Document vBk4nQmNapzdRey8Yv2GZodbE

\ INTERNAL CORRESPONDENCE **r,> RECEIVED UNION CARBIDE CORPORATION OLD RIDGEBURV ROAD, DANBURY^CT OBB17 To (Namfl) Diviton Location Armm Distribution Copy to Oete Originating Dept Area SuOiect March 23, 1984 HS&EA P-2 Epidemiology FSP The attached paper by Dr. Philip E. Enterline was presented at the 1983 Annual Hatch Symposium in Pittsburgh. This represents a very good discussion of the problems of distinguishing "natural clusters" of a disease in occupational population groups Vfrom clusters caused byhealth hazards in the workplace. This article is of great value in' placing the results of our mortality surveillance program in proper perspective, and indicates some examples that we might use to explain the problem to our workers and to the public. Although Phil acknowledges the difficulties in explaining the problem to the general "lay" public, he does not offer any advice! It is of interest that he uses the Texas City brain cancer study to illustrate the difficulties with investigations of "clusters". I believe that all corporate and divisional health and safety managers would benefit greatly from reading this paper thoroughly. SGA/sar Attachment S. G. Austin, Sp.D. i 4710B / UCC 097510 REACTING TO CANCER CLUSTERS IN THE WORKPLACE by Philip E. Enterline # Director, Center for Environmental Epidemiology and' Professor of Biostatistics Department of Biostatistics Graduate School4of Public Health University of Pittsburgh Pittsburgh, PA 15261 Clusters of Cancer Our past experience and successes in detecting .occupationally caused cancer and In identifying carci*nogens in the occupatio*nal environment have made us alert to the potential of quantitative epidemiology for identifying new environmental hazards. Almost every week our attention is focused on an unusual disease cluster somewhere -- perhaps related to some hazardous human exposure. There must be literally hundreds of thousands of amature epidemiologists ready to alert health authorities to unusual disease experiences in the population. This is both a blessing and a curse. On the one hand, our past experience has shown that health surveillance is an < important way to discover environmental causes of disease and insure continued progress in public health. On the other, intense surveillance clearly leads to many false alarms. Moreover, intense surveillance does not always lead to identification of a causal agent and may place government, industry, and labor in a difficult moral and ethical position. Chance, of course, can play a role in the way disease occurs in a population. To understand this it is important to see what is meant by random. Table 1 shows three series of the numbers, 1 and 2. In the first row the l`s and 2*s were placed in random order using a table of random numbers. Jn the second row, 1 *s and 2's were alternated, while in the third row they were clustered. If we were to observe number sequences represented by the / UCC 097511 2 second or third rows in any population of numbers, we would suspect that some factor other than chance is at work and in the case of Table 1 this is true. Of course, clustering and separation can occur by chance, so we can't be absolutely su/e when we see a cluster; that chance is not at work. Suppose we were to search for clustering in a series of events known by the way they were generated to be random. Table 2 showS a section drawn at random from a table representing a million random digits developed by the Rand Corporation many years ago. There seems to be no clustering or separation of numbers here. * Numbers appear to be in truly random order. Table 3 shows a section in the table of random digits we found by a little searching. Note here a cluster of 6 sevens in the center of the table. Clearly if we search random events we can find clusters of events that when examined in isolation do not appear random. Indeed, were we to test these selected observations for statistical significance they would probably be statistically significantly clustered. If we didn't know how they were selected, we could be misled into believing we'd discovered something. Several years ago I was contacted by the Medical Director of the Shell Oil Company, and asked if I would be interested in conducting a study of workers who were using solvents -- benzene, toluene and methyl ethyl ketone -- to remove wax from crude oils for the purpose of making lubricating oils. The unit in which these men worked is appropriately called the lubes-dewaxing unit and the process they were using is common to almost the entire petroleum refining industry. I've been interested in solvents and their relationship to leukemia and felt here was a population that if studied might answer something about this relationship. Moreover, this study seemed to be moving from cause to effect rather than effect to cause. The effect to cause sequence is, of cpurse, what happens when we discover a cluster and then search for the / UCC 097512 3 reason. Much to my surprise, my study showed an excess in prostatic cancer 2 deaths. I know of no reason why solvent exposure would produce cancer of the / prostate. I might have expected an excess in leukemia, but found none. My report led to two other investigations of lubes-dewaxing workers in other refineries both testing a prostatic cancer hypothesis. One showed a small excess and one a small deficit. 