6.4.1 Smoking and other potential confounders
Three categories of potential confounding risk factors are adjusted for in the case-control analysis. These are smoking x worker location interaction (16 categories), history of respiratory disease (four categories), and employment in other high risk occupations (five categories).
Smoking is of particular concern because of the strong associations (higher ORs) and because of the marked difference in risk between surface and UG workers. The risks of lung cancer among surface workers show typical E-R patterns with ORs rising steeply with increased cigarettes/day among both ex-smokers and current smokers. This expected pattern is not observed among UG workers as light and heavy smokers have about the same ORs, and this is true for light and heavy ex-smokers as well (). A possible explanation for this is that smoking information was subject to misclassification (the smoking information for cases was mainly from next-ofkin) and potentially resulting in imperfect adjustment and residual cofounding by smoking. The risks of smoking are considerably greater overall with >90% of cases having 3 to 12-fold increased ORs (their ) ().
In addressing the issue of confounding we remind the reader that two criteria must be met for a variable to be a confounder. These are (i) it must be a risk factor, and (ii) it must be associated with exposure.
The first criterion is clearly met in this study, as potential confounders (e.g., smoking, history of respirable disease, employment in high risk jobs) are risk factors as shown in their and .
The second criterion is only partially met. Smoking is associated with exposure among UG workers as shown by the lower prevalence of smoking among higher exposed UG workers. The only other data provided on criterion 2 are found in their which indicates little or no association of current smoking with DE exposure in all study subjects. This second finding, summarized in , indicates little or no need for adjustment for confounding from current smoking in the major analyses involving all cases and controls because the second criterion for being a confounder is not met. Therefore, there should be little or no adjustment effect for smoking. Herein lays a major limitation in the results of this study.
We will discuss the second criterion as well as the unexpected size and direction of the confounding effects reported in this study. The authors indicated that smoking is a negative confounder among UG workers, so when smoking adjustments are made the effect is to increase the crude ORs. On page 9 the authors indicate there is “negative confounding from cigarette smoking because current smoking was inversely related to diesel exposure in underground workers. That is the prevalence of smoking was 36 and 21% among lowest and highest cumulative REC tertiles respectively.” The negative confounding effect of smoking with these prevalences is calculated to be about 0.7; that is the confounded OR will be about 0.7 times the true OR if the strength of association for smoking is five (McNamee 2003
), which approximates the RR among UG current smokers (). The observed negative confounding effect of smoking among UG workers lagged 15-years is calculated as: (confounded OR) ÷ (unconfounded OR) = 3.75 ÷ 5.9 = 0.64 (Page 9). In this instance, the estimated and observed apparent effects of confounding (presumably mostly from smoking) appear similar. This negative confounding effect from current smoking is shown by “somewhat higher” adjusted ORs compared to ORs without smoking in the model. The differences between ORs without smoking in the model and HRs from the cohort study are effects from other confounders ().
“Smoking” in this instance presumably includes current and former smoking. The differences between adjusted ORs and HRs shown in are presumably due largely to confounding from smoking × work location plus history of respiratory disease and employment in high risk jobs ().
Figure 24 Adjusted and crude lung cancer ORs stratified by confounders from employment in other high risk occupations and history of respiratory disease ( in Silverman et al., 2012).
The confounding effects of smoking and other confounders may also be observed by comparing adjusted and crude ORs among UG workers as shown in –. The maximum difference occurred with 15-year lagged REC exposures where the adjusted OR is 2.8 times higher than the crude OR in the highest exposure quartile; that is the confounding factor is 0.35 (1.80 ÷ 5.10) among UG workers.
Figure 25 Crude and adjusted ORs for lung cancer and unlagged cumulative REC; ORs adjusted for 24 smoking × mine location, history of respiratory disease >5-years and history of high risk job for lung cancer >10-years; Crude ORs calculated (more ...)
