Dear Editor

The paper by Kraus and colleagues[1] in the December 2002 issue of Occupational and Environmental Medicine addresses the important issue of the relationship of personal exposure to possible effect in an industrial setting. After reading this paper I would like to make some comments with regard to the design, conduct and statistical analysis of the study.

In an area where exposure assessment and confounding effects are so important, it is interesting to see that seemingly important associations are being drawn with so little information.

Kraus and colleagues state the goal of the paper as “To correlate the prevalence of respiratory tract symptoms and diseases with dust and fibre exposure in the soft tissue industry in Germany” rather than to investigate whether such a relationship actually exists.

The authors state that: “In every company pure cellulose was the basis of the production process. Recycled paper was not a relevant component of the products.”, however, in the introduction they site many references of toxicological studies that used insulation cellulose (Isofloc, which is ground up used newspapers sprayed with boric acid) and other not pure cellulose products. The contaminants in used newspapers with boric acid would be expected to produce a radically different toxicological response than inhaled pure cellulose. Only studies that used pure cellulose of similar source and composition as used in the plants in this study group should be sited and for such studies the route of exposure and doses should be provided.

Sampling: From the text, it appears that in this study, data was obtained on dust measurements in various places in the 7 chosen German soft tissue companies. These were then compared to symptoms of persons working in these companies.

The authors state that “According to the employers’ information, we interviewed all persons from the different workshops employed during the time period 1996–98.” They then explain that “The data concerning dust measurements were gathered from 1991 to 1997.” Thus, it appears that the dust measurements were not directly related to the individuals with the symptoms nor were they even necessarily coinciding with the presence of the symptoms. There is no mention of how and where within each plant the exposures were determined, of whether the dust levels were similar from 1991 to 1997 and whether there was any personnel monitoring to determine exposures. However, the authors do state that “Because of differences in the exposure intensity between the seven companies a cumulative exposure index was generated for describing the individual exposure.” And as such mean exposure levels were used for comparison.

The confidence that can be placed in conclusions drawn from samples depends in part on sample size. Small samples can be unrepresentative just by chance, however, the scope for chance errors can be quantified statistically. Given this importance, why haven’t the authors stated the sample sizes in each of the groups used in the statistical analyses?

More problematic are the errors that arise from the method by which the sample is chosen. In situations with high dust levels there is more likelihood of sampling which would be atypical of the dust levels more generally. Such systematic errors cannot usually be measured, and assessment therefore becomes a matter for subjective judgment. Systematic sampling errors can be avoided by use of a random selection process in which each working condition has a known (non-zero) probability of being included in the study sample. However, this requires an enumeration of all working conditions in each plant over the entire sampling period (1991 – 1998).

Not only was there no mention of such a sampling procedure being performed in this study but any sensitivity to specific plant conditions has been lost through the use of mean values.

Group composition: The authors then gloss over the choice of controls which were persons from the “management department”. Certainly the working condition and environment of office workers is not comparable to that of maintenance workers, electricians and mechanics. Also of concern is the disproportionality in the controls compared to exposed in terms of number, sex and smoking history. No mention is made of age and how long the persons in each group worked in the plant. This information would permit the reader to assess whether the symptoms were associated with either age or length of employment. Also, the smoking histories are not comparable between the groups. From the means in Table 1, there is a positive association between exposure group and smoking which is never discussed in the paper. If smoking habits were asked “in a detailed way” as stated, why haven’t the data have been presented? As there appears to be a dose relationship with smoking and exposure group, the authors should have discussed in the introduction the possibility that smoking can also produce similar effects as reported in this paper and provide appropriate references.

The authors mention using an attenuation factor (“divided by four and multiplied by individual time of exposure”) under recommendation of technical experts. This implies that it was not possible to obtain any kind of relationships using the company individual monitoring data in relationship to the individuals working in each company. What is the rational and scientific basis for this? Without such information, the choice of cut points for the attenuation factor appears arbitrary and leads the reader to wonder whether the choice of cut points was determined iteratively in order to find an attenuation factor which produced correlations?

Statistical analysis: The authors use the Cochran-Armitage trend test without adjustment for other variables and even say “that the results are prone to being confounded”. Yet, they discuss at length the results from this test in Tables 3 and 4. Further, it is not at all clear that even this analysis was performed correctly. Hothorn and Bretz (2000),[2] explain that the Cochran-Armitage trend test is a test based upon a linear dose response relationship and that the test lacks power for other shapes. Most of the parameters shown in Tables 3 and 4 of the Kraus paper do not appear to have a linear dose-response.

