Epidemiologic Perspectives & Innovations - Latest Comments

Response to Erren and Morfeld, 2011

Sally Hutchings — 2012-01-13T19:31:09Z

We have read the paper by Erren and Morfeld (2011) [1] with interest and offer the following comments on the concerns expressed by them about our work estimating the burden of occupational cancer in Britain [2]. We agree with Erren and Morfeld that burden of disease studies inform public health decision making by providing useful indicators of the contribution of different risk factors and indeed the results from our study are already being used for this purpose.
(i) Causality
Burden of disease studies always face the key issue of which diseases and hazards to include. In our study, a pragmatic decision, after discussion at one of the three international workshops held during the project, was to include all occupationally-related carcinogens and occupational circumstances defined by the International Agency for Research on Cancer (IARC) as group 1 (definite human carcinogen i.e. sufficient evidence of carcinogenicity in humans, causality established) and 2A (probable human carcinogen i.e. limited evidence of carcinogenicity in humans, causality credible but bias and confounding cannot be ruled out, and sufficient evidence of carcinogenicity in animals); these classifications are made following review and assessment of all available evidence of carcinogenicity by an expert working group and are respected worldwide. A supplementary table in our BJC paper [2] gives results for IARC group 1 carcinogens only and we discuss the fact that omission of shift (night) work and breast cancer (classified as group 2A) greatly reduces the overall burden of occupational cancer for women. However, our results, following on from the IARC classification, have increased the awareness of and interest in breast cancer and shift work resulting in more research both in the UK and elsewhere to investigate the nature of the risk e.g. from different shift work patterns; this will contribute to development of optimum shift work patterns to reduce risk.
(ii) Methodological issues
We agree that the methods may be subject to biases and uncertainty and that interpretation of results needs to take these into account. We included a table of biases in one of our papers and the likely impact these would have [3]. We are currently carrying out sensitivity analyses of different sources of bias on our results and expect to publish these soon. In response to Erren and Morfeld¿s particular points:
Levin¿s equation
We are aware of the well documented biases that may result from using Levin¿s estimator for the attributable fraction with adjusted relative risks. For Great Britain, population based estimates of exposed proportions amongst cases that would allow the use of Miettinen¿s AF estimator with adjusted relative risk estimates were rarely, if ever, available, so that using Levin¿s estimator which requires estimates of exposed proportions in the population as a whole was the only currently available option. We have investigated the size and direction of the bias that this introduces into our estimates of AF in practice, based on the range of proportions exposed and relative risks used in our study. If adjusted relative risks are lower than unadjusted, the bias in the AF estimate is downwards, i.e. AFs are underestimated, and vice versa. The relative (%) bias is consistently slightly less than the % difference between the (observed) adjusted RR (RRa) and unknown unadjusted RR (RRu). So for example if RRa/RRu = 0.9 [(RRa-RRu)/RRu=10%], the mean bias across all our estimates would be 9.8%, if RRa/RRu = 0.5 mean bias = -48.4%, etc. Our results indicate that this source of bias is in general small compared with other sources of bias, for example from assumptions about cancer latency and staff turnover and the effect on the estimates of numbers ever exposed, the absence of estimates of the proportion in the workplace exposed where CAREX data was unavailable, and the general scarcity of exposure level measurement data and dose response relative risk estimates [4].
We emphasise in all publications that the results are useful for assessing relative contributions to the cancer burden of the different occupational carcinogens and work in different industry sectors, given that all estimates are subject to some, generally similar, magnitude and direction of bias.
AF estimation based on broad definition of exposure
Introducing bias by collapsing categories as described in the discussions of broad definitions of exposure was not an issue in this study. However categorising industry sectors into broad categories regarding overall `higher¿ and `lower¿ exposures is indeed a limitation of our study. Again this was a pragmatic decision to address data limitations and is discussed in our paper [2]. Although for many carcinogens some dose-response risk estimates may be available there is a paucity of reliable British data on which to estimate the proportion exposed at different levels between and within industry sectors. We have been careful to use estimates of relative risk from studies that were conducted in populations where exposure levels are representative of the level of risk to which British workers are likely to have been exposed. In our extension of the methodology for predicting the future burden under different intervention scenarios we have generally expanded the categories to four [5].
