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Chapter VI STATISTICAL METHODS 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. â 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. 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 and the problem of non-overlapping measurements. â Among the numerous measurements or at- 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 io 72

Statistical Methods 73 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 signifi- 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 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 w-dimensional surface formed by groups of probabilities of Â» 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 variation. â 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 Total observations within an exposure treatment Indicator: Male Female Sex Ratio ("Stillborn fNeonatal fNo malformation IT- 1 II , H death [Malformation ^Liveborn . . . No neonatal I death ?â¢ Birthweight rStillborn {Neonatal death No neonatal death fNo malformation |_Liveborn . . . [Malformation o Malformation |- Birthweight Birthweight Stillbirths Neonatal Death FIGURE 6.1 â 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 V 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

74 Chapter VI Genetic Effects of Atomic Bombs 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 /'= 1, 2 p, designates the group, ;= 1, 2, . . . , HJ, designates the indi- vidual within a group (2Â»i=Â»), Â»v< = the intercept of the /'* group, j84=the regression coefficient of the ;'* group, and Â£y= random, independent errors with vari- ance a3. Within this model, we may work out the expec- tations of the following quantities: (1) The mean square for y after correction for the group means but not for regression on x. This quantity would be 22 (?â->.)2 (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 22 (*,->,) VI2 1 y^J J (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 *(J>-jM-\~] >â-Â»,),' [J If now we let and 2)3*2 (*Â«- < I We find the expectations for a given set of xij to be E ( jeÂ») = E(s*) =* Jo Â« - To â Jo i i y - x4) * Now, if we define the second and third terms of E(s02) as (rd2 and (702, we can write Or, since /â/(/(,â 1) is essentially unity, we could in the above have written with little error n-p An objection could be made, of course, that the meanings of ad2 and ac2 depend upon the sample pattern of the xtj. Let us assume, how- ever, (a) that the sample of size Â« = 2Â»4 was drawn from a population of size N which divides into f> groups with N, individuals in a

Statistical Methods 75 group, (b) that the within-group variance of x is ax2 in all groups, (c) that the sample is random and large with the restriction (d) that â /. N' In this event, stable meaning can be given to (7d* and acz. Define Now v= and '"'â¢ ' /â N Clearly under the assumptions and restrictions just given, /3=j80 to a close approximation and {s (*<,- S Then we see that to a close approximation 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 â.J ft 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 The percentage ascribable to between-group variation in the relation to x is obtained by computing 100(L, â = per cent of the variation re- maining after correction for group means that is ascribable to the common regression, and = per cent of the variation re- maining after correction for the group means and common regression that is ascribable to the different regressions. When and L2 are near unity, as in our data, lOO^-l) and 100(1,,â 1) differ but negligibly from 100 (I^âl)/!^ and 100 (L2 â 1)/L2, and we shall employ the former. If Lx and Z,2 differ materially from unity, then 100 (Lt - 1 ) /Lt 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(1,t â 1) and 100(L2 â 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 offspring. 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

76 Chapter VI Genetic Ejects of Atomic Bombs 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) Consanguinity. â Among these data over 90 per cent of the observations represent observations on pregnancies occurring to unre- lated parents. Thus, if warranted, all preg- nancies occurring to consanguineous unions could be excluded without an exorbitant loss of 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 and parity. â 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 of covariance. (3) Economic status. â 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 and curettage. â 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 concepti. 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 differences 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. (5) Positive serology. â 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. â 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.

Statistical Methods 77 (7) Repeat registrations. â 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 Rejected observations. â As would be surmised in a study of this kind, there 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 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.1 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 Hiroshima Nagasaki Unregistered births 2,372 892 Registered births Consanguinity 2,184 2,979 Induced terminations where birthweight less than 2,500 gms 379 338 Unknown birthweight 274 209 Unknown parity â 2 Gestation less than 21 weeks, or unknown and infant less than 2,500 gms 149 44 Unknown sex 4 8 Unknown maternal age â â Unknown distance 177 164 Exposed in one city, now residing in other city... 52 152 Total 5,591 4,788 (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- peared 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.

78 Chapter VI Genetic Effects of Atomic Bombs 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 analysis of the attribute data. â 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 2x2x2 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 can 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