More details of the results of the logistic regression analyses should have been presented to support the conclusions stated by the authors. At least an estimate of the percent variation in the data explained by each of the logistic regressions should be provided in the tables in order to assess the importance of each relationship. Grouped and individual R2 values are well documented in Statistical texts and can be calculated for each logistic regression in order to assess importance.

Results: The authors should have clearly state whether they used inhalable dust or respirable dust in each analysis. Respirable is probably more relevant, however, Table 2 indicates that there were only 24 respirable dust measurements. With 4 exposure categories (Controls, <_25 _25100="_25100"/>100) and 7 companies this would amount to less than 1 respirable dust sample per category per company over an 8 year of monitoring period! It is more likely that they used the inhalable dust measurements for which there were 105 measurements. Even with the inhalable dust measurements, this would amount to less than one inhalable dust measurement every two years per category per company!

The authors state that “The mean sampling time was 1.97 hours (range 0.16–3.8).” This amounts to each category in each plant being monitored for mean of 7.4 hours over a working time of 14,400 hours. Even if all 105 inhalable dust measurements were performed in one work year (which they were not), each category in each plant would have been monitored for a mean of 7.4 hours over a working time of approximately 1800 hours/year.

Yet, the authors are suggesting that somehow these few samples are representative of what 441 workers were exposed to over an 8 year sampling period. Not only are the samples not chosen correctly but the small sample size assures that these measurements are not representative.

The need for statistical significance also seems to have escaped the authors when discussing the disease parameters. The data presented indicate that none of the disease parameters are significantly different from the controls, yet the authors state that “However, sinusitis, laryngitis, and chronic bronchitis (a disease parameter) showed increasing odds ratios with increasing cumulative dust exposure (table 5).” What is the validity of stating this when there is no statistical significance in the relationship?

Again, in the discussion, the authors state that “After adjustment for smoking habits, chronic bronchitis was no longer significantly associated with dust or fibre exposure. However, the highest odds ratio (1.57) in the subgroup with longest and highest exposure suggests some deleterious potential.“ This is very worrisome that the authors suggest that there is a ‘deleterious potential’ when in fact there is no statistical basis from the data (95% CI of 0.7 to 4.0) for making such a statement.

In Tables 7 and 8 the authors group the ‘Diseases’ as part of the ‘Symptoms’ no longer differentiating between Diseases and Symptoms.

They then go on to state that “For example, intensity and duration of exposure have an almost equal influence on the symptom “blocked nose”. The calculated ORs rise with increasing exposure intensity from 6.4 to 10.8 and with increasing exposure duration from 6.4 to 12.5.” Fortunately, in Table 7 they present the 95% confidence limits which are (shown in parenthesis) for these values 6.4 (1.2 to 49.7) and 10.8 (2.9 to 70.5) which suggest that 6.4 is not different from 10.8 statistically. Not surprising given the statements by Kraus and colleagues, Tables 7 and 8 present no measure of statistical significance for any of the parameters yet they state that “For symptoms of the upper airways, clear dose- response relations could be found with relation to cumulative exposure indices”. This is certainly not supported by the data presented in these tables.

Discussion: Again the authors cite references to articles not dealing with the same pure cellulose as used in the plants. If there are studies using the same pure cellulose, then a discussion of the route of exposure and the exposed dose compared to what is seen here should have been included.

The Ericsson reference and others are not quoted correctly from the publications. As an example, Ericsson states that “There was a dose- dependent increase of symptoms from the upper respiratory tract. However, coughing and coughing with phlegm were not found to be more common among persons with heavy exposure compared to those with low exposure to the dust“, indicating that the Ericsson results are not comparable to those in the current manuscript.

The statement by the authors that “As expected, because of the distribution of inhalable and respirable dust fraction, symptoms of the lower respiratory tract have a weaker association with exposure after adjustment for confounders (for example, cough, phlegm, dyspnoea, and exercise induced dyspnoea)” should from the data presented in the paper be changed to state that “As expected, due to the distribution of inhalable and respirable dust fraction, symptoms of the lower respiratory tract have no statistically significant association with exposure after adjustment for confounders (e.g. cough, phlegm, dyspnea, exercise induced dyspnea).”

The question of respirator use in the plants should have been investigated. If respirators were used even by some employees, then any association to the measured dust levels for those persons is no longer valid.

I hope that the critical readers of your journal will decide based upon the statistical significance of the data whether there is a basis for stating that a relationship exists between exposure and effect in the soft tissue industry.

References

(1) T Kraus, A Pfahlberg, O Gefeller, H J Raithel, Respiratory symptoms and diseases among workers in the soft tissue producing industry. Occup Environ Med 2002;59:830–835.

