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Prepped by Ollie Stewart 

Document Number: 

7)11-1-128 

Docket Number: 

A-83-22 

Printed 4/18/2008 9:58:21 AM Sheet 7 of 182 

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- -£>, 

£GAO-CD-y/-^ 

JZCA.<£. c. I- 3o 

ir~x~ I *&• 

Claire B« Ernhart 

February, 1984 

Comsies&ts 

WL. 

Chapter 12 

Air Quality CrifcErSLa for Lead 

Previous reviews covering various pojrtifoms of this material have been 

provided to EPAo Copies of these are appended* lather than repeating 

portions of these, they will be referred to by tlbeir dates and page numbers 

as Indicatedo 

Note: Recommended inserts in text are inddaafted by underlines, deletions by 

brackets. 

Section Page Para. Line 

12.4.2 41 3 14-15 

12.4.2 41 4 4 up 

12.4.2.2.1 52 1 10-11 

12.4.2.2.2 54 3 13 

12.4.2.2.2 54 3 18 

12.4.2.2.2.1 

Recommend deletion of the Cowan and 

Leviton,1980 and Needleman and Landrigan, 1981 

references since they cite methodologically 

poor research as examples of sound techniques. 

Change multiple comparisons to regression 

analysis. Cohen and Cohen, 1983, new edition. 

"It should also lead exposure." There is 

not sufficient evidence to substantiate this 

statement. See discussion of studies below. 

...growing evidence indicates that moderately 

high lead exposures not leading to diagnosed 

[overt] lead Intoxication..." describes the 

available <2^idence more accurately. 

Seven criteria were listed on p. 41. Inappropriate generalization and interpretation 

characterizes--a number tof the studies. Failure 

to Isolate decision raaking about, say,- Inclusion or exclusion of subjects, from knowledge 

of other features of th® aSata can lead to 

serious bias. 

See My Jan. 83 review, j>.7 and April 82, p. 7. 

The analyses of data are limited with 

continuous variables truncated. This leads to 

oddities, such as a significant finding for 

Full Scale IQ but not for Verbal or Performance 

IQ. Cutting variables Jin this way can lead to 

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' I 

fortuitous results. Perhaps more Importantly, 

covariates are not controlled. Given small 

effect sizes, the Inclusion of the maternal 

intelligence measure in analyses might have 

eliminated statistical significance. This is t 

one of those studies in which what is not ••;,* | 

included is of interest. Uhy;dld the inves ti-**"*" 

gators not present results'relating the dentine 

lead measures and the outcome variables? The 

longitudinal data set is appropriate for the 

purpose. Omissions can cover discrepant 

findings. 

12.4.2.2.2.1 60 2 3 up Jan. 83, pp. 2-4. Example of stretching. 

12.4.2.2.2.1 61 2 14 More stretching. In this case, there were a 

large number of tests. 

12.4.2.2.2.1 61 3 Perino-Ernhart. See appended memorandum. 

12.4.2.2.2.1 62 2 Ernhart et al. See appended memorandum. 

12.4.2.2.2.1 63 3 12 up The consistency found may simply be due to the 

limited control of confounding variables in 

most of these studies. Since lead exposure 

tends to be related to other factors that are 

related to poor outcome, limitations in this 

regard will replicate across studies in a way 

that can give the appearance of consistent, 

though small effects. Replication exacerbates 

this kind of bias. What is amazing is that 

there is so little evidence of effect for 

asymptomatic high levels. 

12.4.2.2.2.1 63 3 9 up This is the issue of threshold. See Jan. 83, 

pp. 9-10. 

12.4.2.2.2.2 66 2 6 up Another example of stretching. One of the 

really remarkable things about the Smith study 

is that the sample size is quite large, large 

enough to have the statistical power necessary 

to detect very small effect sizes. As stated, 

p. 67, a larger proportion of tooth doners were 

of a higher social class than non-doners. This 

difference is extremely small and reaches 

statistical significance because of the very 

large sample size. It is an interesting 

incidental finding and does not reflect a 

selection bias that limits generalizability. 

There were more than enough working class 

participants to provide adequate variance to 

detect an effect, given there was one. 

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12o4o2o2o202 67 

12.4.2.2.2.2 68 

12.4.2.2.2.2 68 

12.4.2.2.2.2 69 

3 

2 

3 

1 

1 up 

18 

7 

12.4.2.2.2.2 67 1 10 Hhy bring In Yule and Lansdown, 1983? There 

are no significant social class differences in 

that study. 

12.4.2.2.2.2 67 2 19 The correlations of -0.32 and -0.06 did not 

control for confounding variables. After 

control of covariates, the J_ for lead was less 

than LOO. Stretching again. On Yule and 

Lansdown, see above. 

"approached significance" is not acceptable. 

Stretching again. 

See ray Sept. 82 comments. 

The consistent pattern observed may well be 

nothing more than consistency of covariate 

effects. 

12.4.2.2.2.3 70 2 10 Sept. 82 comments. 

12.4.2.2.2.4 71 1 4 This study is as seriously flawed as others by 

the same investigator. Since it's new, I'll 

step out of this restrictive format to write a 

short comment dated Feb. 84. 

12.4.2.2.2.5 71 3 See Jan. 83, p. 6. 

12.4.2.2.2.5 71 4 See my comments on Otto, Feb. 83. 

13.5.2.2 31 3 5 up I'm not sure I'd agree with this without seeing 

some statement regarding the fact that effects 

at moderate levels, say 30 to 50 pg/dl, given 

they hold up in adequately designed research, 

may be reflecting an earlier higher exposure 

level. See Jan. 83, pp. 9-10 on the issue of 

threshold. 

13.5.2.2 33 2 5 The Otto studies are better than some in this 

area, but calling them "of considerable 

importance*3 is not justified in view of the 

problems in interpreting their results. See 

Feb. 83. 

13.5.2.2 33 3 12 up The only studies reported to date with 

plausible data on persistence of effect are 

those of De la Burde and associates and myself. 

As noted earlier, there are major problems in 

her studies. Wo amount of stretching can lead 

to an interpretation of persistence of effect 

from my early lead measures to the later 

measures of intelligence, behavior and other 

variables. 

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13.5.2.2. 35 2 3 The suggestion in this paragraph that there Is 

increasing evidence of impaired neuropsychologic functioning at blood lead levels below 30 

to 40 Vg/dl is simply not warranted. The 

recent U.K. studies, and particularly the well 

conducted M. Smith research, are important in 

this regard. It's telling, I believe, that the 

better the research, with good control of 

confounding variables, the less the likelihood 

of positive findings. 

13.7.3 43 Table See Jan. 83, p.11. Tou are still reporting 

figures in a way that all urban children within 

the age categories and all potential fetuses of 

urban women are at risk from lead exposure. 

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/£i2flO-(JV-2i-CL 

jLfi.ec /. 30 

Claire B. Ernhart 

February, 1984 

Comments on 

David, O.J., HoffnamD S., & Grad, G. Penicillamine in the treatment of hyperactive children with moderately elevated lead levels. In: Rutter, M.5 

Russell Jones, L , Eds. Lead versus health: Sources and effects of low level 

lead exposure. New York, N.Y.: Riley, 1983, pp. 297-317. 

This is a study of 54 children identified as hyperactive without 

identified etiology for hyperactivity who also presented lead levels in the 

range of 25 to 55 yg/dl whole blood. Data from a group of 14 children with 

histories of lead poisoning were also reported. The group of 54 children was 

divided into three groups with blinded administration over a 12 week period 

of (a) penicillamine and a placebo resembling methylphenidate, (b) 

methylphenidate and a placebo resembling penicillamine, or (c) placeboes for 

both drugs. The group with the history of lead poisoning received the 

penicillamine and the placebo for methylphenidate. The results were 

interpreted as indicating that treatment with penicillamine, which reduced 

blood lead level, also reduced teacher ratings of hyperactivity, parent 

ratings of hyperactivity, scores on an impulsive-hyperactive scale and a 

conduct disorder scale of a parent symptom questionnaire and a rating of a 

physician completed clinical global impression. There are three Major 

weaknesses in this study. 

Regression effects. The subjects were selected on the basis on extreme 

scores on the instruments to be used as outcome measures or correlates of 

these. This fits exactly the situation in which a regression effect leads to 

the appearance of a treatment effect. (See the classic Campbell-Stanley 

monograph on quasi-experimental design.) The situation becomes a bit 

confusing, however, in that children were admitted to study only if the score 

on the TRS hyperactivity scale was greater than 2.5, yet the mean baseline 

scores on this factor shown in Table 3 were 2.2 or 2.3. Maybe another 

administration between selection and start of study was subject to regression 

effects. At any rate, the change attributed to treatment is suspect. 

Random assignment. Aside from the history of lead poisoning group, 

assignment to treatment was described as random, but several exceptions and 

variants confuse the issue. Some children with histories of lead poisoning 

were assigned non-randomly to the methylphenidate or to the placebo group. 

Eight children treated in the first year with methylphenidate or placebo were 

later included in the penicillamine group. (Apparently they entered the 

study twice.) There was a "chance preponderance" in the assignment of 

children to the penicillamine condition in the first two years, leading to a 

disproportionate number in that group. There was a high drop out rate in the 

placebo group. Between group drop out rates are not other wise mentioned; 

differential mortality may be relevant. (Campbell-Stanley.) Statistics 

comparing groups on baseline measures are not provided but we note that 

children assigned to methylphenidate were initially high on the parent rating 

of hyperactivity (Table 4) and children assigned to the placebo control were 

initially rated low on the physician completed global impression scale. 
P.7 

Comments on David, et al., 1983 .2 Claire B. Ernhart 

Statistical analysis. The appropriate statistical analysis would be 

MANOVA of repeated measures of all outcome measures considered as a set. The 

hypothesis of a differential penicillamine effect would then be tested by an 

interaction effect. (This could help take care of the above mentioned 

problem with statistical regression since regression should be similar across 

treatments.) Given significance with this, breakout univariate statistical 

test8 could be justified. Instead we see a large number of t-tests, with 

some reported as significant at .10, one-tail. 
P.8 

£<2fiO(:7>-2/Zj 

Claire B. Ernhart 

February, 1984 

Response to 

Memo Dated November 30, 1983 

from Lester D. Grant 

Subject: Corrigenda for the First External Review Draft 

of 1983 Revised EPA Criteria Document, 

Air Quality Criteria for Lead 

This response is made to the section on Page 3 which indicates a 

aodification of Chapter 12, p.12-62 of the draft of the above Indexed 

document. This modification concludes "Pending resolution of methodological 

problems with the Ernhart data set and/or publication of adequate reanalyses, 

the subject studies are not considered further in this document." 

This statement implies that I failed to conduct the reanalyses suggested 

by the Expert Committee convened to review this study and one other. In 

fact, all reanalyses suggested at the initial review in Inarch, 1983 were 

conducted and further work was undertaken to clarify issues raised in the 

course of these reanalyses. I did not do one additional analysis suggested 

by a Committee member after all other analyses were completed. It is my 

opinion, and I will discuss this again in this response, that the suggested 

reanalysis is irrelevant to the question of whether the data support the 

hypothesis that there are identifiable effects of lead at low levels of 

exposure. 

For the purposes of this document, however, the implication of failure to 

cooperate is less important than consideration of the quality of the data as 

they relate to the questions under review. A manuscript is now being 

prepared for publication of the reanalyses that were conducted. Pending 

completion of this, however, a number of features of the study are clearly 

delineated in the materials provided to the Committee and are relevant to the 

inferences being drawn in the document in preparation. 

I will start with a response to particular items of criticism pertinent 

to my work as listed in Appendix 12-C, November 14, 1983 version. Items not 

mentioned are either not seen as areas of difficulty or the reviewers 

consider the difficulty to be minor. 

It is important to note that many of the suggestions for corrections or 

reanalyses had been made earlier or had been anticipated in the course of my 

reanalyses and that these had been Incorporated into the summary report 

supplied in August, 1983. In some sections of the revised Appendix 12-C it 

appears as if the reviewers copied the August 25, 1983 version (written 

before receipt of my summary report) with little or no consideration of the 

material supplied in the summary report or in my October 7, 1983 memo in 

response to the first version. In general, I appreciate the work of the 

Committee, but the failure to consider the work that I did is disappointing. 

This work was conducted at the request of the Committee and was quite 

pertinent to the issues raised. I can understand the problems facing the 

members of the Committee in the handling of the other study under review and 

the press of time for the preparation of a report. Nevertheless, the 

conclusions drawn with respect to my work bespeak a disinterest in the 

reanlyses requested and supplied. 
P.9 

B. 1, p. 11, (d). As indicated in the the Summary Report, p. 4, item 1, 

lead levels for as many as possible of the children in the follow-up data set 

were corrected. 

B. 2. p. 12, (a). I agree that the Amnions Quick Test is less valid than 

short forms of the WAIS, however administration of even a short form of the 

WAIS would have resulted in an unacceptable and biasing refusal rate. The 

use of the QT was an appreciable improvement in the state of the art for that 

time and the use of even this valid an indicator of parent intelligence was 

not seen in other studies of this topic until some time later. Some degree 

of validity is indicated by its correlation with the other variables in the 

study, including the very fact that stepwise analyses gave it priority over 

all other measures, including parent education. If its reliability was very 

low, it could not have functioned, as it did, in rendering previously 

significant lead effect analyses non-signfleant. If it had been more valid, 

the small variance associated with lead would probably have been reduced even 

further, given the direction of effects in this research. 

B. 2. p. 13, (e). The errors in the Perino data were found and 

corrected. 

B. 3. p. 15. The comments made about statistical analysis are well taken. 

However, the requested statistical analyses with lead and all available 

confounders had been made and reported. See Summary Report, p. 5, item 2. 

B. 3. p. 16. Tests of interaction with the most relevant confounder, 

parent IQ, had been made. See Summary Report, p. 5, item 4. 

B. 3. p. 16, (a). Corrections for unreliability were not undertaken, but 

one technique for coping with this was employed in that a composite index of 

the lead measures was also analyzed. See Summary Report, p. 5, item 3. 

B. 3. p. 16 (c). Only very slight differences would have resulted from 

regressing the school age intelligence test scores on age, as opposed to the 

use of extrapolation. We had analyzed the preschool data using both age 

regressed scores and normed scores and found no difference even though the 

norms for that age range seemed inadequate. Earlier in the review (B. 2. 

p. 14, (d)), the reliability of the scales, even with interpolated scores, 

was considered to be considerable. 

