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OCR for page 72

Chapter V!
STATISTICAL
THE problems posed when one attempts to
employ survey data in an analytical fashion are
legion. As a consequence, it is doubtful whether,
given a body of survey data, any two competent
statisticians would evolve essentially the same
approach. Accordingly, it seems important that
an attempt be made to establish the line of
reasoning which led to the final form which the
analysis of the Japanese data assumed. In this
chapter, therefore, we shall set out in some de-
tail the analytical plan, and consider briefly the
tests of significance to be employed.
6.1 The problem and the general plan;. It
has been previously stated that the purposes of
this study were to answer the questions, "Is
there a difference between the progeny of ir-
radiated and non-irradiated parents?", and "If
a difference exists, how is it to be explained?"
The latter question is, of course, outside the
purview of statistics, but the former may be
paraphrased in terms of the general statistical
problem posed by this study. We may state the
problem as follows: What is the significance of
the association of parental exposure with those
variables indicative of genetic damage due to
irradiation? A meaningful answer to this ques-
tion requires that no differences with respect to
any of the indicators exist between the exposure
groups being compared save those differences
which have been taken into account in the course
of the analysis or which arise from exposure
experience itself. Available to us are the follow-
ing two collections of data:
1. Observations on some 75,000 pregnancies
terminating sometime after 20 weeks of gesta-
tion. These observations are distributed over two
cities and 25 parental exposure combinations.
2. Clinical and anthropometric examinations at
9 months of age of some 21,000 infants
randomly selected from pregnancies comprising
( 1~ . These observations are also distributed
over two cities and 25 parental exposure com-
binations.
72
METHODS
.The fact that observations have been obtained
in two cities permits us to view these data as
constituting two approximate replications of
one basic experiment.
While the basic problem is readily formulated
statistically, its solution is complicated by two
factors, namely, extraneous (concomitant) varia-
tion and differing numbers of observations in
the various exposure cells. Before we consider
the impact of these factors on the form of the
analysis, let us examine the indicators of radia-
tion damage, that is, the measurements by which
we shall attempt to determine whether radiation
has or has not resulted in a measurable effect
upon the outcome of pregnancy terminations.
6.2 Indicators of radiation damage o`nd the
h~r)hl~m of '2nn-overlabbin~ measurements.-
r ~ ` ~ r~---o -------------------
Amon~ the numerous measurements or at
O
tributes by which a newborn infant or a
9-months-old child may be classified there exist
at least six which a priori may be expected to
reflect genetic changes due to irradiation. These
six indicators of genetic damage are (1) the
sex ratio, (2) birthweights, (3) measurements
of bodily development, and the frequencies of
(4) stillbirths, (5) neonatal deaths, and (6)
gross malformations. As has already been made
clear, none of these measurements is a unique
yardstick of radiation damage; this is an in-
herent difficulty in the problem. Moreover, it
is apparent that these indicators are not all
mutually independent measurements of radia-
tion damage. Some are correlated, and many
would measure, to some degree, the same ge-
netic damage.
Extrapolation from experiments involving the
irradiation of laboratory animals at the relatively
low levels obtaining in Hiroshima and Nagasaki
suggested that the effects appearing in the hu-
man populations in question would undoubtedly
be small, small enough that such effects would
be demonstrable only with a very large sample
(review of literature in Chapter XV). This in

OCR for page 72

Statistical Methods
conjunction with the lack of unique indices of
radiation damage led us to believe that it was
advisable to attempt to develop a method
whereby information gained with respect to the
various indicators of radiation damage would
be additive, e.g., a method permitting combin-
ing information from tests of significance
through the chi-square transformation of prob-
abilities. This required that the tests of signi~S-
cance performed on various segments of the
data be independent of one another. It was
clear, however, that insofar as children who
were grossly malformed were apt to be stillborn,
or stillborn infants were apt to be small, tests
on malformation and stillbirths, or stillbirths
and birthweight, would not be wholly inde-
pendent measures. We chose to remove effects
73
for example, amounted to less than 3 per cent
of the total observations.
Presumably the device just described would
not be necessary were we able to combine non-
independent tests of significance. However, as
Wallis (1951) has pointed out, to combine de-
pendent tests of significance requires that we
be able to specify the e-dimensional surface
formed by groups of probabilities of ~ events
which are not all necessarily equally probable.
To specify this surface, we must know the exact
kind of dependence which is present, and we
obviously do not know this.
6.3 Concomitant vocation. As stated ear-
lier, the analysis of these data is complicated
not only by extraneous variation, but also by
disproportion in the number of observations
EStillborn (Neonatal
iNo malformation ],Liveborn I
Malformation No neonatal
~death ~Birthweight
Total
observations
within an
exposure
treatment
No malformation JStillborn
Female ~|Liveborn
(Malformation
Indicator: Sex Ratio Malformation Stillbirths
(Neonatal
| death
No neonatal
~ death~ Birthweight
Neonatal DeathBirthweight
F~GuRE 6.1-A schematic representation of the method of sorting the data to obtain non-overlapping
indicators.
such as those just indicated by a pyramidal
handling of the data. Under the scheme em-
ployed, the first attribute to be measured was
the sex ratio. This was followed by the fre-
quency of malformation. In this and all subse-
quent partitions sex was taken into account. All
grossly malformed infants were then excluded,!
and the frequency of stillbirths obtained. The
stillborn infants were discarded in turn, and
birthweights distributed on the remainder. Thus
the frequencies of stillbirths in the various ex-
posure categories were based only on those
infants with no clinically obvious malformation.
Similarly, birthweights were based only on those
liveborn infants without clinically recognizable
gross abnormalities. The order of the testing is
indicated in Figure 6.1. This approach must
lead to the loss of some data. However, the
advantages to be gained by having measure-
ments which were essentially non-overlapping
seemed to outweigh the loss in data, particularly
since the "loss" with respect to birthweight,
within the exposure cells. The problems posed
by the latter we shall treat of presently; for the
moment let us concern ourselves only with
extraneous variation.
In Chapter N1 attention has been called to a
rather large number of variables in which the
exposure subpopulations differ significantly
within or between cities. Thus, the reader has
been apprised of differences in (1) the fre-
quency of consanguineous marriages, (2 ~ mean
maternal age at birth of a registered infant, (3)
mean parity, (4) the frequency of "D and C,"
(5) the frequency of a positive serology, (6)
the frequency of induced abortions, (7) the
frequency with which repeat registrations oc-
curred, and (8), possibly, the economic status
of the parents. A number of these concomitant
variables are known to influence the outcome of
pregnancy terminations, for example, the fre-
quency of malformation increases with increas-
ing age, and birthweight increases with parity.
We might rightly ask, however, whether the

