Re: Cohen's Fallacy

[BERNARD L COHEN <blc+@PITT.EDU>]

	My response to the paper quoted by Rad health below was published

in J. Radiol. Prot. 21:64-65;2001. It is reproduced below following the

paper it responds to in the same journal.

	Several times Rad health has attacked my work by quoting published

papers by Field et al and by Lubin, but he has never noted my

published responses to these papers. Is that proper behavior for a

scientist? Here he has done it again; can that be accidental?



On Sun, 27 Jan 2002, Rad health wrote:

>

> J. Radiol. Prot. 20 (June 2000) 221-222

>

> LETTER TO THE EDITOR

>

> Reply to `Explaining the lung cancer versus radon exposure data for USA

> counties'

>

> Sarah Darby and Richard Doll

> Clinical Trial Service Unit, University of Oxford, Nuffield Department of

> Clinical Medicine, Harkness Building, Radcliffe Infirmary, Oxford OX2 6HE,

> UK

>

> Professor Cohen states in his letter that his analysis `encompasses all of

> the Doll suggestions'. It is, however, logically impossible for it to have

> done so using data at the level of counties. This is because the effect of

> cigarette smoking on the relationship between residential radon and

> individual lung cancer risk will be determined by the relationship between

> smoking status and lung cancer among the individuals within each county.

> Unless smoking is irrelevant to lung cancer risk (which we know to be

> untrue) or smoking status and residential radon are uncorrelated within each

> county (which seems unlikely), the relationship between residential radon

> and lung cancer at the county level will differ from that at the level of

> the individual in a way that cannot be overcome by including corrections for

> smoking habits at the county level, even if these corrections correctly

> represent the smoking habits of the individuals within each county. The

> difference in the relationship between a risk factor and a disease rate at

> the level of the individual and at an area level is the ecologic fallacy and

> is described in detail by Greenland and Robins (1994) and Morgenstern

> (1998). Lubin (1998) has also demonstrated that biases caused by the

> ecologic fallacy can be of any magnitude from minus infinity to plus

> infinity.

>

> In two recent studies (Lagarde and Pershagen 1999, Darby et al 2000),

> parallel individual and ecological analyses have been carried out of

> identical data from case-control studies of residential radon (Peshagen et

> al 1994, Darby et al 1998). These analyses have shown that, in addition to

> any bias caused by the ecological fallacy, ecological studies of residential

> radon and lung cancer are also prone to biases caused by determinants of

> lung cancer risk that vary at the level of the ecological unit concerned. In

> these two examples, the additional variables were latitude and urban/rural

> status respectively. The explanation of these variables is not yet well

> understood and they may well be, in part, surrogate measures for some

> aspects of the subjects' smoking history not accounted for by the measures

> of smoking status that have been derived from the individual questionnaire

> data and used in the analysis of the data for individuals. They had only a

> minor effect on analysis at this level but a substantial effect on the

> ecological analyses. The presence of these variables is further evidence of

> the pitfalls of ecological studies.





	--The following is my published response to the above.



J. Radiol. Prot. 21 (March 2001) 64-65



LETTER TO THE EDITOR



Radon exposure and the risk of lung cancer



Dear Sir



Our study found a very strong negative correlation between lung cancer and

radon exposure in USA counties

(Cohen 1995), a discrepancy with the positive correlation predicted by

linear-no-threshold theory (LNT) of

over 20 standard deviations. Drs Darby and Doll (2000) suggested that an

explanation for this discrepancy

may lie in the ecological fallacies. My purpose here is to consider that

issue.



The classical `ecological fallacy' arises from the fact that the average

exposure does not, in general,

determine the average risk, as is obvious for situations where there is a

threshold. But we avoid this problem

by designing our study as a test of LNT - in LNT, the average exposure

does determine the average risk (e.g.

person-Sv determines the number of deaths).



Darby and Doll suggest that the ecological fallacy applied to corrections

for smoking may be important. But

following BEIR-IV, we use separate risk factors for smokers and for

non-smokers which eliminates this

problem if we assume different average radon exposures for these; this was

shown to have little effect on our

results (Cohen 1998, 1995).



However, the ecological fallacy does arise for other confounding factors

(CFs) - the average value of a CF

does not, in general, determine its confounding effects. Darby and Doll

note that Lubin (1998) demonstrated

mathematically that the error in assuming otherwise can be infinite.