B. 3. p. 16 (d). The fact that the outcome measures were correlated was 

considered, first, in the use of the T2 screening or omnibus analyses for the 

review of the full data set, and, second, in the interpretation of the data. 

The use of multivariate analysis of covariance would have required categorizing subjects into groups on the basis of the lead variables. 

B. 3. p. 16 (e). I certainly agree that it is preferable to keep data in 

a continuous form as opposed to categorization and this is part of the reason 

for using regression analyses. Where the data are categorized, it is usually 

for the purpose of making results clearer to persons not accustomed to 

thinking in terms of proportions of variance, etc. 

B. 3. p. 16 (f). I was not aware that Perino had more high lead cases 

early in the data collection period. His wife had set up the data collection 

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schedule and the numbering scheme. Since he was unaware of the lead levels 

and since he was well trained, I don't think the order had an effect, but it 

wasn't ideal. 

B. 3. p. 17, para. 2-3. This is a aodified version of & more detailed 

suggestion made in the August 25, 1983 Appendix 12-C. I discussed this 

suggestion in my October 7„ 1983 response and I do not feel that oy response 

was given reasonable consideration. 

The critical relationship is between early lead exposure and later 

intelligence. One might also ask if there is a significant relationship 

between early lead and change in intelligence, particularly if there is a 

significant lead effect on the early intelligence measure. And one might 

measure change either as a simple change score, as I did in response to 

Committee suggestion (reported in the Summary Report, p.5, item 5), or by 

regressing the later intelligence measure on the earlier. 

There is no way, however, by which a correlation of two sets of residual 

scores, effectively removing the variance of the early lead measure, can be 

considered to provide a test of lead effects. The fact that blood lead 

levels decrease with age (or, possibly, time) is important; the effects of 

toxic exposure if any, would certainly be greater at the higher level and at 

the earlier age. All the analysis suggested would accomplish might be a 

statement that the extent of the drop in lead level is greater for those 

children who show some increase in measured intelligence and that there is 

less decrease in lead level for those whose Intelligence decreases. Or vice 

versa. 

I thought I had responded quite clearly to this issue in the Oct. 7, 1983 

response to the earlier version of Appendix 12-C and I ara disappointed that 

the opinion of the reviewer in this regard was not clarified more fully. 

There is no question but what longitudinal analysis involving change over 

time, particularly change in the measured outcome variable, is important. 

This is one of the strengths of the study; until the data from the 

prospective studies are available, this is the only study, aside from the De 

la Burde reports, to relate systematically collected early lead measures to 

later intelligence measures. This applies both to the preschool lead 

measures and to dentine lead level as an indicator of early exposure. 

B. 4. The Committee concluded that the blood lead and the psychometric 

measures were adequate, but that confounding measures may not have been 

adequately measured. The measure of parent intelligence must have been 

reasonably valid or it would not have entered data analysis as it did. The 

inclusion of the education measure In data analysis had no effect on the 

results. The data of the Perino study were corrected and were used with the 

1981 data in longitudinal analyses. I believe that the Committee was reeiss 

in failing to consider the reanalyses made and the responses provided in the 

Summary Report, the Response to Appendix 12-C dated October 7, 1983, and my 

letter to Dr. Grant dated October 25, 1983 which would have been received 

prior to the last meeting of the Committee. 

The Yamins dissertation was included in this review and reanalyses were 

made of the data at the request of EPA. This study was not published; we did 

not feel that it was strong enough for publication. If we had been able to 

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correct the blood measures, it might have been feasible to merge these data 

with the Perino data, as indicated on p. 3 of the Summary Report to increase 

the statistical power for cross sectional analysis at the preschool age. As 

it happens, it was rather a waste of time for the Committee to have reviewed 

it in such detail. The Committee Conclusions, p. 21, indicate further that 

the material provided in the Summary Report was not integrated into the 

preparation of Appendix 12-C. 

Conclusions. The quality of the data and the analyses conducted, including 

the reanalyses, in the Perino-Ernhart and Ernhart, et al., studies is 

superior to that of most of the studies treated with credibility in the Draft 

of the Air Quality Criteria for Lead. The dismissal of the findings appears 

to be due to the fact that I challenged the procedures used in another study 

which has been variously described as "classic" or "pioneering." Weaknesses 

in this latter study, and its spin-offs, have been noted by others and a 

careful review of that work was in order. It appears as if my work was also 

subject to review in order to provide an appearance of fairness to the review 

of the other work. 

I did not object since I have nothing to hide and since I felt that this 

would, indeed, facilitate the careful review of the other work. Reanalyses 

were suggested. These were based, in part, on more recently published 

reports regarding problems in the blood analyses used in one of my studies 

and, in part, on suggested variations in data analysis, as the inclusion of 

education as a covariate (though I knew it would contribute nothing) and the 

analysis of change scores. These analyses were done. 

The exclusion of the results of my work from consideration in the Review 

Draft to impart an aura of fairness for the exclusion of a clearly faulted 

work is highly discriminatory. More important than discrimination against my 

work is the exclusion of the findings of that work ln the conclusions to be 

drawn with respect to the effects of low level lead exposure on children. 

Since the Committee failed to'integrate reanalyses into its conclusions and 

simply dismissed the studies as not providing conclusive evidence, it is 

incumbent on me to integrate the findings of these studies. 

Findings of the Perino-Ernhart Studies. 

1. A sample of 80 urban disadvantaged black children with blood lead 

levels ranging from .01 to .07 mg/dl whole blood was tested with the McCarthy 

Scales of Childrens' Abilities. No statistically significant relationship 

was found between lead level and performance on any scale of the McCarthy 

Scales when parent intelligence, birthweight, and parent education were 

entered into the model. This is in contrast to previously reported 

findings. The change is due to an error found in the computation of the age 

of one child and to the previous use of an incorrect terra for degrees of 

freedom in an analysis. Paragraph 3, p. 12-61 of the Review Draft needs 

correction to accommodate these corrected findings. 

2. With this same sample, there is no significant difference between 

moderate and low lead level groups in the correlation of parent and child 

intelligence. This represents a correction of the previous report. The 

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correction is due to the changed intelligence test score for the above 

indicated child. Paragraph 3, p. 12-61 of the Review Draft needs correction 

to accommodate these corrected findings. 

3. Five years later 63 of these children were traced and examined with 

the McCarthy Scales, the Bender Gestalt Test, and several exploratory 

measures. Teacher ratings were obtained and scores on reading tests were 

provided by the schools. The data of one child were excluded on the basis of 

a dentine lead level consistent with frank lead poisoning and clinic obtained 

environmental evidence supporting that inference. 

The most important analyses of these data are longitudinal, i.e., 

determining the possibility of an effect of the early, preschool lead 

exposure index on the later outcome measures. These are particularly 

critical analyses both because lead levels at the preschool period were 

significantly, and appreciably, higher than those recorded five years later 

and because preschool children are considered to be more vulnerable than 

older children to lead effects. Furthermore, persistent effects would 

undoubtedly be more serious than concurrent, but possibly transitory effects. 

The preschool blood lead levels were not significantly related to any of 

the above listed outcome measures, nor were they significantly related to 

change scores computed for the General Cognitive Index or the Verbal Index of 

the McCarthy Scales. (These were chosen for measurement of change since they 

were the most valid, and probably the most Important of the outcome 

measures.) Of particular importance are the measures of intelligence and the 

teacher behavior ratings since these have been related to lead level in some 

of the methodologically -weaker studies. 

4. Another index of early lead exposure, dentine lead level, was available for 33 of the children (with the outlier case excluded). This was not 

significantly related to any outcome measure. 

5. Blood samples had been collected for all children seen at five year 

follow-up. Technical problems in the analyses for lead required correction, 

but the information required for this correction (hematocrit level) was 

available at the time of the reanalyses for only 45 of these children. 

Analyses of the adjusted school age lead level and a lead level exposure 

construct (preschool lead, school age lead, and free erythrocyte protoporphyrin) were made, with parent Intelligence, parent education, and sex as 

covariates. Of the eighteen analyses (six McCarthy Scales, Reading Level, 

and two change scores) one reached significance at the .05 level. A single 

deviant case may have accounted for this one positive finding in the set. 

Because lead effects might be moderated by social factors, the 

Interactions of the strongest social index, parent intelligence, with the 

adjusted blood lead value and with the lead construct index were analyzed for 

these same nine outcome measures. One of the eighteen analyses was 

significant at the .05 level. The interaction of parent intelligence and 

adjusted lead level was significant for the Perceptual-Performance Scale of 

the McCarthy Scales. This occurred in the absence of significant main 

effects for either variable. While scores were negatively associated with 

lead level for low intelligence parents but positively associated with lead 

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level high intelligence parents. Since there is no main effect in this 

crossover interaction and since there is no reasonable interpretation of 

beneficial effects for high intelligence parents, it is reasonable to infer 

that this is a chance finding in an essentially null set of data. 

6. Considered altogether, the results of these studies lend no support to 

the hypothesis of significant effects of lead exposure in the range 

examined. Of particular Importance is the failure to find any evidence of an 

effect of the early exposure on measures made five years later. 

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HENRY E. MANNING 

PRESIDENT 

GLENN E.POTTER 

VICE PRESIDENT OPEHATIONS 

October 25, 1983 

Dr. Lester Grant 

United States Environmental Protection Agency 

Environmental Criteria and Assessment Office (MD-52) 

Research Triangle Park 

North Carolina, 27711 

Dear Les: 

Volumes I and IV of the Review Draft arrived today. My initial thought was 

that I would wait until after the Committee meeting this week to respond 

since you will, I presume, be revising the relevant sections accordingly. 

(Corrections of the previously reported positive findings of the PerinoErnhart data will be most necessary.) However, the presentation of the 

Committee's comments on 12-62 was such that I decided to make the following 

points for their consideration at the meeting. 

I didn't much appreciate the statements on 12-61 and 12-62 regarding the 

exclusion of parent education from the data analyses. In both papers and in 

oral exchange with Herb on the matter, I stated that parent education was not 

entered because it didn't contribute significantly to the model under any 

circumstance after parent I.Q. was entered. Both by stepwise and by a 

rationally based hierarchical model, parent I.Q. must enter first. The 

enclosed summary statements from the analyses summarized in my August report 

indicate that one can take parent education and enter it in any way that any 

one might like and it wouldn't make a difference for any analysis. There are 

parts of my work with which one might disagree, but the contention that I 

failed to control parent education should not be one of them. 

The Ammons QT isn't great, I know, but administration of a WAIS under the 

circumstances would have resulted in an unacceptable and biasing refusal 

rate. The use of the QT was better than not using anything. Some degree of 

validity is indicated by its correlations with the other variables in the 

study, including the very fact that stepwise analyses gave it priority in the 

selection procedure. The term "questionable utility" overstates its 

limitations. 
P.15 

I don't agree with the statement on 12-59, line 3, that de la Burde and 

Choate conducted the only study that was not either retrospective or crosssectional. Given the problems that I reported as a result of my reanalyses, 

the one very important finding that still holds is that there was no 

significant relation between the early, and appreciably higher, preschool 

lead levels and any outcome measure five years later. Because the earlier 

blood lead indices were higher and because children are considered to be more 

vulnerable at a younger age, these exposure data are particularly important. 

Since early lead level and schoolage tests were not affected by the various 

difficulties noted by the Committee and found by me in the reanalyses, this 

is worth more than the rather incidental indication on line 14, 12-62. If 

there is any relationship of interest in these data by now, it is in the 

existence of this demonstration that moderate levels of lead in the early 

period did not have an effect great enough and persistent enough to be 

detected on any of the measures used five years later; 

There is, of course, a power problem in making an interpretation of minimal 

or no effect. With alpha set at .05, power at .80, k = 4 (three covariates 

and lead), n = 62, and the R2 = .27 for GCI 77, the detectable effect size 

(increment in variance associated with lead) would be.128. If alpha is 

changed to .01, it would be .190. I'm not sure how one would handle the 

power issue for multiple non-independent outcome measures such as we have in 

this kind of research. Maybe Larry has some suggestions. 

Once again, I appreciate the objective and knowledgeable approach taken by 

the Committee in this review. 

Sincerely yours, 

Claire B. Ernhart 
P.16 

JZ£- 3 . C. /. 3& 

February, 1983 

Comments on Electrophysiology and Lead - Dave Otto's work 

The TS or tone-shutter procedure is described as following a classical conditioning paradigm, but the CR and the UCR appear to be reversed in direction. It 

is then appropriate to say that "Pb exposure interferes in some way with conditioning or learning in children?" (Otto, et al., 1981, p. 236). These data are 

based on 35 conditioning trials. Because of artifacts, these were not enough data 

to describe the course of conditioning. Usable data were obtained from 41 children, 

but some had as few as 10 artifact-free trails. 

Significant effects of lead and lead-by-age were reported (Otto, et al., 1981). 

On the basis of the linear model including lead and the lead-by-age interaction, 

predicted regression lines were computed for the most extreme ages and other age 

groups. (These were not empireally and independently derived from the respective 

ages.) There appears to be no significant Pb effect for the older age (48 - 75 

months) group. This will be a concern if we try to replicate at age four years. 

Is there any reasonable explanation of age interaction? The numbers at the respective ages and lead levels are relatively low for the interpretations drawn and the 

necessity of a replication is clear. 

The authors did replicate with a sample of 28 children reevaluated two years 

later. (Some had not been included in the earlier report becasue of artifacts, 

but all had blood lead data from two years earlier.) Blood lead data dropped an 

average of 11 pg/dl. This appears to be a secular rather than a developmental 

change since it occurred for older as well as younger children. 

Although neither age blocks nor trial blocks correspond exactly, it is 

possible to consider part of the results as a replication. These are trial blocks 

1 - 40 for two age groups. For neither age group and for neither PbBl (two years 

earlier) nor PbB2 (current) indices was the previous finding replicated, yet Otto 

(paper for Rutter-Jones book, p. 6) said that "the same linear relationship of 

SW voltage, age and Pb was observed." 

