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Mortality of petroleum refinery workers
  1. S Parodi1,
  2. F Montanaro1,
  3. M Ceppi1,
  4. V Gennaro1
  1. 1National Cancer Research Institute of Genova, Largo R. Benzi, 10 Genova, Italy; stefano.parodi{at}
    1. K Satin2,
    2. W Bailey2,
    3. K L Newton2,
    4. A Y Ross2,
    5. O Wong3
    1. 2ChevronTexaco, PO Box 1627, Richmond, CA 94802-0627, USA; ksat{at}
    2. 3Applied Health Sciences, Inc., PO Box 2078, San Mateo, CA 94401, USA

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      Mortality of petroleum refinery workers

      We would like to comment on the paper by Satin and colleagues,1 which reports an update of a mortality investigation on two cohorts of petroleum refinery workers. The authors claim that one of the major aims of their study was the assessment of “health risks relative to more contemporary levels of exposure and work environments”. Nevertheless, they explicitly admit that a previous investigation in such cohorts,2 using the population of California as referent, found a strong “healthy worker effect” (that is, a significantly lower than expected mortality risk from cardiovascular disease and lung cancer). In our opinion, this observation, along with some other drawbacks, only in part expressly acknowledged in the paper, might have biased most of the results obtained, leading the authors to draw unreliable conclusions. We shall discuss this issue in detail, illustrating the main possible biases and how we believe they should have been interpreted.

      Comparison bias

      Exposure effects should be assessed in cohort studies by comparing the exposed cohorts with at least an unexposed one, as similar as possible in all relevant aspects.3

      The new results by Satin et al have confirmed the occurrence of the“healthy worker effect” observed in the previous follow up. Such a finding may indicate a comparison bias concealing the associations, if any, between exposure and health risks.2 In fact, occupational cohorts may differ from the general population in many features that have been associated with various risk factors, including socioeconomic status and personal habits.3 The presence of a comparison bias, at least in the Richmond refinery cohort, seems to be suggested by the risk for leukaemia in the subgroup with the shortest duration of employment (⩽5 years), which is more than four times lower than the referent population (and nearly seven times lower than those of workers who worked the longest—that is, >30 years). Finally, the lack of data on smoking, whose differential distribution is among the main factors known to be responsible for the “healthy worker effect”, should have suggested a more cautious interpretation of the results of analyses about diseases associated with such a risk factor, especially lung cancer. Owing to the quality of the data analysed, most of these limits are unavoidable. However, in our opinion, the authors should have taken them into account in discussing their results. For instance, the low leukaemia risk observed, in particular, for workers hired after 1949, should not have been considered as evidence of a lack of effect of quite low doses of benzene.

      Dilution effect

      Petrochemical workers are likely to experience different kinds and levels of exposure by job category. As a consequence, results from an analysis carried out by pooling together different exposure categories may be affected by a dilution effect—that is, an underestimation of the true mortality risk associated to exposure.3 For example, Gennaro and colleagues4–6 highlighted an excess of lung cancer risk among petroleum workers exposed to asbestos in an Italian refinery, which became evident only by using an unexposed job category as an internal referent group. In this investigation, the most heavily exposed group (maintenance workers) was 38% of the whole cohort of employees, similar to the proportion (36%) reported in a previous study on 10 US refineries.7 Furthermore, white collar workers constituted 22% and 21% of the workforce among the Italian and US refineries, respectively, suggesting that the composition of this kind of cohort tends to be similar, at least in Western countries. Unfortunately, the quality of the data in their possession prevented the authors from carrying out risk analyses by job category, and they did not discuss the possibility that the inclusion, if it occurred, of a notable proportion of workers scarcely or not at all exposed may have caused a significant lowering of the estimated risks.3

      Moreover, the inclusion in the present analysis of workers employed after 31 December 1980, thus inflating the at risk population estimates (person-years), could have further contributed to diluting the possible risks, in addition to preventing a precise comparison with the previous update. In fact, a long lag time is expected between exposure and disease occurrence for most of the cancer sites considered. The mean time of follow up was roughly 33 years for workers hired before 1949 and only 23 for those hired after 1949, but the authors have not provided any information about the group employed since 1981, making it impossible to estimate the true risks associated with prolonged exposures. Comparing the paper by Satin et al to the previous follow up,2 the number of workers enrolled after 1980 could amount to 3600 (that is, 31% of the subjects hired after 1949) and the corresponding follow up ranges from 1 to 15 years. However, these data do not allow the calculation of either the corresponding person-years at risk or the number of deaths which occurred.