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 Hiroshima Nagasaki Total Total infants seen 38,421 38,205 76,626 â â â Rejected because the pregnancy was unregistered, parental exposure was unspecifiable, consanguinity or other obser- vations were incomplete (see Table 6.3) â â â 3,478 1,868 5,346 Considered for consanguinity 34,943 36,337 71,280 â â â Rejected consanguinity â â â 2,113 2,920 5,033 Considered for maternal age 32,830 33,417 66,247 â â â Rejected multiple births â â â 365 451 816" Considered for sex ratio 32,465 32,966 65,431 â â â Considered for malformations.... 32,465 32,966 65,431 â â â Rejected malformations â â â 313 281 594 Rejected congenital heart dis- ease â â â 44 53 97 Total â â â 357 334 691 Considered for stillbirths 32,108 32,632 64,740 â â â Rejected stillbirths â â â 472 482 954 Considered for neonatal deaths... 31,636 32,150 63,786 â â â Rejected neonatal deaths â â â 414 480 894 Considered for birthweights 31,222 31,670 62,892 â â â 'In 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 OBSERVATIONS WITH THE CAUSE OF REJECTION Available observations Rejected observations Hiroshima Nagasaki Total 3,422 1,882 5,304' 694 828 1,522 140 308 448 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 â â â Total infants considered under the 9-months program 11,346 10,442 21,788 Rejected consanguinity â â â Rejected incomplete measure- ments â â â Considered for neonatal death... 10,512 9,306 19,818 â â â Rejected neonatal deaths â â â 484 458 942 Considered for malformation 10,028 8,848 18,876 â â â Rejected malformations â â â 183 195 378 Considered for anthropometrics... 9,845 8,653 18,498 â â â â¢ 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.

80 Chapter VI Genetic Effects of Atomic Bombs 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 nijlc the observed number of indi- viduals and by pljk the true proportion, under any given hypothesis, of observations in the (//Â£)-thcell where /'=1, 2; ;=1, 2; andÂ£=l, 2, and where /', ;', 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 (/; with k), (2) the influence of sex on the effect of city on the variate (;' on k among /), (3) the influence of city on the effect of sex on the variate (/ on k among ;), (4) the influence of sex on the variate for each city (/ with k for each ;'), (5) the influence of city on the variate for each sex (;' with k for each i) , (6) the influence of sex on the variate when cities are pooled (/' with k ignoring ;'), and (7) the influence of city on the variate when sexes are pooled (; with k ignoring /') . Let us now examine each of these comparisons in terms of their meaning and the tests which they afford. (1) The influence of sex and city on the variate. â 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 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 /=1, . . .r; ;'=1, . . .J, and k = l, 2, then the degrees of freedom are <Â»-l). (2) and (3) The influence of sex on the effect of city on the variate, or the influence of city on the effect of sex on the variate. â The null hypothesis is now ei . 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 (râ 1) (sâ 1). This use of the term interaction appears to be due to Bartlett (1935). (4) and (5) The influence of sex on the variate for each city, or the influence of city on the variate for each sex. â 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 Ha'-pMl=pil.p.lk and or and where now S A ik = SM = 1 (or Spllk = ifc Ik fk 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 (rt â 1), (rx â 1), etc., where rl = r.i â . . . = 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. â 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 or p.ik=p.j.p..k asserts that the variate has the same distribution over the sexes neglecting the cities (or over

Statistical Methods 81 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 (râ 1) or (j â 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 c msidered 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 w-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 a x2 which is the sum of the ^ 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 %-. 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 x2 and degrees of freedom are additive within sets but not 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

82 Chapter VI Genetic Effects of Atomic Bombs though the degrees of freedom are additive, the x2's are not. Thus in (d) we will have Source D F city (unadjusted) sex (adjusted) Total ("-l) and for (e) we will have Source D F sex (unadjusted) city (adjusted) Total (r-1) (rs-l) In the Â»-way classification, the interaction hypotheses are more numerous. For example, in a four-way table with dimensions h, i, j, and k, we have "First order interactions" (1) h on k among / (2) h on k among ;' (3) / on k among ; "Second order interactions" (1) h on k among /' among ;'. 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, 1952), 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 and where xl 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 ^2, 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 analysis of the measurement data. â 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

Statistical Methods 83 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 m1 = mt= ... =mk, 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 suffi- 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- 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, *,j, 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 (/;') th cell is 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 (/;) cell is 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

84 Chapter VI Genetic Effects of Atomic Bombs 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 />-variate normal populations and where 2j is the variance-covariance matrix in the /'* class. 2. The equality of k means for each of p vari- ates for k />-variate normal populations with the same covariance matrix. The |, 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 - 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.

Statistical Methods 85 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 further problems. â 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 within-cell heterogeneity. It is patent that so long as the observations within a cell repre- sent values of a random variable the observa- 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. (2) Usually a departure of the within-cell distribution from normality with possible plurimodality.3 (b) Non-uniform 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) Uniform 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-uniform 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 â or concealment of true ones, provided (a) the within-cell heterogeneity does not reflect an effect of irradiation itself, but 8 A discussion of the circumstances under which the combination of Gaussian disttibutions leads to plurimodality can be found in Harris and Smith (1947). These authors consider the case of but two parent distributions.

86 Chapter VI Genetic Effects of Atomic Bombs rather the operation of some purely con- comitant factor or factors, and (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. 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 alia 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 effects 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 use of exposed persons as controls. â 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

Statistical Methods 87 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 V 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 not be demonstrable in the 3x3 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 Presentation of material. â 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.