There was a significant Pb effect for the later tirals (41 - 100) for both 

early and later lead indices, but the Pb by age interaction was significant only 

for the earlier Pb index. (For 12 of the 28 children the PbB data were the same 

between replications.) Interesting enough, however, the direction of the interaction 

was reversed. (In the Dusseldorf report, scatterplots were mentioned but not 

provided, so I'm looking at extreme-age predicted regression lines.) Now there 

appears to be a slight, and probably non-significant negative relation of SW 41 - 100 

and PbBl for older children but a positive and probably significant regression of 

SW 41 - 100 on PbBl for younger children. This is the reverse of what had previously been reported for SW 1 - 35 and PbBl. This, too, is inconsistent with 

"the same linear relationship of SW voltage, age and Pb was observed." These reversals and discrepancies are not addressed. If these pieces of what appears to 

be a higher order cross over interaction situation (Pb x age x trial blocks x replication) are meaningful, the rationale of these reversals is not given. The negative correlation between early and late trial blocks makes for still more confusion. 
P.17 

-2- February, 1983 

The conclusion that there is a significant linear relationship of SW voltage 

and PbB within a range of six to 55 pg/dl deserves discussion. The first study, 

in which PbB went as low as six pg/dl, was not replicated. For the data of the 

second trail block of the second study, the confidence intervals of the projected 

regression lines of the two extreme ages overlap so completely in the area of 

PbB < 30 pg/dl that there may actually be little or no effect in this range. 

Otto makes a point of the linearity of the model, but with relatively few subjects 

and the form of the interaction, it may be incorrect to say that there are significant effects at the lower end of the PbB range. 

Although Otto has been duly cautious in stating that these measures have not 

yet been validated, he has discussed his results in terms of harmfulness at lower 

levels of PbB. From these studies it's difficult to determine which direction of 

effects is associated with lead at what age. How then can we even say what direction of SW effect is harmful? 

On the basis of the Otto et al. (1981) paper we would assume that a negative 

voltage is deleterious, at least in early trials for children below age 4 years 

(with little or no indication for older children). With the full age range of the 

second study, the SW 1 - 40 is correlated negatively with IQ. This suggests that 

negative voltage in the early trail blocks is beneficial. Whatever is going on, 

statements about "harm" seem premature. What is the basis for the statement that 

SW effects, which can go in either direction, represent CNS impairments?" 

Otto and his associates are to be commended for undertaking a difficult task. 

They are more knowledgeable about some aspects of research design than are some of 

the other investigators working in the lead effects topic. The use of linear 

analysis as opposed to ANOVA indicates a recognition of power considerations and modelsthe data array more appropriately. Unfortunately, the proportion of variance 

accounted for in the analyses is not reported. The correlation of .04 between PbBl 

and SW 41 - 100 is very strange (could it be a typo?) given the significant regression of SW 41 - 100 on PbBl. 

This set of papers is confusing. When one adds the cubic trend line of EEG 

spectra gain in the Benignus report, the situation becomes even stranger. 

Benignus et al. recognized that currently obtained PbB values are likely to 

be lower than previous peak values. This is an important point in view of current 

attempts to attribute effects to very low exposure levels. 
P.18 

-,--,,., • 

/ECAO - <?7> - #/• & ZLfl •£•€./. 3 a 

Clair e B. Ernhart 

Sept. 22, 1982 

Comments on 

Winneke, G., Hrdina, K.G., and Broekhaus, A. Neuropsychological 

studies in children with elevated tooth lead-concentrations. Part I: 

pilot study. International Archives of Occupational and Environmental 

Health (in press) 

Winneke, G., Kramer, V., Broekhaus, A., Ewers, U. , Kujanek, G., 

Lechner, H., and Janke, W. International Archives of Occupational and 

Environmental Health (in press) 

In these related studies, Winneke and his co-authors have made a concerted effort to evaluate possible lead effects in population with less 

exposure to lead based paint than is the case for U.S. children. In both, 

the major index was tooth lead. Some failure of concordance between samples 

is noted; this is consistent with the observations of Needleman, et al. 

(1979) and of Ernhart, et al. (1981). Blood lead data (but not EP) were 

available for 83 of the children. The correlation of .47 between the two 

indices is consistant with the correlation of ,43 reported by Ernhart, et 

al. (1981). 

In the first study^ the participation rate was higher for controls than 

for the lead group; matching was used for control of social factors. In 

the second study the participation rate was unrelated to lead; after testing 

the relationship of lead to a number of control variables, a single dichotomous 

variable, "socio-hereditary background (SHB)" was formed. A positive score 

in this was obtained if either parent was an unskilled worker cr if the 

child attended secondary school. In neither study were parental intelligence 

or the caretaking environment measured. This is a very important weakness 

given the very tenuous quality of the findings. As noted elsewhere, the 

direction of bias associated with failure to control such variables is 

toward finding an effect which is not there. 
P.19 

-2-

The selection of outcome measures is reasonable. It is based on 

previous findings by other investigators and, in the case of the second 

study, on the results of the first. I think that Winneke is to be commended for restricting the outcome measures to those specified by the 

hypotheses^ (p. 11, prepublication copy), but I'm not sure exactly what 

was included in table 9 which is missing from my copy. 

The basic strategy of hierarchical organization in the second study 

is, of course, appealing to me. However, including the experimental 

reaction time measure in the Type I hypotheses test is stretching things 

a lot, and I'm not at all sure I'd have the GFT in there. (It would have 

been good to see measures of academic achievement there.) More importantly, 

and unfortunately, the strategy of hierarchical organization to form sets 

for multivariate analysis was not followed. 

The interpretation of the statistical results concerns me greatly. I 

can see a rationale for one tailed tests, though I've never seen them noted 

when effects are large. Here, though, we see statistical tests that are 

just above the .05 level, one tail for the GFT, in both studies discussed 

as if they were quite robust (Lancet, Sept. 4, 1982) without recognition 

that inclusion of another, even rather weak, control variable in the analysis 

would wash them out completely. This same point applies to the references to 

statistical tests as being borderline significant at p^O.10, one tail. The 

reaction time measure is one of those that is "borderline significant" 

(p<^. 10, one tail); in the Lancet letter it is identified as being affected by 

environmental lead. 

In the second study, when behavior rating questionnaires were discussed, 

items were summed into a single score as a "screening step." I assumed a 

protection procedure was being used (as in Fisher's "protected t") to reduce 
( :• -i 

P.20 

. -3-

the likelihood of Type I error. Not so. When no significant lead effects 

were found, the scales were still opened up to item-by-item analyses and 

described (Lancet) as significant even though variance for a single item 

rarely exceeded 3% and, once again, important control variables were not 

included. 

Tables and graphs for results without residualizing for the SHB 

variable are not appropriate as evidence of a lead effect. (They do show 

that even this simple covariate reduces the variance that might be attributed 

to lead in an analysis in which it is not incorporated.) 

Finally, in a study in which the findings are so minute, more attention 

should be paid to studywise error. Winneke, et al< (extended study) mentioned this and the lack of control for parental IQ and caretaking environment, yet they interpreted their very marginal results as evidence of the 

effects of lead exposure. 

After reading these papers, I wonder how far one can stretch? And 

what is this overwhelming need to find lead effects in the absence of 

sufficient evidence? 
P.21 

January, 1983 

C B . Ernhart 

Comments Regarding Those Portions of Chapters 12 and 13, Draft, Air Quality Document for Lead Concerned with Neurotoxic Effects on Children 

INTRODUCTION 

The task of the reviewer of this topic was difficult and the effort to present a balanced picture is appreciated. 

The following supplements the materials previously submitted and I am repeating particular points only when the issue seems to me to require further 

emphasis or expansion. 

General Comments 

I was "pleased to see the problems of statistical analysis, generalization and 

interpretation, and the need for "blind" examinations added to the list on page 

12-40. One of my general comments is that I do not think enough attention is paid 

to some of these issues in the review of particular studies, particularly control 

of confounding variables and the failure either to use appropriate multivariate 

statistics or to consider studywise error. 

In addition to the quality of each study, the reviewer has considered the 

consistency of results across studies. An emphasis on consistency across studies 

is important, particularly in this area in which research is very difficult and 

expensive and in which obtained effects are small. Three observations on this 

topic of across-study consistency will be discussed, (a) important sets of data 

or analyses have been omitted, (b) consistency can be consistency of bias, and 

(c) the attempt to make results consistent with the interpretation of a single 

study has lead to "stretching". 

Omission of Data Sets and Analyses. With a very few exceptions, the reviewer 

has included only published papers. Certainly some unpublished reports should 

be allowed to fade rapidly out of view. With respect to this highly controversial 

topic, however, a person who is strongly committed to a given position may accumulate data or conduct analyses the results of which are not consistent with 

his/her position and may then fail or even refuse to share them with other scientists reviewing the topic. 

This is one of the more serious problems in the research program of Herbert 

Needleman. There are many questions regarding the 1979 paper which could have 

been averted by more complete presentation of results. These omissions are particularly important for the across-study review because this one relatively large 

study, conducted by an assertive investigator, appears to have been selected as 

a standard or referrent, the conclusions of which may or may not be buttressed 

by the results of other reports. Thus the failure to provide complete reports 

of study features and analyses is critical to the entire enterprise covered in 

this section. 

Some additional analyses of the data of this study were provided in a paper 

(Bellinger and Needleman) that Dr. Needleman refused to share with the group in 

August because it was under editorial review. (The purpose of the priviledged 

communication for a manuscript under review is to prevent prior study and publication by another. Since no one else could publish analyses of this data set, 

this basis for not sharing the analyses is not valid.) Analyses included in this 
January, 1983 

C B . Ernhart 

report are important to the questions under reivew. Given that it is now in press, 

circulation to EPA and directly concerned investigators prior to the workshop 

might have been helpful. It is possible that features I noted therein that are 

contrary to the investigator's position will have been edited out. 

Another report (1981) of a replication supported by EPA (Contract# 68-02-2217) 

has not been reviewed in the draft. It has not been published, presumably because 

the results were not significant. The failure to report a nonconformatory replication is an important omission. Dr. Needleman objected at the workshop to the 

discussion of this study on the grounds that he hadn't had time to revise for publication. Since this was contracted by EPA, should not the report be of such a 

quality that EPA and the interested public can utilize the findings? (That it is 

a disorganized manuscript describing a rather poorly designed study is something of 

an insult to the funding agency, but that's another issue.) Comments on the study 

will be provided below. In the report to EPA of that replication there is mention 

of psychological test data collected with that sample. There appear to be no published reports of these data. 

Data sets of the size generated in these studies are very important. I do 

not feel that an investigator has the right to conceal results nor should we ignore such results as are publicly available but which were not published. 

Consistency of Bias. The importance of confounding variables was indicated 

on pages 12-43. What is not indicated is that uncontrolled confounding variables 

in this research tend to bias in the same direction, since other risk conditions 

are usually correlated with lead level. Furthermore, some of the more critical 

confounding variables, more limited parent IQ and less than optimal caregiving environment, are not considered in most of the studies.. It may not be fair to 

fault an investigator because the state of the art at the time a study was planned 

or other practical considerations (as limited funding) led to non-inclusion of 

some important covariate. It's up to us, however, to be aware of the confounding 

and to use due caution in the interpretation of results. Even when a confounding 

variable is entered into statistical analysis, the results is an undercorrection 

which is seldom recognized by the investigator (Reichardt, 1979). It is crucial 

to recognize that this bias due to confounding is pervasive across studies and that 

it should be considered in discussing consistency of results, particularly when 

effects are small. On page 13-44 of the draft, the small size of some of the 

psychological effects was mentioned. Small effects, if they are true effects, may 

be quite important, given the incidence of exposure at the indicated levels. To 

decrease the functional capacity of a large number of individuals to an extent 

not considered to be deviant in an individual is still a very large loss to 

society. The problem with small obtained effects in research is that it is very 

hard to differentiate lead-related effects from the consequences of everything 

else that is happening to these individuals in a study. 

Stretching. The reviewer stated that there is one study (Needleman, 1979) 

that provides the strongest evidence, to date, of association between low level 

lead exposure and neurotoxic effects, i.e., intellectual and behavioral deficits 

in children, but that there are unanswered questions. Other studies are then 

cited as supporting this position on the basis of partial replication. These results 

are described as "striking" (p. 12-84). In each of these studies however, the 

investigator has stretched very minimal findings in an attempt to provide an interpretation consistent with the Needleman position. 
P.23 

-3- January, 1983 

C B. Ernhart 

In some instances, the stretching is statistical, as in reference to trends 

(not significant) inthe data or in the use of alpha <_ .10, one-tail, for statistical significance. Failure to consider the effects of the direction of bias due 

to uncontrolled confounding variables characterizes all of these studies. In his 

pilot studies of attainment and intelligence and of teacher behavior ratings, 

Yule stated very clearly that parental intelligence and caretaking environment 

were not considered. The behavior ratings described in the second paper were 

interpreted as replicating the Needleman results, but the four lead level groups 

did not differ significantly on total score or on ratings of hyperactivity or 

impulsivity. (These are often incorporated into descriptions of minimal brain 

dysfunction.) Results across the four lead level groups did not follow a doseresponse pattern. No child in the highest lead group was hyperactive. Distractability and disorganization, which might be considered significant in the Needleman 

EPA contract replication were not significant in the Yule et al. study. When the 

number of significant items across all scales (seven) was compared with expectations 

on the basis of chance (four), the results are pretty thin, yet Yule et al. considered them as being impressive in their similarity to those of Needleman. 

The Yule-Lansdown work now under way is better designed and I hope that the 

need to be consistent with a study considered to be central does not influence 

the inferences drawn. 

The next instance of stretching is in the Winneke studies. Although Winneke 

carefully qualifed his results in his paper (the extended study), the need to 

stretch very marginal findings was apparent in a letter to Lancet. His letter and 

my response, not published,have been supplied previously. Yule et al. and Winneke 

et al. do present their results in such a way that one can separate results and 

inference and they are aware that there are limitations to their studies. 

Comments on the Thatcher papers have been sent to EPA. The evidence of 

stretching is clear. I did not respond to his reply because the situation seems 

fairly obvious. I did.-write to him asking if he could provide a plot of intelligence residualized on covariates against the lead index. (I had just seen my 

outlier plot.) He did not reply. One point should be noted: In the JLD paper 

he did not indicate that cadnium was a confounding variable.. 

In spite of noting all the problems in thse studies, the reviewer appears 

to be concurring with this stretching. For example, in the discussion of the 

extended Winneke et al. study, much of the near significant (p < 0.10 onertail) 

material is listed and then treated as if relevant; "...significant attentional 

deficits attributable to lead were found,..." when effects at p < .05 (one-tail) 

were limted to CFT (like the Bender-Gestalt Test). These effects were so minimal 

that uncontrolled confounding variables could very easily account for the effect. 