OCR for page 72

74
effects of these variables are of sufficient conse-
quence to lead to misinterpretation of the radia-
tion effects, or to the obfuscating of a real effect
if one should exist. It is obviously impossible
to answer this question categorically with regard
to all of the concomitant variables. It is possible,
however, to make a general appraisal of the
effect of these variables, and then to make a
value judgment with regard to whether or not
the effect of a given concomitant is of a magni-
tude large enough to warrant consideration in
the analysis of a given indicator. The methods
of appraisal are not fully rigorous but are de-
scriptive and convenient to use. Since the use
of these methods is not widespread and since
concomitant variation is a major problem in the
analysis of the data to be presented in subse-
quent chapters, we shall present the methods
which we have employed in some detail.
In the case of a continuously distributed indi-
cator we shall employ the ratio of two residual
mean squares obtained under different assump-
tions regarding the population sampled, to esti-
mate the amount of variation in the indicator
ascribable to a concomitant variable and to varia-
tions in the relation between the indicator and
a concomitant variable. The basis for using the
ratio in this way was first pointed out to us by
Dr. H. L. Lucas, Jr. whose argument, which is
unpublished, we have been kindly permitted to
reproduce here. The argument is as follows:
Consider the variable y, which is known or
thought to be influenced by the concomitant
variable, x. A simple model of this relationship
would be
where
Genetic EJects of Atomic Bombs Chapter VI
(2) The mean square for y after correction
for (a) the group means and (b) the common
regression on x. This would be computed as
-p-1 ~ j
:~(Yii-Yt)Xij]2 -
>> (yij-yt) 2_ >> (Xij Xi) 2
i;
(3) The mean square for y after correction
for (a) the group means and (b) separate re-
gressions on x in each group. This residual
mean square we compute as
~2
1 f [> (Yij -Yi) Xij] 2
n-2p i `(yij yi) Al >(Xij-Xi)
If now we let
and
fo= offs=> (n,, - 1) = n-p
>~> (Xtj-Xt) 2
It_ ~ i
>> (Xij-Xt) 2
j
We find the expectations for a given set of
X1j to be
E (So2) = (72 + f ~ (~t _ §) 2> (Xtj-Xi) 2
+ 1 p2~> (xij-Xt) 2
fo ~ i
E (SC2) = (J2 + ~ ~ ~ (§i-p) 2> (Xtj-Xi) 2
fo- ~ i
E<~2'=~2
y,I,j= mI,+,BlXii'+ ~]
Now, if we define the second and third terms
of E(so2) as ~42 and act, we can write
i= l, 2, . . ., p, designates the group,
j=l, 2, . . ., n', designates the indi- E(~2~=~2+<,~2+a2
vidual within a group (ink = ~) ~E (IC2) = ~2 + fo ~42
m'=the Intercept of the Ith group, f
if`= the regression coefficient of the its E (s2) = (J2
group,
and Random, independent errors with vari
ance a2.
Or, since fo/(fo-1) is essentially unity, we
could in the above have written with little error
E(sc2) =CT2~42
Within this model, we may work out the expec
tations of the following quantities: An objection could be made, of course, that
(1) The mean square for y after correction the meanings of ~42 and ~c2 depend upon the
for the group means but not for regression on sample pattern of the xi;. Let us assume, how
x. This quantity would be
>> ()i}-yi) 2
2 i j
so =
n_p
ever, (a) that the sample of size n=~?;, was
drawn from a population of size N which
divides into p groups with N. individuals in a

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Statistical Methods
75
group, (b) that the within-group variance of Now
x is ~2 in all groups, (c) that the sample is lOO(L-1) . .
random and large with the restriction (d) that L =per cent of the variation re
maining after correction for
group means that is ascribable
to the common regression, and
1°°~2 - 1) =per cent of the variation re
2 maining after correction for
the group means and common
regression that is ascribable
to the different regressions.
ft N
f = N
In this event, stable meaning can be given to
~2 and ace. Define
~ (pi-Cot oft ~ (~t _ Coy 2Ni
and
2= ~- ~
~fo N
>§ift >§iNi
No= f N
o
Clearly under the assumptions and restrictions
just given, ~B=`Bo to a close approximation and
Er' ~ j `' ] =~ 2
~ fo
E[ ~] = a~2-
ft
Then we see that to a close approximation
d ~ $
TIC =ho a~
These are definitions in terms of population
values. In practice, of course, instead of large
random samples, arbitrarily chosen samples of
any size may be used that satisfy the restrictions
and
Ni -
fo No
Id-Xi)2 >~(Xij_Xi)2
i = ~ i =~ 2
fo
to a close approximation.
To estimate, now, the percentage of variation
in y ascribable to the common relation to x, we
form the ratio
~ 2
Lo
1=s 2
C
The percentage ascribable to between-group
variation in the relation to x is obtained by
computing
sc2
L2= s2
When L, and L2 are near unity, as in
our data, 100~`L~-1) and lOO(L2 - 1) differ
but negligibly from 100 (ILL-1~/L~ and
100 (L2 - 1 ) /L2, and we shall employ the
former. If L1 and L2 differ materially from
unity, then 100 (`L'-1 ~ /L, and 100 (L2 - 1 ) /L2
are appropriate when one wishes to speak of the
per cent of the total variation due to a specified
source. Even under the latter circumstance,
however, 100 (L'-1) and 100 (L2 - 1) would
be appropriate if one should wish to speak of
the per cent increase in error variance which
would result from a failure to remove a given
variance source.
It seems appropriate at this point to comment
briefly on the simplifying assumptions which we
have used in the foregoing presentation. In the
main these assumptions are not particularly
restrictive when one notes that the purpose of
this procedure is not a precise estimate of the
variation contributed by a particular variance
source, but rather to determine the order of
magnitude of the contribution of this source.
In the case of a discrete indicator, we shall
employ a method devised by Krooth (1955) for
the analysis of the "importance" of an effect of
maternal age on the presence or absence of some
character among the mother's offsprin'g. A slight
modification of Krooth's method has been neces-
sary to permit estimating, independently, the
"importance" of parity in addition to maternal
age. This modification, which merely involves
holding one concomitant constant while meas-
uring the other, will be apparent from a study
of the tables dealing with maternal age and
parity in Chapters VIII, IX, and XI.
Generally, problems posed by concomitant
variation are met by one or another of the fol-
lowing three techniques: balanced sampling,
covariance analysis, or the addition of another
way of classification to the analysis wherein this

