Krebs_1970_History of TCA cycle

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The History of the Tricarboxylic Acid Cycle 
H. A. Krebs
Perspectives in Biology and Medicine, Volume 14, Number 1, Autumn
1970, pp. 154-172 (Article)
Published by Johns Hopkins University Press
DOI:
For additional information about this article
https://doi.org/10.1353/pbm.1970.0001
https://muse.jhu.edu/article/405199/summary
[200.137.65.107] Project MUSE (2024-09-19 20:15 GMT) UFES-Universidade Federal do Esp�rito Santo
THE HISTORY OF THE TRICARBOXYLIC ACID CYCLE*
H. A. KREBS]
I have often been asked how the work on the tricarboxylic acid cycle
arose and developed. Was the concept perhaps due to a sudden inspiration
and vision? It was of course nothing of the kind, but a very slow evolu-
tionary process, extending over some five years beginning (as far as I am
involved) in 1932. At that time the problem of the intermediary stages
of the pathways of anaerobic energy metabolism—glycolysis and alcohol
fermentation—had been established in outline by 1932, but knowledge of
the pathways of oxidation was very fragmentary. What was known can
easily be summarized. There was the principle (though not the enzymic
mechanism) of the ^-oxidation of fatty acids. There was the concept of
oxidative deamination of amino acids and of the decarboxylation of the
resulting a-ketonic acids. A survey ofthe knowledge ofintermediary path-
ways of oxidation in the early 1930s is to be found in Oppenheimer [1].
The only hypothesis outlining a pathway of the intermediary stages of
carbohydrate oxidation was that put forward by Thunberg [2] and sup-
ported by Knoop [3] and Wieland [4]. It assumed that two molecules of
acetate—formed from lactate via pyruvate or by /3-oxidation of fatty
acids—condensed to form succinate which was taken to undergo oxida-
tion via fùmarate, malate, oxaloacetate and pyruvate to form one mole-
cule of acetate:
coo-
coo-coo-coo-
CH
-2H CH2 -2H CH +H2O CHOH
+ —»- ? —>- Il—>- I
CH3
CH2CHCH2
coo-coo-coo-
coo-
2 acetatesuccinatefumaratemalate
* The second Verne R. MasonMemorial Lecture, University ofMiami, January ???a. Permission
to publish has been granted by the Howard Hughes Medical Institute. Publication costs were kindly
contributed to Perspectives by Miles Laboratories, inc.
t Metabolic Research Laboratory, Nuffield Department ofClinical Medicine, Radcliffe Infirmary,
Oxford, England.
I54 H. A. Krebs · Tricarboxylic Acid Cycle
Perspectives in Biology and Medicine · Autumn 1970
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COO-COO-CO2
-2H COCO+H2O - 2H +
---------y ? ---------»- ? ------------------------->-
CH2CH3COO-
COO-+CO2CH3
oxaloacetatepyruvateacetate
This scheme was based on the oxidizability of some of the postulated in-
termediates, but there was no evidence supporting the key condensation
reaction which, as we now know, does not occur in living cells. This
weakness, and the general ignorance ofthe pathway ofoxidation of food-
stuffs, were fully recognized.
In 1932, whilst working as an assistant physician in the Department of
Internal Medicine at Freiburg University, I carried out many experiments,
mainly on kidney and liver slices, on the oxidizability of substances which
might be expected to be intermediates. The idea behind this work was
that intermediates must be identifiable on account oftheir ready oxidation.
There seemed to be no metabolic links between the oxidizability of the
dicarboxylic acids and the oxidation of foodstuffs—especially ofcarbohy-
drate and fat. Therefore we tested a large number of other substances
which paper chemistry suggested as intermediates. Some of these experi-
ments were done in collaboration with Dr. P. Ostern, a visitor from the
laboratory of J. Parnas in Lwow, and the only published paper from this
work is a manometric method for the determination of oxaloacetic acid
by Ostern [5], a method widely used until it was superseded by more
sensitive and more specific spectrophotometric methods. The striking
impression which these experiments left in my mind was the fact that
citrate, succinate, fumarate, malate, and acetate were very readily oxidized
in various tissues, with the formation ofbicarbonate and CO2 (see table i1),
and that the rates of oxidation of these substances were compatible with
the view that they played a major part in tissue respiration; but this had
already been shown much earlier—in 191 1—by Batelli and Stern [6].