(2) Hothorn LA and Bretz F. Evaluation of Animal Carcinogenicity Studies: Cochran-Armitage Trend Test vs. Multiple Contrast Tests. Biometrics Journal 2000;42(5):553-567.

Dear Editor

I have only recently had an opportunity to see the OEM online abstract of this paper[1] but I did see the unpublished original version in the Health Department archives whilst I was Chief Medical Officer on Montserrat from late 1998 to late 2000.

My first comment is that this survey of schoolchildren was carried out in February 1998 and yet it has only now been published in a scientific journal more than 5 years later. This is of some relevance since the highlights of the paper published in the BMJ on 12 April 2003 [2] comment that since the time of the first eruption in 1995 the children “have had an excess of respiratory illness” and that “few were receiving recommended appropriate treatment”. This statement is misleading. It may well have been true up until 1998 but it is certainly not true for the period beyond that time. The reality of children more heavily exposed to heavy ash falls experiencing more wheeze and asthma than those less exposed has been convincingly demonstrated in the paper. However most of the children living on Montserrat since 1998 have been in the north of the island and only intermittently exposed to relatively lighter falls of ash.

My own clinical experience and that of visiting paediatricians is that the prevalence of asthma and asthma like symptoms is no higher than other parts of the Caribbean and may even be lower. A survey carried out by the Health Department of resident children in June 2000 [3] found the prevalence of “wheeze ever” in all schoolchildren to be 22.7% (compared with 27.7% in all children in the 1998 survey). This survey also found the prevalence of “asthma ever” to be 13.8% compared with 9.8% in the 1998 survey. The 2000 survey found no association with exposure to higher ash levels but it must be recognised that in 2000 very few children were exposed to anything like the levels experienced between 1995 and 1998.The treatment that has been given to children experiencing asthma has been along conventional lines as recommended by paediatricians in the United Kingdom.

Further evidence of the lack of any continuing serious adverse effects of volcanic ash on respiratory health comes from a one year survey of all clinic attendances by all age groups on Montserrat during 1999.. This survey found no correlation between weekly clinic attendances for respiratory symptoms and episodes of ash venting or increased ground ash levels. A further study by the Institute of Occupational Health in Edinburgh [4] carried out in October 2000 found a prevalence of asthma of 8.1% and of chronic bronchitis of 6.7% in a group of 421 workers on Montserrat occupationally exposed to high levels of ash. A subsequent survey of 440 Montserratians relocated to the United Kingdom [5] found a prevalence of 14.2% for asthma and 14.0% for chronic bronchitis.

My second and most important comment is that by far the most important adverse effects of the volcanic eruptions relate to the social and economic disruption and its effect on the life and health of the people. In my paper in the West Indian Medical Journal [3] I have described a change in population demographics with a fall in the productive group and a rise in more dependent people, loss of older female family providers, more elderly people becoming dependant on the state, increases in anxiety and depression in the elderly, changes in the diet and increasing obesity in children and increases in domestic violence.

One of my concerns whilst on Montserrat was that most of the academic input following the disaster was put into vulcanology and respiratory health. Some valuable findings have come out of this work but no formal academic input was made into other more serious matters, especially on the health side.

Fortunately the outstanding health problems of Montserat have been addressed by the health department with the help of the UK Department for International Development and the Pan American Health Organisation but much remains to be done. The importance of this was dramatically emphasised with the reports of a massive dome collapse on 12/13th July and ash venting which uncharacteristically smothered the inhabited north of the island. Such a big eruption could easily demoralise some of those not already traumatised. However we can expect the resilience of the remaining population of around 4500 people to carry them through yet again in spite of all the social and economic disruption which has had a far more profound influence on their health than the purely physical effect of the ash.

References

(1) L Forbes, D Jarvis, J Potts, and P J Baxter. Volcanic ash and respiratory symptoms in children on the island of Montserrat, British West Indies. Occup Environ Med 2003;60:207-211.

(2) BMJ family highlights. Inhaling volcanic ash effects breathing. BMJ2003;326:785.

(3) Avery JG The Aftermath of a Disaster. Recovery Following the Volcanic Eruptions in Montserrat, West Indies. West Indian Medical Journal; in press.

(4) Cowie HA, Searl A, Ritchie PJ, Graham MK, Swales C et al. A health Survey of Workers on the Island of Montserrat. Research Report.TM/02/02. Edinburgh: Institute of Occupational Medicine; 2002

(5) Cowie HA, Searl A, Ritchie PJ, Graham MK, Hutchison PA, Pilkington A. A Health Survey of Montserratians Relocated to the United Kingdom. Research Report TM 01/07. Edinburgh: Institute of Occupational Medicine; 2001.