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76 Genetic Effects of Atomic Bombs Chapter VI
classification corresponds to intervals in the
distribution of the concomitant variable. We
will have occasion in analyzing these data to
employ all of these alternatives save the tech-
nique of balanced sampling. The latter was not
employed because in those instances where it
was applicable, exact balancing led to a very
large loss of data, and balancing in terms of
intervals in the distribution of the concomitant
variable does not generally relieve one of the
responsibility of a covariance analysis. We shall
now turn to a brief consideration of the courses
of action adopted in each of the concomitant
variables.
( 1 ) Consangair~i~y. Among these data
over 90 per cent of the observations represent
observations on pregnancies occurring to unre-
lated parents. Thus, if warranted, all preg
. . . .
nannies occurring to consanguineous unions
could be excluded without an exorbitant loss
oil data. The justification for and the decision
to exclude these terminations rests primarily on
two factors. Firstly, Schull (in manuscript) and
Morton (in manuscript) have shown fairly
general, if not large, effects of consanguinity on
pregnancy outcome as here measured. In the
main, these effects consist of an increase in
frequency of malformation with increasing con-
sanguinity, an increase in infant mortality with
increasing consanguinity, and a decrease in
birthweight. Secondly, the distribution of con-
sanguineous marriages by parental exposure is
such as to introduce a bias (tending to mini-
mize exposure differences if such exist).
(2) Maternal age arid parity. Adjustment
for one or both of these variables has been
undertaken for all indicators save the anthropo-
metric measurements obtained at 9 months of
age. For the analysis of the malformation data,
stillbirth data, and infant mortality data, com-
pensation for these variables took the form of
adding to the analysis another level of classifi-
cation. For the birthweight data, compensation
for these variables took the form of an analysis
~ .
01 covarlance.
(~3) Economic status. In respect to only
one variable, birthweight, has an attempt been
made to determine the effect of economic status.
This stems from three considerations. Firstly,
it was possible to obtain information on the
economic status on only 10 per cent of the
infants, so that adjustment for this variable, in
the total data, is impossible. Secondly, economic
status is probably of importance only insofar
as it is a measure of nutritional standards.
Thirdly, the only differences with regard to
economic status in these data which are demon-
strable are between cities and not parental ex-
posure. It seemed dubious, therefore, whether
any form of adjustment which could be enter-
tained would justify the effort.
(~4) Dilatation arid curettage. The more
or less standard procedure in Japan for inter-
rupting a pregnancy or treating a woman fol-
lowing a spontaneous abortion consists of dilat-
ing the cervix and curetting the uterus. It seems
logical to suppose that repeated performance
of this routine can lead to the formation of
sufficient scar tissue in the uterus to pose an
obstacle to the successful implantation and de-
velopment of subsequent concept). On this
thesis the frequency of D and C was investi-
gated with the full knowledge that possibly no
adequate adjustment could be determined if
exposure or city differences obtained. In Chap-
ter V, we have indicated that while city differ-
ences obtain, no exposure dill erences are demon-
stable. We are inclined to view the recorded
city differences as being largely a reflection of
differences between the cities in the enthusiasm
with which this question was approached by the
. . . . .
examining physicians. No attempt has been
made to take into account this variable.
(S) Positive serology. Congenital syphilis
markedly affects the frequency of stillbirths,
and the neonatal mortality rate. Again, informa-
tion on maternal serology was limited to but 10
per cent of the total sample. This sample, how-
ever, revealed that, within cities, no significant
differences exist among exposure groups (see
Sec. 5.4~. The paucity of data precluded-any
attempt to take into account this variable in
the analysis.
(~6) Induced abortions. The liberalization
of the Japanese abortion law has resulted in a
large-scale interruption of pregnancies. This
could obviously pose a serious bias if in some
parental exposure categories more interruptions
occurred than in others. Moreover, undetected
interruptions could play havoc with an attempt
to assess the "importance" of parity on a given
indicator. The data reveal no consistent ex-
posure differences although the city rates are
significantly different (see Sec. 5.5). This vari-
able has been ignored in the analysis of the
indicators.

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Statistical Methods
(~7) Repeat registrations. We have stated
that in the course of this study some mothers
registered more than one pregnancy. Since the
indicators being used are in part genetically de-
termined, there will be a non-zero sib-sib corre-
lation for many, if not all, of them. Therefore
when repeated births involving the same parent
or parents are entered into the radiation sub-
classes, these entries will be non-independent.
The tests of significance which follow assume
that each entry is independent. Consequently,
the standard errors, or their equivalents in more
complex tests, may in general be slightly too
low, since there is actually rather less informa-
tion than the test assumes. The data suggest that
the frequency of repeat registrations is not the
same over all exposure cells (see Sec. 5.6~. The
bias which this might introduce into the esti-
mates of within-cell variances would probably
be small in view of the number of repeat regis-
trations. We have, as a consequence, ignored
the fact that repeat registrations occur with
different frequencies in the various exposure
cells.
In general, in the succeeding chapters we shall
have occasion to present analyses of the data
where, on the one hand, the effect of con-
comitant variation is ignored, and, on the other
hand, some adjustment has been made for one
or more of the above-mentioned concomitants.
The primary purpose of presenting the analysis
in this extended fashion is to enable the reader
to judge the necessity of correcting for con-
comitant variation, and to ascertain the effects
of such corrections on the data.
6.4 F(ejecled observations.-As would be
surmised in a study of this kind, fleece arise in-
stances in which observations of dubious validity
occur, and instances where the information rela-
tive to a particular variable is incomplete. In
Table 6.1 are presented the number of infants
who were excluded from the final analysis of
the "at-birth" data along with the reasons for
exclusion. Several entries in this table require
comment. Firstly, it will be noted that the two
largest numbers of rejections, in each city, occur
by virtue of the fact that the pregnancy was un-
registered (and these pregnancies are known to
be biased exposure-wise and in the frequency
with which abnormal terminations occur), or
the pregnancy occurred to parents related as
first cousins, first cousins once removed, second
cousins, or occasionally closer or slightly more
77
remote relationships. Secondly, a fairly large
number of rejections occurred where the infant
was described as representing an "induced
termination where the birthweight was less than
2,500 grams." The argument for rejecting these
infants hinges primarily on the word "induced."
In Japan, it is customary to view any termination
in which medicinal or mechanical assistance was
given to the laboring mother as an induced
termination." This definition, while a patently
plausible one, is much broader than occurs else-
where. It was generally agreed that any preg-
nancy which was terminated before the natural
occurrence of labor could not be scored in this
study. The reason for this is two-fold, namely
TABLE 6.1 THE NUMBER OF INFANTS REJECTED
FROM THE STUDY, TABULATED BY REASON
FOR REJECTION
Unregistered births 2,372
Registered births
Consanguinity 2,184
Induced terminations where
birthweight less than
2,500 Ems 379338
274209
2
Hiroshima Nagasaki
892
2,979
Unknown birthweight
Unknown parity
Gestation less than 21 weeks,
or unknown and infant
less than 2,500 Ems
Unknown sex
Unknown maternal age
Unknown distance
Exposed in one city, now
residing in other city 52 152
149 44
4 8
Total . .
..177164
5,5914,788
( 1 ) the possibility that such terminations would
be non-randomly distributed with respect to
parental exposure, and (2) the high probability
that an induced termination will result in a still-
born infant, or one dying during the neonatal
period and wherein the cause of death is di-
rectly or largely attributable to the inducing
agent. Our problem, therefore, was that of sort-
ing out of all terminations loosely labelled
"induced" those in which there was probably a
true induction of labor. The only reasonably
reliable standard for which data existed ap-
peered to be birthweight. It seemed highly prob-
able that if an induced termination gave rise to
an infant weighing less than 2,500 grams then
1 This use of the word "induced" did not become
known to us until a large number of terminations had
been scored as induced in the Japanese sense.