Non-additivity of AFs
As we say in our earlier paper, multiple exposures and other non-occupational risk factors need to be considered when combining the AFs for different risk factors [3]. Cancer is a multifactorial and multistage disease that may not be due to any single sufficient cause but rather a sequence of `hits¿ over a life course. For example, smoking alone may not be sufficient to cause lung cancer and those who get it are likely to have been exposed to several lung carcinogens and possess other characteristics such as some form of inherited susceptibility. The mathematical implication of this is that the sum of attributable fractions for several exposures may be greater than 100%, with the amount exceeding 100% being partly due to synergistic interactions among the risk factors [6].
Two separate issues are included here, namely the bias introduced when combining the AFs for disjoint (non-overlapping) exposures, and the problem of allocating attributable fractions between competing risks when the overall AF estimate may exceed 100%.
Upward bias is introduced from directly summing marginal AFs for disjoint exposures. This bias is reduced, although not eliminated, if the AFs are combined using a product sum [7,4]. We have estimated the size of this bias and it is again small compared to the other potential sources of bias that we have identified above.
As we were only considering occupational exposures and not attempting to identify all contributing carcinogenic risks, for no cancers did our combined estimates of attributable fraction approach 100%. Therefore the necessity to adopt a procedure to allocate synergistic interaction effects between competing exposures did not arise.
Excess deaths versus premature deaths
We agree of course that death is inevitable and that burden of disease estimates per se should not be interpreted strictly as indicating that removal of the exposure will reduce permanently the annual number of deaths attributed to a risk factor [8]. The UK Committee on the Medical Effects of Air Pollutants in their report on the mortality effects of long-term exposure to particulate air pollution suggest that attributable burden in terms of deaths should be considered as the number of excess deaths together with their associated loss of life [9]. They use life table approaches in their estimation. However, we have also used our approach to estimate disability-adjusted life-years (DALY) which consist of years of life lost through death and years of life lived with a disability. We will be publishing a paper reporting this aspect of our study in the future.
In Summary:
We feel that the estimation of attributable disease burden is an important tool in public health for informing risk reduction. We would encourage decision makers to consider all the summary measures studies such as ours provide i.e. disease/hazard risk estimates, proportions of the population exposed, attributable fractions, attributable numbers of deaths and incidence and DALYs, when developing their risk reduction strategies and to take into account biases and uncertainties where possible.
Full details of all the data sources, justification for choice of data and the results of our study will be available shortly in a dedicated supplement of the British Journal of Cancer (Under review).
References
1. Erren C and Morfeld P. Attributing the burden of cancer at work: three areas of concern when examining the example of shift-work. Epidemiologic Perspectives and Innovations 2011, 8:4.
2. Rushton L, Bagga S, Bevan R, Brown TP, Cherrie JW, Holmes P, Fortunato L, Slack R. Occupation and cancer in Britain. B J Cancer 2010, 102: 1428¿1437
3. Rushton L, Hutchings S, Brown TB. The burden of cancer at work; first steps to prevention. Occup Environ Med 2008, 65: 789-800
4. Hutchings S and Rushton L. The burden of occupational cancer in Britain: statistical methodology. B J Cancer (suppl), in press.
5. Hutchings S and Rushton L. Towards risk reduction: predicting the future burden of occupational cancer. American J Epidemiology 2011, 173: 1069-1077.
6. Vineis P and Kriebel D. Causal models in epidemiology: past inheritance and genetic future. Environ Health Global Access Science Source 2006, 5:21
7. Steenland K and Armstrong B. An overview of methods for calculating the burden of disease due to specific risk factors. Epidemiology 2006, 17: 512-519
8. Brunekreef B, Miller BG and Hurley JF. The brave new world of lives sacrificed and saved, deaths attributed and avoided. Epidemiology 2007, 18: 785-788.
9. Committee on the Medical Effects of Air Pollutants. The mortality effects of long-term exposure to particulate air pollution in the United Kingdom. COMEAP, 2010 [http://comeap.org.uk/images/stories/Documents/Reports/]

The Stratify macro has been updated and enhanced

Klaus Rostgaard — 2010-11-19T04:05:39Z

Dear reader,

In the fall of 2010 I updated and enhanced the stratify macro substantially.

