Rapid Responses to:
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Rapid Responses: Rapid Responses published:
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Splenic infarcts as a manifestation of fever of unknown origin (FUO)
- Daniel Cuevas-Ramos, Virginia Pascual-Ramos, and Miguel Villalobos-Gollás (1 March 2004)
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Claims of no harm: a call for improvement of medical reporting in medical journals
- Michal R Pijak, Frantisek Gazdik (1 March 2004)
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Absence of evidence and the importance of confidence intervals
- Douglas G Altman, J Martin Bland (3 March 2004)
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Interpreting the epidemiologic evidence concerning environmental tobacco smoke and coronary heart disease
- Geoffrey C. Kabat, James E. Enstrom (5 March 2004)
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Re: Interpreting the epidemiologic evidence concerning environmental tobacco smoke and coronary heart disease
- Jon P. Krueger (6 March 2004)
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A Laymans View
- Robert Feal-Martinez (7 March 2004)
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Re: Re: Interpreting the epidemiologic evidence concerning environmental tobacco smoke and coronary heart disease
- Wiel M Maessen (8 March 2004)
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Re: Re: Interpreting the epidemiologic evidence concerning environmental tobacco smoke and coronary heart disease
- James W Austin (11 March 2004)
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Re: Re: Re: Interpreting the epidemiologic evidence concerning environmental tobacco smoke and coronary heart disease
- Adam Jacobs (13 March 2004)
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Secondary Motives....
- Michael J. McFadden (14 March 2004)
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UNRELIABILITY OF SCIENTIFIC PAPERS AS EVIDENCE
- Clifford G. Miller (16 April 2004)
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In response to Clifford Miller's opinions on medical science
- Jeffrey Mann (17 April 2004)
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Re: In response to Clifford Miller's opinions on medical science
- Clifford G. Miller (18 April 2004)
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Absence of evidence is not evidence of absence is a false statement
- Ron Law (11 August 2004)
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Re: Absence of evidence is not evidence of absence is a false statement
- John P Heptonstall (13 August 2004)
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Re: Absence of evidence is not evidence of absence is a false statement
- Clifford G. Miller (13 August 2004)
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Where do you get these people?
- Richard M Lindley (15 August 2004)
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Absence of evidence is not THE SAME AS evidence of absence is a TRUE statement
- Sam Lewis (15 August 2004)
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Chiasmus: entertaining and ambiguous
- Robert A. Da Prato (17 August 2004)
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Daniel Cuevas-Ramos, Resident of Internal Medicine Instituto Nacional de Ciencias Médicas y Nutrición, Virginia Pascual-Ramos, and Miguel Villalobos-Gollás
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Splenic infarcts as a manifestation of fever of unknown origin (FUO) We read and enjoyed Alderson?s editorial1 suggesting that ?Absence of evidence is not evidence of absence?, although not only applicable to statistical analysis but also as important just at the clinical level as it can become evident in the following patient studied by us. A 55 year old male patient was hospitalized for study because, during the last two months, he has been presenting intermittent fever as high as 40°C. We documented the presence of fever in the afternoon of every day, with chills, tremor, tachycardia, piloerection and diaphoresis, every day started at 19:00 to 20:00 hours and persist for 2 to 3 hours on average. We started only symptomatic treatment with acetaminophen but it did not work and the fever followed the same pattern. We took a careful history, including travel and occupational histories, sexual practices, dietary, exposures to animals or chemicals; we performed a detailed physical examination and reassessed the patient frequently but the fever was the unique manifestation. We approached the case as fever of unknown origin and a wide variety of diagnostic tests were practiced to him but every study was negative or normal. The initial diagnostic evaluation included: * Complete blood count, with differential and platelet count.