Figure 27 Crude and adjusted ORs for lung cancer and 15-years lagged cumulative REC for expanded exposure categories; ORs adjusted for smoking × mine work location, >5-year history of respiratory disease, and >10-year history of high risk (more ...)
The differences between crude OR and adjusted ORs are also quite large among the total cohort, but in the same general range as the differences observed among UG workers. For example, the crude ORs are 46 and 28% of the adjusted ORs in the quartile and expanded categorical analyses lagged 15-years ( and S2, and ).
Figure 26 Crude and adjusted ORs for lung cancer and 15-year lagged cumulative REC; ORs adjusted for smoking × mine location interaction; >5-year history of respiratory disease and >10-year history of high risk jobs for lung cancer; crude (more ...)
As a side note, effects of residual confounding from risk factors other than smoking appear comparable to the apparent effect of smoking (). Whether they are confounders cannot be evaluated because we don't know whether they are associated with DE exposure. If they are associated with DE exposure their potential confounding effect is expected to be relatively small compared to smoking because relative risks and prevalences are less. For example, >10-years employment in a high risk job is associated with <two-fold increased OR, and all other years show no increased risk (). With six cases in this exposure category, the potential confounding effects may be minor. Risks of respiratory disease are greater, with 9-fold and 2.5-fold increased ORs for 13–14% of cases with <5-years and >5-years of respiratory disease, respectively ().
A critical factor in the finding of a “negative confounding effect” of smoking is that it is applicable to UG workers only; it is not applicable to the overall results. The prevalence of smoking among controls is 23, 27.9 and 25% among high, medium and low exposure tertiles among all current smokers (, their ). This contrasts with prevalences of 21 and 36% among UG current smokers in the highest versus lowest cumulative REC tertiles. The similarity of smoking prevalences by DE exposure among all controls indicates negligible association between smoking and DE, and therefore small or negligible confounding among all participants. Moreover, the primary focus in the case-control study is on all participants, not just UG workers. In the complete cohort of all workers there is no apparent confounding from current smoking in the case-control study.
If true, this limitation dramatically changes the results and conclusions derived from this study. Confirmation of this hypothesis of negligible confounding from smoking requires more information and analyses from the authors and independent investigators, but we will present a rationale for our conclusion that there is negligible confounding from current smoking and the purported E-R trends associated with DE exposure are largely due to incorrect adjustments for non-existent confounding from smoking.
Since smoking is commonly shown to be a positive confounder in occupational SMR studies of lung cancer, the usual adjustments for smoking (if attempted), reduce the SMR (as workers generally smoke more than the general population and so smoking is associated with exposure). But this is a nested case-control study, so the referent group is not the general population but is comprised of workers with lower DE exposure (but not necessarily less exposure to cigarette smoke). In E-R analyses it is commonly assumed that smoking prevalence is largely independent of exposure. That is, smoking prevalence is often similar at high, medium and low exposure levels. When this occurs smoking is not a confounder, or the differences in distribution may be small so effects of confounding will also be small. But the literature also indicates that the association of risk factor and exposure has rarely if ever been considered (or at least data are rarely presented) in E-R analyses where adjustments are made for smoking.
Data shown in from Silverman et al. were used to calculate the prevalence of smoking among controls by exposure to REC. These data indicate that current smoking cannot be a strong confounder, and at most is a very weak confounder, because current smoking is not associated with REC exposure. The prevalence of smoking among controls does not vary significantly by cumulative REC tertiles (i.e., 23 vs. 27.9 vs. 25%). Therefore there is no association of current smoking and DE exposure, and current smoking cannot be a significant confounder ().
If current smoking is not a confounder there should be little change in crude ORs when adjustments are made for smoking. There could be confounding effects from ex-smokers, history of respiratory disease and employment in other high risk jobs, as those risk factors could be associated with REC. While those data are unavailable, it seems likely that their distribution may be similar enough to the distribution of current smoking to produce relatively weak associations with DE exposure and therefore weak adjustment effects.
