Cohen's Fallacy and Doll

["Rad health" <healthrad@HOTMAIL.COM>]

Dr. Cohen,



I did not post your response, because it was not responsive to the letter of 

Darby of Doll.  Please do me the favor of responding to this quote from Doll 

and Darby.  "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."



Cohen does not have information on the relationship between smoking and lung 

cancer within counties.  Drs. Field and Smith have been making this same 

point as Doll and Darby in their Forum paper and subsequent letters, yet 

Cohen has not responded specifically to this charge.  Dr. Field gave you a 

way to possibly correct for this problem a few days ago on this list, but 

you said you preferred to do it your own way, which you haven't.



I think Sir Richard Doll knows a bit more about epidemiology then either of 

us.



http://www.britcoun.org/science/science/personalities/text/ukperson/doll.htm





Doll is Recipient of the Gold Medal of the Royal Society of Medicine and the 

National Award for Cancer Research.  Tobacco was introduced into Europe at 

the close of the 15th century as a treatment for disease and as a 

recreational drug.  Doll was the first person to identify tobacco as a 

causal factor for MANY diseases.



>From 1948 until 1969, Sir Richard Doll, a physician-turned-researcher, 

>worked in England's Medical Research Council's Statistical Research Unit, 

>at first under Sir Austin Bradford Hill (as in Bradford Hill Criteria for 

>causality) and then as the Unit's director.

With Sir Austin, he carried out a study of the causes of lung cancer which, 

in 1950, established its relationship to smoking.  He also initiated a study 

of the mortality of doctors in relation to their smoking habits which 

demonstrated that smoking was related to many other diseases including heart 

disease.



Don



>From: BERNARD L COHEN <blc+@pitt.edu>

>To: Rad health <healthrad@HOTMAIL.COM>

>CC: internet RADSAFE <radsafe@list.vanderbilt.edu>

>Subject: Re: Cohen's Fallacy

>Date: Mon, 28 Jan 2002 11:02:33 -0500 (EST)

>

>

>	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

> >

> > 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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