3 ' 4 The authors of the negative study thought perhaps my findings were due to chance, while the authors of the positive study supported their small excess with the findings from my study. Last year it occurred to m to ask the Medical Director at Shell why he had asked me to do the study in the first place. I learned that the reason for the study was that workers at the lubes-dewaxing unit had noticed that several co-workers had died of prostatic cancer and wondered if it might have something to do with their job exposures. That is, they had detected a cluster. They reported this to plant management, plant management to headquarters, and I was asked to do a study. Of course, I could do nothing less than discover the prostatic cancers that were the reason for my doing the study in the first place. Let's see what could have happened here. Suppose there are no exposures in the lubes-dewaxing unit that cause prostatic cancer but that there are many dewaxing units and some of these are being watched for disease excesses by workers, or management, or somebody's epidemiologist, or unions, or government in just the same way we searched tables of random numbers to detect a cluster. Under such scrutiny most watchers will discover nothing, but some are sure to discover something., Without knowing how many lubes-dewaxing units are being watched there is no way to evaluate the clusters discovered. It Appeared from my study that exposures in lube-dewaxing units caused something. / UCC 097513 4 i when in fact I probably had no evidence one way or the other. This is called the multiple comparisons problem in the statistical literature and it must be a very common problem in all scientific data / gathering. When a series of data are examined and only parts'are reported based on outcome, the common tests of statistical significance do not apply. It is possible, of course, to ask* if a relationships is biologically plausible, but sometimes when dealing with cancer our data base here is limited. To further illustrate how chance can create relationships, we had our computer generate 12 samples ea<Jh consisting of 10 two digit random numbers. We then computed the 12 means shown in Table 4. Note that these means range from 34.8 to 62.4. We then tested the null hypothesis that the largest mean is not statistically significantly larger than the smallest and were able to reject this with a t test at P < .05. This is analogous to, for example, testing differences in IQ's of children born in various months of the year. Giyen the manner in which the numbers were generated for Table 3, clearly the only reason for the difference is chance, and the reason* for the significant t test is the way means were selected for testing. We violated the prime conditions set up for applying the t test in two ways. First, we examined all 12 means (in a series of 12) and selected only the extremes for testing, thus violating a condition of independence. Then we tested only the hypothesis that the larger number was significantly larger than the smaller number -- not merely that it was different. I had no a^ priori reason for doing this. All this seems fairly obvious when we can see the big picture; that is, when we know everything that has been examined to yield our observations. It 'is not so obvious when we are shown only a piece of the big picture. / UCC 097514 5 Unfortunately, there is often no way of reconstructing the big picture. Generally we know little or nothing about the conditions that lead to the selection of epidemiologic observations reported in the literature. We could / call on our knowledge of biology, other epidemiologic observations, or just some good epidemiologic logic to convince ourselves that what is reported is not just a chance observation. Better still, we could develop a hypothesis and set about testing it with an entirely new data set. Usually verification takes time, however, and there is the moral dilemma in delaying action on findings when they may in fact be important. Even when we know how data are selected and how many comparison^ have been made, how cah a disease excess be dealt with when chance is a likely explanation? Clusters within Clusters Sometime ago the health manager for a paint manufacturing company called me about an excess in colo-rectal cancer observed in their workers. The company had participated in a national study involving 32 paint plants and they were one of three plants that showed an excess for this cause of death.^ The excess was statistically significant (P < .05). My ^immediate reaction was that in 32 trys at least one and possibly two plants would have a statistically significant excess or deficit for colo-rectal cancer at the .05 level, and that this might have been only a chance occurrence. After all, P = .05 simply means that the null point hypothesis will be rejected incorrectly at this level one time in 20. In this case, a test of significance was in effect carried out not once but 32 times. Surely one or two of these should have been statistically significant by chance alone. This was little comfort to the health manager. "What should I tell my workers?" he wanted to know. This did indeed pose a problem. I could hardly ay that they didn't hve an excess, since the cases existed to prove that they / UCC 091515 6 did. It would be difficult to explain that his plant was just unlucky. Clearly a situation like this calls for some further investigation. There were twelve deaths from colo-rectal cancer in the paint plant / cohort during the 12 year period 1958-70. This was over three times as many as would have been expected. Table 5 shows some data regarding these 12 deaths. Note the cluster of cases who*were hired in the period 1950-52. This suggests that either there was a large build-up in personnel during the years 1950-52, or that there was some unique exposure for workers hired during these years that caused colo-rectal cancer, or that something else