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78 Genetic F,jects of Atomic Bombs Chapter VI
induction was an overt attempt to end the
pregnancy rather than an attempt to assist the
parturient mother. Lastly, a comment is in order
regarding the category "gestation less than 21
weeks or unknown and the infant less than
2,500 grams." It has been mentioned that the
rationing system obtaining in these cities pre-
sented possibilities for error and that occasion-
ally a pregnant female registered prior to the
time when the law permitted. This would
present no problem if the pregnancy continued
past the time officially designated for registra-
tion. If, however, the pregnancy terminated,
naturally or artificially, prior to the 21st week,
then the registration represented a type of preg-
nancy not normally coming to our attention.
Since such registrations could not be viewed as
necessarily representative of pregnancies ter-
minating before 21 weeks of gestation and be-
cause of a possible exposure bias, it seemed
advisable to reject them. In some instances,
mothers would not or could not provide in-
formation which would permit an estimation
of the length of gestation. Accordingly if the
duration of gestation could not be estimated
and the infant was apparently premature (as
judged by birthweight), the termination was
excluded.
To appraise the effect on the data available
for analysis of the most frequent cause of ex-
clusion of registered pregnancies, consanguinity,
the reader's attention is directed to Table 5.1
wherein the distribution by exposure of the
consanguineous unions is given. It will be noted
from Table 5.1 that exclusion of the consan-
quineous marriages is more at the expense of
the unexposed and lightly exposed parents than
the heavily exposed parents.
The reader will find in Tables 6.2 and 6.3 an
accounting, at representative stages in the analy-
sis, of all observations which were rejected from
the"at-birth" or "9-months" data. An explana-
tion will be found in the tables for those re-
jections which have not been accounted for in
the previous paragraphs of this section, in Sec-
tion 6.2, or in Section 6.3~1~.
6.5 The ar7alys~ of the attribute data. The
analysis of attribute data presents a number of
formidable problems not the least of which is
the appropriate specification of the hypotheses
of interest. More exactly, difficulties arise in the
formulation of hypotheses regarding "main ef-
fects" and "interactions." Specification of these
hypotheses becomes increasingly difficult as the
number of ways of classification of the observa-
tions increases. The statistical literature outlin-
ing tests of significance in multi-way classifica-
tions of attribute data is surprisingly scanty,
when one ignores that portion of the literature
devoted to transformations necessary to fit at-
tribute data into one of the conventional meth-
ods of handling measurement data. Until re-
cently, the one and only case to be considered
in any detail was the 2 x 2 x 2 system of classi-
fication (Bartlett, 1935~. A generalization of
Bartlett's approach is to be found in Roy and
Kastenbaum (1956), on which we shall draw
freely. The latter authors succeed in more
sharply defining the parallelism between the
analysis of variance for continuous data and the
analysis of attribute data.
The method of analysis which we shall out-
line in the succeeding paragraphs is complex.
Lest the reader doubt the necessity of so com-
plex an analytical form it is worth pointing out
that our problems stem largely from the numer-
ous ways in which these data are partitioned.
The approach could certainly be simplified by
ignoring some of the ways in which we have
elected to partition the data such as, say, city
of birth, sex, and the concomitant variation. It
is our contention that such an omission is un-
justifiable. If one accepts this point of view,
then there is no alternative known to us other
than a multi-way analysis. In attribute data, this
poses problems often more complex than those
which arise in the analysis of continuously dis-
tributed data. Our approach is essentially one of
pooling information from different ways of
classification but only after such pooling car; be
shown; to be justified. When pooling cannot be
justified, alternative statistical procedures, to be
explained later, will be adopted. Few, if any,
instances in the statistical literature exist
wherein attribute data have been employed in
the fashion required here. This is a commen-
tary, in part, on the difficulties which arise when
multi-way classification of attributes occurs, and
on the biological complexity of the indicators
of irradiation damage.
Before we discuss some of the particulars in
the analysis of the Japanese data, we shall con-
sider in some detail the basic arguments under-
lying the tests of "main effects" and "interac-
tions." For illustrative purposes, let us examine
a simple problem. We shall assume that we are

OCR for page 72

Hiroshima Nagasaki Total
Total infants seen 38,421 38,205 76,626
Rejected because the pregnancy
was unregistered, parental
exposure was unspecifiable,
consanguinity or other obser-
vations were incomplete
(see Table 6.3~.........
Considered for consanguinity.....
Rejected consanguinity .......
Considered for maternal able.....
Rejected multiple births.......
Considered for sex ratio.........
Considered for malformations....
Rejected malformations .......
Rejected congenital heart dis
34,943 36,337
32,830 33,417
32,465 32,966
32,465 32,966
Statistical Methods
79
TABLE 6.2 AN ACCOUNTING OF THE NUMBER OF OBSERVATIONS CONSIDERED AT REPRESENTATIVE STAGES
IN THE ANALYSIS OF THE AT-BIRTH DATA AND THE NUMBER OF REJECTED OBSERVATIONS
WITH THE CAUSE OF REJECTION
Available observations Rejected observations
Hiroshima Nagasaki Total
71,280
66,247
65,431
65,431
3,4781,868
2,1132,920
365451
313281
5,346
5,033
816a
594
ease 44 53 97
Total 357 334 691
Considered for stillbirths 32,108 32,632 64,740 - -
Rejected stillbirths 472 482 954
Considered for neonatal deaths 31,636 32,150 63,786 - -
Rejected neonatal deaths - - - 414 480 894
Considered for birthweights 31,222 31,670 62,892
aIn Hiroshima one set of registered triplets and 181 sets of registered twins occurred; in Nagasaki
there were one set of registered triplets and 224 sets of registered twins.
TABLE 6.3 AN ACCOUNTING OF THE NUMBER OF OBSERVATIONS CONSIDERED AT REPRESENTATIVE STAGES
IN THE ANALYSIS OF THE 9-MONTHS DATA AND THE NUMBER OF REJEcTED OssERvAT~oNs
WITH THE CAUSE OF REJECTION
Available observations Rejected observations
r
Hiroshima Nagasaki Total
Hiroshima Nagasaki Total
Total infants on whom there exists
some follow-up study 14,768 12,324 27,092
Rejected inadequate exposure
history, infant not part of
9-months program, etc
Total infants considered under the
9-months program 11,346 10,442 21,788
Rejected consanguinity - -
Rejected incomplete measure
ments
Considered for neonatal death. . . 10,512 9,306 19,818
Rejected neonatal deaths - - 484 458 942
Considered for malformation 10,028 8,848 18,876
Rejected malformations - - 183 195 378
Considered for anthropometrics 9,845 8,653 18,498
' A word about this total is in order since it may appear to the reader as an inordinate loss of informa-
tion. This total includes 5,089 infants who were seen at some age other than 9 months (in fact, 8-10
months). Many of these entries represent visits to the newborn malformation verification clinics. The latter
infants are, of course, scored under the "at-birth" program. A second major contributor, particularly in Hiro-
shima, to this total of 5,089 infants stems from the initial indecision as to the "best age" at which to examine
the infants. Some of the first infants seen under what was subsequently called the 9-months program were a
year and a half old. These children have been rejected here in order to minimize differences between cities
and, within cities, between exposure categories in the age at examination. The importance of standardizing,
insofar as possible, the age at examination need hardly be labored.
3,422 1,8825,304 a
694 8281,522
140 308448