1 This unpublished experiment, carried out in 1933, illustrates the increased oxygen consumption
and the formation of bicarbonate in kidney cortex after addition of the salts ofvarious organic acids.
Bicarbonate formation indicates complete combustion. Less bicarbonate was formed than was ex-
pected from the O3 uptake required for complete oxidation because intermediates accumulated, e.g.,
fumarate and malate when succinate was the substrate. Slices were incubated in Warburg manometers
in a saline medium containing initially 2 raM bicarbonate. After 60 minutes' incubation, the slices
were removed and the bicarbonate content of the medium was measured manometrically.
I55
After my enforced emigration from Germany I continued experiments
in this field in Cambridge between 1933 and 1935, though my main re-
search during that time was on other topics—the oxidation ofamino acids,
the properties ofD-amino acid oxidase, and the biosynthesis of glutamine
in animal tissues [7-9]. The problem of the intermediary stages of respira-
tion remained in the forefront of my mind as one of the big unsolved
problems of biochemistry, and I often pondered about new experimental
approaches.
TABLE 1
Oxidation of and Bicarbonate Formation
from Organic Acids in Guinea Pig
Kidney Cortex Slices
Substrate
Added
None
Acetate
Succinate
Fumarate
Malate
Pyruvate
O2 Uptake
(/jmole/g dry wt/hr)
670
1340
1520
1290
1340
1070
Bicarbonate
Formation
(Mmole/g dry wt/hr)
0
393
555
705
756
318
The Work of Szent-Györgyi
In 1935, Szent-Györgyi began to publish a series of important papers
[10, 11] on the respiration of suspensions ofminced pigeon-breast muscle.
Being a flight muscle requiring much energy, the oxidizing capacity of
this tissue is exceptionally high. This high activity was important because
it facilitated the measurement ofmetabolic changes. Szent-Györgyi studied
in particular the metabolic behavior of the C4-dicarboxylic acids and his
main finding was a catalytic acceleration of respiration by succinate, fuma-
rate, and malate. Small amounts of these substances caused increases which
were much greater than expected for the complete oxidation of the added
material. His interpretation of the effect, however, was inadequate. It was
based on his correct observation that oxaloacetate is very readily reduced
to malate, even aerobically, and he suggested that the malate-oxaloacetate
system might act as one ofthe hydrogen carriers between the fuel ofrespi-
ration and molecular oxygen; that the hydrogen atoms of the substrate
were transferred to oxaloacetate and thence to O2. At that time, it must
156 H. A. Krebs · Tricarboxylic Acid Cycle
Perspectives in Biology and Medicine · Autumn 1970
be remembered, information on electron transport from substrate to O2
was very incomplete. The precise roles of the pyridine nucleotides, flavo-
proteins, and cytochromes were not yet clear. Szent-Györgyi believed
that the malate-oxaloacetate system might be similar to the action of
these hydrogen carriers:
coo-coo-
I I
CHOH OTT CO— zxl
CH2 +2H CH2
COO"coo-
malateoxaloacetate
He held the view that the functions ofmalate and oxaloacetate were not
to serve as a fuel, but to serve as catalysts; as hydrogen carriers between
foodstuff and cytochrome. He did not consider malate and oxaloacetate
as intermediates in the oxidation of carbohydrate; in fact he was not at
all concerned with intermediary metabolism, but solely with hydrogen
transport. His concept failed to offer an adequate explanationof the effect
ofmalonate which was known to inhibit cell respiration and, at low con-
centrations, to be a specific inhibitor of succinic dehydrogenase. This
meant that succinic dehydrogenase must play a key role in respiration and
any scheme of respiration must therefore provide a key place for succinic
dehydrogenase. Szent-Györgyi's concept did not do this, but I must em-
phasize that his papers were important contributions to biochemical
thought and technique.