We also applied for erythrocyte sedimentation rate and the result was 110 millimeters per hour (mm/h). We found that in a review paper were reported elevations above 100 mm/h among 263 patients with FUO and 58 percent had malignancy, most commonly lymphoma, myeloma or metastatic colon cancer; and 25 percent had infections such as endocarditis, or inflammatory diseases like rheumatoid arthritis or giant cell arteritis2. Based on this information we complemented the evaluation with imaging of the head and lumbar puncture, protein electrophoresis, endosocopy and colonoscopy, transthoracic echocardiography, bone marrow aspiration with biopsy and a temporal artery biopsy. The results were not conclusive for any entity that could explain the fever. An exploratory laparoscopy with liver biopsy and splenectomy was the last diagnostic tool we decided to do, and the only finding was splenic infarcts in the histopathology report. As a result of the surgical findings, we search for conditions associated with peripheral embolism, for example, prothrombotic disorders or endocarditis with septic embolism, however they were also ruled out, and we ended the approaching of the patient?s studies with a transesophageal echocardiography whose result was also normal. After surgery and spleen resection the fever did not present again and, without any other treatment, the patient, until now, still remains asymptomatic. Despite extensive evaluation, in 10-15% of patients with FUO the diagnosis remains elusive3. In the case we are reporting it seems that we finally got a diagnosis and the patient is probably cured, but the evaluation was quite costly and time-consuming, and still with non- conclusive, only suggestive, evidence that the FUO was secondary to splenic infarcts. Which is in accord with Alderson?s conclusion that: ?We need to create a culture that is comfortable with estimating and discussing uncertainty?,1 however, not only relevant from the statistical point of view but also from the everyday clinical perspective. References: 1. Alderson, P. Editorial: Absence of evidence is not evidence of absence. BMJ 2004;328:476-477. 2. Zacharski LR, Kyle RA. Significance of extreme elevation of erythrocyte sedimentation rate. JAMA 1967; 202:264. 3. Davies GR. Fever of unknown origin. Clin Med 2001; 1:177 Authors: Daniel Cuevas-Ramos, MD, resident of Internal Medicine Virginia Pascual-Ramos, MD, consultant of Rheumatology and Internal Medicine Miguel Villalobos-Gollás, MD, resident of Surgery Instituto Nacional de Ciencias Médicas y Nutrición "Salvador Zubirán". Department of Internal Medicine. Calle Vasco de Quiroga # 15. Deleg. Tlalpan, CP 14000, México, D. F.
México.
Competing interests: None declared Editorial note
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Michal R Pijak, Department of Internal Medicine, Division of Clinical Immunology Slovak Medical University, Limbova 12, 833 03, Bratislava, Slovak Republic, Frantisek Gazdik
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EDITOR-Phil Alderson is rightly critical that researchers should improve precission and language in interpretation of non-significant results.(1) This issue, however, is not a new one. We are therefore surprised that this demand does not go for medical reporters as well. In fact, even a cursory review of recent BMJ medical reports reveals that inappropriate claims of no effect occur frequently. A typical example is given by the Scott Gotlieb´s report of results of a recent study published in Pediatrics.(2) It is stated, both in heading and in the body of this report, that there is "no connection", "no relation", "no link" between MMR vaccine and autism. Morover, the reporter failed to note study limitations and potential conflicts of interests. So the readers might be left with erroneous impression that the controversy relating to the risk of MMR vaccine is definitely resolved. A number of papers published recently criticized press coverage for exaggerating the benefits and minimizing the harms.(3-5) As pointed out by freelance journalist Ray Moynihan "A growing body of evidence suggests that too often medical reporting looks more like promotion than journalism."(5) It is therefore hard to believe that editors of BMJ, which is a leader in promotion of evidence based medicine, can tolerate such a poor quality of medical reporting. In closing, we would argue that it is time that a similar standards of publishing scientific informations in medical journals will be applied to both researchers and medical reporters. Michal R Pijak, consultant in rheumatology, allergy and clinical immunology, Frantisek Gazdik, associate professor of clinical immunology, Slovak Medical University, Institute of Preventive and Clinical Medicine,
Limbova 12, 833 03 Bratislava, Slovakia