is going on. There was no personnel build-up1 in 1950-52. In fact, the largest hire year \ was 1946 with a fairly constant pattern of hires thereafter. Age patterns for hires also didn't differ much from year to year. How, then, could it be that seven out of twelve men who died of colo-rectal cancer were hired during the brief period 1950-52? There are several interesting things about these seven cases. First note their ages at hire. The youngest was 39, and the oldest was 74 years of age. Second, all died of colo-rectal cancer in less than 19 years of date of hire (6-18 years). For most cancers we know that the latent period is usually much longer than this. Obviously, the next move was to find out just what these seven men did in the paint plant and what their exposures were. There did not appear to be any common exposure at the paint plant that related these seven men to each other. The cases clustered but exposures did not. Moreover, I know of no substance or exposure to paint production that is related to colo-rectal cancer. An obvious area for further inquiry was to see where the seven men hired during the years 1950-52 and who died of colo-rectal cancer worked before , UCC 097516 7 't coming to the paint plant. Recall that they were all 39 years of age or older at the time they were hired and must have worked for a considerable' period elsewhere. The notations about previous employment on the personnel records i did not suggest any comon earlier employment, but were too brief to be of real help. The paint company itself seemed to be "not guilty" and since it is in the business of making paint, and not cancer research probably shouldn't finance further inquiry. Moreover, the problem was too isolated to be of much interest to anyone else. Can we really be sure that this cluster of cases was only a chance occurrence? Perhaps there was causal factor involved.* It's even possible that some new knowledge about the etiology of colo-rectal cancer lies buried here. My guess, however, is that this was indeed a chance cluster within a chance cluster and that further study would tell us nothing. I don't, know, however, how this kind of situation can be explained to the workers at the paint plant. Starting with a Difference After deciding what to tell the workers, it would be wise to see if any additional cases occur. One problem we would encounter here is whether to include in the study the cases that led to the study in the first place. I recall something I read many years ago I believe was written by Donald Mainland about this problem, but in a context somewhat different than the one I've presented here. I've lost the reference but haven't forgotten the message. The setting was an NIH Study Section meeting called for the purpose of reviewing requests for additional support by investigators conducting clinical trials but who have ryn out of money. It does not seem unreasonable that some member of the Study Section would ask for a report on how each trial rfas gone up to that point before making a decision on continued funding. We / UCC 097517 8 might call this an "interim report". For one group of investigators things may be going ail wrong. Perhaps the control group is actually doing better than the study group, or things are i about even. A second group of investigators may report enthusiastically that things are going great. The treatment group is doing very well and with only a few more cases the difference between the treatment and controls will be statistically significant. Somehow the second group of investigators seems to be more deserving, of support than the first and in the absence of other considerations some Study Section members may argue that they are clearly the most deserving of additional funding. Not so clear, however, is the fact that if these members prevail a selection will have been made on the results to date, with the negative experiments likely to be terminated, and the positive experiments allowed to move ahead. Of course, those allowed to go on will include in their final report results to date. Such encouraging results are unlikely to be discarded. What in effect has happened, however, is that a new group of experiments has been initiated but this time the starting point is not the same for cases and controls, but rather somehow the starting point is one in which cases are given a head start. It's like a race between two runners in a 100 yard dash who are hypothesized to have equal running ability, except that one is given a 10 yard lead over the other. Who is likely to win? This can be called the "interim report fallacy". It must be fairly common. Suppose instead of a NIH Study Section the sponsor is a drug company looking for a new product. Certainly it would be tempting to continue to invest in projects where a discovery is likely to be made and terminate the rest as early as possible. This example serves to illustrate a basic principal and that is, if you start with a difference you're likely to end UCC 097518 i 9 with a difference. So clearly the index cases that lead to an epidemiologic investigation and which generate a hypothesis can't be used to test that hypothesis. Some new independent observations are needed. # In actual practice is it really possible to ignore the indek cases? Had I known that a cluster of prostatic cancer cases were the reason for my study of the lubes-dewaxing unit workers at the oil company, would I have been criticized if I left these cases out of my study? This is a tough decision to make. To date I know of no one who has had the nerve to leave out index cases. A good example is the1 recent concern ^about brain tumors in the chemical