For example, consider annual income as a CF that might confound the radon

versus lung cancer relationship -

maybe very poor people have lower radon and, for unrelated reasons, have

higher lung cancer rates than

others. A problem with ecological studies is that average income is not

necessarily a measure of what fraction

of the population is very poor. A case-control study does much better; in

principle, it selects cases and

controls of matched incomes.



Our approach to this problem is to use a large number of CFs. For the

example under discussion, we use as

CF the fraction of the population in various income brackets, <$5000/year,

$5000-$10 000/year, ..., >$150

000/year (10 intervals in all). In addition, we consider combinations of

adjacent brackets, and other related

characteristics such as the fraction of the population that is below the

poverty line, the percentage

unemployment, etc. It can be shown that a necessary (but not sufficient)

condition for a CF to have an effect

on our discrepancy with LNT is that it have a strong correlation, at least

25%, with radon levels, and none of

the above CFs have a correlation larger than 7%. This convinces me that

income is not an important

confounder of the lung cancer versus radon relationship. It is not a

mathematical proof, so my mind is open.

If someone can devise an acceptable model in which income does have an

impact, and this is not taken care

of by our CF, I will be happy, and even relieved, to concede.



But what about Lubin's mathematical proof? It's easy to demonstrate its

validity. Our results would be

explained if those with an income that is an integral multiple of $700

have 1000 times higher lung cancer rates

than all others, in which case lung cancer rates would depend on what

fraction of the population has those

special incomes. We have no data to show that such incomes are not

strongly correlated with radon levels,

and as Lubin showed, the error in our study could be essentially infinite.

But such a model is not acceptable

for two reasons:



(a) it is not plausible;



(b)it would also not be taken care of in case-control studies as they

don't match incomes with that accuracy.



This introduces two obvious corollaries that must be attached to Lubin's

demonstration, but were not

included in his mathematical treatment. Without them, his treatment is not

applicable to the `real world'. What

is needed is a model that avoids these two limitations, and neither I nor

anyone else has been able to devise

one.



Of course annual income is not the only CF that must be worried about.

Another example is age distribution.

Case-control studies match cases and controls by age, but in our study

average age in a county does not

represent differences in age distributions. We do use age-adjusted

mortality rates which take care of the gross

aspects of that problem, but there are limitations in the age-adjustment

process. Our solution is to use as CF

the percentage of the population in each age bracket, <1 year, 1-2 years,

..., 80-84 years, >85 years (31 age

brackets in all), and to also use combinations of adjacent age brackets.

Only one of these has a correlation

with radon above 4%, and after further investigation of that case

(correlation 7.7%), we concluded that

confounding by age distribution could not explain our discrepancy.



There are few, if any, other bases on which case-control studies match

cases and controls, but in our study

we gave similar treatments to a host of other potential confounding

factors - educational attainment, urban

versus rural differences, ethnicity, occupation, housing characteristics,

medical care, family structures, etc.

We have found nothing that can explain our discrepancy.



Let me comment more generally on Lubin's mathematical proof. I have had

extensive experience as a

theoretical physicist, a field heavily characterised by mathematical

proofs. I know the game very well and can

testify that physicists do not derive something mathematically and say

`that's the way it is'. At every stage

they test results numerically with `real world applications'. In fact,

more often they work with real world data

to reach a conclusion, and then `dress it up' for publication by

developing a mathematical treatment. If a

mathematical treatment shows something questionable, it is always easy to

develop plausible practical

numerical examples to settle the question. For example, I can easily show

how any other published ecological

study can give invalid results, and why our study is different from these.



I can't prove that there isn't an unrecognised CF that can explain the

great discrepancy between our data and

LNT (of course, an unrecognised confounder can also nullify the results of

any epidemiological study). We

have certainly exerted a great effort in looking for one, without success.

Our paper has been out for five

years, and no one else has found one. Unless someone does, I will believe

that there is no such CF, and that

our discrepancy with LNT is explained by the fact that LNT fails badly in

the low dose region where there

are no other data to test it.



The other issue raised by Darby and Doll, involving parallel individual

and ecological analyses, has been

addressed in a recent paper (Cohen 2000).



Yours faithfully,



Bernard L Cohen

Department Of Environmental and Occupational Health

100 Allen Hall

University of Pittsburgh

Pittsburgh, PA 15260

USA



URL: stacks.iop.org/0952-4746/21/64

DOI: 10.1088/0952-4746/21/1/102













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