(Note that Bender-Gestalt results are not significant in any other study.) The 

reviewer than went on to try to find a rapprochement between the Winneke and 

Needleman results. The possibility that there is no true effect at these levels 

does not appear to have been considered. The importance of confounding due to 

caretaking environment was recognized by the reviewer in considering the Milar 

et al. studies. Why not others? (Note: I appreciate the efforts made by the 

reviewer but I do not think he gave anywhere near enough weight to the problems 

pervading these studies, particularly the study placed at dead center.) 
P.24 

_4_ January, 1983 

C B . Ernhart 

What is this need.to stretch to get results consistent with those of 

Needleman? The work of Yule et al. and Winneke et al. is sound enough that 

stretching to get a publication should not be necessary. Being asked to give 

talks, be an expert witness, appear on TV, etc. does not seem to be reason 

enough. A good part of it may be the idea of wearing the white hat (ED Groth III, 

EPA testimony, April 1982) and being on the"environmentalist" side of things. 

Being concerned about the environment should not interfere with scientific research, but I believe it does. Being an environmentalist makes one appear to be 

for the little guy (Love Canal, Times Beach, etc.) and permits making business 

a scapegoat for various societal problems. And, as Martin Bax^ pointed out, 

blaming lead for the problems of children makes it easier to ignore the more 

immutable and troublesome conditions which we know affect children, particularly 

disadvantaged children. Finally, one last factor which my lead to stretching to 

draw inferences consistent with the Needleman position is the absolutely brutal 

treatment one gets from him.if one does not. 

Behavior Ratings - The Needleman Study 

On page 12-68 of the review, the Needleman behavior rating scale is mentioned. 

It was suggested at the workshop that the oft reproduced graphs from the Needleman 

(1979) paper be reproduced in the Air Quality Document. I object very strenuously. 

There was absolutely no control for confounding variables in that presentation. 

My data showed no hint of an effect with similar teacher ratings and a more homogeneous population. Milar et al.2 found no evidence of behavioral effects of 

moderately elevated lead exposure. As noted elsewhere in these comments, the 

data of Yule et al., also without control of confounding, can be considered as 

supportive only by stretching. 

Of particular interest, however is a replication by Needleman (Contract# 

68-02-2217, EPA, 1981) of the teacher rating study. This was ignored in the 

draft of the Document. Once again, the teacher rating data were obtained for a 

large number of school children and shed deciduous teeth obtained for a large 

number of these were analysed for dentine lead. Covariate data (called followup data) were obtained for males and psychological tests were administered. The 

later data are not reported here or elsewhere. Separate graphic presentations 

were made of the behavior ratings for each. While the highest lead group usually 

had the highest prevalence of each rating (except for hyperactive and impulsive, 

female) the dose-response pattern was not as clear as in the previous report. 

These graphically presented data were also not adjusted for covariates. 

Cluster analyses were conducted but the method was not specified. The 

first cluster contained five items, the second and third, two each and others 

were two single item clusters. Errors, reflections of items, inconsistencies 

in numbers, and confusing writing make the scale construction procedure difficult 

to follow but the result appears to be this: 

1. Cluster 1. Not persistent, dependent, poor overall functioning, less 

able to follow simple directions, less able to follow sequences. "Follow simple 

directions" was dropped because of low frequency of unfavorable ratings. (Note 

also that it was almost flat in the graphic presentation.) To receive a favorable 

score on the cluster a child had to be favorable on each item; to receive a negative 

score he had to be unfavorable on each. All other cases were dropped. (What a waste 

of data!) 
P.25 

-5- January, 1983 

C B. Ernhart 

Cluster 2. Hyperactive, impulsive. An unfavorable score resulted from 

having been rated on either or both scales, a favorable score resulted from 

having no unfavorable rating. No cases were dropped for this scale. 

Cluster 3. Distractable, disorganized. For this scale a positive score 

resulted from having both items positive; a negative score from both being negative. Cases with one positive and one negative were eliminated. 

Clusters 4 & 5. Frustrated, daydreams, were single items, all cases included. 

Covariate data were collected for a portion of the sample which was selected 

to include disproportionate number of hyperactive males (and no females). 

Multiple logistic analysis was used in a model which first tested the covariates (for the cases having them) in a stepwise manner and then tested the 

effect of adding the five levels of dentine lead into the model. In addition to 

the statistical test, relative risk ratios were obtained to determine the increased risk of scoring positive on the scale, as described above, with increasing 

levels of lead. 

One one scale, distracted-disorganized, was related to lead level and on this 

only for the highest lead, >_ 18.20 ppm, was there a greater risk than for the 

referent, or lowest group. There was no evidence of a dose-response relationship. 

Oddly enough, in this same analysis with a p_ value lower than that for lead, children in a mid brithweight range (6 lb, 15 oz - 7 lb, 8 oz) were significantly 

more at risk than low or high birthweight children. Since this is not consistent 

with any reasonable interpretation of birthweight effects, it appears that the 

analysis is faulty in some regard. 

Considered altogether, this replication, with some control of confounding 

variables, failed to support conclusions from the 1979 study. While the study 

design if off in some respects, the oddities should not have biased against 

getting an effect, given there is one, and the study should not be ignored. 

Because the draft stated (p 13-42) that results of behavior ratings are 

"striking and consistent" I might note that in a letter to the Central Docket 

Section (A-l30) EPA, dated May 20, 1982, Shapiro and Marecek reported examiner 

ratings for attention span showning no systematic lead effect. There was some 

tendency toward higher ratings on lethargy and flattened emotional affect (both 

inconsistent with hyperactivity and impulsivity) but these do not appear to be 

significant. These were not included in a recent revision of the paper - maybe 

they're too unreliable to be of interest, but they are contrary to the consistency 

the reviewers sees on this issue. 

"Blindness" in the Conduct of Research 

I was glad to see the need for "blindness" added to the list of research 

issues. Most investigators now recognize the need for the person administering 

treatments in a clinical trial or observing and coding results in epidemiological 

as well as clinical trials to be blinded, when possible, as to the nature of the 

treatment. The idea of blindness is to segregate information such that there is 

no contamination between cause-side and effect-side information. This need for 
P.26 

-6- January, 1983 

C B. Ernhart 

segretation of information applies to more than the administration of treatment and 

the observation of results and should apply when data organization and subject 

exclusion decisions are made on either side of the relational barrier. 

Data reduction is essential when there are a large number of variables. 

Often each alone is relatively insensitive, as in the case with test items. Data 

reduction usually consists of summation of items grouped conceptually or empirically 

on the basis of factor analysis or a similar procedure. It is essential that this 

procedure be done independently of the data to which these reduced variable scores 

will be related. In the Burchfiel et al. study the data reduction was deliberately 

conducted to include only items that differentiated the risk groups. As I indicated in a previous review for EPA, the chosen variables reached significance 

in the frequency expected by chance. When I pointed this out in a letter to Lancet, 

Needleman replied that this was handled later in the analysis by the jack-knife 

technique. There is no way that the jack-knife could correct for the bias in 

the item selection procedure. If this had been done as a procedure to develop an 

EEG screening test for lead level (don't ask me why) the procedure would be appropriate but it would then need to be cross validated with an independent sample. 

As a test of whether there are electrophysiological sequelae of low lead exposure 

this study is so seriously flawed that it should receive no^ credibility in the 

present review. This very serious problem is not noted in the present draft. 

There is no indication in the Needleman behavior rating replication study 

(EPA Contract* 68-02-2217) that the persons conducting the unspecified cluster 

analysis and scale formation were unaware of the lead status of the children. The 

formation of these scales is not consistent with usual psychometric procedures 

and resulted in the exclusion of the data of large numbers of children. Under the 

circumstances, the person making the psychometric decisions should be blinded regarding lead status. . 

When the data of already examined subjects are to be excluded for cause, 

the person making the decisions should be blind to either the outcome or the risk 

condition and preferably to both. I have previously commented on the very high 

exclusion rate of the Needleman (1979) study and the very real possibility of bias 

in the differential loss rate between groups. Willingness tD participate has often 

been related to risk condition. Of those actually tested in the Needleman study 

32% of those with usable dentine data were excluded (second stage exclusion) for 

not being discharged from the nursery with the mother, possible head injury, 

plumbism, and bilingual home. Frequencies for the specific reasons are not given. 

A large number of bilingual-home cases have been excluded at an earlier stage. 

Given the high rate of exclusion at the first stage, the 32% exclusion rate of 

data for these already tested cases is extremely high. Theoretically, at least, 

these exclusions (aside from bilingual home) would remove cases that jiave more 

behavioral problems or perform more poorly than the included cases. 

Consider the teacher rating data. First, contrary to a written statement in 

the paper and in the current review the tested children (M = '253) and children excluded at the first stage (N = 235) did differ on teacher rating of Low overall 

functioning, (x2 = 4.85, p < .05). This is not very critical. What does get unusual looking is a contrast of the rating data for hyperactivity and impulsivity 

for the high lead group (n = 58 or 57) in Table 3 and that portion of the distribution 
P.27 

-7- January, 1983 

C B. Ernhart 

in Figure 2 from which those cases must have been drawn. If the person making 

the decisions for exclusion of the already tested group was not blind to the 

already collected data (lead, teacher ratings and other data) a bias may have 

entered. Analyses of the data of the tested but excluded children would help to 

clarify the situation. These children should be the same as or poorer than the 

same lead-group children whose data were included in the final groups (ns = 100 + 58), 

Incidental Comments on Particular Studies 

Comments of different aspects of specific studies have worked their way into 

this discourse at several points and I'll not pull them all together now. (I 

hope that prior comments still stand and are not considered to be subsumed in 

this. There isn't time to redo it all.) 

de la Burde' and Choate. With data available from several separated examinations (and even the infancy data), so muchmore could have been done in this 

analysis. Some control of confounding could have been used. Variables could 

have been continuous, not forced into nominal, measurement. Multivariate analysis 

could have been used. It is a shame not to utilize precious data more efficiently. 

I wish they had given us dentine lead and outcome measures just as I wish Needleman 

had reported his blood lead and outcome results. (There would have been some regression effect in the latter, but it still could be helpful.) 

David and Associates. See appended letter. 

Pi hi and Parke. Once again lead is confounded with other metals in hair 

analysis. 

Beattie and Moore Studies. These studies are interesting examples of retrospective research using unusual indicators of fetal exposure. What else could 

have been related to residence in an old-plumbing house? What characteristics 

of the mother affect her ability to metabolize lead? Excessive alcohol use and/or 

poor nutrition (iron balance, calcium, etc.) are possible candidates. We will 

learn more about these considerations as the better conducted of the prospective 

studes start to produce results. 

Electrophysiological Assessments. I do not yet know all I want to about this 

technique but it does not take a specialist in the technique to see the serious 

design flaw of the Burchfiel work. The Benignus and Otto studies appear to be 

satisfactory, given the caveats provided in the articles and by the reviewer. 

Needleman, H.L., Leviton, A., Bellinger, P.. Lead-associated intellectual 

deficit. N. Engl. J. Med., 1982; 306, 367. At the workshop Dr. Needleman said 

that this letter should be reviewed in the Document. Let's look at-it. Control 

of confounding variables was ignored, although these were considered important in 

the 1979 paper. A risk ratio (of IQ <_ 80) was presented as if lead was the only 

condition systematically differentiating the groups. Verbal IQ was used rather 

than the customary and reliable Full Scale IQ. IQ <_ 80 was selected as a cut-off 

score. This is not conventional for mental retardation or any other usual division. 

However, of the verbal IQ values under 100 in the graphed data, this cut-off 

yields the largest relative risk ratio. 

The M. Smith study in the U.K. must be considered. Even if it isn't published, 

the striking failure to replicate the Needleman work indicates that the inferences 

drawn ("striking and consistent") need to be toned down. 
P.28 

-8- January, 1983 

C B. Ernhart 

The statement at the bottom of pages 12-83 to the effect that the Needleman 

study "...can be most reasonably interpreted as clearly demonstrating an association..." simply is not reasonable. The many problems noted in various reviews 

of this study, his refusal to share with other scientists some of his own highly 

important analyses, the very selective method of data presentation, and even his 

inability to replicate his results suggest that building an interpretation on this 

foundation is highly risky. Further comments are provided in a letter published 

in Contemporary Psychology (copy appended). 

Ernhart Studies. The presentation of the means in the summary table gives 

the impression of an unduly large effect; these were not adjusted for covariates. 

For the Reading, Exploratory and Conners data it looks as if you got the ns, not 

means. Means were not published. 

Page 12-67. The statement that the mean blood lead level for my moderately 

elevated group dropped from 46.5 to 32.4 isn't quite right. The divisions provided in Table 1 of my paper were done to facilitate the T^ analyses reported in 

Table 3. These are data for the 63 children available at the second test. First 

we divided them on the preschool lead values, with ns of 40 and 23. The mean of 

46.5 correctly indicates the preschool PbB value for the orignial moderate lead 

children still available at the follow up. With this split, we related preschool 

lead (dichotomized) to school age outcomes as shown in Table 3. We could not use 

the same cut off for the school-age dichotomization because the higher lead group 

v/ould have been quite small and because vie would have had to make an arbitrary 

decision about classification for values 31-39 (not present in the mg/lOOml units 

of the preschool lead analyses). 

If we had done what the reviewer thought we had, i.e., retained the preschool 

grouping and provided school age PbB means for these groups we would have provided 

faulty data because of the inevitable regression occurring when an arbitrarily 

divided group is examined on a variable correlated with the variable on which the 

division was made. The significant decrease in variance would also exacerbate the 

regression effect. A decrease in lead level for the initial high lead group would 

have represented both change over time, as reported for the entire group (top of 

p. 915) and regression effects. 

The drop in variance with deletion of the outlier child is to 2.6 percent 

common variance. The 4.4% reported (personal comunications) was based on residual ization only on parent IQ. When we ran analyses to ascertain that the subscales variances also dropped we included sex to make the analyses parallel those 

reported in Table 5 of the 1981 paper. Sex was not significantly related to GCI 

but it was related to the Motor Scale so we regressed all variables on sex as 

well as parent IQ in the analyses. 

The Perino-Ernhart two correlation contrast continues to elicit interest. 

The Bellinger Needleman paper (1983 in press, J. Pediatrics) should be interesting 

in this regard. 

Page 12-85, line 2. Strike "mainly". I guess the reviewer had only the 

personal communication, not the manuscript for this. 
P.29 

_g_ January, 1983 

C B. Ernhart 

Comments on Chapter 13 

The chapter is well organized and well written by a reviewer who is clearly 

aware of all issues involved. The presentation is appropriate to the task of 

providing a reasonably concise statement of what is known for the use of agency 

decision makers. 