Response to Swaen et al.

Authors Craig Steinmaus1, 2 Allan H Smith1 Martyn T Smith1

Authors affiliations 1. School of Public Health, University of California, Berkeley, University Hall, Berkeley, CA 94720-7360, USA 2. Office of Environmental Health Hazard Assessment, California Environmental Protection Agency, 1515 Clay St., Oakland, CA 94612

Corresponding author Craig Steinmaus, School of Public Health, University of California, Berkeley, University Hall, Berkeley, CA 94720-7360, USA e-mail: craigs@berkeley.edu

Sir, The differences in methods between our meta-analysis and that of Swaen et al. did not “vastly alter” our most important finding or change our overall conclusion.1,2 Our major conclusion was that evidence of an association between benzene and non-Hodgkin lymphoma (NHL) could be found when analyses were focused on results from highly exposed workers and were appropriately adjusted for the healthy worker effect. In their analysis of high exposure benzene studies, Swaen et al. implemented a series of differences in the data used from the studies compared to our own. But despite the fact that every single one of their major changes resulted in a lowering of the summary relative risk, Swaen et al. also found a statistically significant elevated relative risk in the high exposure studies (RR = 1.33 (95% CI, 1.02-1.74)), just as we did. Even after they adjusted for heterogeneity, the relative risk remained statistically significant if correctly estimated. The one-sided p-value after this adjustment can be estimated from their confidence interval to be 0.03. Since our a priori hypothesis was that benzene increases, not decreases, the risk of NHL, a one-tailed p-value is clearly most appropriate here.

The Swaen et al. use of the all-cancer standardized mortality ratio (SMR) to adjust for the healthy worker effect assumes that benzene or any of the other agents that the benzene-exposed workers are exposed to will not cause any other cancer type. However, benzene is a well known cause of leukemia and risks of this cancer were elevated in many of the studies used in our meta-analyses. Relative risks of other cancers such as lung cancer and mesothelioma were also elevated in some of the studies, probably due to co-exposures like asbestos that can commonly occur with benzene. Because of these increases in other cancers, the use of the all- cancer SMR probably biased the Swaen et al. summary relative risks towards the null. Without this bias, the Swaen et al. summary relative risks would have been higher than they reported and even more similar to our results than they already are. In any case, as we noted above, using different data and different methods, Swaen et al. have produced additional evidence that benzene increases the overall risk of non-Hodgkin lymphoma in the available studies to date in a manner which is unlikely to be due to chance.

References 1. Steinmaus C, Smith AH, Jones RM, Smith MT. Meta-analysis of benzene exposure and non-Hodgkin lymphoma: biases could mask an important association. Occup Environ Med 2008; 65:371-8. 2. Swaen GMH, Tsai SP, Burns C. Meta-analysis on benzene exposure and non Hodgkin lymphoma (Letter to Editor). Occup Environ Med:TBD

Copyright The Corresponding Author has the right to grant on behalf of all authors and does grant on behalf of all authors, an exclusive license (or non- exclusive for government employees) on a worldwide basis to the BMJ Publishing Group Ltd and its Licensees to permit this article to be published in Occupational and Environmental Medicine editions and any other BMJPGL products to exploit all subsidiary rights, as set out in our license.

Dear Editor

Quoting both dictionary definitions and statuory requirements, Koh and Aw's education article [1] limits the definition of occupational "health surveillance" to the detection of adverse health effects resulting from occupational exposures. In doing so, they exclude international and national requirements for occupational health and medical surveillance to assess fitness for work.

Looking at the hazard of ionizing radiation, international recommendations,[2] European Directives [3] and UK National Legislation [4] all identify a requirement for surveillance where the primary purpose is an assessment of the individual's fitness for post. Similarly, in considering surveillance of divers, a key element of requirements is an assessment of fitness for work. On a more general level, both in the public and in the occupational setting systems of health surveillance exist for drivers where it is clearly nonsense to suggest that this is aimed at the detection of adverse effects resulting from time behind the wheel. It is therefore suggested that the authors' conclusion needs to be expanded to identify a requirement for periodic examination of individuals, not only to detect reversible ill health, but also to assess fitness for work.

References

(1) Koh D, Aw T-C. Surveillance in occupational health. Occup Environ Med 2003;60:705-710

(2) Recommendations of the International Commission on Radiation Protection publication 60: 1992

(3) Basic safety standards for the health protection of the general public and workers against the dangers of ionising radiation European Union Counsel directive 1996/29/EURATOM 13th May 1996

(4) The Ionising Radiations Regulations 1999 (UK statutory instrument).