1. Alderson P. Absence of evidence is not evidence of absence. BMJ 2004;328:476-7. 2. Gottlieb S. Study finds no connection between MMR vaccine and autism. BMJ 2004;328:421. 3. Cassels A, Hughes MA, Cole C, Mintzes B, Lexchin J, McCormack JP. Drugs in the news: an analysis of Canadian newspaper coverage of new prescription drugs. CMAJ 2003;168:1133-7. 4. Schwartz LM, Woloshin S. The media matter: a call for straightforward medical reporting. Ann Intern Med 2004;140:226-8. 5. Moynihan R. Making medical journalism healthier. Lancet 2003;361:2097-8. Competing interests: None declared |
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Douglas G Altman, Professor of Statistics in Medicine Cancer Research UK/NHS Centre for Statistics in Medicine, Oxford OX3 7LF, J Martin Bland
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Since our 1995 BMJ note[1] the title “Absence of evidence is not evidence of absence” has been used several times. We would like to record that the first medical publication with that title seems to have been that of Hartung et al in 1983[2] – we were not aware of it when writing our 1995 article. Phil Alderson revisits the difficulties associated with the interpretation of non-significant results. He suggests that one should never claim that there is “no effect” but rather that authors should recognise that their results are compatible with a range of possible findings: “researchers should be precise in their language and avoid the temptation to save words by reducing the summary of the study to such an extent that the correct meaning is lost.” Just so. Sadly, papers published in the same issue of the BMJ do not adhere to this good advice. Koivunen et al.[3] conclude from their trial that “adenoidectomy...is not effective...it cannot be recommended”, yet the 95% CI for the primary outcome (further episodes of otitis media) is compatible with about an 18% absolute risk reduction at 24 months. The clinically important difference sought was a 25% reduction. Kariminia et al.[4] state that “hands and knees exercise with pelvic rocking...did not reduce the incidence of persistent occiput posterior position at birth”; the 95% CI was from 1.8% reduction to 2.5% increased risk. This trial had over 2200 participants and sought a risk reduction of 2.5%. Marre et al.[5] conclude that “low dose ramipril...has no effect on cardiovascular and renal outcomes”; the RR of the combined endpoint was 0.97 (95% CI 0.85 to 1.11). The result was thus compatible with a 15% reduction as against the 20% that was deemed a priori to be clinically important. We think that confidence intervals are superior to P values for the reporting of the results of trials.[6] It should be borne in mind, however, that confidence intervals in general give a somewhat optimistic view of the uncertainly of a trial’s findings. They reflect only the uncertainty due to sampling variation, and only that part due to random allocation, not the variation which might arise because the patients in a trial are only a sample of the available population. They take no account of other issues such as failure to follow the protocol, non-random loss to follow up, and so on. True uncertainty is greater therefore than indicated by confidence intervals. Thus, for example, the observation by Karminia et al.[4] that “The confidence intervals show that at most the exercise might decrease the incidence of occiput posterior position by up to 1.8% or increase it by up to 2.4%” is too strong, even discounting the 5% chance of being outside the confidence interval by definition. While all these three trials had non-significant effects for the primary outcomes, none has unequivocally ruled out some benefit of the treatment being investigated although in no case was the prespecified clinically important treatment effect within the confidence interval. However, others may judge that a smaller benefit would be clinically useful. Even when a clinically useful effect has been ruled out, it is not justified to claim that there is no effect at all. Thus all of these papers use words that cannot be justified: “is not effective”, “did not reduce”, and “has no effect”. 1. Altman DG, Bland JM. Absence of evidence is not evidence of absence. BMJ 1995;311: 485. 2. Hartung J, Cottrell JE, Giffin JP. Absence of evidence is not evidence of absence. Anesthesiology 1983;58:298-300. 3. Koivunen P, Uhari M, Luotonen J, Kristo A, Raski R, Pokka T, Alho O-P. Adenoidectomy versus chemoprophylaxis and placebo for recurrent acute otitis media in children aged under 2 years: randomised controlled trial. BMJ 2004;328:487-90. 4. Kariminia A, Chamberlain ME, Keogh J, Shea A. Randomised controlled trial of effect of hands and knees posturing on incidence of occiput posterior position at birth. BMJ 2004;328:490-3. 5. Marre M, Lievre M, Chatellier G, Mann JF, Passa P, Menard J; DIABHYCAR Study Investigators. Effects of low dose ramipril on cardiovascular and renal outcomes in patients with type 2 diabetes and raised excretion of urinary albumin: randomised, double blind, placebo controlled trial (the DIABHYCAR study). BMJ 2004;328:495-9. 6. Gardner MJ, Altman DG. Confidence intervals rather than P values: estimation rather than hypothesis testing. BMJ 1986;292:746-50. Douglas G Altman, Cancer Research UK/NHS Centre for Statistics in Medicine, Oxford J Martin Bland, Dept. of Health Sciences, University of York Competing interests: None declared |