With respect to biological effects (Section 13.5) the Introduction (pp. 13-37 

through 13-39) poses the issues in a logical and judicious manner. 

Page 13-42. For the reasons indicated elsewhere in these and previous comments, 

references to the Needleman (1979) require even further qualification on the basis 

of methodological problems. The paragraph at the bottom of p. 13-42 extends into 

this document the stretching discussed earlier. The most extreme example of this 

is the discussion of attentional deficits, indexed by ratings, as "striking and 

consistent". What happend to the Ernhart et al. teacher ratings? Those of 

others, including the Needleman EPA supported replication certainly do not contribute to "consistency". 

Page 13-43, line 9. Change "two" to "five". I would rewrite that sentence: 

"When reevaluated five years later mental retardation was observed in one child 

whose blood-Pb level was 60 pg/dl and whose dentine lead level was consistent 

with very excessive lead exposure. Other children who had blood-Pb levels of 40 

to 70 pg/dl as preschoolers showed no evidence of persisting effect when parental 

intelligence was taken into account." 

Page 13-43. The Burchfiel et al. study is so seriously flawed that is should 

be deleted from the review. 

Page 13-44, line 5. When referring to small effects, it might be appropriate 

to indicate that the direction of bias associated with some of the methodological 

limitations of these studies is toward finding or exaggerating small effects, i.e., 

consistency of bias. 

Page 13-46, last paragraph. The use of "new neuropsychologic" findings to 

buttress the impetus toward revising the blood-Pb criteria downward is simply not 

warranted by the quality of the findings. A very important issue, not addressed 

here, is the establishment of a threshold at blood-Pb levels current at the time 

of the neuropsychologic evaluation. This issue requires elaboration. 

Threshold. An important issue identified in this section is the specification 

of a threshold of effect for cognitive deficit and for other psychological deficits. 

High level lead exposure can produce deficits in intelligence. ^Deficits are 

highly probable in a child presenting symptoms, particularly encephalopathy. 

Furthermore, it is quite possible that deficits can occur with high level lead 

exposure when there are lead related symptoms that are not diagnosed and, possibly, 

when there are no apparent health symptoms. 

If there are no deficits associated with low level exposure, it follows that 

there is some level of exposure at which a deficit may be observed. Given the 

variability between individuals, it is not likely that a fixed value can be 

determined. Thresholds may also vary between functions and there certainly are 

variations in the sensitivity of assessment instruments. 
P.30 

-10- January, 1983 

C B. Ernhart 

The author of the draft appears to be seeking a value in terms of blood 

lead level for the threshold for intellectual deficit. The merits of the specific 

studies are discussed elsewhere but here I want to point out a major problem in 

the determination of this threshold. This is the probable time span between the 

occurrence of the risk factor (deleterious level of lead exposure) and measured 

deficit. During this time period it is highly likely that the blood lead level 

will have decreased while the consequent damage persists. Thus the deficit is 

attributed to levels of exposure which are inappropriately low. The problem is 

particularly relevant in research on the developing child. 

The peak of exposure usually occurs during the early preschool years with 

blood lead level evidence of the exposure decreasing over time. However, the 

most sensitive indices of effect are the more valid tests of intelligence and 

achievement which are not administered until several years after the peak exposure. 

Thus it is invalid to infer that the lead level data collected concurrently with 

the test of effect can identify the threshold of effect. 

If Needleman had related his blood lead data (about age 3-4 years) to his 

intelligence test data we might have a better idea of this. All we have is the 

mean Pb value of 35.5 for 23 (40, not 15%) of the high tooth lead cases. There 

are two problems with using this as a threshold: (a) the threshold level for the 

dentine lead has not been published; it is not appropraite to let it coincide with 

the cut-off for inclusion in the high lead group, and (b) the high lead group was 

selected to be extreme, hence blood lead (correlated with dentine lead .43 in my 

study) will suffer regression effects and be unduly low. 

The reviewer recognized that there may be changes in blood lead values from 

the time of damaging intoxication. These are almost invariably changes downward 

as a function of increasing age. (If they were changes upward from minimially 

damaging levels the child would probably become sufficient symptomatic to arouse 

attention.) The effect of this drop from peak for the establishment of a researchdetermined threshold is not recognized. 

There is another temporally related design problem in the attempt to relate 

effect and current indices of exposure. Not only does an index of exposure, say 

blood lead, decrease over time from the point of peak exposure, it will probably 

decrease in a somewhat variable way (not constant for all cases) as a function of 

continuation of exposure, nutrition and other idiosyncratic factors. Thus the use 

of current levels to estimate peak or threshold levels is in error both in absolute 

level and, to some degree, in relative positioning of subjects. This latter problem 

would tend to dilute a lead effect, given there is one, and operate toward a failure 

to find a true effect. On the basis of this argument, I should have had a strong 

relationship between my preschool age lead levels and school age intelligence and 

a weaker relationsihp between the current (school age) blood lead and intelligence. 

Such was not the case except insofar as the single outlier can be considered independently of the whole sample. 

This teasing apart of early and later correlates of effect badly needs more 

data and I think we have to reserve decisions on this and on the related threshold issue until the results of the prospective studies are available. 

Given the limited information now available, the line: "30-50,cognitive 

(CNS) deficits,children" should be deleted from Table 13-11 and the reason for the. 

deletion given. The possibility that the same problem applies in the Otto and 

Benignus studies of electrophysiological changes should be considered. 
P.31 

•11- January, 1983 

C B . Ernhart 

Page 13-57 & 13-58. Table 13-13 is an example of How-to-Lie-With-Statistics. 

A naive reader, like a reporter, could very well lift these figures to exaggerate 

the extent of problems associated with lead exposure. All this is taking one 

risk factor, urban residence and computing the number of urban residents. What 

is not indicated is that the majority of urban residents are not at risk. How 

about computing the portion of the population that is black and calling that the 

risk factor? 

Concluding Comment. At the workshop, Dr. Piomelli commented that preventive 

medicine dictates that attention be given to conditions that are precursors of 

poor health. He is right, of course. While this consideration might be mentioned 

in Chapter 13, it is important that we do not use it to distort the information 

provided in the Document. It is not our position to make policy. If we give 

undue weight to the results of inadequate studies or if we attribute adverse effects 

to unduly low indicators of exposure, we are, in effect, inappropriately assuming 

the decision making responsibility. We cannot assume a world of infinite resources 

available for children (and others). There are costs which will obtain if we 

specify an unduly low threshold for, say, psychological sequelae of exposure. 

Among the more serious costs may be the diversion of resources from the really 

serious problems of children. We must also consider the costs of further efforts 

to remove lead from the environment in the reduction of the benefits to society 

of the use of this resource. 

References 

1. Bax, M. Editorial. Lead and imparl*ed abilities. Developmental Medicine and 

Child Neurology, 1981, 23^, 565-566. 

2. Milar, CR. , Schroeder, S.R., Mushak, P., Boone, L. Failure to find hyperactivity in preschool children with moderately elevated lead burden. Journal 

of Pediatric Psychology, 1981, 6_, 85-95. 
P.32 

ZHTA.£ d l. 3d 

Low Level Lead Exposure: Its Effects on Intelligence and 

Behavior of Children 

Claire B. Ernhart, Ph.D. 

This paper is prepared at the request of the Lead Industries Association, 

Inc. as part of the testimony presented to the Environmental Protection Agency 

at hearings on April 15-16, 1982. The topic of inquiry is the desirability of 

changing regulations regarding permitted levels of lead in gasoline. 

The issue I am discussing is the possible effect of low level lead exposure 

on the intelligence and behavior of children. After careful review of the 

published studies of others, and my own data, I have reached the opinion that if 

there are such effects, they are minimal. The effects that have been reported 

are small and have not been obtained consistently across studies. 

More importantly, there are a number of methodological problems in these 

studies, including my own. These can lead to biases or distortions in the 

findings. Some of these biases are one-sided, i.e. they lead to finding an 

effect which might not be there or to exaggerating a real effect. When there is 

a true effect which is very robust, we might be able to ignore these biases. 

However, when a reported effect is small or is not replicated by others, it is 

imperative that we scrutinize the design and procedures of the studies to 

identify such problems. The methodological issues may be classified into five 

categories: 

1. Control of Confounding Variables 

2. Selection and Recruitment of Sample 

3. Indices of Lead Exposure 

4. Choice and Reporting of Performance Measures 

5. Study-Wise Error and Sample Size 

Control of Confounding Variables 

Control of confounding variables is the single most important problem in 

this area of research. Confounding variables are other conditions which may be 

associated with the study varia'ble, in this case lead, and which may influence 

the specified performance variable. Higher lead levels are often found in 

children whose parents have lower intelligence and less education and who are 

less able to provide a stimulating home and child rearing atmosphere. These 

conditions can and do influence performance measures. 

A particularly important confounding variable is parent intelligence. It 

has long been known that this is the single most important correlate of child 

intelligence. Let us look at what happens when this is omitted or included in a 

study of lead effects. 
P.33 

Page 

Percent of Variance in Child Intelligence Accounted for by Lead Indicator Without 

and With Control of Parent Intelligence 

Preschool 

Intelligence 

Measure 

Preschool 

Blood 

Lead 

School Age Intelligence Measure 

Preschool 

Blood 

Lead 

School Age 

Blood 

Lead 

School Age 

Erythrocyte 

Protoporphyrin 

School Age 

Dentine 

Lead 

Without Control of 

Parent Intelligence 

10.2** 6.3* 17.6** 8.4* 3.1 

With Control of 

Parent Intelligence 

1.2 a* 1.4 7.7* 4.5 0.0 

a Birth weight is also controlled in this figure. 

* P < .05 

** P < .01 

The data are from two studies (1,2) in which I have participated. To 

simplify the table, I am here presenting only the results for the General 

Cognitive Index of the McCarthy Scales. (This corresponds to I.Q.) The figures 

represent portion of the variance in child intelligence related to variance in 

the indicated lead index. Except for the dentine lead results, all variances in 

which parent intelligence is not controlled are statistically significant. With 

inclusion of parent intelligence, the variances decrease dramatically and only 

two of the five barely reach simple (single-variable) statistical significance. 

In the large majority of studies, parent intelligence is not considered. It is 

apparent that this confounding variable can lead to a false conclusion that 

there is an effect or the exaggeration of an existing effect. 

Using a similar mode pf analysis but controlling for age, sex and a simple 

index of social class, Yule, Lansdown, et al. (3) reported that only 2 1/2 to 4 

1/2 percent of the variance in intelligence is associated with lead. This is 

statistically significant. I wonder, however, if it would have been if parent 

I.Q. had been included in their design. Yule, et al. do carefully qualify 

their results and express a concern for the appropriate control of social 

factors. In their ongoing studies they are including intelligence test data 

from both the father and mother as well as detailed information on social and 

family factors. They are quite knowledgeable about methodological issues and I 

look forward to reading their further reports. 

I hope that the importance of parent intelligence as a confounding variable 

will be recognized by other investigators. In other published studies to date, 

only the 1979 Needleman, et al. report (4) includes this as a covariate. 

As suggested by Yule, et al., parent intelligence is not the only 

potentially confounding variable in these studies. For example, Milar and 
P.34 

Page 

colleagues (5) have reported that quality of stimulation and form of discipline 

in the home (Caldwell's HOME Scale (6)) are related to lead exposure. Rutter 

(7) has commented that even with a more comprehensive measurement and control of 

parental characteristics, family circumstances, and social environment there may 

still remain a small effect attributed to lead which is actually due to social 

or genetic factors. 

Moving away from social variables, we find another possibly important 

confounding variable that has not been mentioned in any published study of 

cognitive and behavioral effects. Iron deficiency is not unusual in the 

population of children most at risk of lead exposure, that is, the urban inner 

city child. Incidentally, according to one of my colleagues in hematology, we 

will see an increased incidence of iron deficiency in our inner-city hospital. 

This prediction is based upon reduced support of the WIC program. Iron 

deficiency has been shown to increase susceptibility to lead. Furthermore, high 

levels of lead can lead to iron deficiency - the two conditions are not 

independent. Oski and Honig (8) and my colleagues at Case Western Reserve 

University, Lozoff and Brittenham (9), have related iron deficiency to 

developmental deficits in young children. Iron deficiency in elevated lead 

level children may well be producing effects sometimes attributed to lead. We 

are now including measures of serum ferritin in our research protocols. 

Another aspect of the control of confounding variables has not been 

mentioned in investigations other than my own. It is well known in 

psychometrics that the measurement of psychological and social factors includes 

error. For most purposes, it is not biasing or distorting; it merely increases 

the difficulty of seeing an effect. When we use such a measure as a control 

variable in analyses of covariance, regression models, etc. or even in 

matching, the correction is not complete. In other words, when we think we have 

controlled for, say, parent I-Q., we have only partially controlled for it. The 

direction of the bias is toward undercorrection. I know of no effective 

satistical solution for this. What is important is that investigators be aware 

of this when they make interpretations of the small effects we see in these 

studies. 

Summary. (a) Control of confounding variables is probably the single most 

important problem in this area of research. (b) Major factors that could be 

related both to lead level and to child performance are not included in most 

studies: these include parent intelligence, a number of social factors, and 

possibly, iron status, (c) Statistical techniques used to control confounding 

variables almost invariably undercorrect. (d) The direction of bias in this 

research is toward finding an effect that might not be there or increasing the 

apparent magnitude of an actual effect. 

Selection and Recruitment of Sample 

Two issues are of concern here. The first is the choice of the sample, the 

second is differential or biased loss of eligible cases. 

Once an effect has been well established, the extent of the effect can be 

determined by selecting samples representing the entire population. Until then, 

it is more efficient to study the population most at risk for the target 

condition - one is more likely to find the effect, given it exists. Aside from 

proximity to an inadequately controlled industrial source, the children who are 

most apt to have elevated lead levels are from inner-city, low socioeconimic 
P.35 

Page 

status families. It was a sample of disadvantaged urban black children that we 

used in the research mentioned previously. 

Selection from a more restricted source has another advantage - the sample 

is more homogeneous and the effects of social factor confounding are lessened. 

Let us consider a discrepancy between two sets of data. These are teacher 

ratings of children using almost identical items. Within the Needleman, et al. 

study (4) there are significant differences between groups. In mine (2) there 

are no significant differences and the overall level is less favorable. 