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80
Genetic EJects of Atomic Bomlos Chapter VI
dealing with a variate of the presence-absence
variety, say, presence or absence of malforma-
tion, classified by sex and city. Our data, then,
form an array of eight cells, and we shall
denote by niJk the observed number of indi-
viduals and by ptjk the true proportion, under
any given hypothesis, of observations in the
(ijk)-th cell where i=1, 2; j=1, 2; and k=l,
2, and where i, j, and k are, respectively, the
classifications with regard to sex, city, and the
variate under study. In such a table, there are
only seven comparisons with regard to k which
can be made, namely, (1) the influence of sex
and city on the variate (ij with k), (2) the
influence of sex on the effect of city on the
variate (j on k among i), (3) the influence of
city on the edect of sex on the variate (i on k
among j), (4) the influence of sex on the
variate for each city (i with k for each j), (5)
the influence of city on the variate for each sex
(j with k for each i), (6) the influence of sex
on the variate when cities are pooled (i with k
ignoring j), and (7) the influence of city on
the variate when sexes are pooled (j with k
ignoring i). Let us now examine each of these
comparisons in terms of their meaning and the and
tests which they afford.
(1) The znfner~ce of sex and city on the
where now
variate. Under this comparison we are con-
cerned with whether the variate is independent
of the sex-city cell, or, alternatively stated,
whether the variate is distributed homogene-
ously over the sex-city cells. The null hypothesis
in this instance is
Ho pijk = pi]. p..k
and asserts that the variate has a uniform distri-
bution over the sex-city cells, that is, that the
ratio of individuals in category k = 1 to the
individuals in category k = 2 is the same in each
sex-city cell. This hypothesis affords the basis
for a test which might be termed "total x2,'' and
which is, in effect, an omnibus test of the effect
of city and sex including, of course, interaction.
Non-significance implies no effect of city or
sex. The degrees of freedom associated with this
test are 3. In general, if i=l, . . .r; j=l, . . .s,
and k=l, 2, then the degrees of freedom are
(~-1~.
(2) and (3) The influence of sex or the
efect of city on the variate, or the in5~e?~ce of
city on the ef ect of sex on the variate. The
null hypothesis is now
H . P,2,Pi'~ _ P22~P'
PotoP, oo P2'tPt2,
and asserts that the variate has the same distribu-
tion with respect to cities for all sexes (or sexes
for all cities). This hypothesis affords the basis
for a test which we shall term a test of "inter-
action," or more specifically, the "interaction
of sex with city (or city with sex) ." Non-signifi-
cance at this level does not imply no effect of
sex or city, but merely that the effect of city is
the same over all sexes (or sex over all cities).
The degrees of freedom associated with this
test are 1, or for the general case (r-1 ) (s-1 ) .
This use of the term interaction appears to be
due to Bartlett (1935 ~ .
(4) and (5) The irzldaence of sex on the
variate for each city, or the influence of city on
the variate for each sex. Under this compari-
son we are concerned with whether the variate is
homogeneously distributed over sexes for each
city (or cities for each sex). It is important to
note that the null hypotheses, which are
Ho: ptik = pti.P., k
and
pi2k = pit. p.2k
Pijk = P~i.Pt.k
P2ik = p2 j. p2.k,
Pow = ~Pl2k = 1 (or Sheik = ~P2ik = 1 ),
Ok Ok jk jk
do not specify that the variate must have the
same distribution over sexes for all cities (or
cities for all sexes). This hypothesis affords
the basis for a test of the effect of city (or sex)
on the variate for each sex (or city). There can
be as many such tests as there are sexes (or
cities). The degrees of freedom associated with
each test are 1, or in general (rl-1 ), (r2 - 1 ),
etc., where r, = rat = . . . = r. The x2's associated
with these individual tests are additive; the sum,
however, confounds "main effects" and "inter-
action."
(6) and (7) The variate with sex, or the
variate with city. Under this comparison we
are concerned with whether the variate is dis-
tributed homogeneously over all sexes neglect-
ing cities (or all cities neglecting sexes). The
null hypothesis which is
Ho pt.k = Pt..P..k
or
p.jk= p.j.p..k
asserts that the variate has the same distribution
over the sexes neglecting the cities (or over

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Statistical Methods
cities neglecting sexes). The hypothesis affords
a test of the effect of sex (or city) on the
variate assuming (1) no main effect of city (or
sex), and (2) no interaction between sex and
city. This we shall term a "main effects" test.
The degrees of freedom associated with this
test are 1, or in general (r-1) or (s-1~.
We shall now turn our attention to the ap-
propriateness of these tests as illustrated by the
analyses of the Japanese data. Essentially we
are concerned with testing (1) whether sex has
an effect on our variate independent of cities,
(2) whether city has an effect independent of
sex, and (3) whether the effects of sexes and
cities can be considered independently. Or, to
use the language of the analysis of variance, we
are concerned to measure (1) the main effect
due to sexes, (2) the main effect due to cities,
and (3) the interaction of sex with city. The
procedure for testing, which we shall outline
as it would occur in the three-way table we have
used for illustrative purposes, is quite general
and can be extended to an '~-way table. The
procedure is as follows:
1. Test the hypothesis of "no interaction" of
sex and city with the variate.
2. If the hypothesis of "no interaction" is ac-
cepted, then
(a) Test the hypothesis of "no main city
effect," ignoring sex.
(b) If the hypothesis of "no main city ef-
fect" is accepted, then test the hypothesis of
"no main sex effect" ignoring city.
(c) If this hypothesis is also accepted, then
we may accept the general hypothesis of no
main effects and no interaction.
(d) If the hypothesis of "no main city ef-
fect" (ignoring sex) is rejected, then a test
of the sex effect may be influenced by the
city differences. We are free to test the hy-
pothesis of "no main sex effect" ignoring
city only if cities are equally or proportionally
represented among the sexes. If this does not
obtain, that is, if the cities are disproportion-
ately represented among the sexes, then any
differences in sex when city is ignored are
apt to be attributable to the differences be-
tween cities. Unless these city differences are
taken into account, a test of the effect of sex
confounds the effect of city. One possible way
of getting around this problem is to consider
the hypothesis of "no main sex effect" at
each city level. The test of this hypothesis is
81
a As which is the sum of the As tests at each
city level, with appropriate degrees of free-
dom (the sum of the individual tests). We
shall term this test the "sum test" of sexes.
This test will answer the question "Is there a
main effect of sex on the variate, assuming
no interaction of sex with city but a possible
contribution of city?" By this procedure we
may pick out the levels of city which con-
tribute most heavily to the total x2. We will
refer to this test as a test of the sex effect
adjusted for cities, the "adjustment" being
merely a consideration of the sex effect at
all possible levels of cities. In the absence of
an interaction, this will be our best test of
the sex effect.
(e) If the hypothesis of "no sex effect"
ignoring cities is rejected, we follow the same
procedure as outlined in (d).
(f) If both hypotheses, namely, "no main city
effect" and "no main sex effect," are rejected,
we follow the procedure outlined in (d) for
both effects. This would yield two sets of
tests. It is important to note that the As and
degrees of freedom are additive within gels
bolt riot between sets.
3. If the hypothesis of "no interaction" is re-
jected, then the tests of sex ignoring city, and
of city ignoring sex may be biased. Accordingly,
our procedure will be as follows:
The effect of sex will be evaluated at each
level of city, and city at each level of sex. Here,
however, the "sum test" obtained by the addi-
tion of the two X2 tests of sex (one for each
city) or the two X2 tests of city (one for each
sex) is not a meaningful test of the main effect
due to sex or city. This stems from the fact that
the presence of an interaction reveals a signifi-
cant inconsistency in the direction of the effect
of the ways of classification on the variable.
Otherwise stated, the "sum test" as a test of
main effect is not meaningful because it con-
founds interaction.
In Chapter V, and in the chapters to follow,
we have adopted the convention of indicating
(1) each of the individual tests whenever ad-
justment is necessary, and (2) the "sum test"
only when the "no interaction" hypothesis is
accepted.
The adjusted tests in 2(d), (e), and (f)
above are somewhat analogous to adjusted tests
in the analysis of variance in the sense that