industry. In 1978 an employee at a Union Carbide plant at Texas City, Texas, reported to the Occupational Safety and Health Administration that there appeared to be an unusual cluster of brain tumors among his coworkers. This stimulated an investigation by the company and an investigation by the government, both of which included the index cases. fi * 7 Of course, both of the analyses of data from this particular plant showed an excess in brain tumors. How could it have been otherwise? On the other hand, neither the company nor the government could find any chemical exposure or OQ exposures that were uniquely associated with these brain tumor cases. * Employees have been notified by the company of the excess, but since the cause is unknown there appears to be nothing that can be done about it. This is a difficult situation for everyone. There are lots of questions. Should materials, manufacturing processes, or products be changed? Should brain tumor cases now be compensated by Union Carbide? Can or should anyone using products from the plant sue for, third party liability? CONCLUSION ' As I read the history of occupational medicine my impression is that / UCC 097519 10 nearly all of the important early discoveries proceeded from effect to cause, rather than cause to effect. Clearly we are still doing this so the situation isn't much different today than it was then. The difference is that because we're very sensitive to occupational.hazards, and because we know that where they exist they can usually be corrected and lives saved, we are looking much harder and communicating much more effectively. All this has produced a great amount of information that is difficult to interpret and act upon. I don't know why there was an excess in prostatic cancer among workers at a lubes-dewaxing unit in an oil refinery. I don't know why a cluster of colo rectal cancer deaths appeared afoong workers in a% paint*plant. I don't know why a cluster of brain tumors appeared in a Union Carbide chemical plant. I suspect, however, that these observations could be analogous to the discovery of a cluster of sevens in a table of random numbers, and that we'd better think of some way to explain this to a public rapidly being conditioned to the notion that every effect has a cause, and the idea that failure to identify the cause is a failure in an elaborate mechanism now in place to safeguard the health of the American worker. UCC 097520 / 11 '9 4 Table 1 i Three Series of Numbers, One in Random Order Group 1 Group 2 Group 3 2112112122 1212121212 1111122222 UCC 097521 12 Tab le 2 A Section of a Million Random Digits 36513 38382 93091 13302 06498 1 48937 65024 74743 15360 91705 41340 31159 40277 12996 39255 54267 45044 52814 87696 83262 82075 18070 95337 85560 38949 08290 02775 49272 69031 63965 06306 06179 93551 78082 05231 59335 28693 87645 13207 57430 84686 71801 99192 08320 21409 Source: p. 167, lines 8310-8324, Reference 7. % / ucc 097522 13 Table 3 A Section of a Million Random Digits Showing Clustering 44332 85439 84935 4 10792 48414 20349 46473 34304 22707 72877 77278 32936 36115 04858 09716 35906 92265 29656 88210 91067 71480 04122 77441 77770 41561 04880 00241 46717 67536 77255 00429 25291 50007 29374 68253 56852 57713 12104 31176 36903 23484 24803 15238 37041 65136 Source: p. 19, lines 905-919, Reference 7. UCC 097523 / 14 t Tab*le 4 Sample Means of Twelve Random Samples of Two Digit Numbers Sample Number Mean 1 47.3 2 41\3 3 62.4 4 34.8 5 55.2 6 48.8 7 48.0 8 49.5 9 42.2 10 60.3 11 57.7 12 49.0 f / UCC 097524 15 # Table 5 Twelve Cases of Colo-Rectal Cancer Occurring in a Paint Plant Date of Hire 1907 1921 1932 1943 1946 1950 1951 1951 1951 1952 1952 1952 Age at Hire 25 28 23 56 19 52 47 74 56 39 42 63 Duration of Employment 41 42 35 8 1 16 8 6 18 18 3 3 Latei Peril 53 52 35 33 19 16 17 14 7 18 12 6 UCC 097525 / References 1. The Rand Corporation. A Million Random Digits with 100,008 Normal Deviates. The Free Press, Glencoe, IL, 1955. 2. Enterline, P. E.: Mortality among workers from Shell Oil Company's Lubricant:'s Dewaxing Unit at Deer Park, Texas. Report On Shell Oil, January, 1978, 3. Wen, C. P., Wong, 0., Tsai, S. P., Gibson, R. L.; Epidemiology of refinery workers with solvent-related exposures. Presented at the 11th Conference on Environmental Toxicology at Dayton, Ohio on November 9. 1980. 4. Alderson, M. R., Rattan, N. S.: Mortality of workers on an isopropyl alcohol plant'and two MEK dewaxing plants. Br. J. Ind. Med. 37:85-89 1980. 5. Morgan, R. W., Kaplan, S. B., Gaffey, W. R.: A general mortality study of production workers in the paint and coatings manufacturing industry. J. Occ. Med. 23:13-21, 1981. 6. Austin, S. G., Schnatter, A. R.: A cohort mortality study of petrochemical workers. 0. Occ. Med. 25(4).*304-312, 1983. 7. Waxweiler, R. J., Alexander V., Leffingwell, S. S., et al.:Mortality from brain tumor and other causes in a cohort of petrochemical workers. J. Nat. Can. Inst. 70:75-81, 1983. 8. Austin, S. G., Schnatter, A. R.: A case-control study of chemical exposures and brain tumors in petrochemical workers. J. Occ. Med. 25(4):313-320, 1983. 9. Leffingwell, S. S., Waxweiler, R., Alexander, V., Ludwig, H. R., and Halpern, W.: Case control study of brain cancers among workers employed by a Texas City, Texas Chemical Plant. May, 1983 (unpublished). 1 i UCC 097526 Distribution J. B. Browning B. B. Ballantyne (So. Charleston) W, E. ^Chambers R. C. Cope N. W. Gaines D. H. Glenn (Texas City) H. L. Greenberg T. G. Fortney (Indianapolis) W. E. Hoerger W. C. Kuryla ^A. A. Lang B. C. Lewinsohn T. A. Lincoln R. R. Rankin F. S. Provenzano (Texas City) A. R. Schnatter H. <J Teta R. Van Mynen R. C. Wise UCC 097527