Most of the things that appear as post-processing in this paper is now performed by default internally in the macro. Also the BRTF statement has been replaced by the SRTF statement which has exactly the same syntax, but is more general. Most examples in the paper have to be modified slightly to work in the same way (often just the addition of COMPLETE=no as an option). These changes have been made in the textfile containing the macro and sample code. The enhancements made have made the macro (relatively) more useful for Cox regression, which can now be performed directly on output data from the stratify macro. Also see my new suggestions for making a “period” time scale in the manual.

The updated macro is available in the same place as before on sourceforge.net.

Klaus Rostgaard
The author

a few clarifications

John Cologne — 2010-11-19T04:05:19Z

This excellent article by Turner, Dobson, and Pocock is highly welcomed and long overdue. A couple of points made in the article will be obvious to most statisticians, but might benefit from some clarification for persons with less sophisticated statistical training or experience.

First of all, one example is given where a null hypothesis of no effect could be rejected with two groups but not four. This is counter-intuitive to the statement elsewhere in the article that "dichotomies should be avoided". The reason is because it depends on the underlying, unobserved true effect. How many groups and where to place cutpoints depends heavily on the shape of the effect. I have encountered situations where it was possible for data with a strong linear relationship to demonstrate a significant two-group difference but not global heterogeneity with a large number of groups. Hence the conclusion by the authors that trend tests can sometimes be more powerful. An important question is when trend tests are more powerful: since this depends on the unknown underlying effect, who knows?!

In regards to that point, it is said that a trend test will be substantially more powerful when "the relationship between the risk factor and outcome appears to be monotonic". Naturally, if we test what we see appearing in the data, it will be a powerful test; indeed it will inflate the significance of the test. Unless purely for descriptive purposes, trend tests should be based on subject matter consideration, not on review of the data.

The fact that some case-control studies based quantiles on controls only may be due to the desire to base cutpoints on the population distribution of the risk factor, as the controls are more representative of the general population for a rare outcome and strong risk factor given the over-sampling of cases. However, there are instances, such as a counter-matched nested case control study, where basing cutpoints on the distribution of risk factor in the cases can be beneficial in terms of efficiency.

Finally, although the authors mention it elsewhere in their article, they do not include among their recommendations the need to report all categorizations assessed and analyzed, not just those whose results are reported. Thus, I would add recommendation #14: "Report and describe all categorizations attempted or analyzed, even if the results were rejected and not presented in the paper, and state why the chosen method was preferred". This will reveal dredging expeditions and allow readers to better assess the inferential merits of the reported results.

Re: Estimating uncertainty in observational studies of associations between continuous variables: Example of methylmercury and neuropsychological testing in children. Reply by M. Goodman, P. Mink and L. Barraj

Michael Goodman — 2007-12-06T19:49:26Z

We thank Drs. Budtz-Jørgensen, Keiding and Grandjean for their comments. The following is our response to the specific concerns raised in their letter.

1. … the paper rests on an apparent disagreement between the findings of epidemiological studies carried out in the Seychelles and the Faroe Islands. However, we have previously shown that the results of the Seychelles study are sufficiently variable to be in statistical agreement with a mercury-associated deficit on the Boston Naming Test reported from the Faroe Island.

RESPONSE: Systematic errors are unavoidable in observational epidemiology, and it is reasonable to assume that neither the Seychelles Child Development Study (SCDS) nor the Faroe Islands Study (FIS) are immune to imperfections of study design and implementation. For this reason it is only fair that our sensitivity analyses addressed uncertainty in both studies.

2. Goodman et al. could have reached the same conclusion, had they converted the cord blood regression coefficient from the Faroes study to the hair concentration scale (multiply by 5) for comparison with the regression coefficient of the Seychelles study. A combination of the two estimates would generate a statistically significant effect, as was also reported by Axelrad et al. based on a meta-analysis of the studies in New Zealand, Seychelles, and Faroes.