The Work ofMartius and Knoop
A further milestone was the report by Martius and Knoop [12, 13], in
March 1937, of the discovery of the biological pathway of oxidation of
citrate. My own efforts in solving this problem (never published) were
based on the idea that acetone dicarboxylic acid ( /3-oxoglutarate) and
acetoacetate might be intermediates; they came to naught. Martius and
Knoop showed that citrate is rearranged, via cis-aconitate, to isocitrate
and then dehydrogenated to a-oxoglutarate, which was already known
to undergo dehydrogenation to succinate:
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coo-
c/0H
I ^CH2- COO-
CH2
coo-coo-
I I
-H2O C-CH2-COO- +H2O HC-CH2-COO-
------->- I!-------* I
COO-
citrate
CH
I
coo-
cis-aconitate
CHOH
I
coo-
isocitrate
coo-
-2H HC- CH2- COO-
CO2
+ H2C- CH2- COO-
CO
I
coo-
oxalosuccinate
H2C-CH2-COO- +H2O - 2H
CO
coo-
a-oxoglutarate
coo-
+ CO2
succinate
This work thus linked the oxidation ofcitrate with that of succinate, and
immediately helped me to interpret an observation I had made just before
the paper ofMartius and Knoop appeared, that not only fumarate, malate,
and succinate, but also citrate stimulated catalytically the respiration of
minced pigeon-breast muscle.
The Crucial Experiments
The main facts relevant to the discovery of the tricarboxylic acid cycle
known early in 1937 were, briefly summarized: (1) there is a pathway of
degradation ofcitrate leading to the formation, via the dicarboxylic acids,
of pyruvate; (2) the rate of oxidation of the di- and tricarboxylic acids
in some animal tissues is very high and comparable to the rate ofcell respi-
ration; (3) under suitable conditions, cell respiration can be stimulated
catalytically by the di- or tricarboxylic acids; (4) cell respiration is in-
hibited by malonate. It was this information which led to the formulation
of the idea that citrate might arise from oxaloacetate and be a derivative
ofcarbohydrate. Martius and Knoop [14] had already shown in 1936 that
a nonenzymic formation ofcitrate occurs when oxaloacetate and pyruvate
are treated with hydrogen peroxide in an alkaline medium. So I set to
work to test whether oxaloacetate and pyruvate formed citrate enzymical-
Iy. The answer proved to be in the affirmative; but there remained quan-
titative requirements to be satisfied; it had to be shown that the rates were
rapid enough. It also had to be shown that the conversion ofcitrate to a-
158 H. A. Krebs · Tricarboxylic Acid Cycle
Perspectives in Biology and Medicine · Autumn 1970
oxoglutarate occurred at sufficient speed in animal tissues generally.
Martius and Knoop had demonstrated the reaction qualitatively in liver
preparations, and liver is very special tissue. The tests for the reactions in
muscle were positive and quantitatively adequate. Sufficient evidence was
thus available in support ofthe cyclic concept as shown in figure ? [14-16].
Carbohydrate
I
triose-P or lactate
pyruvate (?)
oxaloacetate
/
malate
fumarate
\
citrate
\
cis-aconitate
isocitrate
./
a-oxoglutarate
Fig. i
Triosephosphate or pyruvate were formulated as a source of the two addi-
tional carbon atoms required to form citrate from oxaloacetate, because
carbohydrate was thought to be the main fuel of respiration in muscle
tissue. In 1937 the time was not ripe for solving the problem of the precise
mechanism of citrate synthesis.
The scheme established a link between the known reactions of the
di- and tricarboxylic acids on the one hand, and carbohydrate degrada-
tion on the other. It correlated many facts concerning oxidative reactions
and gave a coherent picture of the pathway of oxidation ofcarbohydrate.