      Statistical analysis

      The authors have indirectly evaluated the effect of exposures using the period of hiring (before versus after 1949) and the number of years worked as factors. Due to the lack of more precise measures of the polluting concentrations, such substitute variables are of course necessary, even though in our opinion, the analysis for another cut off after 1949 (for example, 1969 or 1979) might have yielded some additional information about the variation of such risks over time. Furthermore, a possible confounding effect between the period of hiring and the other variables (for example, length of exposure and latency) should have been taken into account, for instance, either by applying a multivariable statistical model, such as the Poisson regression, or by stratified analysis.8

      Insensitive indicators

      Mortality rates may be poor indicators of cancer risk for disease sites with a good prognosis, for example, leukaemia and larynx cancer.3 For this reason, comparisons based on mortality rates might be affected by lack of statistical power. Moreover, the authors admit that the potential inaccuracy of diagnostic information from death certificates may have caused misclassification between asbestosis and pneumoconiosis. However, this inaccuracy might have also affected the risk estimates for specific leukaemia types. While the authors do not report any results for unspecified leukaemia, another investigation on petrochemical workers9 found surprisingly much higher risks for both “acute unspecified” and “cell type unspecified” leukaemia than those for each specified cell type, including acute myeloid (AML). In our view, when data come from death certificates, risk estimates for different leukaemia cell types must be interpreted with extreme care. In particular, the authors’ claim that “the lack of any increase in AML ... argues against benzene’s role in the increase of MM and NHL found here” is not justified.


      Cohort studies based on mortality data and not including an internal group as a control may be affected by several biases. For this reason, the estimates of association between exposure to toxic chemicals and health risks obtained by these studies should be considered with caution.

      Moreover, the observed excess of risk, if any, should not be ignored simply on the basis of the lack of statistical significance. The need for further investigations for a better evaluation of such risk, for instance, through nested case-control studies, should always be suggested.


      Authors’ reply

      Parodi et al raised several comments on our cohort mortality study of petroleum refinery workers in California.1 Their comments are general in nature and apply to most, if not all, occupational cohort mortality investigations in general and refinery studies in particular, including such studies conducted in the USA, the UK, Canada, and Italy.2–7 We have discussed the same issues in our original paper. Below we will reiterate and expand our discussion of these issues in the order raised by Parodi et al.

      The first comment raised by Parodi et al is the potential impact of the healthy worker effect (HWE) in our study. More specifically, Parodi et al conjectured that the HWE might have masked an excess of leukaemia, particularly in employees hired after 1949. The HWE is a potential problem common to all cohort studies that use general populations as the basis for comparison. All petroleum cohort studies conducted in the USA, the UK, Canada, and Italy are equally vulnerable. However, when raising the HWE as an issue, one must consider the following points. First, it is generally recognised that the disease most strongly affected by the HWE is cardiovascular disease and that the HWE has little impact on cancer. This view is supported by studies from the USA, Canada, and Europe.8–11 Second, the HWE diminishes over time after hire. Monson8 estimated that the HWE generally lasted about 15 years. In our study, there was no significant increase of leukaemia among employees 20 or 30 years after hire, regardless of hire date (before or after 1949). Therefore, the lack of a leukaemia excess in our study was not likely due to the HWE. Monson summarised most sensibly the impact of the HWE as follows: “The healthy worker effect is relatively weak in comparison to causal excesses that can be detected in epidemiologic data.”

      The second comment raised by Parodi et al concerns the lack of exposure information in our study that would have allowed us to classify workers by exposure and to conduct more detailed exposure specific analyses. Again, the lack of detailed exposure information is a general problem for all retrospective cohort studies, and our study of California refinery workers is no exception. We acknowledged this limitation in our original paper. A similar comment regarding the lack of detailed classification of workers by exposure or job activity was raised previously concerning the finding of lung cancer in another study of US petroleum workers, but subsequent detailed analyses by job title revealed no increase of lung cancer for insulators, pipe fitters, electricians, boilermakers, or maintenance workers.12 The most appropriate approach to deal with specific exposures is to conduct cohort based or nested case-control studies. Such nested case-control studies have been conducted subsequently for a number of cohort studies of petroleum workers in the USA, the UK, and Canada.13–16 Detailed exposure information (including quantitative estimates) was collected on individual cases and controls in these investigations. Furthermore, comparisons in these case-control studies are internal, thus avoiding the HWE. Based on nested case-control studies, Rosamilia and colleagues13 did not find any relation between lung cancer and asbestos exposure at a US refinery; Wong and colleagues14 did not find any increase of leukaemia, kidney cancer, or multiple myeloma in relation to gasoline (hence, benzene) exposure among US petroleum workers; Schnatter and colleagues15 did not find any relation between lymphohaematopoietic malignancies and benzene exposure in Canadian petroleum workers; and Rushton and Romaniuk16 concluded that there was no evidence of an association between benzene exposure and lymphoid leukaemia, either acute or chronic, among petroleum workers in the UK. Thus, none of the nested case-control studies contradicted the findings of the original cohort studies; nor is it axiomatic that the absence of analyses based on detailed exposure information automatically implies masked health effects.

