett E., 196, 198, 211,
  229-30

tetranucleotide theory, 144
thymonucleotides, see deoxyribonucleic
  acid

thymo-polynucleotidase, 185
thymus, as source of DNA, 135, 136
Tillett, William S., 44-47, 98, 113
tobacco mosaic virus, 162
transformation of pneumococcal sero-
  types, 51

by cell-free extracts, 82-85
clinical applications of, 93
confirmation of, 77-78, 79
discovery of, 72-77
early theories of, 77, 81, 92, 134
effect of DNase on, 197-98
frequency of, 199-200
in vitro, 79-82, 106
serum factor dependence of, 95-96,
199

variability of, 83, 85, 95, 106, 110-
  11, 114, 124, 128, 152
viruses and, 206
transforming extracts:
bacterial cultures for, 103-4, 120,
  126, 130, 151

C carbohydrate in, 157
DNA in, 108-9, 112, 133, 134, 147,
157

enzyme studies on, 108, 112-13,
114, 143

extraction methods for, 101, 110-11,
127, 131-32

fractionation of, 84, 107-8, 112,
  114-15, 124, 127, 132-33, 135,
   158
lipids in, 157
polysaccharides in, 91, 108, 115, 130
potency of, 111, 130, 147, 149
proteins in, 94, 129, 147, 157
RNA in, 107-8, 157, 188
transforming principle (TP), 85, 92
arguments against DNA as, 216-19
assays for, 106-7, 140, 160
autolytic enzyme destruction of, 92
DNA as, 136, 138-39, 146-47, 154-

55, 187, 190, 217
effect of ascorbic acid on, 184
effect of oxidation on, 184

elimination of polysaccharide as, 129,
134-35, 154

enzyme sensitivities of, 94-95, 108,
112-14, 143, 158, 181
physical properties of, 138-39, 158
RNA separation from, 131, 139
specific activity of, 217
specific soluble substance separation
from, 115, 131, 139
ultraviolet-light sensitivity of, 94
viruses and, 203-4
see also deoxyribonucleic acid;
deoxyribonucleic acid, pneumococ-
cal

trypsin, 94, 157, 178
Twain, Mark, 21
type III polysaccharide, see specific

soluble substance

ultracentrifuges. 138-39, 149, 160, 217
ultraviolet light, 94
United States Naval Reserves, Rocke-

feller Hospital unit of, 131

Vanderbilt University, 155
Van Slyke, Donald D., 65, 163
Vendrely, C. and R., 219
virulence, pneumococcal, 58-59

encapsulation and, 54, 63-64, 74-75
viruses:

nucleic acids of, 203-4, 224
transformation and, 159, 206

viscosimeters, 176, 177
vitamin C (ascorbic acid), 184

Warburg, Otto, 224-25
Wassermann tubes, 106, 120
Watson, James D., 223, 227, 229, 231
Watson, Robert F., 177
Webster, Leslie T., 43, 49
"When Does Information Become

Knowledge?" (Wyatt), 228
White, Ben, 125
Wright, Sewall, 221
Wyatt, H. V., 200, 228-29

Yale University, 221

Zeitscht-ift fiir physiologisches Chemie,
  185
Zepp, Helen, 41