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Geoffrey C. Kabat, Epidemiologist New Rochelle, NY 10804, James E. Enstrom
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In his editorial “Absence of evidence is not evidence of absence,” Alderson provides clear and useful guidelines for interpreting and reporting the results of medical research.1 His concluding paragraph states that “considering results of a particular study in the context of all available research which considers the same question can increase statistical power, reduce uncertainty, and thus reduce the confusing reporting of underpowered studies.” We agree with Alderson that “such an approach might have clarified the implications” of our recent cohort study which focused on environmental tobacco smoke (ETS) and coronary heart disease (CHD) mortality.2 Indeed, this approach makes clear that our null study is similar in design to most other ETS cohort studies and that our results are statistically equivalent to the results of the vast majority of existing studies. Furthermore, our study has substantial statistical power and reduced uncertainty, since it is the second largest of about 25 ETS-CHD studies. Still, as we made clear in the paper, our results do not rule out a small effect. Unlike the situation in randomized clinical trials, where the independent variable is well defined, the independent variable (exposure) is not well defined in studies of ETS. Almost all studies have relied on spousal smoking history or self-reported qualitative estimates to define ETS exposure. More accurate measurements based on detailed personal monitoring indicate that nonsmokers have a mean exposure to ETS that is roughly equivalent to smoking 10 cigarettes per year.3,4 Thus, if one takes account of the totality of the evidence, one would expect the association of coronary heart disease mortality with passive smoking to be much weaker than the association with active smoking and consistent with our findings. Indeed, it would be at the limit of what epidemiologic studies can reliably detect. Alderson’s guidelines should be extended to address the uncritical quantitative summaries of the ETS-CHD studies, where many uncertainties are swept aside in order to attribute causal significance to an excess risk of about 25%. Meta-analyses of the studies have been done in a mechanical fashion without considering the quality or comparability of the results that are being combined.5,6 Use of Alderson’s guidelines should lead to a better understanding of the uncertainty associated with the weak epidemiologic evidence on passive smoking. 1. Alderson P. Absence of evidence is not evidence of absence. BMJ 2004;328:476-477. 2. Enstrom JE, Kabat GC. Environmental tobacco smoke and tobacco related mortality in a prospective study of Californians, 1960-98. BMJ 2003;326:1057-61. 3. Phillips K, Howard DA, Bentley MC, Alvan G. Measured exposures by personal monitoring for respirable suspended particles and environmental tobacco smoke of housewives and office workers resident in Bremen, Germany. Int Arch Occup Environ Health 1998;71:201-12. 4. Jenkins RA, Palausky A, Counts RW, Bayne CK, Dindal AB, Guerin MR. Exposure to environmental tobacco smoke in sixteen cities in the United States as determined by personal breathing zone air sampling. J Expos Anal Environ Epidemiol 1996;6:473-502. 5. Bailar JC. Passive smoking, coronary heart disease, and meta- analysis. N Engl J Med 1999;340:958-9. 6. Shapiro S. Meta-analysis/shmeta-analysis. Am J Epidemiol. 1994;140:771-8. Competing interests: As described in reference 2. |
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Jon P. Krueger, n/a n/a
