INDIANA UNIVERSITY
BLOOMINGTON, INDIANA

June 19, 1956

Dr, Joshua Lederberg
Department of Genetics

The University of Wisconsin
Madison 6, Wisconsin

Dear Josh:

I am enclosing comments on your manuscript about phase
variation in Salmonella instead sending them to Jim Crow
only. You probably knew that the manuscript had been sent
to me for refereeing. In any case, whether you knew or

not, I think I would rather discuss the matter directly
with you than send comments to Crow and have him transmit
them to you anonymously. You will see that i had very

great difficulty with the most important part of the paper
and I think it is quite necessary to modify it in such a
way that readers will not suffer in the same way that I

have in trying to test the validity of your statements

and to understand your meanings as you go along in the

text. Not until I got to the discussion was I really

clear as to the nature of the evidence for your conclusion
and the nature of your reasoning about it. This is the main
difficulty which I think needs ironing out and I think,
through the comments I have made.on the earlier parts of

the paper before I really understood your drift in the
discussion, that you will see how the changes should be made.

I am really very much impressed with the importance of
the analysis and feel that it is, of course, exceedingly
important for us in our interpretation of the phase
variation in Paramecium.

With very best regards to you and Esther,

Cordially yours,

i.
T. M. Sondeoborn

TMS: jws
Page 3, Par, 1. What you say here is, in a general way, correct and intelligible
but I think that the situation could be made a little clearer by separating

the various types into two groups, dealing first with one and then with the
other, because they have different meanings. Thus, the i:b and 1.2:enx

types really are the only ones that imply what you state about the two groups
of genetic homologies although the sentence in which you discuss this suggests
that all three of the missing types lead to this conclusion. I would therefore
advise omitting reference to the absence of i:1.2 at this point and delay
mentioning it until after you have discussed the homology groups and begin

to discuss, as you do in the next paragraph, the phenomenon of transduction
itself. Finally, at the end of the first paragraph, where you state the
factors within each group are mutually interchangeable by transduction, it
would seem to me good to add the complementary statement: "But factors

within different groups are not interchangeable by transduction." Otherwise
you emphasize the conclusion without giving due emphasis to the major fact

on which the conclusion rests.

Now, when you come to the second sentence in the next paragraph, of course
you would have to make a modification if you omitted mention of the i:1.2
class in the preceding paragraph. That would be easy. Simply say after
the first sentence: "There is also a third class which fails to appear

in the previous example, namely, i:1.2. The absence of this class indicates
further, etc."

Page 6, Line 4. I am surprised that you permit yourself to be so categorical
and absolute in this statement. I would admit that one would expect the
relative masses of the cytoplasm in recipient and donor to suggest a
disparity in the results, but I am quite unwilling to say as strongly as

you do that the phase should be inherited entirely from the recipient in
transduction. Nothing is known about the mass of determinative material

in the cytoplasm and it may be selectively absorbed by the migratory virus.
This all seems unlikely, but I think it points up that you should be a
little bit less absolute in your statement here.

In this connection there is a probably crazy experiment that might be fun
to run just in order to permit you to make a more positive statement about
the matter. Suppose, for example, you were to expose cells in a given
phase 1 to virus from a culture which was in phase 2 and had a phase 2
different from that of the recipient. Could you readily detect whether
exposure of the recipients to the virus increased the frequency of
recipient cells which transformed to phase 2 without showing the phase 2
specific antigen of the host? What I am driving at is to see whether the
virus brings or can bring into the recipient something which changes its
phase by a mechanism other than that of introducing a different allele

for that phase. This, if it happened, would perhaps suggest that the phage
can carry a cytoplasmic determinant of phase irrespective of the specific
antigen produced in that phase.

Page 6, I don't agree with the whole line of argument presented on this
page. What you are in effect saying is that if there is a cytoplasmic
state system of determination, then no other system of determination should
have any effect. I believe this is a fundamental misstatement of the
situation. And I can support it by facts from Paramecium if you wish.

To indicate the general nature of them, I can sgy this much. I have
noticed in certain crosses between different strains that the expected
development of heterozygosity for the pre-existent phase in the descendants
of each exconjugant sometimes does not take place. Instead, the phase
changes to some other one. This can all be explained very readily on the
basis of the phase-environment relations in the two strains that were
crossed. The new heterozygous genotype may have a different reaction system
to environment than the previous homozygote did. Factors other than the
cytoplasmic state thus play a part in determining which phase is expressed.
Of course this is in agreement with what we know about the role of environ-
mental conditions in influencing the cytoplasmic state itself. The main
point in all this, of course, is to emphasize that the existence of a
cytoplasmic state system of determination does not necessarily mean that
other factors are not involved in determining the phase. But, as you

state the case here, the argument against the existence of a cytoplasmic
state system is based solely upon the demonstration that something else can
affect the issue. This seems to me a totally unjustified type of argument.

When I read the remainder of the discussion 6n this page for the first time,
I was astonished at the way you interpreted the results. It did not become
clear to me why you did this until I had read mich further in your paper.

