RE: Confounders and Coincidences

[epirad@mchsi.com]

Ted,



People have given both suggestions and numbers.  Dr. Cohen states that he 

shows their numbers are implausible, but he only considers just one factor at 

a time like his estimated smoking rates rather than a group of co-linear 

factors (smoking, SES, Education, etc.).



We have also answered your question before in the HPJ, see below - 



Nonetheless, the bottom line is that it is certainly worth exploring the 

validity of the LNT.  But an ecologic study is clearly not the way to do it. 





Field, R.W., Smith, B.J., and Lynch, C.F. Cohen’s Paradox, Health Physics 77

(3): 328-329, 1999.



Dear Editors:



WE APPRECIATE the opportunity to respond to Cohen's letter-to-the-editor 

(Cohen 1999a) regarding our rejoinder (Field et al. 1998a). The rejoinder 

focused on Cohen's attempts (Cohen 1995,1997) to test the Linear No-Threshold 

Theory (LNTT) using ecologic data. In our initial publication on this topic 

(Smith et al. 1998), we demonstrated that Cohen erroneously used the wrong 

model to test the LNTT. We also demonstrated that when more valid Iowa county 

lung cancer rates were regressed on Cohen's mean county radon levels, the 

large negative associations Cohen noted between radon concentrations, obtained 

from short-term radon measurements, and lung cancer disappeared for Iowa. This 

letter addresses several important points that Cohen either continues to 

ignore or continues to contest.



Cohen (1999a) continues to challenge scientists to suggest a plausible 

explanation to explain the inverse relationship he notes between mean county 

residential radon measurements and mean county lung cancer mortality rates. We 

will call this inverse relationship "Cohen's Paradox." Cohen (1999a) states 

that his challenge is for someone to suggest a "not implausible model" as a 

possible explanation and that the burden of proof will be on him to show 

that "the explanation is highly implausible." We maintain that even if 

additional plausible models are offered, Cohen will likely not be able to 

explain his own paradox. Cohen has not accepted the fact that it may be 

impossible to explain Cohen's Paradox in definitive analytical terms with his 

existing data because it is not always possible to identify empirical sources 

of ecologic bias from aggregate (ecologic) data alone (Field et al. 

1998a).



Cohen (1999a) states that he has not been able to explain the inverse 

relationship (Cohen's Paradox) for his studies even with years of effort. We 

are not surprised. Cohen (1999a) continues to miss the point made previously 

(Greenland and Robins 1994; Smith et al. 1998; Field et al. 1998a) that 

characterizing biases is often extremely difficult in ecologic studies of 

geographic regions because of the high probability of interacting covariates 

that may differ across these regions. Greenland and Morgenstern (1989) point 

out that ecological control of a covariate contributing to ecologic bias will 

usually be inadequate to remove the bias produced by the covariate even in the 

absence of measurement error. Researchers (Greenland and Robins 1994; Lubin 

1998; Smith et al. 1998; Archer 1998; Goldsmith 1999) have already presented 

very plausible theoretical examples of how Cohen's data can produce incorrect 

and even contradictory risk estimates. Cohen has rejected 

all of these examples.



Lagarde and Pershagen (1999) recently performed concurrent analyses on 

individual and aggregated data from a nationwide case-control study of 

residential radon and lung cancer in Sweden. The authors reported that the 

results confirm that ecologic studies may be misleading in studies of weak 

associations. So, are Cohen's negative point estimates a true effect or are 

they attributable to bias? To move the explanation beyond the theoretical 

level, analyses would require individual level data beyond the quality of 

Cohen's aggregate data.



Cohen continues to maintain that his ecologic studies avoided the ecologic 

fallacy, because he was testing the BEIR-IV LNTT model (Cohen 

1997,1998,1999a). Cohen also continues to deny our assertion (Smith et al. 

1998; Field et al. 1998a) that he was not testing the BEIR-IV LNTT model. As 

we stated (Smith et al 1998; Field et al. 1998a), Cohen's risk model is not 

the BEIR-IV risk model. Cohen attempted to equate his derived LNTT model to 

the BEIR-IV model by applying unsupported primary and secondary rigid 

assumptions. The assumptions all have both an error associated with them and a 

non-linear component, which as previously pointed out, cannot be 

quantitatively described. Rather than providing references to support the 

validity of his assumptions, Cohen defends his use of these assumptions (Cohen 

1999a) by stating that they are the same assumptions as used in essentially 

all case-control studies.