RESPONSE: Rescaling in the Axelrad (2007) paper did not change the interpretation of the Boston Naming Test result for the SCDS study [1]. Using the original scale, the β estimate was -0.012 with a standard error of 0.046; after rescaling, the corresponding estimate changed to -0.038 (SE 0.144). Performing a meta-analysis on the two studies does not eliminate, but merely hides, the disagreement between FIS and SCDS results. The New Zealand study did not use BNT.

3. The analyses of the Seychelles and the Faroe Island data have included a large number of covariates. The mercury effect estimate originally reported from the Faroes changed only negligibly by including a large number of additional covariates including many of those Goodman et al. consider important.

RESPONSE: We agree that the impact of unaccounted confounding alone may be modest; this was confirmed by our sensitivity analyses. However, as shown in Figures 1 and 2 in our paper, when combined with other modest sources of bias the overall error may be substantial.

4. The analyses carried out by Goodman et al. fail to take into account the effects of the covariates already adjusted for, and the calculations erroneously indicate that unbiased effect estimation can be achieved without knowing the relationship between the confounders present and the unmeasured confounder.

RESPONSE: We used adjusted effect estimates in our sensitivity analyses. Our paper does not indicate that that unbiased effect estimation can be achieved without knowing the relationship between the confounders present and the unmeasured confounder. Unfortunately, we did not have information on relationship between the confounders present and the unmeasured confounder. This particular caveat of our sensitivity analyses is discussed in the article along with other limitations.

5. The authors further assume that the unmeasured confounder has an unrealistically high correlation with both exposure and outcome variable. Assumptions on information bias and selection bias are also extreme.

RESPONSE: The differences in exposure levels between participants and non-participants in the FIS have been reported [2, 3] and, in fact, exceed the differences assumed in our selection bias simulation. The reported participation rate in the SCDS also falls within the proposed scenarios [4]. We demonstrated the potential effect of confounding by home environment and the need for a comprehensive parental IQ evaluation in an earlier publication [5]. The correlation coefficients between potential confounders and exposure are similar to those reported in the FIS. The potential misclassification due to fatigue, timing and sequencing of testing and lack of adequate blinding also finds support in the literature [6, 7].

6. Preliminary data from the Seychelles suggest that adjustment for beneficial effects of fish intake in that population will also result in mercury-associated deficits becoming statistically significant, in accordance with the findings from the Faroes.

RESPONSE: The relevance of the abstract by Strain et al (2007) is unclear as it does not appear to examine the BNT results [8]. We are pleased, however, that Strain and colleagues felt it was necessary to examine uncertainty associated with previously unaccounted confounding.

In conclusion, we would like to re-emphasize that our sensitivity analyses aimed to estimate the potential systematic error for each study and in either direction. We are well aware that sensitivity analyses that are based on assumptions may be less informative than those based on real data. Nevertheless, in the absence of sensitivity analyses, one implicitly assumes that systematic error had no effect on the study results, an assumption that is even more difficult to defend. We hope that the methods of our sensitivity analyses will prove informative and helpful to researchers who wish to examine uncertainty in their data or in published studies by other researchers. Whether or not our findings add to the “current understanding of developmental neurotoxicity caused by maternal methylmercury exposure” is, of course, a matter of opinion.

References

1. Axelrad DA, Bellinger DC, Ryan LM, Woodruff TJ: Dose-response relationship of prenatal mercury exposure and IQ: an integrative analysis of epidemiologic data. Environ Health Perspect 2007, 115:609-615.

2. Grandjean P, Weihe P, White RF, Debes F, Araki S, Yokoyama K, Murata K, Sorensen N, Dahl R, and Jorgensen PJ.: Cognitive deficit in 7-year-old children with prenatal exposure to methylmercury. Neurotoxicol Teratol 1997, 19:417-428.

3. Grandjean P, Weihe P: Neurobehavioral effects of intrauterine mercury exposure: potential sources of bias. Environ Res 1993, 61:176-183.

4. Marsh D, Clarkson TW, Myers GJ, Davidson PW, Cox C, Cernichiari E, Tanner MA, Lednar W, Shamlaye C, Choisy O, Hoareau C, Berlin M: The Seychelles study of fetal methylmercury exposure and child development: Introduction. Neurotoxicology 1995, 16:583-596.