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82 Genetic Efects of Atomic Bombs Chapter VI
though the degrees of freedom are additive, the
x2's are not. Thus in (d) we will have
Source
city (unadjusted)
sex (adjusted)
Total
and for (e) we will have
sex (unadjusted)
city (adjusted)
Total
D F
(s-l)
s(r-1)
(rs-1)
Source D F
(r - 1)
r(s-1)
(rs - 1)
In the e-way classification, the interaction
hypotheses are more numerous. For example, in
a four-way table with dimensions h, i, i, and k,
we have
"First order interactions"
(1) ~ on k among i
(2) h on k among j
(3) i on k among j
"Second order interactions"
(1 ) ~ on k among i among I.
While the procedure for testing outlined in the
previous pages can be so extended that our ini-
tial test is a test of "no second (or higher)
order interaction," we shall in the analysis to
follow assume, in general, that all interactions
higher than the first are not significant. The
validity of this assumption can, of course, be
questioned. In the event that serious ambiguity
in the interpretation of "main effects" or "first
order interactions" might arise through ignor-
ing the higher order interactions, then the
second order interactions will be explored. In
view of the great amount of labor involved in
the calculation of the first order interactions,
involving in this case simultaneous cubic equa-
tions with one unknown for each degree of
freedom, the Michigan Digital Automatic Com-
puter has been utilized.
The above outlined procedures are, obviously,
not the only possible approaches to these data.
However, the logical basis for some of the al-
ternative, simpler methods, such as Brandt's
factorial chi-square, have not been set out in
detail in the statistical literature. Other alterna-
tives which will find favor in some quarters are
(1) to transform the attribute data and employ
an analysis of variance on the transformed
variate (see Eisenhart, 1947, or Rao, 19 5 2 ), or
(2) to attempt a regression form of analysis of
the indicator on dose of irradiation. With re-
gard to the latter, we believe this approach is
fraught with danger for at least two reasons.
Firstly, the estimates of average dose in each of
the five categories of parental exposure are most
tenuous, and secondly, even if these estimates
are reasonably reliable the distribution of doses
within a given category of exposure is unknown.
In the latter connection, it seems most probable
that in many, if not all, exposed cells the median
dose will be less than the mean dose (judging
from the distance distribution of survivors).
Be that as it may, for the data to follow on sex
ratio, malformation, stillbirth, and neonatal
death, one or more of these alternative methods
of analysis was routinely performed. Since these
alternatives did not give rise to results differing
substantially from those obtained by the method
of Roy and Kastenbaum, the results of the al-
ternative analyses will not be presented.
The use of chi-square as a test of significance
in the procedure outlined here requires certain
assumptions regarding the distribution of X2
where
(Xi-mi) 2
=~
-i mi
and where xi and mi are respectively the ob-
served number in a cell and the expected num-
ber based on some null hypothesis. Cochran
(1952) has discussed these assumptions in con-
siderable detail, and has formulated a number
of operating rules regarding the minimum ex-
pectation in a cell. One of these rules, on which
we shall draw heavily, is concerned with tables
with more than 1 degree of freedom and some
cells with expectations greater than 5. Cochran
asserts that x2, without correction for continuity,
is a satisfactory approximation in this instance.
In instances where the expectation in a cell was
less than two, the effect of this cell on the total
chi-square was carefully noted. When the total
chi-square was significant and due in large
measure to a single cell with an unusually small
expectation, an alternate scheme of classification
was employed to increase the expectation in the
various cells.
6.6 The Catalysis of the measurement data.
In general, in the analysis of the measurement
data, that is, the data with respect to birthweight
and the anthropometric measurements obtained
at 9 months of age, we have had occasion to

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Statistical Methods
employ three common statistical procedures,
namely, the analysis of variance, the analysis of
covariance, and the analysis of dispersion. As is
frequently true when one passes from a theo-
retical consideration of a test of significance to
the application of such a test to a body of data,
certain of the assumptions underlying the test
cannot be met in the strict sense. It seems ap-
propriate, therefore, that we consider the as-
sumptions underlying the tests here employed,
indicating where the data do not or may not
satisfy the assumptions, and then to discuss
briefly the variations of the basic tests necessary
to meet certain problems posed by these data.
Firstly, let us consider the analysis of variance
when there exist multiple ways of classification.
In the classical test of the significance of the
differences in a set of k means associated with
a main effect, we make four basic assumptions
in order to test the null hypothesis that m,.=
m2 = . . . = me, namely,
1. that the observations in a cell (for all cells)
are values of random variables distributed about
a true mean which is a fixed constant;
2. that the true cell means are simple additive
functions of the corresponding marginal means
and the general mean;
3. that the observations are uncorrelated, and
have equal variances; and
4. that the observations are jointly distributed
in a multivariate normal distribution.
For a detailed consideration of these assump-
tions the reader is referred to Eisenhart (1947~;
we shall concern ourselves merely with the
validity and importance of these assumptions
as they bear on the Japanese data. Assumption
(1) needs no comment since it is basic to any
statistical analysis, in a sense, and is merely an
assertion that we are dealing with random vari-
ables. Assumption (4), which to some extent
impinges on assumption (1), is probably not
strictly satisfied in the Japanese data. In general,
it has been found that variables such as height,
weight, etc., are non-normal; however, the de-
parture from normality is generally not su~-
cient to jeopardize seriously the validity of the
test. Moreover, the analysis of variance is known
to be very insensitive to non-normality (see
Box, 1953~. From the purely practical stand-
point, assumptions (2) and (3) are the most
troublesome. Assumption (2), the assumption
of additivity, disallows the possibility of inter
83
actions. Alternatively stated, if additivity does
not prevail then we assert that there are inter-
actions between the ways of classification; how-
ever, when additivity does not prevail, we can
still obtain a test of the main effects. The princi-
pal effect of non-additivity rests in the altera-
tion of the model from which the effects of
classification are estimated, and the generaliza-
tions of which the new tests will admit. As an
illustration, suppose we have a variable, xij,
which we shall assume is normally distributed.
Suppose, moreover, that a given observation can
be classified with respect to properties A, and
properties B. The additivity assumption asserts
then that the expected value of x in the (ij)th
cell is
E(xij) =m+A~+Bj,
that is, that the expected value is a linear func-
tion of the true general mean, the effect due to
A, and the effect due to B. Alternatively, if
additivity does not obtain, then the expectation
in the (if) cell is
E(Xij) =m+A~+Bj+ (AB)ij,
that is, the expected value is a function of the
general mean, of A, of B. and a function of A
and B taken conjointly. In the orthogonal case
of the analysis of variance, whichever of these
hypotheses obtains, the computation of the
sums of squares due to interaction and to main
effects remains the same. The difference between
the models enters the picture only in the forma-
tion of the appropriate variance ratio, and its
interpretation. If additivity prevails, then our
test of the main effect due to A, say, is the ratio
of the mean square due to A to the mean square
within cells (error mean square). If additivity
does not obtain, then we may make the com-
parison just stated or we may compare the mean
square due to A with the mean square interac-
tion. The former test would permit us to draw
inferences with respect to A only over the cir-
cumstances which obtain with respect to A in
this experiment. The latter ratio would permit
us to make broader statements regarding the
effect of A. For example, if the effect of
mother's exposure was judged by the ratio of
the mean square due to mothers to the mean
square within cells and if an interaction involv-
ing mothers and, say, cities obtained, then we
could make statements regarding mother's ex-
posure only with respect to the situation ob-
taining in Hiroshima and Nagasaki. On the