All epidemiologic study designs have their own set of limitations. In fact, we 

have pointed out that inadequate measurement data can affect the validity of 

case-control studies as well as ecologic studies (Field et al. 1996,1997). The 

limitations and assumptions of radon case-control 

epidemiologic studies, which use individual rather than ecologic data, have 

been presented elsewhere (Lubin et al. 1990; Field et al 1996). However, the 

nature of potential biases inherent in case-control studies is often quite 

different from an ecologic study. For example, case-control studies are not 

subject to cross-level bias. While case-control studies have their own 

inherent limitations, controlling for potential confounders in a well-designed 

case-control study is much easier than dealing with confounders in an ecologic 

study.



Many of the assumptions used by Cohen in his ecologic study design are not 

required for the case-control study design. For example, Cohen's ecologic 

studies assumed that smoking duration and intensity are the same for each 

individual within a specified region. Unlike ecologic studies, case-control 

studies collect data at the individual level so that detailed smoking 

histories can be available to use for adjustments. We previously showed (Smith 

et al. 1998) that when Cohen's adjusted smoking percentages for males and 

females were regressed on radon levels, significant (p < 0.00001) negative 

associations between smoking and radon were noted for both males and females. 

In addition, when we (Smith et al. 1998) repeated the regression of lung 

cancer mortality rates on Cohen's adjusted smoking percentages, the resulting 

R2 values indicated that Cohen's smoking summary data explained very little 

(23.7% for females; 34.5% for males) of the variation in lung cancer mortality 

rates. It is not surprising Cohen cannot control for these risk factors using 

aggregate data. In addition, Cohen's ecologic studies make numerous other 

assumptions not required for newer case-control designs (Field et al. 1996).



Cohen (1999a) continues to offer explanations for how the conclusions of other 

published ecologic studies can be wrong. We (Field et al. 1998a) offered the 

large scale ecologic study by Menotti et al. (1997) as an example of an 

inverse relationship between average blood pressure and stroke mortality 

rates. Cohen did not have actual data from the study (Menotti et al. 1997) and 

therefore could not attempt to explain the paradoxical finding in definitive 

analytical terms. However, we would be interested in Cohen's definitive 

analytical explanation for why the large negative associations disappeared for 

the Iowa data when we regressed the more valid county lung cancer rates for 

Iowa on Cohen's own mean county radon levels for Iowa (Smith et al. 1998). As 

we mentioned previously, Iowa serves as an ideal site for a radon 

epidemiologic study because it possesses the highest mean radon concentrations 

in the United States (White et al. 1992), a population with low mobility, and 

a quality cancer registry (Field et al. 1996). In addition, because of the 

large number of counties in Iowa (99), Iowa data provide a finer ecologic 

breakdown per percent population compared to much 

of the rest of the U.S. data set assembled by Cohen. Cohen offers to provide 

specific quantitative explanations for why other ecologic studies can give 

false results, but he has yet to provide a persuasive argument for our 

findings in Iowa (Smith et al. 1998), which predominantly use his aggregate 

data.



Cohen (1999b) states, "I have never claimed that our studies support hormesis, 

since such an interpretation suffers from the ecologic fallacy." We agree with 

that claim by Cohen. However, Cohen has not provided persuasive evidence to 

show that his test of the LNTT also does not suffer from the ecologic fallacy. 

Cohen attempts to test the LNTT by analyzing averaged multivariate 

distributions of aggregate data, followed by analyses using more county level 

summaries to correct the potential biases. Because of the heterogeneity within 

the county summaries, the aggregate data provide very little confounder 

control, especially in the presence of non-linear dependencies (Field et al. 

1998b) and interactions (Greenland and Robins 1994). It is a fallacy to think 

that Cohen's inferences made from aggregate level data can be applied to 

individual level exposure-response relationships, especially when Cohen is not 

even testing the BEIR-IV formula.



Piantadosi (1994) pointed out that "a single result at odds with theory should 

not discredit the theory unless the source of data and analysis meet the most 

rigorous methodological criteria." Cohen's data, assumptions, and study design 

failed to fulfill these criteria. Nobel Laureate, Sir Peter Medawar (1979) 

wrote, "I cannot give any scientist of any age better advice than this: the 

intensity of the conviction that a hypothesis is true has no bearing on 

whether it is true or not. The importance of the strength of our conviction is 

only to provide a proportionately strong incentive to find out if the 

hypothesis will stand up to critical evaluation." Time will tell if the LNTT 

will stand up to critical evaluation or fall. Nevertheless, we oppose the 

critical evaluation taking the form of an ecologic study.



