I agree heartily with professor Fields on this much:
Prediction is uncertain with application of group data to individuals
(which we physicians must do constantly)..
Have you heard the story about the statistician who drowned,
wading a stream that AVERAGED one foot in depth?
"All categories are arbitrary, separated only for convenience."
is one way our problem has been stated.
When we count, especially human beings or their diagnoses, data is
always lost because no two individuals (counts) are identical.
Managed medical care has never been successful, largely for this reason.
So, ecologic or group data can only suggest the risk to an individual. Case control studies also have uncertain inference of data appilcability to other persons.
However, we must reject at the p< 0.001 level the null hypothesis,
"Chance (or any of hundreds of cofounders, especially smoking) explains
the negative association of home radon samplings of 1 to 5 pCi/l
with USA county lung cancer mortality rates (compared with homes having
< 0.5 pCi/l"). That data is elegantly and skeptically supplied by B.
Cohen.
This null hypothesis rejection is incompatible with the linear, no-threshold
theory LNT that produced ALARA.
Furthermore, this rejected null hypothesis and the many animal and human
confirmations - like the 4,000 case NSWS case control study - suggest that
ionizing radiation in dose of 1-10rem/year is "an essential trace energy"
(Cameron) -
like a vitamin.
Howard Long
"Field, R. William" wrote:
Ruth,Ecologic fallacy is merely an inappropriate conclusion regarding relationships at the individual level based on ecological data (Kelsey et al. 1986).
However, ecologic studies inherently have many weaknesses that lead to an inappropriate conclusion. For example,
1) in case-control studies nondifferential (or random error) exposure misclassification usually causes bias toward the null. However, in an ecologic study nondifferential misclassification can drive either sizable under or over estimation of the exposure disease relationship.
2) Using summary measures (like sales tax to represent smoking prevalence) for a county is very inadequate to control for confounders.
3) Some factors that are not confounders at the individual level can be at the ecologic level. To have any hope of control for confounding at the county level, you need very detailed information on the confounding and exposure variable distributions within a county. That is why I previously suggested to Dr. Cohen that he try to obtain this information (method suggested by Guthrie).
4) Jim Muckerheide often cites the large numbers of counties in Dr. Cohen's studies. But, the availability of large numbers does not eliminate biases no matter if you had an infinite number of counties. Large numbers do help improve the precision (narrow confidence bands), but the large numbers have no effect on reducing biases. In other words, the finding can be precisely wrong.
5) I have seen no data from Dr. Cohen to show that the risk factors within counties are not correlated. Unless the risk factors are purely additive (and I see no evidence of that), the dose response findings for the ecologic study will be biased.
Ruth, in your example below, the population is not at all defined so the concept of collective dose and collective risk can not be used. Collective dose and collective risk can only begin to be considered valid if the exposed population can be well described and quantified. For example, many groups of workers who may have a higher risk of exposure can be quantified by age, job description, sex, length of employment and a multitude of other factors. The general (working) group I described above has many more demographic details than is available in ecologic studies. If you don't have better demographics than are available in a county ecologic study, you likely should not be using the collective dose concept.
Pardon my short answer, but I am swamped with other work related demands right now.
Best Regards, Bill
At 09:45 AM 2/12/2002 -0500, RuthWeiner@AOL.COM wrote:
Dear RADSAFERsI am working my way through both Field et al (and some ancillary papers kindly sent me by Dr. Field) and Dr. Cohen's papers (thatnk you, Bernie, for sending them). I am trying to understand the papers with all their nuances. I believe this can be done by a reasonably competent scientist like me (Ph. D. -- chemistry) without special training in epidemiology, but from time to time I will post questions -- real questions to which I would like real straightforward answers -- on RADSAFE. Let me say at the outset that these questions are not intended to castigate anybody or take sides. If I use the LNT in a question, it doesn't mean I endorse it. The questions are for information. (and if they sound repetitive to the individual who accused me of "me too-ism" well, that can't be helped). So here is my first question, about the "ecological fallacy."
Let us say the cumulative dose to a population of 10,000 persons is 1000 PERSON-rem. Then, according to the LNT, one might expect 0.5 excess cancer in that population of 10,000 (0.0005*1000 = 0.5). One can also, independently, say that the average dose is 0.1 rem (1000/10,000 = 0.1), or 100 mrem. But to say that therefore the average expected cancer incidence would be 0.000005 (0.0005*0.1) is the fallacy in question. Essentially, "average individual cancer expectation" or whatever is meaningless. Have I got it right? If not,what is my mistake?
(The LNT conversion from rem to cancer is from ICRP 90, page 22)
Ruth Weiner, Ph. D.
ruthweiner@aol.com
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