Comparison of Relationship of Lead Level Classifications to Teacher Rating Items 

in Two Studies* 

Teacher Rating Item Ernhart, Needleman, 

et al. 1981 et al. 1979 

Low Moderate Low High 

Lead Lead Lead Lead 

Easily frustrated 

Hyperactive 

Impulsive 

Distractible 

Daydreams 

23 

20 

37 

33 

13 

19 

9 

19 

31 

25 

11 25 

6 16 

9 25 

14 36 

15 34 

* Lead levels as defined within respective studies 

A major difference between the studies was that the Needleman, et al. 

sample was more heterogeneous with respect to social factors. Since these are 

correlated wih lead exposure, and have not been controlled in these data, it is 

possible that they caused the appearance of a lead effect. 

A serious problem in some studies is failure to recruit subjects identified 

for inclusion in a study or attrition in longitudinal study. Such loss is more 

likely to occur among families who are socially and economically disadvantaged. 

These families are often quite mobile and tracing is difficult. Parents are 

often not motivated to bring children to a research center. With considerable 

effort and examination in homes or schools one can keep loss to a low level. 

When extensive loss occurs it is not random with respect to lead level. In the 

Needleman et al. paper (4), the loss rate due to lack of interest and mobility 

was appreciably and significantly greater for the high lead group than for the 

low lead group. 

The direction of bias associated with extensive differential loss rate is 

not always easy to determine. Since only minimal information about these cases 

can be obtained, the effect of exclusion in a given study is unknown. A higher 
P.36 

Page 

loss rate in higher lead groups reduces the available data for the 

identification of an effect, given it exists, or for the identification of a 

threshold level, if there is one. 

Summary. (a) One is more likely to find an effect, given there is one, by 

studying a population with a higher exposure level, '(b) Confounding variables 

may be less relevant in a more homogeneous population. (c) Without extensive 

effort to minimize loss rate, loss due to lack of parental interest will be 

higher in high lead groups. 

Measurement of Lead Exposure 

The most frequently used index of lead exposure is blood lead level. This 

is considered to be a rather unstable index. Systematic repetition of blood 

lead measurement has not been used. 

Dentine lead from shed deciduous teeth has been the index in the Needleman, 

et al. report (4), in a recent study by Winneke and colleagues (10), and it was 

one of several indices in my work. Variability (or nonconcordance) within and 

between teeth from a given child is noted in all three studies. A recent report 

of a study with dogs (11) indicated a discrepancy between central and lateral 

incisors. This descrepancy increased as dosage increased. 

Erythrocythe protoporphyrin is a sensitive indicator of tissue effect and 

is now used in some screening programs. Interestingly, it also reflects iron 

deficiency and high values require further tests to differentiate conditions. 

The indices are correlated, but the correlations we obtained, which are 

shown in the table, are not high enough for interchangeability. The table also 

includes preschool blood lead values obtained five years prior to the other 

indices. Although blood lead decreased significantly, the between years 

correlations did not differ much from the between indices correlations. 

Means, Standard Deviations, and Intercorrelations of Lead Values 

Variable Descriptive 

Statistics* 

Intercorrelations 

Blood Lead Measures 

Preschool School FEP Dentine 

Lead 

Preschool blood lead 32.5 + 12.7 

School-age blood lead 26.9 + 7.2 

Free erythrocyte pro- 27.2 + 19.6 

toporphyrin (FEP) 

Dentine 6.0 + 5.9 

.46t .46t 

.51t 

.52t 

• 43t 

.66t 

* N = 63 except for dentine data for which N 

t P < .01 

= 34 
P.37 

Page 

One solution to the problem of choice of an index, given the instability of 

each, is the use of several indices in a given study. To date, this approach 

has been used only in our work. (Needleman, et al. had earlier (4-5 year) 

blood lead values for 81 of their children. They did not report the relations 

between these lead levels and any outcome measures for their high and low lead 

groups. These data couid have provided another test of the important question 

of persistence of effect.) 

Summary: (a) Most studies use a single index of lead level although each 

has some degree of unreliability and the intercorrelations among these are not 

high, (b) Use of several indices in the same study will result in more precise 

identification of lead effects, if any. 

Choice of Performance Measures 

Performance measures selected for study should meet two criteria: (a) they 

should be psychometrically sound and, (b) they should be indicators of whatever 

attributes one expects to be affected by lead. Types of measure may be 

hierarchically organized according to the importance and psychometric merit of 

available procedures. 

Some investigators have reported lead effects with measures that are not 

psychometrically standardized. In fact, for some, published procedures are not 

available. While the inclusion of a few experimental procedures is reasonable, 

reporting the results of these in the absence of positive findings with measures 

with known characteristics simply clouds the field. The reader does not know 

just what is measured, let alone how well it is measured or how the data compare 

with data from other research uses. With measures of unknown psychometric 

characteristics, a strong possibility of chance findings must be entertained. 

Furthermore, as discussed later, there are problems that are not ususally 

recognized in having a large battery of procedures. One should have a strong 

rationale for the inclusion of experimental procedures at the cost of 

standardized procedures. 

The more important measures include intelligence, academic achievement (for 

school age children), behavior, and perceptual-motor skills. This order 

reflects both availability of psychometrically sound measures, and, probably, 

importance for the developing child. 

Most investigators include reliable and valid individually administerd 

tests of intelligence. Where positive findings are reported, they are most 

likely to be obtained with these instruments. Effects are small and, as 

indicated above, most investigators fail to include any consideration of 

parental intelligence and have only limited information regarding pertinent 

social factors. 

If children are of school age, standardized measures of school performance 

are indicated. Yule, et al. (3) reported significant effects of lead on 

several academic achievement tests, but once again their study is limited in its 

control of social factors including parent intelligence. De la Burde and Choate 

(12), McNeill and Ptasnik (13), and Needleman, et al. (4) have with failed to 

find significant lead effects with reliable standardized measures of academic 

achievement. If lead has an effect that is more than minimal, it should have 

been detected with these measures. 
P.38 

Page 

Behavior (hyperactivity, short attention span, impulsiveness, etc.) can be 

rated by teachers, parents, or examiners. De la Burde and Choate (12) reported 

significant lead effects with examiner ratings but did not control social 

factors. Milar and associates (14) report no evidence of lead effects on two 

parent rating scales of activity and one free-field experimental measure of 

gross activity. These results, considered with the previously mentioned 

Needleman, et al. teacher ratings, which lack control of confounding variables 

and our negative findings lead to the conclusion that the evidence for lead 

effects on behavior is quite tenuous. 

There is little consistency in results relating lead to psychomotor 

function. Positive findings with the Bender Gestalt test are reported by two 

research groups (de la Burde and Choate (12) and Winneke et al. (10)) but four 

other groups failed to find significant effects. Positive findings have not 

been obtained with other standardized procedures. The occasional significant 

findings reported with experimental procedures have not replicated by other 

investigators. 

Summary. (a) Some performance measures are unstandardized experimental 

procedures of unknown psychometric quality. Nevertheless, positive results with 

these are sometimes emphasized while negative findings with well standardized 

procedures are ignored. (b) Measures may reasonably be ordered: intelligence, 

academic performance, behaivor disburbance, and psychomotor skills. Positive 

findings with the better standardized measures of intelligence and academic 

achievement are more critical than those with the more experimental behavioral 

rating and psychomotor procedure. 

Study-Wise Error and Sample Size 

One might think that the inclusion of a very large number of performance 

measures improves a study since it decreases the liklihood that something 

important is overlooked. Some investigators, however, have not been aware of 

the associated problems. When there are a large number of statistical tests on 

a set of data there is a drastically increased liklihood that some of the 

results will be statistically significant in the absence of a true effect. If, 

for instance, one had statistical analyses of five independent (uncorrelated) 

performance measures in the absence of a true effect, the probability of 

obtaining at least one analysis "significant at the .05 level" is .23, not .05. 

One could reduce this risk to .05, study-wise, by requiring an .01 level for the 

individual analyses. If the number of individual statistical analyses is 

increased to, say, 50, the probability of having one or more individual analyses 

of independent variables reach the .05 level in the absence of true effect is 

.92. In order to reach a study-wise error rate of .05 one would have to ignore 

any statistical analysis for which the calculated probability is greater than 

.001. This situation is not farfetched. The lead study that appears to have 

the largest number of individual (or univariate) statistical tests is that of 

Needleman et al. (4) with at least 52 performance measures. By these 

calculations only two statistical tests in that study should be considered. 

These are two trial blocks of the experimental unstandardized reaction time 

procedure. 

The above is somewhat oversimplified since the performance measures are 

certainly not independent. Failure to consider the intercorrelations among 

performance measures can lead to distortions in the statistical analyses. 

Unlike some of the other biases in these procedures, the directions of 
P.39 

Page 8 

distortion are not always predictable. 

There are effective procedures to reduce the number of statistical analyses 

in a large data set. These inlcude data reduction techniques and the use of 

multivariate statistics. As a bare minimum, the investigator should interpret 

very conservatively a very few "statistically significant" tests in group of 

tests of outcome measures. This caution is not common in this area of research, 

yet failure to consider the issue is probably as important as inadequate control 

of confounding variables. 

A related technical issue is the relation of sample size to the size of the 

set of variables. A reasonable rule of thumb is that the ratio of number of 

subjects to number of variables should be about 10/1. Most of us have violated 

this to some extent, but the most flagrant violation is in the Needleman et al. 

report (4) with its very large number of variables. The problem is that if the 

data had been analysed by appropriate use of multivariate procedures, there 

would not have been enough statistical power in the analysis and true effects, 

if any, might not be detected. The direction of distortion here is not easily 

predicted but statisticians warn that distortions may be quite serious. 

Summary. An investigator with a large number of performance measures must 

carefully consider several major technical difficulties: (a) the univariate 

statistics which are most frequently used will greatly increase the liklihood of 

concluding that there are effects which are not true, (b) intercorrelations 

among performance measures leave one unable to make adequate corrections for 

these error rates and distort the study-wise probability situation in ways that 

can 't be predicted and, (c) in order for the appropriate multivariate 

statistical tests of a large data set to be reasonably powerful, a very large 

number of subjects must be enrolled. 

Implications 

The methodological issues raised are not trivial. Where a direction of 

bias can be identified, as for inadequate control of confounding and inadequate 

handling of study-wise error, the direction is toward exaggerating an existing 

effect or reporting an effect which is not there. When we considered all 

published studies and our own data in light of these issues we found that we 

could not support a statement that low level lead exposure influences the 

intelligence or behavior of children. 

Infants as £ Special Group 

The conclusions drawn so far have dealt with preschool and school age 

children. It has been suggested that infants prior to birth and in the early 

period of infancy might be particularly vulnerable to toxic effects since this 

is the time of maximal brain development. The hypothesis is being studied at 

several centers, including ours. The prospective study design appropriate for 

this takes time; at the moment all I can provide is preliminary data reflecting 

exposure of the fetus. 

Levels of lead in cord blood are low. We collected maternal and cord 

bloods from a preliminary sample of 67 mother-infant pairs. This is from a 

population at risk for high lead values. The sample is of low socioeconomic 

level. The women reside, often in older housing, in the inner city area of an 

industrial city. The incidences of poor nutrition, smoking, alcoholism, and 

polydrug use are considerably higher than for the general population. It is 

possible that women occupationally exposed or who engage in unusual behavior 
P.40 

Page 9 

(pica of pregnancy, drinking moonshine liquor, etc.) will have higher lead 

values; aside from aberrant conditions our means will be about as high as one 

might find. The means are about 16yg/dl whole blood for both maternal and cord 

samples. The highest cord lead level was 23.9yg/dl whole blood. These figures 

are appreciably below the lead levels of 30-35 ug/dl suggested in several 

sources as being associated with some risk to the fetus or newborn. 

We have not completed collecting the data to determine whether there are 

cognitive and behavioral effects associated with these levels. My expectation 

is that effects, if any, with neonates, will be minimal and nonpersistent. This 

expectation is based in part on the evidence available for older children and, 

in part, on experience in infancy studies. Newborns are more robust than is 

usually thought. If we exclude markedly damaged infants, those of us doing 

research on infant development, find it difficult to demonstrate persisting 

effects of neonatal risk conditions such as anoxia or prematurity. 

In studies of the development of infants at risk, parental, social, home 

stimulation, and nutrition factors overwhelm other variables. When we do lead 

research we are trying to detect a possible faint signal through continuing 

noise. The children most likely to be exposed to lead are these most likely to 

be poorly nourished, to live in substandard housing, to have a mother who is 

herself a child, to have no visible father, to have one or both parents actively 

abusing drugs, to witness or be victims of stress and violence, and are least 

likely to have remedial or enriching education opportunity... We are here 

considering the possibility of a just noticable difference associated with lead. 

The real concern should be with the reduction of programs to ameliorate the real 

problems of these children. 

I recently wrote that there may be a risk of frank lead poisoning in 

vulnerable children and that this risk justifies limitations on lead in 

gasoline. The statement was made out of an interest in being very conservative 

pending continuing research results. Three conditions, which I had not 

completely reviewed, would support this conservative position. First, there 

must be a reasonable number of children of elevated lead level who might be near 

a threshold of effect. Second, these children would not have been identified by 

screening programs with the consequent removal of primary sources of exposure. 

Third, the increase in airborne lead associated with changes in gasoline 

additives must be great enough to increase the lead level in these children to 

the point that they cross a threshold of effect. Information on these condtions 

is beyond my expertise. 

I'd like to quote from an editorial by Martin Bax in Developmental Medicine 

and Child Neurology. 

"It is very tempting to accept some physical aspect of the environment - be 

it blood lead, food additives or too much sugar - as the cause of children's 

problems. By doing so, we need look no further at the child and his family and 

can avoid uncovering the uncomfortable fact that adults are not invariably 

sensitive to children's needs. This of course extends beyond meeting their 

simple physical needs to providing an environment in which cognitive and social 

skills can develop. Knowing one s own frailties, it is unwise to point the 

finger at another human being and easy to elect the petrol tanker as the source 

of all the mischief." 
P.41 

References 

1. Perino, J. and Ernhart, CB . The relation of subclinical lead level to cognitive 

and sensorimotor impairment in black preschoolers. Journal of Learning Disabilities, 1974, I, 616-620. 

2. Ernhart, C.B., Landa, B. and Schell, N.B. Subclinical levels of lead and development deficit - a multivariate follow-up reassessment. Pediatrics, 1981, 67, 

911-919. 