R. William Field

Brian J. Smith

Charles F. Lynch



College of Public Health

Department of Epidemiology

N222 Oakdale Hall

University of Iowa

Iowa City, IA 52242

References



1.Archer, V. E. Cohen's home radon-lung cancer data suggests positive 

association. Health Physics Society Newsletter June 1998.



2.Cohen, B. L. Test of the linear no-threshold theory of radiation 

carcinogenesis for inhaled radon decay products. Health Phys. 68:157-174; 1995.



3.Cohen, B. L. Lung cancer rate vs. mean radon levels in U.S. counties of 

various characteristics. Health Phys. 72:114-119; 1997.



4. Cohen, B. L. Response to criticisms of Smith, Field, and Lynch. Health 

Phys. 75:23-28; 1998.



5.Cohen, B. L. Response to "Rejoinder" by Field et al. Health Phys. 76:439-

440; 1999a.



6.Cohen, B. L. Comment on letter by Straja and Moghissi. 76:318; 1999b.



7.Field, R. W.; Steck, D. J.; Lynch, C. F.; Brus, C. P.; Neuberger, J. S.; 

Kross, B. C. Residential radon-222 exposure and lung cancer: exposure 

assessment methodology. J. Exposure Analysis and Environmental Epidemiology 

6:181-195; 1996.



8.Field, R. W.; Steck, D. J.; Neuberger, J. S. Accounting for random error in 

radon exposure assessment. Health Phys. 73:272-273; 1997.



9.Field, R. W.; Smith, B. J.; Lynch, C. F. Ecologic bias revisited, a 

rejoinder to Cohen's response to "Residential 222Rn exposure and lung cancer: 

testing the linear no-threshold theory with ecologic data". Health Phys. 75:31-

33; 1998a.



10.Field, R. W.; Smith, B. J.; Brus, C. P.; Lynch, C. F.; Neuberger, J. S.; 

Steck, D. J. Retrospective temporal and spatial mobility of adult Iowa women. 

Risk Analysis: An International Journal 18:575-584; 1998b.



11.Goldsmith, J. R. The residential radon-lung cancer association in U.S. 

counties: a commentary. Health Phys. 76:553-557; 1999.



12. Greenland, S.; Morgenstern, H. Ecological bias, confounding, and effect 

modification. International J. Epidemiol. 18:269-274; 1989.



13. Greenland, S.; Robins, J. Invited commentary: ecologic studies-biases, 

misconceptions, and counterexamples. Am. J. Epidemiol. 139:747-760; 1994.



14.Lagarde, F.; Pershagen, G. Parallel analyses of individual and ecologic 

data on residential radon, cofactors, and lung cancer in Sweden. Am. J. 

Epidemiol. 149:28-274; 1999.



15.Lubin, J. H.; Samet, J. M.; Weinberg, C. Design issues in epidemiologic 

studies of indoor exposure to radon and risk of lung cancer. Health Phys. 

59:807-817; 1990.



16. Lubin, J. H. On the discrepancy between epidemiologic studies in 

individuals of lung cancer and residential radon and Cohen's ecologic 

regression. Health Phys. 75:4-10; 1998.



17.Medawar, P. B. Advice to a young scientist. Reading, MA: Basic Books, A 

Subsidiary of Perseus Books, L.L.C.; 1979.



18.Menotti, A.; Blackburn, H.; Kromhout, D.; Nissinen, A.; Karvonen, M.; 

Aravanis, C.; Anastasios, D.; Fidanza, F.; Giampaoli, S. The inverse relation 

of average blood pressure and stroke mortality rates in the seven countries 

study: A paradox. European J. Epidemiol. 13:379-386; 1997.



19.Piantadosi, S. Invited commentary; Ecologic biases. Am. J. Epidemiol. 

139:761-764; 1994.



20.Smith, B. J.; Field, R. W.; Lynch, C. F. Residential 222Rn exposure and 

lung cancer: testing the linear no-threshold theory with ecologic data. Health 

Phys. 75:11-17; 1998.



21.White, S. B.; Bergsten, J. W.; Alexander, B. V.; Rodman, N. F.; Phillips, 

J. L. Indoor 222Rn concentrations in a probability sample of 43,000 houses 

across 30 states. Health Phys. 62:41-50; 1992.



> Please help out a simple non-epidemiologist.  If it is so easy for a

> confounder to reverse a curve such as Cohen's, then why is no one willing to

> make up a plausible example, with numbers, that will simply do that?  That's

> what he has repeatedly asked for, and all he gets is generic speculation

> that such a thing is possible.  It's possible that the phase of the moon

> could do it, too, but we won't really know until someone puts in some

> numbers and it checks out.

