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Bp r 16, 1953

Dr. Re A. Brink

Managing Editor, Cenetics
Genetics Building
University of wisconsin
Madison 6, \isconsin

dear Ur. Brink:

It is not easy, believe me, for an outsider to form a well ~fouried
Judgment. in the difficult field represented by Appleyari's paper.

I therefore submit the following comments with zenuine humility and
full recognition that my lack of firsthand experience with the mterial
probably renders me to some extent unfit for this Job. On the other
hand, there is ut present apparently such a deep ad vigorous split

of viewpoint und opinions among workers in the field that there may

be geome compensating advantages to consulting an outsider, For that
reason I have less hesitation in comrenting.

Page 1, paragraph 2 - Objection might be raised to the impression
created by this paragraph. He identifies asymmetry of recombination
with the donor-acceptor hypothesis of Hayes. This is not the only
possible hypothesis and another has been proposed by the Lederbergs
an: Covalli., Further, he identifies F* with donor and F7 with
acceptor, without reference to the discoverers and namers of Ft and
F~ (the Lederborgs ind Cavalli}. On the whole, it seeus to me that
the ;ortrayal of the situation is not a just representation of "our
current pic-ure." It is only one side of the picture, but it entails
bringing in work of the other side (F* and F~) without credit or
reference,

On the main body of the paper I have no comments to make, but the
discussion (pp. 11-13) seems to «e to be open to the following criti-
cisms and comments?

(1) Since lysogenicity for both lambda-s and lambda-cl are closely
linked to gal, the chromosome determines both the carriage of prom
lambda und the kind of lambda released. From this he concludes that
lysegenicity 1s not due to cytoplasmic lambda under genie control, But
if the two kinds of lamba were controlled by two closely linked <enes,
respectively, the observations would not be incompatible with cyto~
plasmic localization of lambda, Hence, I cannct see that tis rossibillity
is excluded, or even rendered improbable.

(2) A major fact in the discussion is that lysogenicity interferes with
recombination and that the interference is greater in double lysovenics
than in single lysogenics. This is held to favor the view that some=

thing extra is -<$ixch n 5 legis in lysogenics, tore
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Dr. R. 4. Brink Page 2 October 16, 1953

in double lysogenies. I adnit that this is a pos:ible interpretstion,
but is it not also true that the frequency of crossing over varics
with many physiologic and environmental conditions and that change in
frequency need not be due to mechanical interference of the kind he
postulates? If recombination is here due to crossing over or something
like it, then change in ite frequency might be a result of physiologic,
rather than mechanical, disturbances due to the presence of prophage.
He scems to reject this possibility without explanation, ‘hy? Is

the disturbance in recombination confined to gal?

(3) Throughout this argument he also has an implied, but unstated,
assumption which needs to be made explicit, for, when stated, it reveals
a weakness in the argument. He believes that prop age is attached over
a region, or at least at nore than one point. In this way he accounts
for the possibility of carrying more than one kind of prophage, Further,
his argument about mechanical interference with recombination is based
on greater interference by two prophages than by one. This therefore
implics that when one prophage is present it is attached at only one
point, or at least over a emller revion than is occupied by two kinds
of prophage. But it is not clear why this should be so unless the
different kinds of prophage are specifically restricted to different
chromosome regions, And if that is eo, then my argument above about
cytoplasmic localization of prolambda, cach kind umier the eontrol of

a different locus, must be admissible. If there is no specialization
of the chromosom region involved, then the whole region should be
available for one kind of prophage when only one kind is present und
should be shared by two kinds of prophage when two kinds are present,
In both cases, the region of chromosome occupied would be the same.
This leaves no mechanicul basis left for great :r interference with re-
combination by two kinds of prophase than b one, and my argument for
physiologic interference 1s strengthened. So, regardless of which
alternative is accepted, Appleyard's discussion seems to me to be
defective.

(i) He cites in his argument a point made in an as yet unpublished paper,
namely, that in double lyso;enics one cin obtain reconbination of the
characters of the carried prophages, This is believed to support the
view that they are carried in adjacent positions on the ciromosome, Of

course I have not seen this paper and it may be unfair to question the
argument; but since it is cited here as a relevent point, I raise a
doubt about the argument. 4s I understand the biology of lysogenics,
there is occasional spontaneous loss of prophage and occasional spon
taneous lysis. sould .ot this provide ample possibility for oceasional
recombination of phage characters in the usual way without any necessity
of resorting to adjacent position in the chromosome to exrmlain it?

(5) As part of his argument for the mechanical irterference in recombi-
nation, he tries to show that «he interference evidenced by reduction
in the frequency of gal "transfer" is not due to lethality of the

COPY
Dr. R, A. Brink Page 3 Ustober 16, 1953

missing recombinants through induction of lambda maturation in these,
The argument appears to me to involve some or all of the following
assumptions, which are implied but not stated: (a) a single lysogenic
is resistant to action of lambda of a different kind; (b) if a cell
carries a prolambda, i.e., if it is lysogenic, then it must be in a
condition suitable to receive and carry another kind of lambda as a
sccond lysogenic; (c) if one kind of prolambda is carried in "attached"
position, introduction of another lambda (or prolambda) will not result
in imucing mturation of lambda. Not being an expert in this field,

I am not sure whether all of these assumptions are sound, but I have the
impression they are not. If I am correct in this and in concluding that
the assumptions are implied, then the argument is unsound and differ-
ential survival is an alternative explanation of the apparent interference
with reecmbination.

From the above coments, you will see that I have grave doubts about

the validity of the discussion and the main conclusions in the paper.

If my criticisms are sustained by another referee or admitted by the
author, it seems to me that thorough revision of the discussion and con=
clusions might fairly be called for. The facts in the paper Ido not
question, and these are of sufficient interest and importance to

warrant publication in Genetics. As I see the situation, there are two
main facts: (1) recombination does not occur between the loci involved
in double lysogenicity (or in crosses between the two single lysogenics) ;
(2) the apparent frequency of "transfer" of gal is reduced in lysogenics,
more so in double lysogenics. A paper adequately setting forth these
facts ani soundly discussing their significance would be worthy of
publication in Genetics; but I believe the present manuscript does not
soundly diseuss them,

Yours,

T. M. Sonneborn
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