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84 Genetic Ejects of Atomic Bombs Chapter Vl
other hand, if our contrast involved mother's
exposure and the interaction of mothers and
cities, then our statements with respect to the
effect of mother's exposure would apply to other
cities subjected to the same exposure conditions
experienced by these two cities and where these
other cities may be assumed to fulfill the re-
maining experimental conditions. While both
of these comparisons have meaning, in general
we shall be concerned with the broadest possible
statement regarding mother's effect. It might be
noted that the use of the interaction to test main
effects is not good when the cell numbers are
unequal (either proportionate or disproportion-
ate). For a more complete discussion of this
aspect of the analysis of variance the reader is
referred to Fisher (1949~.
Assumption (3) may be violated because the
observations within a cell are correlated, or the
variances are unequal, or both. If the variances
are unequal and if we are contrasting but two
means, we face the classical Fisher-Behrens
problem (Fisher, 1939~. For our purposes two
comments here seem sufficient. Firstly, it is not
inconsistent to test the same body of data under
the hypothesis that the means are equal and the
variances are equal, and under the hypothesis
that the means are equal but the variances un-
equal (the Fisher-Behrens problem). Secondly,
the work of Box (1953, 1954 a and b) sug-
'gests that the test of the equality of a set of
means is not seriously affected if there exists
only a moderate inequality of the variances and
if the cell numbers are equal ("moderate" en-
visages an inequality of the variances wherein
the larger is three times the smaller). Much
larger discrepancies, however, arise if the same
moderate inequality exists, and if the cell num-
bers are markedly unequal. The inequality of
the cell entries becomes less important as the
differences in the variances diminish. When an
inequality in the variances exists in these data,
this inequality is small and can be ignored with-
out seriously jeopardizing the inferences which
may be drawn from the tests on the means.
Thus far we have considered only tests on the
means; needless to say, we shall also be inter-
ested in testing the equality of the variances.
The assumptions for a valid test of the variances
are less numerous. We merely assume that we
are dealing with values of a random variable
which are normally distributed and uncorre-
lated. Comparison of the variances of a series of
exposure cells has meaning, however, only if
all extraneous sources of variation which may be
dissimilarly distributed between the exposure
cells are removed. To see that this is true will
be a matter of prime concern in the succeeding
chapters.
The assumptions for a valid test of the
equality of variances and means set out in the
preceding paragraphs have been phrased in a
manner appropriate to the univariate case. By a
slight extension, these assumptions are equally
valid for the multivariate case wherein we ana-
lyze the dispersion of a set of observations.
Specifically, in the multivariate case we shall be
concerned with testing two hypotheses, namely,
1. The equality of the dispersion matrices of k
p-variate normal populations
H :== ·~. =>
and where hi is the variance-covariance matrix
in the ith class.
2. The equality of k means for each of p vari-
ates for k p-variate normal populations with
the same covariance matrix.
Ho:~=42= ·-. =(ke
The (i are now vectors of means.
The approach to these data which we have
outlined in this and the preceding section calls,
in essence, for the use of so-called "omnibus"
or "portmanteau" tests.2 Not all readers will
subscribe to this since omnibus tests tend to be
less sensitive with respect to a particular com-
parison than a more specialized test. The pri-
mary justification for the omnibus test is, in
our minds, the fact that such a test does not
require the measure of specification of the al-
ternatives to the null hypothesis required by a
more specialized statistical tool. It is our opinion
that, with the possible exception of the sex
ratio, our knowledge with regard to the types
of changes which may arise in human beings
consequent to parental irradiation is so poorly
understood as to make any real attempt to
specify direction of change specious. To some
our attitude will seem much too conservative,
and for those readers we would point out that
the more specialized tool is quite useless under
the wrong conditions (Pearson, 1936). Fur-
thermore, since the problem of radiation-in-
duced genetic change in human beings may
2 An omnibus test is generally defined as one that
has good discriminating power with regard to a large
variety of alternatives to the null hypothesis.

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Statistical Methods
well constitute the most important problem in
human biology in our generation, we believe
quite strongly that at this stage our approach
must be an open-minded one which does not
draw too heavily in any particulars upon infra-
human data, the more so because of the great
gaps which exist at present in comparable ob-
servations on laboratory material. The prior
specification of a subset of alternatives to the
null hypothesis required by a specialized test
would imply a greater knowledge of the genetic
effects of irradiation on the indicators here
studied than we are willing to assume.
6.7 Some farther problems. There remain
two more subjects for our consideration regard-
ing the analysis of the measurement data,
namely, within-cell heterogeneity and unequal
numbers of observations within cells. Firstly,
a brief description of what we have elected to
term withirz-cell heterogeneity. It is patent that
so long as the observations within a cell repre-
sent values of a random variable the obsena-
tions will be heterogeneous in the sense that
they will not all be like-values. The heteroge-
neity with which we are concerned is not of this
variety, but rather the heterogeneity which
arises if the observations within a given cell
are drawn at random from not one but several
normal parent populations. We are concerned
with such heterogeneity since it represents a
violation of assumption (3) in Section 6.6. Let
us consider what may happen when this cir-
cumstance prevails. There are two chief aspects
of the problem:
1. The parent populations may differ with re-
spect to the mean, with respect to the variance,
or with respect to both the mean and the
variance.
2. The parent populations may or may not be
represented with the same relative frequency in
each of the several exposure classes. If the rela-
tive frequencies are identical among the several
exposure cells, we shall say the heterogeneity
is "uniform."
What now are the consequences of within-cell
heterogeneity? Let us tabulate the case:
1. Within-cell heterogeneity with respect to the
mean alone.
(a) Uniform consequences
( 1 ) Inflation of within-cell sum of
squares, thus reducing the sensitivity of
the test.
85
(2) Usually a departure of the within-cell
distribution from normality with possible
plurimodality.3
(b) Nor;-~niform consequences
(1 ) Those listed for the uniform case.
(2 ) In the event that the within-cell
heterogeneity arises from concomitant
variation, having nothing to do with ir-
radiation, a spurious heterogeneity of cell
means may be observed, or a true hetero-
geneity of cell means may be concealed.
2. Within-cell heterogeneity due to variances
alone.
(a) Unif orm consequences
(1) Departure from normality (persist-
ence of higher cumulants but no pluri-
modality) .
(2 ) Inflation of within-cell sums of
squares, leading, as before, to a reduction
in the sensitivity of tests.
(`b) Non-ur~iform consequences
(1) Those listed for the uniform case.
(2) In the event that within-cell hetero-
geneity arises from concomitant variation
having nothing to do with irradiation, a
spurious heterogeneity of cell variances
may be observed, or a true heterogeneity
of cell variances may be concealed.
3. Within-cell heterogeneity with respect to
both means and variances.
Consequences
Any or all of those listed above may
prevail.
It is thus clear that within-cell heterogeneity
may lead to any or all of the following:
1. Departures from normality.
2. Inflation of the within-cell sums of squares
with consequent reduction in the sensitivity of
statistical tests.
3. Detection of spurious statistical effect or
concealment of true ones, provided
(a) the within-cell heterogeneity does not
reflect an effect of irradiation itself, but
3 A discussion of the circumstances under which
the combination of Gaussian distributions leads to
plurimodality can be found in Harris and Smith
(~947~. These authors consider the case of but two
parent distributions.