5. Mink PJ, Goodman M, Barraj LM, Imrey H, Kelsh MA, Yager J: Evaluation of uncontrolled confounding in studies of environmental exposures and neurobehavioral testing in children. Epidemiology 2004, 15:385-393.

6. Baron I: Neuropsychological Evaluation of the Child. New York: Oxford University Press; 2004.

7. Sattler J: Assessment of Children: Cognitive Applications. 4th edn. San Diego: Jerome M. Sattler, Publisher, Inc.; 2001.

8. Strain J, Bonham M, Davidson P, Myers G, Thurston S, Clarkson T, Stokes-Riner A, Janciuras J, Sloane-Reeves J, Cernichiari E, et al: Long-chain polyunsaturated fatty acids and mercury. Presented at the International Conference on Fetal Programming and Developmental Toxicity; Faroe Islands. 2007

Second response by M. Goodman, L. Barraj, P. Mink and D. Flanders

Michael Goodman — 2007-12-06T19:36:36Z

It is not correct that we “assumed a correlation of 0.8 between an unmeasured confounder and the BNT response.” Rather we assumed a range of correlations with a minimum of 0.2 and a maximum of 0.8. Budtz-Jorgensen and colleagues suggest that unaccounted confounding did not affect their study results, thereby offering an assumption of their own. We accepted this assumption and re-ran the sensitivity analyses to correct only for information and selection bias. The results were as follows.

For the Faroe Islands Study (FIS) after adjusting for information and selection bias the slope (SE) changed from -0.0190 (0.0063) as originally reported by the FIS group to -0.0022 (0.0392). As a reminder, adjustment for selection, information and confounding bias in our paper resulted in a corrected FIS slope of -0.0024 (0.0439). For the Seychelles Child Development Study (SCDS) the observed slope was -0.0120 (0.0460), adjustment for information and selection bias changed the result to -0.0122 (0.2000). In our paper, further correction of SCDS results for confounding produced a slope of -0.0132 with a SE of 0.2240.

In summary, even if one were to argue that the effect of unaccounted confounding should be ignored, it is important to remember that the overall uncertainty associated with systematic error may be a result of bias from multiple sources. Thus, even in the absence of any unaccounted confounding, our conclusions remain essentially the same.

rejoinder

Esben Budtz-Jorgensen — 2007-12-06T19:36:11Z

Aurthors: Esben Budtz-Jørgensen and Niels Keiding (Department of Biostatistics, University of Copenhagen, Denmark)

Philippe Grandjean (University of Southern Denmark, Odense, Denmark; and Harvard School of Public Health, Boston, MA, USA)

As a rejoinder to Goodman et al.'s response, we would agree that sensitivity analyses can be useful when evaluating evidence from observational studies. However, such calculations are informative only if based on realistic assumptions about the unknown parameters. Thus, an observed exposure-response relationship can always be removed by postulating the presence of a strong unmeasured confounder. Correlations between the confounder and the exposure and response parameters should therefore be realistic and based on available evidence. In their analysis of the Faroese data, Goodman et al. assume a correlation of 0.8 between an unmeasured confounder and the BNT response. Accordingly, the confounder would explain 64% of the variation of this outcome. This assumption is extreme. In our recent publication (1), we included an extended set of 20 potential confounders, but, together with mercury exposure, they accounted for less than 24% of the variation. In their response, Goodman et al. fail to comment on their misleading assumption. Rather than raising questions on the validity of the Faroes results, their study suggests that unrealistic assumptions are required to explain away the significant impacts of developmental methylmercury exposure.

References

1.Budtz-Jørgensen E, Keiding N, Grandjean P, Weihe P: Confounder selection in environmental epidemiology: Assessment of health effects of prenatal mercury exposure. Ann Epidemiol 2007, 17: 27-35.