Like almost every new concept, the idea of the tricarboxylic acid cycle
159
was severely criticized by some biochemists [17-19], but the majority soon
accepted it as a working hypothesis. The scheme was primarily drawn up
with reference to the oxidation of carbohydrate and of those amino acids
which were known to provide intermediates related to those derived from
carbohydrate. There was no evidence at that stage supporting the view
that the carbon skeleton offatty acid could also enter the cycle, but it was
soon recognized that the cycle also provides an important pathway for
the synthesis of cell constituents [20].
Subsequent Elaboration of the Tricarboxylic Acid Cycle
The basic scheme of 1937 has stood the test oftime. There was evidently
a major gap concerning the mechanism of citrate formation from oxalo-
acetate and pyruvate. The solution of this problem had to await the dis-
covery of coenzyme A by Lipmann ten years later [21-23]. In the years
following this, Ochoa [24-26] and Lynen [27, 28] established acetyl co-
enzyme A as the intermediate which reacts with oxaloacetate to form
citrate:
pyruvate ----->- acetyl coenzyme A -, dtrate CqA _
oxaloacetate —'
Coenzyme A was also found to participate in the formation of succinate
from a-oxoglutarate with succinyl coenzyme A as intermediate [29, 30].
These elaborations are included in the extended current version of the
cycle as shown in figure 2.
From 1943 onward it also became clear—thanks mainly to the use of
isotopie carbon—that not only carbohydrate but also fatty acids and ketone
bodies can supply carbon atoms for the synthesis of citrate [31-34], and
in the early 1950s the schools ofLynen and Ochoa [35, 36] demonstrated
the formation of acetyl coenzyme A from fatty acids and ketone bodies.
It was this work which established the tricarboxylic acid cycle as the ter-
minal pathway of oxidation of all major foodstuffs. Although originally
it was put forward to account for the oxidative processes ofmuscle tissue,
it gradually became evident that all respiring animal tissues, as well as
microorganisms and plants, employ the same terminal pathway ofoxida-
tion. The cycle contributes about two thirds ofthe total oxidative processes
in organisms which burn carbohydrate, fat, and amino acids. The
presence of the same metabolic pathways in all forms of life indicates that
160 H. A. Krebs · Tricarboxylic Acid
Perspectives in Biology and Medicine · Autumn 1970
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this mechanism of energy release arose very early in the course of evolu-
tion [37, p. 139].
The Ornithine Cycle of Urea Synthesis
It was of relevance to the development of the tricarboxylic acid cycle
concept that the ornithine cycle ofurea formation, which I had discovered
in 1932 [38], provided a pattern of metabolic organization, and I should
therefore explain how the concept of the ornithine cycle arose. When I
acetyl-coenzyme A
¦ oxaloacetate
V2H.
L-malate
H2O
fumarate
2H ^f
succinate
GTP + coenzyme A-*""'\_-' GDP + orthophosphate
succinyl-coenzyme A
2H + CO2 coenzyme A
coenzyme A
citrate
cis-acomtate
isocitrate
oxalosuccinate
a-ketoglutarate
Fig. 2
set out to study the mechanism ofurea formation, I had no preconceived
hypothesis. My idea was that the in vitro system of liver slices, incubated
in a saline medium, provided a novel and easy method for measuring ac-
curately the rate of urea synthesis under a variety of conditions. As one
small rat liver supplies numerous samples, it is possible to carry out many
parallel tests. No comparable method had been available before.Many
biochemists and physiologists—including Otto Warburg—were quite sur-
prised to learn that slices are capable of performing synthetic energy-
requiring processes. Up to that time slices had been used solely for the
study ofdegradative reactions—respiration and lactic acid formation. The
161
use of tissue slices which I had learned in Otto Warburg's laboratory, so
it seemed to me, opened up an entirely new kind of approach to many
problems ofmetabolism. I chose the study of the synthesis of urea in the
liver because it appeared to be a relatively simple problem. Retrospectively,
I must say that I was lucky in making this choice. Other problems which
appeared equally simple proved much more difficult.