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What Enstrom and Kabat don't mention is, we already have a good account of why some reviews conclude that secondhand smoke is harmful to health and others do not: author affiliation. Scientists affiliated with the tobacco industry, such as Enstrom and Kabat, tend to conclude that secondhand smoke is not harmful to health (1). Thus the problem here is not as Enstrom and Kabat claim the difficult evaluation of absence of evidence. Nor is it quality or comparability of results. Rather the problem here is a well funded campaign to pollute the science(2, 3). It is interesting that Enstrom and Kabat in their letter cite more research from tobacco industry affiliated scientists (4, 5). In 1994, the board of the Center for Indoor Air Research (CIAR) complimented and rewarded Max Eisenberg on his "accomplishment" in getting both (4, 5) out. (6) The CIAR is a tobacco industry front that also funded Enstrom and Kabat. I think the evidence for health effects of secondhand smoke speaks for itself. I also find the evidence for tobacco industry campaigns to pollute the science also speaks for itself. 1. Barnes DE, Bero LA. Why review articles on the health effects of passive smoking reach different conclusions. JAMA 1998;279(19):1566-70. 2. Samet JM, Burke TA. Turning science into junk: the tobacco industry and passive smoking. Am J Public Health 2001;91(11):1742-1744 3. Drope J, Chapman S. Tobacco industry efforts at discrediting scientific knowledge of environmental tobacco smoke: a review of internal industry documents. J Epidemiol Community Health 2001;55(8):588-94 4. Phillips K, Howard DA, Bentley MC, Alvan G. Measured exposures by personal monitoring for respirable suspended particles and environmental tobacco smoke of housewives and office workers resident in Bremen, Germany. Int Arch Occup Environ Health 1998;71:201-12. 5. Jenkins RA, Palausky A, Counts RW, Bayne CK, Dindal AB, Guerin MR. Exposure to environmental tobacco smoke in sixteen cities in the United States as determined by personal breathing zone air sampling. J Expos Anal Environ Epidemiol 1996;6:473-502. 6. http://legacy.library.ucsf.edu/tid/hcj82d00 Competing interests: None declared |
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Robert Feal-Martinez, Tenant/Publican The Carpenters Arms Motel. SN3 4ST
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I think it is important that I explain that I am a Motel owner with a pub. I am a life long non smoker, my father died of a smoking related illness and my personal view is that smokers play Russian Roulette with their lives. I have read lots of science over the last 2 years in my roll as The Secretary of a region of the British Institute of Innkeeping who support the voluntary charter on smoking in public places. I do not claim to be a scientist and having reviewed and hopefully understood the evidence, such as it is I have to say that the case put for ETS as a causal link to serious ill health is in my view non existant or at best scant. There are lots of 'smoke screens' erected such as the claim that the evaluation of the 39 year study was tobacco industry sponsored. As I understand it it was in the latter stages when health funding was stopped, when the results were not looking good for the Anti faction that sponsorship was sought and accepted. I think it is also slightly disengenuos to always intimate that science is flawed due to the sponsor. If that were the case then surely it is reasonable to criticise the WHO for acceptong funding for research and no smoking campaigns from the Phaumaceitical Industry who make many millions from anti smoking medicines. Obviously in a medical journal my views can be dismissed as irrelevant and I accept that, but I would like to finally say that to abuse science who ever is the culprit does a disservice to a nobel profession. What I have read of ETS science I have to conclude that the 'anti's' seem to be well ahead in this regard. Competing interests: None declared |
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Wiel M Maessen, Board member of Forces International Netherlands
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Jon Krueger claims to have no special interests in the area of tobacco control. But what about this interview with him that was published on the tobacco.org web site? Quote: I'm a software engineer in California. I became involved in tobacco control in 1992 as a member of a local smokefree coalition. We were trying to get a smokefree ordinance in our community. We did surveys, and there was strong support from both business owners and the public. We also had a clear health case for it.". Then, just pointing to the tobacco industry that they "pollute the science" is the standard way of response in the type of organisations that Mr. Krueger belongs to. These anti-tobacco lobbyists never mention the other industry that is polluting science as I showed in a previous posting here in response to Mr. Stanton Glantz' remarks on the Enstrom & Kabat study. "I think the evidence for health effects of secondhand smoke speaks for itself." doesn't really impress when knowing the background of Mr. Krueger. We are trying to reestablish real science again and not the kind of junk science that people like Mr. Krueger and his kind of kin tend to use.And that, sir, is a shame for all of us who still respect science as an instrument of knowledge – and not of dirty politics. Hiding yourself does not help your case, Mr. Krueger... Competing interests: None declared |