The evidence on the lack of association between smoking and REC in current smokers leads to the conclusion that smoking adjusted ORs in the E-R analyses are unreliable and too large. If the E-R trends are unreliable, then what is the association between lung cancer and REC exposure? If current smoking is not a confounder, then the closest approximation to the ‘true’ relationship is more likely to be the crude ORs.
Calculated crude ORs show a consistent lack of E-R trends (–). These are crude ORs without matching of cases and controls, so the E-R patterns are an approximation of actual trends. But this approximation is likely to be similar to the E-R pattern based on matched calculations. If the distribution of former smokers was similar to that of current smokers, one would expect E-R trends to be similar to the crude E-R trends. If former smokers and cases with other risk factors are much more prevalent at low REC exposure there will be a negative confounding effect and adjusted ORs will be larger than crude ORs. If the reverse occurs there is a positive confounding effect and adjusted ORs should be less than crude ORs. Or there may be little association of formers smokers with DE exposure and negligible confounding from former smoking and negligible adjustment effect on ORs. In this instance, the E-R pattern from crude ORs likely approximates the “true” E-R pattern.
The actual confounding effects should be confirmed as the only data on distribution of risk factors by exposure was for current smokers. The distribution of other risk factors is undoubtedly different than that of current smoking among all participants, but unless markedly different adjustments for their confounding are unlikely to produce large changes in the crude ORs. Until the associations of risk factors and REC are confirmed, E-R trends from this study are unreliable.
The virtual absence of a confounding effect from current smoking and potential minor confounding effects from other variables suggests that the smoking x worker location is the primary cause of the large positive effect on the adjusted ORs. This conjecture is consistent with a similar “adjustment effect” in UG workers where there is a large and negative confounding effect between crude OR and adjusted OR (, ). But there should be only a small adjustment effect because in the absence of surface workers the smoking x work location adjustment effect is zero.
Figure 28 Crude and adjusted ORs for lung cancer and unlagged cumulative REC among underground (UG) workers; ORS adjusted for smoking × mine location, >5-years respiratory disease and >10 years history high risk job for lung cancer; crude (more ...)
Figure 29 Crude and adjusted ORs for lung cancer and 15-year lagged cumulative REC among underground (UG) workers; ORs adjusted for smoking × mine work location, >5-year respiratory disease and >10-year history high risk job for lung cancer; (more ...)
The smoking × worker location adjustment effect appears to be incorrect, and two possible sources of error come to mind.
- Perhaps smoking prevalences for UG workers were used instead of prevalences for the complete cohort as shown in . This possible error is suggested by the use of UG prevalences in the authors' comment regarding negative confounding.
- The statistical model may be unstable because of empty cells as suggested by the large number of adjustments and wide confidence intervals.
Our conjecture suggests that the E-R trends in the case-control study are largely due to upward-biased smoking adjustments and that residual confounding effects from other risk factors are relatively minor. If so, HRs from the complete cohort will be similar to crude unadjusted ORs from the case-control study. shows similar E-R patterns for HRs and crude ORs for 15-year lagged exposures. The primary differences are that HRs are adjusted for worker location, age, race and sex and the referent group are all eligible members of the cohort, while the referent group in the calculation of crude ORs is comprised of 562 randomly selected controls matched by mining facility, sex, age and race.
The implausibly large and positive adjustment effects for confounding that produced the unreliable E-R trends remains unexplained. The authors' conclusions appear to be based on E-R trends in the complete cohort produced by smoking adjustments based on confounding among UG workers. Current smoking is not associated with cumulative REC exposure among all cases and control, so among the complete cohort there should be a negligible adjustment effect for current smoking. Until the anomaly of a large and negative confounding effect is sorted out and confirmed, these case-control results should be considered inconclusive and the authors conclusions potentially unsupported by the data.
Results from the simple comparison of HR and crude OR are consistent with a result of no association of lung cancer and cumulative REC exposures in the DEMS study population. The apparent E-R trends in the case-control study may be due to incorrect adjustments for a negative confounding effect that in large part does not appear to exist.