So together with a medical student, Kurt Henseleit, I measured sys-
tematically the rate ofurea synthesis from various nitrogenous substances
—ammonia, amino acids, various amines, cyanate, pyrimidines [38]. In
one series of experiments we tested whether amino nitrogen could be di-
rectly converted to urea. If this were the case, amino acids might be ex-
pected to form urea more rapidly than does ammonia. Another idea was
the suggestion that one of the nitrogen atoms of urea might come more
or less directly from amino acids and the other from ammonia (an idea
which later work by others proved to be right). We therefore measured
the rate of urea synthesis in the presence of mixtures of ammonium ions
and amino acids. It was in the course of these experiments that we dis-
covered the exceptionally high rates of urea synthesis in the presence of
a combination of ornithine and ammonium ions. The interpretation of
this finding was not at once obvious. It took a full month to find the cor-
rect interpretation. At first we were skeptical about the correctness of the
observation. Was the ornithine perhaps contaminated with arginine? The
answer was "no." Then it occurred to us that the effect of ornithine may
be related to the presence of arginase in the liver, the enzyme which con-
verts arginine into ornithine and urea:
COOH- CH(NH2) - CH2- CH2-CH2-NH ·C^?(arginine)
+ H2O
COOH-CH(NH2)-CH2-CH2-CH2NH2 + CO(NH2)2
(ornithine)(urea)
Arginase, discovered in 1904 by Kossel and Dakin [39, 40], was known
to be present in high activity in the liver of those animals (mammals and
reptiles) which can synthesize urea from ammonia or amino acids [41-44].
The coincidence of the presence of this enzyme and the occurrence of
urea synthesis raised the suspicion of a connection, but for some weeks
162 H. A. Krebs · Tricarboxylic Acid Cycle
Perspectives in Biology and Medicine · Autumn 1970
we were unable to visualize one. The solution of the problem developed
gradually as the ornithine effect was studied in detail. Quantitative tests
showed that ornithine was not a precursor but acted as a catalyst, that is,
it promoted urea formation without being used up. When considering
the mechanism ofcatalytic action, I was guided by the idea that a catalyst
must take part in the reaction and form intermediates. Arginine suggested
itself as the last intermediate of a series and as the immediate precursor
ofurea. This meant that a formation of arginine from ornithine had to be
postulated. Since this would involve the addition of two nitrogen atoms
and one carbon atom, it was further necessary to postulate several inter-
mediates between ornithine and arginine. This line of thought suggested
that citrulline might play a role as an intermediate:
COOH- CH(NH2) - CH2- CH2- CH2-NH- CO · NH2 .
(citrulline)
Fortunately, this substance had just been identified independently by two
biochemists. Wada [45] prepared it from watermelon (citrullus) and
Ackermann [46] isolated it as a product of the bacterial degradation of
arginine. I wrote to both and obtained a few milligrams from each suffi-
cient to do the decisive tests which entirely fulfilled expectations; they
demonstrated the rapid formation of urea in the presence of citrulline
and ammonium salts, in accordance with the scheme:
COOH- CH(NH2) -CH2- CH2- CH2-NH- CO-NH2
(citrulline)
+ NH3
COOH- CH(NH2) -CH2- CH2- CH2-NH- C^!! + H2O
(arginine)
arginase
ornithine + urea
On the basis of these findings it became possible to formulate a cyclic
process ofurea formation from carbon dioxide and ammonia, with citrul-
line and arginine as intermediate stages, as shown in figure 3 .
This work of 1931-32 established the outlines of the pathway by
which urea is synthesized in the liver. The time then did not seem ripe for
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attempts to unravel the enzymic mechanisms involved. The first steps
in that direction were experiments aimed at obtaining a synthesis of
urea in cell-free material, but such experiments were negative in my hands.