3. Yule, W., Lansdown, R., Millar, I.B. and Urbanowicz, M. The relationship 

between blood lead concentrations, intelligence and attainment in a school 

population: A pilot study. Developmental Medicine and Child Neurology, 1981, 

23, 567-576. 

4. Needleman, H.L., Gunnoe, C , Leviton, A., Reed, M., Peresie, H., Maher, C. and 

Barrett, P. Deficits in psychological and classroom performance of children 

with elevated dentine lead levels. New England Journal of Medicine, 1979, 300, 

689-695. 

5. Milar, CR., Schroeder, P.M., Dolcourt, J.L. and Grant, L.D. Contributions of 

the caregiving environment to increased lead burden of children. American 

Journal of Mental Deficiency, 1980, 84, 339-344. 

6. Bradley, R. and Caldwell B. Early home environment and changes in mental test 

performance from 6 to 36 months. Developmental Psychology, 1976, ^12, 93-97. 

7. Rutter, M. Raised lead levels and impaired cognitive/behavioral functioning: A 

review of the evidence. Developmental Medicine and Child Neurology, 1980, 

_22, 1-25. 

8. Oski, F.A. and Honig,.A.S. The effects of therapy on the developmental scores 

of iron-deficient infants. Journal of Pediatrics, 1978, j^2_, 21-25. 

9. Lozoff, B., Brittenham, CM., Viteri, F.E., Wolf, A.W. and Urrutia, J.J. The 

effects of short-term oral iron therapy on developmental deficits in irondeficient anemic infants. Journal of Pediatrics, 1982, 100, 351-357. 

10. Winneke, G. , Broekhaus, A., Kramer, U., Ewers, U., Kujanek, C , Lechner, H. and 

Janke, W. Neuropsychological comparison of children with different tooth-lead 

levels. Preliminary report. Unpublished paper presented at the International 

Conference on Heavy Metals in the Environment. Amsterdam, September, 1981. 

11. Kaplan, M.L. , Peresie, H.J. and Jeffcoat, M.K. The lead content of blood and 

deciduous teeth in lead-exposed beagle pups. In H.L. Needleman."(Ed.), Low 

Level Lead Exposure: The Clinical Implications of Current Research, New 

York: Raven, 1980. 

12. De la Burde , B. and Choate, M.S. Early asymptomatic lead exposure and development at school age. Journal of Pediatrics, 1975, 87, 638-642. 
References (continued) 

13. McNeil, J.L. and Ptasnik, J.S. Epidemiological study of a lead contaminated 

area. Draft final report, Project LH-208. International Lead and Zinc Research 

Organization, 1975. 

14. 

15. 

Milar, C.R., Schroeder, S.R., Mushak, P. and Boone, L. Failure to find hyperactivity in preschool children with moderately elevated lead burden. Journal 

of Pediatric Psychology, 1981, J3, 85-95. 

Bax, M. Editorial. Lead and impaired abilities. 

Child Neurology, 1981, 23, 565-566. 

Developmental Medicine and 
P.43 

jTXfi ,&.C.t- 3& 

Claire B. Ernhart 

October 7, 1983 

Response to Appendix 12-C 

INDEPENDENT PEER-REVIEW OF SELECTED STUDIES CONCERNING 

NEUROBEHAVIORAL EFFECTS OF LEAD EXPOSURES IN NOMINALLY 

ASYMPTOMATIC CHILDREN: 

OFFICIAL REPORT OF FINDINGS AND RECOMMENDATIONS 

OF AN INTERDISCIPLINARY EXPERT REVIEW COMMITTEE 

I'd like first to commend the Committee for the objectivity of 

its analyses and for the care with which it reviewed the materials 

provided. I concur with most of what is included in the report and I 

only wish that I had more and better data with which I could answer 

more definitively the questions posed by the Committee. On only one 

suggestion, discussed below, would I disagree with the recommendations . 

The introduction presented well the more critical of the 

issues relevant to the design of research in this area. The 

weaknesses of cross- sectional designs are well stated. With the 

completion of the very important U.K. studies, we will probably see 

fewer cross-sectional studies. Meanwhile, we are waiting for the 

results and dealing with the difficult problems arising in the 

conduct of the prospective studies. 

The balance of these comments deals with the review of the 

studies by my associates and me. At the time this review was 

written, the Committee did not have my report of further analyses of 

my data. While these were not conducted precisely as suggested by 

the Committee in the report at hand, the major suggestions were 

implemented as well as possible and I feel that further manipulation 

of the data is not warranted. 

Specific Points: 

P.15, first paragraph. All analyses of reading scores had age 

at time of testing entered as the first covariate. Perhaps regressing raw scores for the McCarthy scales on age rather than using 

extrapolated or normed scores would have been.better. I'm concerned 

about the regression effects inherent in that approach. It seems 

highly unlikely that this would influence the results in any 

appreciable way. 

P.15, last paragraph. In the reanalyses provided education was 

forced into the covariate set although it was not significantly 

related to the outcome measure in any analysis after entry of parent 

I.Q. I can see the merits of the backward selection procedure in 

this kind of analysis. In this case, I doubt that taking it back out 

would have made any difference. 
P.44 

P.17 (f). I was unaware that Perino had more high lead cases 

early in the data collection period. His wife set up the data 

collection schedule. Since he was blinded and well trained, I don't 

think the order had an effect, but it was not ideal. 

P.18. I had considered handling the data as a cross-lagged 

panel design as one way of assessing the possiblity that early 

deficits in intelligence could lead to higher levels of lead. As 

noted, the cross correlations were low and not appreciably different 

from each other so I gave up that approach. In some of my present 

work, I'm developing causal models to handle these problems of 

longitudinal relationships. I question, however, whether there is 

much more that can be done in that regard with the set of data under 

review. 

The problems of measuring change are old familiar concerns. A 

simple change score for the intelligence measure was added to the set 

of reanalyses supplied in August. Residuals computed from the 

regression of the later measure on the earlier, as suggested by Dr. 

Jones, would have given a somewhat different resolution of the 

problem, both numerically and in the sense of what the model represents. Aside from all the problems involved in the measurement of 

change, the idea of change in intelligence as a outcome variable 

related to the early exposure index is reasonable. 

One can also put forth a rationale for change in lead level as 

an outcome measure related to early intelligence. (Less intelligent 

children may be more likely to be exposed or more intelligent 

children to stay away from it.) 

In both of the above designs the concern is with the effect of 

the earlier condition on change. What Dr. Jones suggested, however, 

is that both later measures be regressed on the corresponding earlier 

measures; this essentially cancels either as a plausible etiological 

factor in the model. The residualization of the lead measure is of 

particular concern both because the more frequently hypothesized 

direction of effect is from lead to deficit and because lead level 

dropped appreciably from the preschool to the schoolage time of 

assessment. If lead levels in the range under consideration do have 

an effect, the earlier higher levels are of much greater concern than 

the later levels. This is particularly so if there is any 

possibility of a threshold of effect within this range. 

The availability of the early lead measure is what makes this 

a longitudinal as opposed to a cross-sectional study and it is 

important. With the full sample of 62 children, the relatively high 

preschool index of exposure was not significantly related to any 

later outcome measure. 

I object to the statement on p.18, 12th line from the bottom: 

"These simple logitudinal analyses provide support for the hypothesis 

that an increase in blood Pb from ages 4-5 to 9-10 yrs, is associated 

with a decrease in IQ ..." While mean IQ changed very little, mean 
P.45 

Tead level dropped appreciably and very few children actually 

increased in lead level. The use of residual scores in this situation 

leads to the anomalous situation in which actual decreases in lead 

level are identified as increases in residual score form because they 

do not decrease to the extent predicted by the regression. It's 

interesting to look at the actual paired lead levels for the children 

identified by subject number in Figure 1. The greatest "decrease" is 

for #58 whose lead level was 10 on both times of sampling. In the 

range to the right of the mean, the same residual score could be 

obtained both by increasing or by decreasing lead level, depending on 

the initial value. This makes sense from what we know about regression, but it is not very sensible from the perspective of the person 

needing to make decisions about the effects of lead. 

Most certainly the fact of the drop in lead level over time 

should be brought into this discussion. The statement quoted above 

can easily be misconstrued by persons not familiar with this fact and 

with the nature of regression analysis. 

With low cross lag correlations, it's hard to make much sense 

out of the correlation between residuals. It could reflect another 

changing condition not included in the covariates, or, perhaps, 

intra-individual lability or stability. 

Once again though, the most important problem with this model 

for analysis of the data is that it statistically extracts the most 

important variable, i.e., the preschool lead index. 
P.46 

JZp.ts. -t. /.3e> 

Claire B. Ernhart 

SUMMARY REPORT 

Reanalysis of Data of Three Studies 

The Effects of Lead on Children3 

In this report we will be referring to three sets of data. The first 

is the set reported in the Perino-Ernhart paper; the sample for this consisted 

of 80 urban black preschool age children. The second set of data, reported in 

a dissertation by Yamins, was collected using 80 suburban black and 20 suburban white children. The third set of data resulted from a follow-up examination 

of 63 of the children of the first study. 

Various reanalyses of these data have been suggested by different 

individuals, including members of the Peer Review Panel selected by EPA for 

review of these studies and those of another investigator. The rationale for 

each feature of reanalysis and the results obtained will be presented. 

In all three data sets the investigators had followed the strategy of 

incorporating into the statistical analysis only those covariates which significantly reduced the variance of the outcome measure (in a stepwise manner) 

before the entry of the lead variable. Current thinking on the matter-*-'^ is 

that this is not the most appropriate strategy, that covariates should enter 

the model on rational or ja priori grounds. On this basis, Kupper^ recommended 

that parent education, which is correlated with lead level, be entered into 

the statistical model even though it adds little after parent intelligence is 

entered. 

Perino-Ernhart Study 

In the course of conducting the reanalyses to include parent education, 

we found several errors in the data and the previous analyses. One child's age 

was incorrect by one year (38 months rather than 50 months). This changed his 

General Cognitive Index (GCI) from 50 to 86; other scores were correspondingly 

affected. Another child's GCI was incorrect by one point. The degrees of 

freedom used and reported in the tests of significance of the lead effect 

(regression analyses) should have been 1 and 75, not 4 and 75. 

When the data were corrected, none of the analyses were statistically 

significant. The results provided in Table 1 are for the regression analyses 

of raw scores with age as a first covariate and for normed scores. For both 

sets of analyses, the covariates entered prior to the lead data were parent 

IQ, birth weight and parent education. We also computed the corresponding 

analyses without parent education. For the raw score analyses, this provided 

a corrected reanalysis of the published analyses. The results with parent 

education omitted differed only slightly from those provided in Table 1. In 

other words, the previously reported significant association of lead level 

and McCarthy Scale GCI, Verbal and Perceptual-Performance Scales was a result 

of the errors in the previous analyses, not the exclusion of the parent education covariate. 

The assistance of Beth Landa, Janice Yamins and Abraham Wolf in the analyses 

of these data and preparation of this report is gratefully acknowledged. 
Table 1 

Regression Analyses Relating Lead Level 

to McCarthy Scale Scores, Pre-School 

Data, Corrected 1983, N = 80 

Scales 

McCarthy Scales of 

Children's Ability 

Raw Score Data 

Variance Associated 

with Control Variables 

Increment 

Associated with Lead 

Variance £ 

Normed Score,Data 

Variance Associated 

with Control Variables 

Increment 

Associated with Lead 

Variance 1 p_ 

Gen. Cog. Index 

Verbal 

Perceptual-Performance 

Quantitative 

Memory 

Motor 

.85 

.71 

.75 

.70 

.65 

.77 

.006 

.005 

.008 

.001 

.003 

.000 

.10 

.29 

.13 

.58 

.45 

.74 

.31 

.18 

.16 

.15 

.14 

.13 

023 

015 

017 

001 

011 

001 

.11 

.24 

.22 

.76 

.33 

.82 
P.48 

Another frequently cited feature of the previous report was a 

contrast between the correlation of child intelligence with parent intelligence for moderate and low lead groups. The interpretation was that lead 

exposure disrupted the usual relationship of parent and child intelligence. 

When the data were corrected, the correlation for the moderate lead group 

changed from .10 to .25. This is not significantly different (£ = .17, two 

tail) from the correlation of .53 obtained for the low lead group. 

Yamins Study 

Yamins found the data worksheet from which her cards had been 

punched, but the cards and computer output had apparently been lost or discarded. We entered the data from the worksheets into our computer and reran 

her analyses. Errors which appear to have been clerical were identified in a 

matrix of intercorrelations. The corrected matrix has been made available. 

We also reran and confirmed the regression analyses as provided in the dissertation. We then planned to determine whether further corrections in the 

data were indicated. 

One of the first things necessary for further analysis of the Yamins 

data was determining the method of blood analysis. Blood samples obtained by 

finger-stick (micro technique), collected on a filter paper from which punched 

discs were obtained and analyzed by the Delves cup technique £re subject to 

errors of which we had been unaware at the time of the study. Even with great 

care, the finger-stick method yields a higher (about 6 yg/dl) lead level and 

the Delves cup method overestimates National Bureau of Standards results in 

this general range by about 1.95 yg/dl . These errors would relate to the 

level to which effects are attributed; they would not alter statistical significance levels. The third difficulty, however, required recomputation of 

the lead index. Carter^ has reported that low hemoglobin is associated with 

a greater spread of blood over a filter paper. With this greater diffusion, 

the lead remaining in the area assayed by a punched disc is correspondingly 

diminished. Correction formulas provided by Carter are based on hematocrit 

per cent. Combining three sources of error, the adjustment for blood lead 

index could be determined by 53.8 PbB (disc) 7 __ It had been planned to 

Hematocrit % 

compute this for all children for whom hematocrit data were available. Appropriate correction of the present data was recommended by Muschak . 

I planned then to analyze the Yamins data, with corrected blood 

values, in conjunction with the Perino data in order to increase statistical 

power and to identify a threshold of effect if this could be observed. The 

differences between the samples were limited to a) year of recruitment, b) 

use of the PPVT as opposed to McCarthy Scale GCI, c) suburban as opposed to 

urban residence, and d) examiner. The samples did not differ in age, parent 

intelligence, parent education, birth weight, birth order, or sex. The plan 

was to control such differences as were present by entering group as the first 

covariate. Additionally, the group by lead level interaction would have been 

analyzed as a test of the merger of the two samples. 
P.49 

After considerable effort in tracing records and contacts with 

persons connected with the lead screening program, Yamins determined that 

the punched disc technique had indeed been the method used with her subjects. 