Note: The NCI website said non-smokers at the highest level of DE exposure were seven times more likely to die from lung cancer than non-smokers in the lower exposure category (Lacey and Hegstad 2012
). The only data provided in the published report compares non-smoking UG and surface workers with ORs of 0.90 (0.26–3.09) and 1.0 (referent) and REC intensities of 1–423 versus 0–8 µg/m3
6.4.2 Exposure misclassification
Quantitative estimates of exposure appear to be a strength of the DEMS studies and are described in detail in previous publications (Coble et al., 2010
; Stewart et al., 2010
; Vermeulen et al., 2010a
; Stewart et al., 2012
). However, exposure misclassification may still be an important limitation based on questionable accuracy of those estimates as summarized, analyzed and discussed in recent articles and letters to the editor (Borak et al., 2011
; Clark et al., 2012
; Crump and van Landingham 2012
). Among the issues calling the DEMS exposure estimates into question are the following:
- CO has never been used before as a surrogate for DE exposure.
- CO colorimetric indicator tubes are imprecise and unreliable at low concentrations.
- Results from CO indicators are reasonably precise (±25% or greater) at high exposures, but are more imprecise and unreliable at concentrations <5 ppm (Borak et al., 2011). The majority of CO measurements in DEMS reports are <5 ppm, with 20–60% below the limit of detection (about 1 ppm) at the face of the mine with highest CO concentration. Nearly all CO measurements are in the range where precision is generally worse than ±35%.
- Prior to 1976 there were few CO measurements available so estimates of diesel horsepower (HP) in the mines along with mine ventilation rates were used to estimate CO concentrations. Thus, there are two uncertain extrapolations at issue: one from HP to CO, and the other from CO to REC. But there is no consistent relationship between CO and HP (or EC) (Crump and van Landingham 2012).
- Correlations of REC and CO are too low and variable for use in exposure assessment.
- Correlation of REC and CO is highly variable and low; the mean reported correlation was 0.41 ranging from 0.05 to 0.77 in the DEMS mines. Diesel oxidation catalysts (DOC) were introduced into mines in the 1970s and 1980s (Hesterberg et al., 2012). DOCs oxidize CO to CO2, which greatly decreases CO air concentrations and reduces CO:REC ratios (Hesterberg et al., 2012). Decreases in CO are immeasurable at low concentration. At higher REC levels CO will also be higher, and when CO levels are above the LOD the effect of DOCs will be measurable over time by measured reductions in CO levels down to the LOD. Under these circumstances the CO being measured will be less than the actual CO emitted before oxidation and will under-estimate REC levels. Unadjusted effects of this technology may produce biased underestimates of REC, with greater bias at the high end of exposure and decreasing bias as exposures decline. Adjustment for DOC may reduce this bias, but when CO levels are below the LOD, it is not clear how adjustments can be made.
- Confidence intervals for historical levels of CO indicated that more than 60% of the estimates were not statistically different from zero (Crump and van Landingham 2012).
These findings present interesting anomalies. The capability of differentiating job exposures should be greatest at higher exposures where the CO indicator tubes are most reliable. Thus, the confidence intervals should be narrower for those jobs and relatively wider as exposure decreases. If true, there would be greater exposure misclassification among lower exposure jobs than higher exposure jobs. However, greater exposure misclassification at the highest exposures was mentioned as a possible explanation for the attenuation of risks at the highest levels of cumulative exposure in both the cohort study and case-control studies. Presumably the DEMS authors are referencing an increased over-estimation of exposure at highest exposures which could reduce estimated ORs. But the authors provided no basis for any increased misclassification at higher exposures, although this is a possible basis for their rationale. Conjectures of the potential for increased under- or over-estimation of exposure and for increased misclassification at higher concentration needs verification.