Where I had failed Cohen and Hayano [41] succeeded fourteen years
later. By that time much had been learned in general about how to
preserve complex metabolic processes in cell-free homogenates and in
tissue fractions. The development of the techniques for preparing meta-
bolically active cell-free homogenates was a lengthy endeavor in which
many biochemists took part. One of the chief requirements of homoge-
nates turned out to be the need for added cofactors, such as pyridine
ornimme
-?,?
arginine
+CO2
+NH3
+H2O
CO2 + NH3 + ATP—»carbamoyl phosphate
ornithine citrulline
arginine
aspartate
fumarate
arginmo-succinate
164 H. A. Krebs · Tricarboxylic Acid Cycle
Perspectives in Biology and Medicine · Autumn 1970
nucleotides and ATP. The concentration of these factors falls when cells
are disrupted, and their addition restores more or less normal concen-
trations. The work of Cohen and Hayano [47], Ratner and Pappas [48,
49], Ratner and Petrack [50], Jones, Spector, and Lipmann [51], and
of Hall and Cohen [52], carried out between 1946 and 1957, added
carbamoyl phosphate (NH2-COO-PO3H2) and arginino-succinate to
the series of intermediates of the ornithine cycle. Arginino-succinate is
formed from citrulline and aspartate, and reacts further to give arginine
and fumarate according to the following reactions:
COOH-CH(NHa)-CH2-CH2-CH2-NH-CO-NH2 + COO"· CH2- CH(NH2)- COOH
(citrulline) (aspartate)
COOH-CH(NH2)- CH2-CH2-CH2-NH-C = NH
(arginino-succinate)I
NH
I
COO-- CH2- CH- COOH
COOH -CH(NH2) -CH2 -CH2 -CH2- NH- C: NH + COO-- CH: CH- C00~
(arginine)I (fumarate)
NH2
These discoveries led to the present concept of the ornithine cycle shown
in figure 4.
These elaborations not only clarified details of the intermediate stages
but also showed that the second nitrogen atom of urea can be directly
derived from amino nitrogen, without ammonia being an intermediate.
The amino nitrogen of aspartate is formed by transamination from gluta-
mate, and glutamate can obtain its amino group either from transamina-
tion with other amino acids or from ammonia.
The history of the development of the ornithine cycle illustrates the
general experience that at any one time the solution of a problem can be
advanced only to a limited extent. Soon seemingly impenetrable ob-
stacles prevent progress. After a time, however, advances in collateral
fields overcome the barriers—sometimes by circumventing them, some-
times by demolishing, piece by piece, the barriers of ignorance.
165
A General Observation
The history of the tricarboxylic acid cycle makes it obvious that many
biochemists contributed to the development of the concept, each stand-
ing on the shoulders of his predecessors. The names of Szent-Györgyi,
Martius, and Knoop are prominent among those who built up the body
of knowledge from which the concept finally emerged. I cannot help
feeling the aptitude of the remarks of Kekulé, the discoverer of the ring
structure of benzene, on the progress of scientific research [53]. To the
detached onlooker, he pointed out, the comparatively simple story which
represents the finalresult is quite deceptive in respect to the mental
processes which have led to the final picture. If people believed that the
theory of the benzene structure had, complete and finished, sprung like
Pallas Athena from the head of a chemical Zeus, they were mistaken. The
idea had evolved slowly in the course of many years, though it is true
that when one's mind hovers over a problem week after week and year
after year, lightning flashes of vision may occur which help the thought
along. He relates two such sudden visions, one ofwhich occurred to him
on the top of a London bus, but he is quick to emphasize that such visions
and flashes are no more than a very small part of a long-drawn-out mental
process.