She then started to inspect records in the archives of the Nassau County 

Department of Health and found that, at the time of her study, hematocrit 

values were recorded for very few of her subjects. Furthermore, those for 

whom it was recorded appeared to be high lead level children. If there were 

multiple lead determinations (Yamins used mean, highest and most recent lead 

level), hematocrit level might be found for only one of the blood tests. On 

the basis of a review of 15 cases, we projected that we could obtain usable 

hematocrit data for the corrections of the blood lead data for no more than 

10 to 12 of the 80 black children of her study and these would be almost 

exclusively high lead level children. 

This is not sufficient for further analysis and we have concluded, 

quite regrettably, that the Yamins data are not correctable and that no conclusions can be drawn from her study. 

"i 

The Follow-Up Study 

The re-evaluation of 63 of the children seen at the first (PerinoErnhart) study was of particular interest because it provided'the most 

systematic attempt, before the onset of the prospective studies, to relate 

early or preschool lead exposure to later, school age, outcome measures. 

Only McCarthy Scale Scores and Reading Level data were included in 

the present reanalyses. Other outcome measures (including the Bender Gestalt 

Test data) reported in the published paper, yielded results which showed no 

possibility of statistical significance under any form of data manipulation. 

Some of the additional procedures correct our data and method of 

analysis to resolve problems which were unknown to us at the time of the previously published analyses. Others are conducted in response to various suggestions. By virtue of the sheer number of analyses (albeit nonindependent), 

the possibility of identifying significant effects is increased and this wil? 

be considered in the summary of the findings. 

1. The capillary blood samples had been analyzed by the punched disc 

technique as described above. Hematocrit data were available in our files for 

only 46 of the children, including one later excluded as an outlier. In some 

cases the blood samples had been hemolysed and hematocrits could not be determined and in others the data were not recorded on the forms supplied us by the 

New York City Department of Health. (We had hot requested the information at 

that time.) Efforts to obtain these data for those children for whom it was 

missing were not successful since the information was not retained in the 

archival records. The 17 children without hematocrit data were not significantly 

different from the remaining children on the preschool blood lead data (t = .13). 

We did not test differences on other variables, but all looked trivial, as would 

be expected. 
2. Parent education was forced into all statistical models as were 

parent IQ and sex. In general, only parent IQ made appreciable contributions 

to the variance of the McCarthy Scales. 

3. The intercorrelations of lead exposure indicators were only 

moderate. This reflects the well known fact that indicators fluctuate over 

time and that each is related in a different way to body lead burden. It has 

been suggested8 that combining indicators into a single construct index would 

provide a more valid measure of exposure. 

A lead construct index was generated by Converting the preschool age 

blood lead level, the school age blood lead level (adjusted for hematocrit 

percent), and the erythrocyte protoporphyrin levels to z-scores and summing 

these. Dentine lead was not included because the sample size would have been 

depleted still further. Furthermore, aside from the single outlier case 

described below, dentine lead is not even marginally associated with the 

outcome measures. What we are trying to do here is to very deliberately devise 

a lead index which is more likely than the individual scales to be related to 

the outcome measures. This construct scale, then, was related to school age 

outcome measures in the same manner as the independent preschool and school age 

indices. 

4. Developmentalists are aware of interactions of health risk factors 

and social risk factors. For example, the effect of preterm delivery is greater 

in children of lower socioeconomic status than for children with a more enriched 

Q 

environment. Following this direction of thought, it has been suggested .that 

the effects of lead exposure would be greater for children whose parents are of 

lower intelligence. This can be tested in an analysis of the interaction of 

parent intelligence and lead level. 

The possibility of such an interaction was tested by generating two 

variables which were the products of school age lead level (adjusted) and parent 

intelligence and also lead construct and parent intelligence. Each of these was 

tested in the regression models after the variance associated with parent intelligence and the respective lead index were partialled. 

5. Although preschool blood lead level was not significantly related 

to later intelligence measures, it was suggested that it is still possible that 

it was related to change scores. In other words, lead level might be related 

to the amount and direction of change in scores. On this basis Jones^O suggested analysis of change scores for the children seen in the first preschool 

study and the follow-up study. 

As a test of this possibility, change scores for the two most likely 

outcome variables, General Cognitive Index and Verbal Index, were computed to 

form additional outcome variables. 

6. The possibility of a threshold of effect is suggested by the data 

of several studies, most notably in reanalyses^ of the data of one of the more 
P.51 

widely cited studies. In reviewing our data, we noted that one child, JT, was 

markedly different in many respects and probably should have been identified 

as having excessive lead exposure. A summary of what is known about him will 

be presented below. His data were deleted from all analyses reported herein 

except the analyses of the preschool results reported above (Table 1). 

Results, Follow-up Study Reanalyses 

When we computed the z-scores for FEP for the computation of the lead 

construct score we noted that one other child, WJ, had a z-score of 5.16 (own 

data included in computations). Her FEP was a highly deviant 130 ug/dl whole 

blood. In addition to a preschool blood lead level of .05 mg/dl, our records 

indicate three school age lead level analyses. The first was taken shortly 

after the psychometric testing (June 1977). The lead level was 35 ug/dl; the 

sample was too small to do the FEP analysis. The second sample, taken to get 

the FEP, was also a microsample. It was obtained six months later (January 

1978). The lead level was 40 yg (41 adjusted) and the FEP was 130 yg. These 

were the data recorded for analysis. Because of the elevation, a venous sample 

was obtained (March 1978) and the analysis yielded 28 yg of lead, 69 yg FEP 

and 44% hematocrit. In August, 1978, an evaluation for possible anemia yielded 

serum iron of 81 and a TIBC of 296. These are described as normal. The reason 

for the highly deviant FEP is not known, but an inaccuracy in analysis is 

plausible. At the same time, use of the surely more accurate value of 69 

obtained with the venous" sample would not be appropriate. Over the five year 

period of the study her Gen. Cog. Index score changed from 50 to 70; the Verbal 

Score changed from 22 to 21. In the analyses that follow, results for the 

adjusted lead data are presented with and without her data. Her data were 

excluded from the analyses of construct scores, which incorporated FEP and 

from the interaction tests. 

As seen in Table 2, preschool lead level remained unrelated to any 

outcome measure collected five years later. Reference to Tables 2 and 3 

indicates that only two analyses yielded results significant at the .05 level 

and none at the .01 level. Let us look first at the interaction of lead 

(adjusted) and parent intelligence on Perceptual-Performance scores (Table 

3). Lead (adjusted) was not a significant main source in this analysis 

(Table 2). The interaction was of a crossover form with a wide discrepancy 

associated with parent IQ at the higher end of the lead distribution. Furthermore, scores were negatively associated with lead for low intelligence parents, 

as predicted; but positively associated with lead for high intelligence parents. 

The slopes, in opposite directions, were almost equal, for + 1 SD parent intelligence. Since there is no reasonable interpretation for a beneficial effect 

of lead for higher intelligence parents and since the main effect of lead did 

not approach significance, it's reasonable to infer that this is a/-chance finding. 

The one other significant statistical test was for lead (adjusted) . 

and Verbal Scale when the child with elevated FEP was included in the sample. 

There are not sufficient grounds to say that she was impaired as a result of 

lead exposure and/or iron deficiency. If the sample size were larger she might 

well be part of a small group of children at the upper end of the distribution 

whose data would suggest a threshold of effect. 
Table 2 

The Association of Preschool Lead and School Age Lead (Adjusted) 

on Major Outcome Variables 

Outcome 

Variable 

Preschool 

Lead Level 

Control 

Variance 

Increment 

Associated 

with Lead £ 

School Age Lead (Adjusted) 

With 

c Deviant Case 

Control 

Variance 

Increment 

Associated 

with Lead £ 

Without 

Deviant Case 

Control 

Variance 

Increment 

Associated 

with Lead £ 

McCarthy Scale 

Gen. Cog. Index 

Verbal 

Perceptual-Performance 

Quantitative 

Memory 

Motor 

Reading Level 

Change in Gen. Cog. Index 

Change in Verbal Index 

27 

26 

12 

07 

14 

16 

27 

05 

06 

.000 

.029 

.005 

.027 

.029 

.012 

.023 

.026 • 

.007 

.88 

.13 

.59 

.20 

.16 

.37 

.19 

.21 

.53 

.29 

.30 

.09 

.11 

.16 

.31 

.25 

.11 

.07 

.030 

.066 

.004 

.003 

.015 

.002 

.002 

.010 

.036 

.20 

.047 

.66 

.70 

.40 

.•77 

.74 

.51 

.22 

.27 

.28 

.11 

.11 

.14 

.29 

.24 

.16 

.07 

.025 

.052 

.010 

.004 

.010 

.003 

.001 

.024 

.035 

.24 

.09 

.51 

.67 

.49 

.69 

.85 

.28 

.23 

The age at which the reading test was given was entered as the first covariate. 

, N = 62 for McCarthy Scale Variables, 59 for Reading Level. 

CN = 45 for McCarthy Scale VariabJ.es, 43 for Reading Level. • 

N = 44 for McCarthy Scale Variables, 42 for Reading Level. 
Tabic 3 

The Association of Lead Construct Scores 

and Interactions of Lend Indices and 

Parent Intelligence With Ma.lor Outcome Variables 

Outcome 

Variable 

Control 

Variance 

Lead 

b 

Construct 

Increment 

Associated 

with Lend £ 

Interaction 

Lead (Adjusted) by 

Parent Intelligence 

Variance, Prior 

Variables 

Including Lead 

Increment 

Associated 

witii Interaction £ 

Interaction 

Lead Construct by 

Parent Intelligence 

Variance, Prior 

Variables 

Including Lead 

Increment 

Associated 

with Interaction 

-

£ 

McCarthy Scale 

Cen. Cog. Index 

Verbal 

Perceptual-Performance 

Quantitative 

Memory 

Motor 

Reading Level 

Change in Gen. Cog. Index 

Change in Verbal Index 

27 

28 

11 

11 

IA 

29 

24 

16 

07 

.021 

.050 

.002 

.004 

.016 

.000 

.004 

.009 

.041 

.29 

.10 

.76 

.67 

.39 

.88 

.65 

.52 

.19 

.30 

.33 

.12 

.12 

.15 

. .30 

.25 

.18 

.10 

005 

000 

099 

007 

006 

045 

010 

005 

015 

.59 

.92 

.035 

.58 

.61 

.12 

.51 

.64 

.43 

.29 

.33 

- -11 

.12 

.16 

.29 

.25 

.18 

.11 

.000 

.000 

.057 

.024 

.004 

.027 

.022 

.005 

.008 

.99 

.96 

.12 

.31 

.67 

.23 

.32 

.64 

.56 

The age at which the reading test was given was entered as the first covariate. 

N = 44 for McCarthy Scale Variables, 42 for Reading Level. 

W. 
P.54 

+,• 

I t . I \ 

As they now stand, the data do not support an inference of lead 

effects. If there are such effects in the range of exposure sampled here 

they are small. At the same time, the statistical power of these analyses 

is low, particularly since the sample was depleted. Thus the inference bf 

no effect is not justified. It would be possible, I suppose, to derive other 

indices or ways of analyzing these data in the hope of finding positive results, 

but I doubt they'd be any more successful. I continue to believe that if there 

are effects at the low or moderate range here, or in other well designed, 

appropriately conducted, studies they are small indeed. 

« 

The possibility of an effect in higher level children whose caretakers do not identify and/or seek treatment remains. Earlier I indicated 

that the data of one child had been excluded from all analyses save those of 

the preschool outcome data. The evidence suggesting the possibility of mental 

retardation secondary to elevated lead exposure was submitted in a memo dated 

June 6, 1983. To summarize: Blood leads ranged from 31 to 60 ug/dl at various 

times of sampling, with the highest occurring at a preschool evaluation. FEP 

values were moderately elevated. Most critically, the dentine lead level of 

107.35 was highly abnormal. From the time of preschool testing, the intelligence test score (McCarthy GCI) dropped from 80 to 48. At the time of the 

preschool evaluation, records from the N.Y.C. Lead Poisoning Control Program 

indicated pica and the presence of excessive levels of lead in the home. The 

family refused correction. The parents were directed to take the child for 

medical attention but apparently did not comply. The family still lived at 

this residence at our reevaluation five years later. 

This tragic case is consistent with an interpretation of marked lead 

effects at moderately high levels in a child with pica and with preschool 

exposure over a period of time. The inclusion of his data in analyses of low 

level lead effects is not warranted and his data were deleted from analyses 

of the school age outcome measures. 

In conclusion, these sets of data do not support an inference of low 

level lead effects. Unfortunately, the rather low statistical power prevents 

a definitive conclusion of no effect. I just wish it were possible to replicate 

this basic study with a larger sample, with more sophisticated research methods 

and with carefully conducted analyses of venous blood collected specifically 

for research. 
( ' • 

1. Kleinbaum, D.G., Kupper, L.L., & Morgenstern, H. Epidemiologic Research. 

Behmont, Calif: Lifetime Learning, 1982. 

2. Cohen & Cohen, P. Applied Multiple Regression/Correlation Analysis for 

the Behavioral Sciences. Hillsdale: Lawrence Erlbaum Associates, 1975. 

3. Kupper, L.L. Personal Communication. (Peer Review Group) March 17, 1983. 

.4. Mahaffey, K.R., Annest, J.L., Roberts, J., Murphy, R.S. National estimates 

of blood lead level: United States 1976-1980. New England Journal of 

Medicine, 1982, 307, 573-579. 

5. Boone, D.J., Hearn, T., & Lewis, S. Comparison of interlaboratory results 

for blood lead with results from a definitive method. Clinical Chemistry, 

1979, 2i» 389-393. 

6. Carter, G.F. The paper punched disc technique for lead in blood samples 

with abnormal haemoglobin values. British Journal of Industrial Medicine, 

1978, J35 235-240. 

7. Muschek, P. Personal Communication (Peer Review Group) March 17, 1983. 

8. Cohen, J. The Needleman and Ernhart studies on behavioral effects of 

subclinical lead from the perspective of quantitative methodology. ILZRO, 

1983. 

9. Pearson, D.T. & Dietrich, K.N. Unpublished manuscript, 1983. 

10. Jones, L.V. Personal Communication (Peer Review Group) March 17, 1983. 

11. Bellinger, D. & Needleman, H.L. Lead and the relationship between maternal 

and child intelligence. Journal of Pediatrics, 1983, 102 523-527. 

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