Extreme assumptions are unnecessary

Esben Budtz-Jorgensen — 2007-11-14T22:37:24Z

Authors: Esben Budtz-Jørgensen and Niels Keiding (Department of Biostatistics, University of Copenhagen, Denmark)

Philippe Grandjean (University of Southern Denmark, Odense, Denmark; and Harvard School of Public Health, Boston, MA, USA)

The paper by Goodman et al. (1) aims at modeling the impact of extreme uncertainties on the results of an observational study, in this case the risk of developmental neurotoxicity associated with maternal dietary exposure to methylmercury during pregnancy. Thus, the paper rests on an apparent disagreement between the findings of epidemiological studies carried out in the Seychelles and the Faroe Islands. However, we have previously shown that the results of the Seychelles study are sufficiently variable to be in statistical agreement with a mercury-associated deficit on the Boston Naming Test reported from the Faroe Islands (2). Goodman et al. could have reached the same conclusion, had they converted the cord blood regression coefficient from the Faroes study to the hair concentration scale (multiply by 5) for comparison with the regression coefficient of the Seychelles study. A combination of the two estimates would generate a statistically significant effect, as was also reported by Axelrad et al. (3) based on a meta-analysis of the studies in New Zealand, Seychelles, and Faroes.

The analyses of the Seychelles and the Faroe Island data have included a large number of covariates. The mercury effect estimate originally reported from the Faroes (4) changed only negligibly by including a large number of additional covariates (5,6) including many of those Goodman et al. consider important. The analyses carried out by Goodman et al. fail to take into account the effects of the covariates already adjusted for, and the calculations erroneously indicate that an unbiased effect estimation can be achieved without knowing the relationship between the confounders present and the unmeasured confounder. The authors further assume that the unmeasured confounder has an unrealistically high correlation with both exposure and outcome variable. It is no surprise that the result of an epidemiological study is sensitive to assumptions about such a very strong confounder. Assumptions on information bias and selection bias are also extreme.

Recent evidence suggests that the previously published analyses of the data may have underestimated the effect of mercury exposure. We have examined the confounding effect from beneficial influences of fish nutrients and found that adjustment for maternal fish intake during pregnancy leads to an increase in the estimated mercury toxicity (7). Preliminary data from the Seychelles suggest that adjustment for beneficial effects of fish intake in that population will also result in mercury-associated deficits becoming statistically significant (8), in accordance with the findings from the Faroes. We have previously argued that the apparent difference between population studies in New Zealand, Seychelles, and Faroes, is likely due to uncertainties, with little reason for controversy (9). This was confirmed by the meta-analysis of Axelrad et al. (3).

Adjustment for imprecision in covariates and the confounding effects of fish intake would likely make the studies even more similar and result in stronger effect estimates.

The calculations presented by Goodman et al. (1) are therefore of little relevance to our current understanding of developmental neurotoxicity caused by maternal methylmercury exposure.

Email: Esben Budtz-Jørgensen* - E.Budtz-Joergensen@biostat.ku.dk ; Niels Keiding - nk@biostat.ku.dk; Philippe Grandjean - PGrandjean@health.sdu.dk.

* Corresponding author

References

1.Goodman M, Barraj LM, Mink PJ, Britton NL, Yager JW, Flanders WD, Kelsh MA: Estimating uncertainty in observational studies of associations between continuous variables: example of methylmercury and neuropsychological testing in children. Epidemiol Perspect Innov 2007, 4:9

2.Keiding N, Budtz-Jørgensen E, Grandjean P: Prenatal methylmercury exposure in the Seychelles (letter). Lancet 2003, 362: 664-5.

3.Axelrad DA, Bellinger DC, Ryan LM, Woodruff TJ: Dose-response relationship of prenatal mercury exposure and IQ: An integrative analysis of epidemiological data. Environ Health Perspect 2007, 115: 609-15.

4.Grandjean P, Weihe P, White RF, Debes F, Araki S, Yokoyama K, Murata K, Sørensen N, Dahl R, Jørgensen PJ: Cognitive deficit in 7-year-old children with prenatal exposure to methylmercury. Neurotoxicol Teratol 1997, 19: 417-28.

5.Budtz-Jørgensen E, Keiding N, Grandjean P, Weihe P: Confounder selection in environmental epidemiology: Assessment of health effects of prenatal mercury exposure. Ann Epidemiol 2007, 17: 27-35.

6.Choi AL, Budtz-Jørgensen E, Jørgensen PJ, Steuerwald U, Debes F, Weihe P, Grandjean P: Selenium as a potential protective factor against mercury developmental neurotoxicity. Environ Res 2007 (epub).