The ultimate question of concern is whether the unreliability in the exposure estimates changes the E-R patterns or biases the estimated risks. A consistently biased under-estimate (or over-estimate) of exposures produces spuriously over-estimated (or under-estimated) ORs, but probably does not affect overall E-R patterns. On the other hand, a systematic bias at different exposure levels can affect E-R patterns. Limitations in exposure assessments may have larger effects on E-R patterns at higher exposure levels. If the misclassification is related to unadjusted effects of DOCs on CO, under-estimation of REC levels is a plausible outcome. Multiple factors suggest exposure misclassification is probable as discussed below.
(i) Estimated REC exposures are based on extrapolations from samples collected during 1998–2001, many years after the relevant era for estimating exposure levels and after the end of follow-up in 1997. What was being sampled was transitional DE, and the sampled levels were undoubtedly lower than the historical levels of TDE in the mines. DE emissions were progressively reduced by 99% in transitioning from TDE to NTDE, although the decreases in criteria pollutant emissions were probably proportionately greater than CO reductions. Historical REC levels were undoubtedly higher, in part because of the post-1990 diesel engine technology changes, as well as the reduced levels of sulfur in diesel fuel, which all came about due to increasingly stringent regulations applicable to off-road diesel engines (Hesterberg et al., 2012).
(ii) CO samples collected at low exposure levels are inaccurate and CO concentrations from diesel emissions were reduced with the introduction of DOCs, thereby reducing the CO:REC ratio to an unknown extent. DOCs reduce CO:REC ratios, so using CO as an indicator of REC may produce under-estimates of exposure. The proportion of CO exposures below the LOD is too high, so imputation of CO is necessary at these low exposure levels. And different methods for imputation of non-detectable CO levels produce different results (Crump et al., 2012).
If these facts produced under-estimated REC levels, the bias is expected to be more pronounced at higher exposure levels. This follows from the assumption that CO reductions via DOC at low diesel exposures reduce CO emissions to levels near the LOD, which amounts to a small decrease in absolute CO levels. At high diesel exposures, however the CO levels are higher, and the post-DOC CO levels remain above the LOD. Because CO can still be measured by CO indicator tubes at higher exposures, the absolute reduction in CO via DOC oxidation is greater than the reductions to the LOD. For example, if 50% of CO emissions are oxidized to CO2, the measurable air concentration is reduced by 20 ppm if the starting point is 40 ppm, but is reduced by 50 ppm if the starting point is 100 ppm CO.
A recent reanalysis indicates additional cause for concern about exposure misclassification. Although the possible direction of bias is unclear, this review suggests that there are unanswered questions regarding the reliability and accuracy of the exposure estimates used in the DEMS studies (Crump and van Landingham 2012
). These authors outline the difficulties of estimating REC exposures which began with the introduction of diesel engines into the mines in 1940s to 1960s. REC estimates are based on samples collected largely during 1998–2001. Because of the lack of REC data, surrogates were used. CO indicator tube data were fairly numerous 1976–2001, but few samples were available before 1976. As a result, a second surrogate of horsepower (HP) was used to estimate CO levels before 1976, with extrapolations of HP to CO, and then CO to REC. We will list some of the major uncertainties discovered in this analysis and their attempted replication of NCI/NIOSH results.
- The NCI/NIOSH assumption of a linear relationship (exponent = 1.0) between REC and CO does not appear to be valid. That assumption is based on data (Clark et al., 1999; Yanowitz et al., 2000) which do not show a linear relationship (Yanowitz et al., 2000). NCI/NIOSH claimed the Yanowitz et al. exponents amounted to 0.58 (with upper confidence limit <1.0), Crump et al. (Crump and van Landingham 2012) reported exponents ranging from 0.39 to 0.44, and calculated an exponent of 0.30 using an improved method of dealing with CO values <LOD. Other evidence from 11 different types of diesel engines and seven different sites showed no universal relationship between CO and PM (with PM being a surrogate for REC). If there was a relationship it was unique for each engine type, and perhaps for each engine (Clark et al., 1999).