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James W Austin, None Retired 54703
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Mr. Krueger states, "It is interesting that Enstrom and Kabat in their letter cite more research from tobacco industry affiliated scientists (4, 5). In 1994, the board of the Center for Indoor Air Research (CIAR) complimented and rewarded Max Eisenberg on his "accomplishment" in getting both (4, 5) out. (6) The CIAR is a tobacco industry front that also funded Enstrom and Kabat." I think Mr. Krueger would be quite surprised to compare tobacco industry funded personal air monitoring studies, as he was referring to here, to a recent anti-tobacco industry funded study doing similar air monitoring. October 30, 2002, the American Cancer Society announced the results of this study (1), paid for by the Erie/Niagara Tobacco Free Coalition and conducted by people from the Roswell Park Cancer Institute and the American Cancer Society. Dr. Andrew Hyland of Roswell Park Cancer Institute, said, "[N]ow we have real evidence about how high the average amounts of secondhand smoke exposures can be for some workers in Erie and Niagara counties." Here is what they found: Bingo halls-940 nanograms of nicotine per eight-hour shift. Two local bars sponsoring "Marlboro Night"- 814. Stand-alone bars and taverns-539. Places with some smoking restrictions: Workers in bowling alleys-110. Bar areas of restaurants-80 Nonsmoking sections of restaurants that allow smoking in their bar areas-30. Restaurants with enclosed smoking areas-20. Where smoking is completely prohibited-No measurable exposure. Cigarette smokers inhale about 1 milligram of nicotine from every cigarette. (Martin Jarvis, published in the Journal of the National Cancer Institute, determined that the average nicotine intake is 1.31 milligrams per cigarette.) 8 hours exposure in the group most exposed amounted to less than 1/1,000 the nicotine a smoker gets from one cigarette. Therefore, it would take more than one thousand 8 hour shifts to 'smoke' one cigarette. That's almost 5 years. The inhale equivalent from the anti-tobacco funded study of one cigarette approximately every five years is far less than what the tobacco funded studies have shown, which have typically been reported as 6-10 cigarettes per year. Who knows, maybe the Erie/Niagara Tobacco Free Coalition, Roswell Park Cancer Institute, and the American Cancer Society are tobacco industry fronts. (1) http://roswell.tobaccodocuments.org/nic_study/media/Press_Release.htm Competing interests: None declared |
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Adam Jacobs, Director Dianthus Medical Limited, London SW19 3TZ
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I am intrigued by Wiel Maessen’s criticism of Jon Krueger’s links to an anti-tobacco organisation. Maessen is right to draw attention to the motives of those who claim that a body of research supports a particular position, but it is not clear to me what Krueger’s motives are supposed to be. Maessen seems to be suggesting that those who interpret the evidence on passive smoking to conclude that it is harmful to health do so because they belong to an anti-smoking organisation. Why would they join the organisation in the first place? Do anti-smoking groups offer large bribes to encourage people to join? If so, where does the money come from? Or is it possible that people such as Krueger join an anti-smoking group after they have already drawn their conclusions from the evidence on passive smoking and health? Perhaps Maessen could explain what the ulterior motives of the ‘anti- tobacco lobbyists’ are? Is there some mechanism whereby pretending that smoking is harmful, when it is in fact completely safe, would lead to great financial gain? In contrast, it is abundantly clear what motive the tobacco industry has for claiming that passive smoking is harmless. Competing interests: I have an evil master plan to take over the world. When my plan comes to fruition, I shall launch giant orbiting laser cannons into space, and I shall control the world from a hollowed-out volcano, where I shall amuse myself by throwing my enemies into a pool of piranhas. For obvious security-related reasons, I cannot reveal the exact nature of my plan. Suffice it to say, however, that banning smoking in public places is an essential part of it. |
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Michael J. McFadden, Writer Home 19104