The Importance of the Philosophical Outlook
Retrospectively, one may well ask why Martius did not arrive at the
concept of the tricarboxylic acid cycle before me. Why had it not oc-
curred to him that the reactions which he had discovered and studied may
be components of the main energy-yielding process in living matter? My
guess is that this was a matter of scientific outlook—of "philosophical"
attitude. Influenced by his teacher, F. Arndt, Martius regarded himself at
that time (so he once told me) as a "theoretical organic chemist," inter-
ested in reaction mechanisms. The oxidative degradation of citrate was
for him in the first instance a chemical and not a biological problem. He
was therefore satisfied when he had clarified, with great ingenuity, the
pathway citrate —> cis-aconitate —»· isocitrate —»¦ a-oxoglutarate. He did
not concern himself with the question of the physiological role of this
pathway. Therefore he did not explore the quantitative aspects of the
activity of the enzymes of the pathway or compare them with overall
166 H. A. Krebs · Tricarboxylic Acid Cycle
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metabolic rates, nor did he measure the occurrence of the enzymes in
tissues generally.
My outlook was that of a biologist trying to elucidate chemical events
in living cells. I was thus accustomed to correlating chemical reactions
in living matter with the activities of the cell as a whole. By putting to-
gether pieces of information in jigsaw-puzzle manner, and by attempting
to discover missing links, I tried to arrive at a coherent picture ofmetabolic
processes. So my mind was prepared to make use of any piece of informa-
tion which might have a bearing on the intermediary stages of the com-
bustion of foodstuffs. This difference in outlook was, I believe, an impor-
tant factor in determining who first stumbled on the concept of the tri-
carboxylic acid cycle.
Motivation
James Watson, in his recent autobiographical sketch [54], described his
emotional involvement in research as that of the participation in a race.
He sensed a powerful urge to arrive first at the solution ofa big problem—
that of the chemical nature of the gene. It was clear to him that the time
was ripe for the solution of this problem, and he fancied that other scien-
tists, in particular Linus Pauling, were "racing" him.
No doubt most scientists are emotionally involved in the sense ofbeing
deeply committed to their research. I find it difficult, however, to analyze
my own emotional motivation objectively and honestly. I believe that it
was, and still is, very different from that of Watson. On the whole the
sense of competitive "racing" was unimportant to me, because Warburg
had taught me to base my research as far as possible on new, homemade,
research tools. Often, in my case, these were simply new analytical meth-
ods for the quantitative microdetermination of metabolites, or improve-
ments in the manipulation of tissue preparations for metabolic experi-
ments. Warburg himself was one of the greatest pioneers in biochemical
techniques. He developed manometry, spectrophotometry, methods of
enzyme crystallization, and invented the tissue-slice technique. He made
it a rule to start each new attack on a problem with the forging of new
tools.
The use of new methods permits entirely novel approaches, and the
more novel the approach the more unlikely is the coincidence of simul-
taneous attempts elsewhere. When I started to work on the synthesis of
167
urea I certainly felt that it was most unlikely that anybody else at that time
would make the same approach. Watson, on the other hand, not only
relied on methods developed by others—especially those ofmodel build-
ing used by Pauling—but also on the experimental data of others, such as
Wilkins and his team. His therefore was a very special and unusual situa-
tion where the risk ofbeing overtaken was exceptionally large.
As for my motives, a major one is simply an insatiable curiosity and the
thrill one gets from satisfying this curiosity. As Konrad Lorenz has said,
scientific research is in fact equivalent to the playful curiosity of young
animals [55, p. 81]. The thrill of finding the solution to a puzzle is perhaps
related to the pleasure which people derive from solving crossword
puzzles, though manmade puzzles have never interested me when there
are so many natural puzzles awaiting solution. But what is the nature of
the pleasure which the solving of a puzzle provides? Is it the feeling of
satisfaction to have been clever enough? Gratification derived from ex-
pressions of appreciation, either by one's peers or by those who offer
posts, is certainly an inspiring factor.
Another driving force, especially in my earlier days, was my ambition
tojustify my choice ofcareer as a scientist vis-à-vis those who were doubt-
ful about my ability to make a success in this field. These included my
father, a surgeon who had inspired me to take up medicine, my teacher
Otto Warburg (I believe)—and myself.