- The assumed relationship between CO and HP is also problematic. It also is based on (Yanowitz et al., 2000) which showed a non-significant slope (p = 0.08) and large variation (R2 = 0.01).
- HP was based on inventories of diesel engines and mine ventilation data that appears to be rarely available prior to 1976. Vermeulen et al. (2010a,b) indicated they were rarely available during the 1980s.
- The statistical model is unreliable for estimating REC from CO. The NCI/NIOSH test of their model found a median difference of 33% when the model contained a variable that used CO measurements from the 1998–2001 DEMS survey. If CO data from a 1976–1977 survey are used, the mean relative difference is −274%. This test indicates a poor model, even though the 1976–1977 data were used to develop the CO model.
- Crump et al. (Crump and van Landingham 2012) found substantial differences in REC estimates when the CO model was improved. The CO model was improved: by using collected data on the CO:REC relationship rather than assuming an implausible linear relationship; by taking statistical uncertainty into account rather than using only best estimates of parameters; and by using an improved method for imputing CO levels from samples <LOD. The net result was that the NCI/NIOSH REC values for most mines “do not lie completely within the confidence bands” estimated in the Crump et al. analyses.
The inability to replicate the NIOSH/NCI results – finding different results from the same data and unreliable correlations between HP:CO:REC – indicates that the exposure assessments may be unreliable and inadequate for estimating exposure in the cohort and case-control epidemiology studies. Until there is an independent verification of the DEMS exposure results, the DEMS E-R results should be considered unreliable and inconclusive.
6.4.4 Inconsistencies between cohort and case-control results
In the case-control study, it was suggested that the “unlagged approach led to exposure misclassification because recent exposures may not have had sufficient time to contribute to lung cancer risk.” The best fitting continuous models from the case-control study are linear-exponential, with ptrend values of 0.09 and 0.002 for the unlagged and 15-year lagged models respectively. It is not clear why the continuous model ORs continue to decline despite the elevated OR in the last exposure category (). A noteworthy feature in is the shallower and non-significant slope of the unlagged regression model. The peak is shifted to the right perhaps 500 μg/m3 years. Shifting from unlagged to 15-year lagged exposures reduces cumulative exposure so the referent quartile is reduced from <19 μg/m3 years unlagged to <l3 μg/m3 years in the 15-year lagged analysis. No expanded categorical model was provided for the unlagged analysis.
Thus, the rationale for selecting the 15-year lagged analysis does not appear to apply as it did not hold true in the cohort study, nor in the studies the authors cite as consistent with the findings of this study (see discussion below). If DE is increasing the risk of lung cancer, it could exert a carcinogenic effect on the lung through ‘late-stage’ mechanisms such as cell proliferation from chronic inflammation. If this is a mechanism, then unlagged analyses would be preferred to account for these effects potentially occurring in the last 15 years before death.
Appropriate use of lags is a concern for both the cohort and case-control studies. Should a lagged or unlagged model be used as the primary description of the results? In the other cohort and case-control diesel studies with quantitative E-R trends, zero lags were reported as the primary result, and when lags were evaluated there was generally no substantive difference from the zero lag results (See ). What makes the DEMS data set inconsistent with other studies? Why are the p-values so inconsistent across models and dependent on the lag periods?
Summary of diesel-exposed workers in occupational cohorts with quantitative or semi-quantitative estimates of cumulative exposure to diesel exhaust and analysis of exposure-response trends.
It's not clear why the lags are having such an effect on the p values. But one thing we can be sure about is that excluding the last 15-years of exposure reduces the exposure range by reducing cumulative exposure for all individuals except for retirees living more than 15-years after retirement from the mine. But since latency is adequate in this cohort, the 15-year lags are not needed to assure adequate latency. Lags increase the number of referents with cumulative exposure being reduced to zero. For example, in the unlagged analysis there were 50 workers with cumulative REC exposures >964 µg/m3 years; with 15-year lags the exposure range of these same 50 workers has been reduced to >536 µg/m3 years. Does this change in the data set result in an artifact in the p values?