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86 Genetic Efects of Atomic Bombs Chapter VI
rather the operation of some purely con-
comitant factor or factors, arid
(b) the relative frequencies with which the
several parent populations are represented
in each cell are not uniform over all cells.
Clearly, the possibility of within-cell hetero-
geneity has to be explored in all tests, and
wherever important concomitant factors are dis-
covered they must at least be shown to exert a
uniform effect or else be incorporated into the
analysis. To ignore a concomitant variable uni-
formly distributed among the exposure groups
assumes, of course, that the uniformly distrib-
uted variable does not interact with a variable
which may be non-uniformly distributed, and
the inflation of the error sums of squares is
negligible. This topic will be discussed again
in connection with the analysis of birthweight
and anthropometric data.
At. . . . .
/
The analysis of variance (or dispersion) is,
as a general rule, computationally simple and
interpretively straightforward when the num-
ber of observations within a cell is the same for
all cells, or when the number within the cell is
proportional to the marginal totals. This situa-
tion is often referred to as the orthogonal case
of the analysis of variance. Not infrequently,
the numbers within a cell do not satisfy this
stricture of proportionality. When this occurs,
the addition theorem for sums of squares fails
and the usual computational procedures for the
analysis of variance do not yield valid tests of
main effects or interactions. There exist, how-
ever, a number of techniques which are appro-
priate to this situation, among them being the
method of expected subclass numbers (Snedecor
and Cox, 1935; see Snedecor, 1946), the
method of weighted means (Yates, 1934), and
the method of "fitting constants" (inter alla
Wilks, 1938~. In our analysis, we shall have
frequent occasion to employ the method of fit-
ting constants as described by Wilks, and logical
extensions of this method appropriate to the
multivariate analysis of dispersion. In the analy-
sis of the anthropometric data we shall employ
a procedure devised by Rao (1955) which has
the added advantage of permitting one to find
the standard errors of differences in the esti-
mated constants. While this technique allows
for the fact that the cell numbers are dispro-
portionate it does not create additivity among the
tests of main eRects or interactions. There is a
valid test for any set of main effects which can
be used irrespective of the presence of interac-
tion but such tests would confound interaction
if present. For a more complete discussion of
the problem of unequal cell numbers the reader
is referred to Kendall (1946~.
In the normal procedure in the analysis of
variance for the non-orthogonal case, one would
begin by inquiring into the presence or ab-
sence of interactions and, frequently, at the
same time estimating main effects under the
additive assumption. Main effects so estimated
provide, as we have mentioned, only approxi-
mate tests if an interaction is present. If an
interaction is present and a more accurate test
is desired, the main effects must be estimated
anew from a model in which the interaction is
now accounted for. Often, however, approxi-
mate tests of the main effects may suffice if the
primary concern is to ~ establish heterogeneity
between cells and not to inquire exhaustively
into the main effects. We have, in Chapter V,
frequently settled for approximate tests on the
main effects because the presence of an inter-
action no less than main effects differences
reveals heterogeneity between exposure cells.
6.8 The me of exposed persons as controls.
We have indicated that in the analysis of
the data with respect to the various indices of
radiation damage a variety of tests will be
presented. Specifically, we have stated that
analysis will be presented in which either (1)
concomitant variation is ignored, or (2) major
sources of concomitant variation are accounted
for. To this list we now shall add a third com-
parison and indicate its purpose.
It has been stated that each parent of a regis-
tered infant has been placed into one of five
exposure categories depending upon his or her
position relative to ground zero, to the amount
of shielding between the parent and the ex-
plosion, and to the array of symptoms experi-
enced or not experienced following the bomb-
ing. When both parents are considered, then a
given registered infant can be assigned to one
and only one of twenty-five exposure cells.
Unfortunately, the numbers of terminations to
parents one or both of whom were in exposure
categories 4 or 5 are so small as to necessitate
pooling of these exposure categories. Accord-
ingly, in the analysis to follow, an infant will
have been assigned to one and only one of
sixteen exposure cells wherein the appropriate
cell was determined by whether the mother was

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Statistical Methods
in category 1, 2, 3, or 4-5, and similarly for
the father.
It will be recalled that exposure category 1
includes those individuals who were not present
in Hiroshima or Nagasaki at the time of the
atomic bombings. In Chapter ~ we have ad-
vanced reasons for doubting whether category 1
parents afford an entirely valid comparison with
those parents who experienced some measure of
exposure to the bombs. If exposure 1 parents
are not an "adequate control," then the only
meaningful comparison which can be made to
determine the effects of irradiation on our
indices of genetic damage would be a compari-
son involving only those infants where both
parents were present in the city at the time of
the detonation of the bomb. Moreover, even if
one accepts the validity of the comparison
utilizing category 1 parents, a real irradiation
effect would also lead to differences among the
terminations to 2, 3, and 4-5 parents. For these
two reasons, in the analysis of the indicators
there will be presented two analyses, one
wherein the parents one or both of whom are
in category 1 are excluded, and one where they
are included. It should be pointed out at this
juncture that the differences which we can de-
tect by statistical procedures are largely a func-
tion of sample number. Accordingly, it may be
that differences demonstrable in the 4 x 4
comparison including category 1 parents will
87
not be demonstrable in the 3 x 3 comparison
excluding these parents solely because of the
curtailment of sample size occasioned by the
exclusion of the category 1 parents. The differ-
ences among the remaining exposure cells
brought about by exposure. while no longer
significant, should, of course, persist even fol-
lowing exclusion of the category 1 parents.
6.9 Preser~t~io'~ of material. It would be
highly desirable in a problem of this nature to
present in detail the tabulations on which the
various analyses are based. However, these
tabulations are extremely bulky, requiring, even
for presentation in a somewhat condensed form,
an estimated 1,000 pages. Moreover, because
of differences in statistical approach, many in-
vestigators might wish for tabulations other
than those presented. Under the circumstances,
it would seem that the matter of making avail-
able the raw material of this study is best met
by the following procedure: the investigator
who desires to verify some of the calculations
presented in the following chapters, or to ex-
plore other lines of analysis, can apply to the
Division of Biology and Medicine, U.S. Atomic
Energy Commission, or the Committee on
Atomic Casualties, National Research Council,
for a duplicate set of the IBM cards on which
this analysis is based. The investigator must be
prepared to meet the costs of duplicating the
cards and all shipping charges.
O ~1 '