Response to Letters-to-Editor of Health Physics in Sept 1999 issue by Lubin and by Field et al -- for those interested.

[Bernard L Cohen <blc+@pitt.edu>]

	In the July 1998 issue of Health Physics, there was an exchange
between Jay Lubin and me on his criticisms of my paper in the Feb. 1995
issue of Health Physics on"Test of the Linear-No Threshold Theory (LNT)"
by use of data on lung cancer rates vs average radon exposures in 1729
U.S. Counties. My study showed a discrepancy with predictions of LNT by
over 20 standard deviations and this discrepancy was insensitive to a very
wide variety of potential sources of inaccuracy or confounding. While some
points were cleared up in our exchange, Lubin had the last word in which
he made points that I felt had to be refuted. I immediately submitted a
letter on this, but the Editor agreed to publish it only on the condition
that Lubin would get a reply to it and no further discussion would ensue.
I had no choice but to agree to this condition; my letter was published in
the April 1999 issue, and Lubin's reply was published in the Sept. 1999
issue. Since I have no opportunity to respond in print to this Lubin
reply, I respond here on RADSAFE for those interested.
	The issue was that Lubin published a graph purporting to show that
my data were grossly discrepant with the results of case-control studies
of radon in homes. His figure, reproduced as Fig. 1 in my April 1999
letter, extrapolated a linear fit to my low dose data not only ignoring
the non-linear behavior of my data at higher doses that I had pointed out
in a 1996 paper, but also extrapolating far beyond the last point in my
data. He had done this in a previous publication, after which I had
pointed out the error in his doing this both in print and in person, but
he still used that figure in his July 1998 paper and it even appeared as
Fig. 3-2 in the recently released BEIR-VI Report of which he was a key
author. 
	In several previous papers and in my April 1999 letter, I pointed
out that the case-control studies gave the risk to individuals, whereas my
study gave the average risk to populations of counties and therefore
cannot be used to determine directly the risk to individuals -- the
average dose does not in general determine the average risk, as is obvious
in situations where a threshold is involved. Ignoring this problem is
called "the ecological fallacy" and I have pointed this out many times.
Only if one is testing a linear-no threshold theory is "the ecological
fallacy" avoided. That is why I entitled my paper "Test of LNT...", and I
have never claimed that I was determining the risk vs dose to individuals.
For example, the average risk declines very clearly with increasing dose,
but I have never claimed that this can be interpreted as hormesis.
	 Thus the very concept of comparing my data with results of case
control studies is misguided, but in spite of my repeatedly pointing this
out, Lubin persisted in using his erroneous graph to claim that there is a
gross discrepancy between my data and the case-control studies. In my
April 1999 paper, after duly protesting, I accepted Lubin's defiance of
"the ecological fallacy" and went through the exercise of interpreting my
data as risk vs dose to individuals, but doing it correctly, for
comparison with case-control studies. The comparisons were not bad. Of the
33 data points from case-control studies, one would expect 1.7 of them to
lie outside the 95% confidence limits, and that expectation was fulfilled
with one lying above and the other below my data. In reaching this
conclusion, I excluded two additional case-control data points, and
Lubin's Sept. 1999 paper challenged this. His challenge on the Missouri
study was wrong: the point covered data for 91-566 Bq/cubic m and to be
consistent with my data the point would only have to be plootted above 270
Bq/cubic meter. The other excluded point that he challenged was due to the
fact that we were using different "Stockholm studies" - I haven't found
the study he was using, but he was probably correct, so there were
probably 2 points above and one below the 95% confidence limits of the 33
case-control study data points, still not bad agreement with the
expectation, especially if one recognizes that the case-control studies
and their error estimates are far from perfect (they often do not agree
with one another).
	Still, I did not claim that there was no discrepancy between our
data, interpreted Lubin's way, and the case-control studies. The final
conclusion of my April 1999 paper was "there is a tendency for the case
control data to lie above our line, but this is easily explained by the
fact that Lubin's interpretation of our data as 'risk to individuals' is
fallacious. It is a direct violation of 'the ecological fallacy', and I
have repeatedly warned against such an interpretation. The only truly
valid use of our data is as a test of LNT" 
	Lubin's Sept. 1999 letter continues to accept the fallacious
assumption that my data can be directly compared with the case-control
studies, and does elaborate statistical analyses using F-statistics, the
Pearson chi-square goodness of fit statistics, etc and concludes that the
agreement is not very satisfactory. I do not disagree with these analyses,
and I would say that they are simply an elaboration of my conclusion
stated in the previous paragraph above. However I explain the problem as a
violation of "the ecological fallacy" in Lubin's approach.
	Nearly half of my April 1999 paper deals with an explanation for
why Lubin's proffered mathematical proof that cross-level bias can cause
large errors in my study is not valid. He has leaned heavily on this proof
in previous papers, but in his Sept. 1999 letter, he ignores my
demonstration of its invalidity.
	Papers by Field and collaborators have appeared and followed the
same procedures as the papers by Lubin, so I do not have the opportunity
to respond in print to the Field et al letter in the Sept. 1999 issue of
Health Physics. That letter contains dozens of criticisms of my papers,
always with very little detail and no quantitative support. I feel that I
have responded to essentially all of them previously, albeit with little
detail because of limitations in the number of words allowed me by the
Editor -- he initally allowed me 500 words for each letter-to-the-editor,
but did allow me to exceed this moderately. Rather than respond to all the
issues here, I would like to invite anyone who would like a reply on any
one issue raised in the Field et al paper to request it by e-mail; I
promise to respond promptly.


Bernard L. Cohen
Physics Dept.
University of Pittsburgh
Pittsburgh, PA 15260
Tel: (412)624-9245
Fax: (412)624-9163
e-mail: blc+@pitt.edu


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