> 

> Ted Rockwell

> 

> -----Original Message-----

> From: owner-radsafe@list.vanderbilt.edu

> [mailto:owner-radsafe@list.vanderbilt.edu]On Behalf Of epirad@mchsi.com

> Sent: Thursday, May 08, 2003 12:34 PM

> To: Otto G. Raabe

> Cc: radsafe@list.vanderbilt.edu

> Subject: Re: Confounders and Coincidences

> 

> 

> Dear Otto,

> 

> Yes, using ecologic data to control confounding is helpful sometimes.  In

> fact, it does help especially if there are not large inter and intra county

> non linear effects.  However, we know without question that these non linear



> sources of confounding and effect modification exist in Dr. Cohen's data.

> 

> Two papers really do a nice job of adressing this problem.

> 

> Ecological bias, confounding, and effect modification

> 

> S Greenland and H Morgenstern

> 

> Division of Epidemiology, UCLA School of Public Health 90024.

> 

> Ecological bias is sometimes attributed to confounding by the group variable

> (ie the variable used to define the ecological groups), or to risk factors

> associated with the group variable. We show that the group variable need not

> be a confounder (in the strict epidemiological sense) for ecological bias to

> occur: effect modification can lead to profound ecological bias, whether or

> not the group variable or the effect modifier are independent risk factors.

> Furthermore, an extraneous risk factor need not be associated with the study

> variable at the individual level in order to produce ecological bias. Thus

> the

> conditions for the production of ecological bias by a covariate are much



> broader than the conditions for the production of individual-level

> confounding

> by a covariate. We also show that standardization or ecological control of

> variables responsible for ecological bias are generally insufficient to

> remove

> such bias.

> 

> --------------------------------------

> Ecologic versus individual-level sources of bias in ecologic estimates of

> contextual health effects

> 

> Sander Greenland

> 

> Department of Epidemiology, UCLA School of Public Health, and Department of

> Statistics, UCLA College of Letters and Science, 22333 Swenson Drive,

> Topanga,

> CA 90290, USA.

> 

> Bill's insert - (Does this first sentence sound familiar?)

> 

> Abstract:

> 

> A number of authors have attempted to defend ecologic (aggregate) studies by

> claiming that the goal of those studies is estimation of ecologic

> (contextual

> or group-level) effects rather than individual-level effects. Critics of

> these

> attempts point out that ecologic effect estimates are inevitably used as



> estimates of individual effects, despite disclaimers. A more subtle problem

> is

> that ecologic variation in the distribution of individual effects can bias

> ecologic estimates of contextual effects. The conditions leading to this

> bias

> are plausible and perhaps even common in studies of ecosocial factors and

> health outcomes because social context is not randomized across typical

> analysis units (administrative regions). By definition, ecologic data

> contain

> only marginal observations on the joint distribution of individually defined

> confounders and outcomes, and so identify neither contextual nor individual-

> level effects. While ecologic studies can still be useful given appropriate

> caveats, their problems are better addressed by multilevel study designs,

> which obtain and use individual as well as group-level data. Nonetheless,

> such

> studies often share certain special problems with ecologic studies,

> including

> problems due to inappropriate aggregation and problems due to temporal

> changes



> in covariate distributions.

> 

> Regards, Bill

> bill-field@uiowa.edu

> > At 03:52 PM 5/8/03 +0000, Bill Field wrote:

> > >Dr. Cohen wrote -

> > >

> > >Unfortunately, ecological control of a covariate contributing to ecologic

> > bias

> > >is generally inadequate to remove the bias produced by the covariate even

> in

> > >the absence of measurement error.

> > ****************************************************

> > May 8, 2003

> >

> > Dear Bill:

> >

> > Thanks for your comment. You bring up an important point.

> >

> > But it seems to me that the fact that ecological control may not remove

> the

> > bias does not mean that it never helps. If all you have is ecological

> data,

> > isn't testing the effect of ecological control a useful exercise?

> >

> > Otto

> >

> > **********************************************

> > Prof. Otto G. Raabe, Ph.D., CHP

> > Center for Health & the Environment

> > (Street Address: Bldg. 3792, Old Davis Road)

> > University of California, Davis, CA 95616

> > E-Mail: ograabe@ucdavis.edu



> > Phone: (530) 752-7754   FAX: (530) 758-6140

> > ***********************************************

> 

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