I think that you have been unconsciously influenced in the discussion of
this experiment by ideas based on later experiments. Either you should say
that the interpretation is based partly on material to be presented later,
or here you should strictly interpret the results in terms of this experiment
alone. So far as this experiment itself is concerned, I see nothing in it
which is opposed to the cytoplasmic state hypothesis. Since you have a
mixed culture of recipient cells, it could very well be that those which
show transduction of the H) phase were cells which were in the H, phase
while those which show transduction of the Hp phase were those which were
in that phase. To be sure, this leaves you with the unanswered question of
why experiments (a) and (b) should have given different results in the
sense that one yields transduction of phase 1 only while the other yields
transduction of cells in both phases. But this could be due to a secondary
effect, namely, one which depends upon whether the donor antigen genes are
in the active or inactive condition. That is, phase 2 can be transduced
only if the corresponding gene is in the active phase, but phase 1 can be
transduced whether it is in the inactive or active phase. This, then, is a
separate matter and tells nothing about which of the recipient cells are
being transduced. They still could be limited to the ones which were
showing the phase corresponding to the one which appears transduced. The
major comment, then, that I would make on the argument presented on page 6
is that an influence of the donor phase under the conditions of this
experiment need have nothing to do with testing the validity of the
cytoplasmic hypothesis, for the design of the experiment permits no
decision as to the role of the phase of the recipient since both phases

are present in the culture,

Page 7, Par. 2. You have switched designations here from S.heidelberg to
SL 28 in such a way that the reader is confused unless he is thoroughly
familiar with this material or refers back to your description of mterials.
It would be much easier if you used the same designation for this strain

in both parts of the paragraph.
3.

Page 7, last paragraph. I suppose what you say here is correct and
justified, but it is not immediately apparent to the reader that your
conclusion of the transducibility of an inactive b is verified. Might
not the reader wonder whether the b transductions, even though the
predominant ones, were derived from donor cells in an active b phase as
a result of impurity in the donor culture?

I find your discussion of hypothetical expectations on page 10, and their

. tabulation in table 7, in part very difficult to understand. Particularly,
I don't understand hypothesis 3 at all, nor do I fully grasp what you
intend by hypothesis 2. In my opinion, this part of your paper is unduly
condensed and puts the greatest tax on the reader's interpretation as to
what you mean. It seems to me that without some expansion of this material
and some explanation of table 7, the reader is bound to be to some extent
in a fog about your hypotheses and your analysis of them. I, therefore,
very strongly urge that this part of the paper be redone in more detail
with more elaborate exposition.

I also find it difficult to understand how the observed results can all

be reconciled with your favored hypothesis if the results are simply to be
explained on the basis that an inactive H2 gene remain inactive after
transduction. How then do you explain the failure to recover di:r2 or
dl:r2 when dl:d2 is transduced into rl:r2 or the failure to get dl:r2 when
dl:d2 is transduced into rl:r2?

In the third line from the bottom on page 10, should not 121 be 111?

Page 11. Iam continually bothered in the pages leading up to this point

by what seems to be a continual shift from demonstration of the role of the
inactive gene in the donor to the role of the active phase in the recipient.
Nowhere do you bring these two together into a complete picture of the
situation, but, it seems to me, shift from one to the other to the utter
confusion of the reader. Thus, here on page 11 you seem to be saying that
the phase of the recipient is very important. On the preceding page or so
you develop the idea that the activity or inactivity of the Hg locus is
important. One is left with a good degree of bewilderment as to whether these
are two aspects of one interpretation or whether the reader is misunderstand-
ing you in your apparent statements that both factors are important. I'm
really not sure myself whether you mean to lay the entire burden of the case
on the activity of the Hg:locus or whether you are willing to admit that

the phase which is phenotypically expréssed in the recipient is also
important.

Page 12, second line from the bottom. I think both the meaning and the
writing would be improved if "another" were changed to "other."

Now, at last, as I get to page 15 I begin to make sense out of what was
said in the preceding pages. I think it's important for you to realize,
though, how utterly confused the reader can be until he gets to page 15.
Now your hypothesis begins to hang together and one understands what you
mean by the hypothesis of activity vs. inactivity of the Hg locus. It has
4.

not been clearly set forth before in such a way that the data can be
entirely reconciled with the view. Perhaps the reader should have foreseen
this, but he didn't--at least in my case. And I think it is up to you
either to present the hypothesis in the first place with sufficient clarity
so that the reader can understand what you mean, or defer the whole
discussion of the hypothesis until the discussion section. By putting the
hypothesis in earlier in inadequate form, the reader is simply confused
and the whole thing doesn't make sense until he gets to page 15 of your
manuscript. I think some kind of reconciliation of these difficulties is
very much needed to make the manuscript effective. I see now how some of
the objections that I raised earlier can be met, but I don't think the
reader can see that, or is likely to see it, until he gets to page 15 when
the damage is already done so far as his disposition is concerned.

Bottom of page 19. It is quite true, of course, that the work on caryonidal
determination of mating types has recently been bolstered by the work of
Nanney and Caughey on Tetrahymena, but I think it is only fair to call
your attention to the fact that the caryonidal determination of mating type
and its relation to nuclear differentiation had been first discovered in
Paramecium and has been emphasized by me repeatedly since I first found it
in 1937. At first I tried to reconcile this with the possibility of
chromosomal segregation during anlagen formation. But tery early I
obtained evidence against this possibility, and in a Growth Symposium (I
believe in 1946) made a special point of the significance of mating type
determination in Paramecium for developmental differentiation. I don't
mean to say that this ought to be inserted into your paper but I think

it is desirable at least for you to know that the idea and the work go

back much further than the recent work on Tetrahymena,

The second pointin your summary again fails to get across the force of
your conclusion. I doubt whether any reader could grasp from this state-
ment the reasonableness of your conclusion. It just doesn't seem to follow
from the second sentence under this point. Can't you put in another
sentence which will explain more fully the validity of the jump from the
fact to the conclusion?

In Table 5 I have marked two places where an entry has been made as to
the Gal status of the transduced clones. In these cases there were no
transduced clones and therefore neither a plus nor minus under the Gal
column seems to be justified.