7.Budtz-Jørgensen E, Grandjean P, Weihe P: Separation of risks and benefits of seafood intake. Environ Health Perspect 2007, 115: 323-7.

8.Strain JJ, Bonham MP, Davidson PW, Myers GJ, Thurston SW, Clarkson TW, Stokes-Riner A, Janciuras J, Sloane-Reeves J, Cernichiari E, Shamlaye CF, Duffy EM, Robson PJ, Wallace JMW. Long-chain polyunsaturated fatty acids and mercury (abstract 39). Presented at International Conference on Fetal Programming and Developmental Toxicity, Faroe Islands, 20-24 May, 2007 [http://www.pptox.dk]

9.Grandjean P. Mercury Risks: Controversy or just uncertainty? Publ Health Rep 1999, 114: 512-5.

Klemper's Biased Judgement

Stanley Gage — 2006-11-17T21:40:37Z

Klemper, in extrapolating the results of his study, argues in light of his results, that a 90 day antibiotic treatment does not provide any noticalbe improvement in patient health and, therefore, extended antibiotic treatment is of no value.

The conclusion fails to take notice of the fact that an equally vaild argument based on this study outcome would be that a 90 day antibiotic treatment is insufficient to provide any improvement in patient health and that longer duration antibiotic treament may be necesary to reduce or eliminate the efects of desseminatd Lyme.

The real upshot of the issue of the results as published is to question that they were published at all. Publishing bad science is worse than publishing nothing. In the case of the Klemper article the author/researcher obviously approaced the issue with the hypothesis that desseminated or chroninc Lyme does not exist. By fabricating a poorly constructed experiment and then deriving biased and incomplete conclusions and extensions of those conclusion he does the medical and scientific community a significant disservice.

It is unclear in the information presented if the original Klemper study was peer reviewed prior to publication but it is clear that such poorly conducted research does not belong in the respected journals of medical literature.

Thanks for publishing the exellent article, Generalizability in two clinical trials of Lyme disease

Marisa Battilana — 2006-11-17T21:33:17Z

Thanks you for publishing Dr. Cameron's exellent article, Generalizability in two clinical trials of Lyme disease.

In my nearly two years as a volunteer in the Lyme community, I have met over 2,000 people who either have been personally affected by late stage Lyme disease or who know someone who has. The majority of the folks affected benefited greatly from extended treatment with antibiotics, most for more than just a few months. Many found out the hard way that they needed more than short term treatment: when taken off antibiotics, they relapsed within a short time. And, when they resumed treatment, they saw significant improvement.

Articles like Dr. Cameron's are long overdue. Thank you.

Marisa Battilana

NIH Headline Still Stands - Long Enough?

Phyllis Mervine — 2006-11-17T21:32:39Z

Five years after the original flawed description of the New England Medical Center [aka Klempner] clinical trial was posted on NIH websites, thanks are due to Dr. Cameron for providing compelling evidence why it should be changed to “Chronic Lyme Disease Study Shows 3 Months of Antibiotic Treatment Inadequate.”

As one of the patient representatives on the Advisory Panel for the NIH Clinical Trials, I so requested our NIH Lyme program officer Phil Baker in September 2001. Referring to other Panel members who had discussed the limited applicability of this treatment trial, I wrote: “We all know that the NEMC study was not designed to prove, could not prove and did not prove what your current headline suggests that it did prove. Patients are already being affected by the biased reporting of the study results. It would be a serious ethical lapse to allow the biased headline to remain unaltered while doctors and insurance companies use it to justify denials of treatment to seriously ill patients.”

Dr. Baker did not reply and the headline still stands. Five years later patients are still being denied treatment on this basis. Have we suffered enough yet?

NIH News Release: Chronic Lyme Disease Symptoms Not Helped by Intensive Antibiotic Treatment, 12 June 2001

http://www.nih.gov/news/pr/jun2001/niaid-12.htm

NIH NIAID: Clinical Alert: Chronic Lyme Disease Symptoms Not Helped by Intensive Antibiotic Treatment, 12 Jun 01

http://www.nlm.nih.gov/databases/alerts/lyme.html