      Parodi et al criticised the inclusion of employees hired after 1980 in our study, and argued that the latency of these workers (15 years maximum) might not have been sufficient, thus “diluting” the risk of prolonged exposures among those hired in or before 1980. We would like to point out that, first, our investigation is not merely an academic exercise but part of an ongoing corporate medical monitoring programme that includes all employees. Second, an analysis stratified by latency was performed (table 3 in our original paper). The groups with 20–29 and 30+ years of latency did not include any employees hired after 1980 and, therefore, could not have been “diluted” by workers hired after 1980. Third, with regard to prolonged exposures, an analysis stratified by duration of employment was also performed (table 2 in our original paper), and the groups with 15–29 and 30+ years of employment would certainly have had prolonged exposures and the results would not have been “diluted” by employees hired after 1980.

      With regard to statistical analysis, Parodi et al questioned our analysis by period of hire before and after 1949, and suggested cut points of 1969 and 1979. We do not understand the basis of their suggestion. We chose 1949 because of historical exposure patterns. In 1947, the recommended standard for benzene exposure in the USA was reduced from 100 ppm to 50 ppm, which was further reduced to 35 ppm in 1948. Benzene exposure levels in the petroleum industry were significantly reduced after 1949, thus making 1949 a good surrogate measure for exposure.

      Finally, Parodi et al commented that mortality might not be a good indicator of cancer risk. This general comment, of course, applies to all studies based on mortality. In the USA there is no national cancer registry, and it is simply not possible to ascertain cancer incidence in a historical cohort study of more than 18 000 workers that goes back to 1950. In their comments, Parodi et al were concerned with exposures to asbestos and benzene. The cancers related to these exposures are lung cancer, malignant mesothelioma, and acute myeloid leukaemia. These particular cancers have relatively poor prognosis, particularly in the past, and mortality may not be an unreasonable outcome measure. Parodi et al also commented on the diagnostic accuracy of death certificates. Again, this comment applies to all studies based on mortality. It should be noted that diagnostic accuracy varies by disease. For example, lung cancers are seldom misdiagnosed. Although some diagnoses on death certificates may not be as accurate as those based on detailed medical records, relying on death certificates in both the study and reference populations ensures comparability.

      Furthermore, our interpretation of the results was based on not only what we observed, but also the findings of related studies. For example, for non-Hodgkin’s lymphoma (NHL) and multiple myeloma (MM), in addition to our results, we also relied on hospital based case-controls studies which were included in previous reviews cited in our paper.17,18 The diagnoses in these hospital based case-control studies were based on detailed clinical, laboratory, and pathological findings. The conclusion from these hospital based case-control studies is that there is no relation between benzene exposure and NHL or MM. Therefore, our conclusion of MM and NHL based on our study is consistent with other studies in which diagnostic accuracy is not an issue.

      In their conclusion, Parodi et al cautioned that results should not be ignored simply on the basis of the lack of statistical significance and suggested nested case-control studies be conducted for further investigation. We concur on these two points. In discussing the results of our study, we did not ignore any findings simply because they were not statistically significant. We fully recognised that a result might not be statistically significant because the statistical power of an individual study might not be adequate and that the result must be interpreted in conjunction with other similar studies. As one of the objectives stated in our original paper, we assessed our findings (statistically significant or otherwise) in the context of results of other petroleum studies. To take all studies into consideration, we also relied on several reviews and meta-analyses of studies of petroleum workers around the world.12,17–19 For example, based on a combined database of more than 350 000 petroleum workers in the USA, the UK, Canada, Australia, Finland, Sweden, and Italy, Wong and Raabe12 reported that consistently not a single study showed an increase of lung cancer; the summary lung cancer standardised mortality ratio was 0.81, with a 95% confidence interval of 0.79 to 0.83 (based on 5695 deaths). As to the suggestion of further investigations using nested case-control studies, such detailed case-control studies have been conducted among petroleum workers in the USA, the UK, and Canada.13–16 As discussed above, none of these nested case-control studies contradicted the findings of the original cohort studies.

      Therefore, while Parodi et al have raised several limitations common to occupational retrospective cohort studies, we believe that we already have discussed these issues in our original paper and that we have not over interpreted our data.