A third force, which has not left me to this day, is thejustification vis-à-
vis those who support me by putting financial resources and facilities at
my disposal. This desire to justify a trust is, I suppose, the cause of the
same sense of commitment and gratification which every worker experi-
ences from the knowledge of a well-done job.
Envoy
Those ignorant of the historical development of science are not likely
ever to understand fully the nature of science and scientific research. This
can be said in support of the view that scientists should not restrict their
studies entirely to the present edifice of knowledge. They will benefit
from an interest in the history of the erection of the edifice and in the
personal experience of the people who contributed toward it. This plea
was eloquently put in 1927 by L. J. Henderson [56] in his preface to the
English translation of Claude Bernard's book, An Introduction to the Study
168 H. A. Krebs · Tricarboxylic Add Cycle
Perspectives in Biology and Medicine · Autumn 1970
of Experimental Medicine, first published in 1865. Henderson points out
that the formal rigors and impersonal style of scientific literature and the
abstract character of science obliterate the nature of the individuality of
the investigator, his behavior, his mental processes, his failures and mis-
takes. Textbooks and lectures, as a rule being formal, logical, and system-
atic, convey little of the human element of science because (to quote
Henderson's words) "as much as possible science is made to resemble the
world which it describes in that all vestiges of its fallible and imaginative
human origin are removed. Since the publication of Euclid's immortal
textbook this has been the universal and approved usage." Because text-
books and lectures do not ordinarily convey to the student the real nature
of research, Henderson recommended the study of books like that of
Claude Bernard as "an honest and successful analysis ofhimself at work."
I found this book and other more recent autobiographical reminiscences,
such as those published in the Annual Reviews ofBiochemistryand Physiology
and in Perspectives in Biology and Medicine, interesting and revealing. It was
this experience which prompted me to accept the invitation of the Uni-
versity of Miami and the Howard Hughes Medical Institute to give the
Verne R. Mason Memorial Lecture on an autobiographical theme.
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40. ---------. Ibid., 42:181, 1904.
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170
H. A. Krebs · Tricarboxylic Acid Cycle
Perspectives in Biology and Medicine · Autumn 1970
PAX ET AMARE
Man professes love for Man;
Man talks of humanity;
Yet history belies the talk;
History shows Man the lie.
Man has killed Mankind;
Man has killed, always for reason;
Man has killed for vanity;
Man has killed for greed.
Man professes love for Mankind;
Man kills Man; for this love?
Man has killed in God's name;
Man has killed for country.
God is love, some say,
But Man kills in the name of God;
Each side killing for his own God;
Sometimes both sides killing for the same God.
Man professes love for Man,
Yet Man will kill Man
And peace will not be known
And love will not be shown.
Man will destroy Mankind
Unless Man is willing to try
Something different from talk,
Something different from guns.
Man will destroy Mankind
Unless Man decides to try
The one thing he only emits,
The one thing which has been just sound.
Man must express his love for man;
Man must try for peace;
Only then can we believe;
When Man professes love for Man.
171
Man builds weapons, for peace
What an obvious lie !
Man has always used those weapons;
Man will use them now and die!
Man must build peace;
Man must build love;
There is no longer choice,
Except the choice to die.
Richard S. Pope
DEATH
Life's greatest adventure is death,
It seems strange that we shun to explore it;
We cling to that last feeble breath,
And actually seem to abhor it.
But it answers life's most vexing question,
The one we can never forestall;
Is it the beginning of something new,
Orjust the sad end of it all?
Are there Heavens and Hells and Valhallas,
And great Happy Hunting Grounds;
Or should we consider extinction,
As something that's not out of bounds?
The many who've gone know the answer,
I'll know in a suitable time,
And then I'll get busy composing
A verse for the end of this rhyme.
Carl A. Dragstedt
Verse
' Perspectives in Biology and Medicine · Autumn 1970