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Adam Jacobs wrote: "...it is not clear to me what Krueger’s motives are supposed to be." in posing the question as to what the motives of Antismoking researchers would be other than the promotion of truth and good health. The main motivation that has driven most researchers in this area for the last 40 years has been the belief that smoking is an important cause of disease in smokers and the corollary belief that anything and any research that would serve to reduce the practice of smoking is perforce a good and positive thing. Unfortunately, I believe that this motivation has driven many researchers to design and produce research based on the deliberate aim of creating results that will reduce smoking rather than on the aim of simply discovering useful truth. The motivation is good, but the result may not be. Where I see this most clearly happening is in the realm of studies concerning secondary exposure to tobacco smoke. Thirty years ago, at the 1975 "3rd World Conference on Smoking and Health" chaired by Sir George Godber, the conclusion was reached that one of the most powerful weapons in reducing worldwide smoking would be to "foster an atmosphere where it was perceived that active smokers would injure those around them, especially their family and any infants or young children who would be exposed involuntarily to ETS." (Huber et al. Consumers Research Magazine. 04/92) At that time of course there was virtually nothing in the research to support this: Hirayama's study on Japanese wives was more than five years in the offing. I believe that it is the conclusion flowing from that conference through the Antismoking community that has driven many researchers to design, conduct, and interpret studies in such a way as to produce results consistent with the goal of pressuring smokers to quit or not to begin. Thus, when the focus of the overall Antismoking movement began to be on youth and how to discourage youth from taking up the habit in the 1980s, Antismoking researchers bemoaned the fact that young people were not really impressed with statistics pointing to their death at age 70 rather than age 80. In order to reach these youth, approaches were needed that would appeal to their more immediate concerns of money, social acceptance, sexuality, and appearance. Lo and behold... studies of questionable design and importance began to appear and be ballyhooed to the news media about smoking causing young women to wrinkle, young men to become impotent, and all young people to rush to give up smoking when cigarette taxes were raised. (It should not be overlooked that a side motivation with regard to taxes is that Antismoking groups usually pressure politicians to direct significant portions of such increased tobacco taxes to ... surprise... Antismoking groups.) If one looks at the results of studies done on secondary smoke and lung cancer one finds that relatively few of them achieve significant results, although a majority do tend to find insignificant trends toward a very small positive relationship for lifelong exposures without modern ventilation. However, the researchers conducting such studies are highly dependent in their professional lives on receiving research grants and being published in the mainstream literature. Positive results are more likely to be looked on with satisfaction by granting agencies devoted to the reduction of smoking and possibly more likely to be published in a literature with Antismoking beliefs, and thus there is an inherent background bias toward producing such results. I am not speaking of "faking" research, nor am I accusing researchers of conscious dishonesty. In pure science it has long been recognized that a great value should be attached to the "double-blind" approach in order to prevent unconscious or unintentional researcher bias from affecting outcomes. In the case of secondary smoke studies such bias is certainly not unconscious among most researchers in the field, men and women who strongly believe that results indicting secondary smoke will serve to save lives by overall reduction of smoking, and the intention of bias may well be overlooked simply because the bias is assumed to be not bias, but simply realism. I do not think I would be remiss in suggesting that the vast majority of researchers in this area go into any particular study with the belief from the start that there *is* an effect there... if only they can find and prove it. What has happened with disturbing frequency in recent years is the tendency of researchers to conduct a piece of research and then present the essentials of it at a meeting or conference with the strong and clear aim of having those results trumpeted by the press in order to advance such goals as public smoking bans. When the results come out in detail a year or two later, it is seen that the initial proclamations may well have been unfounded... but by then the media spotlight is elsewhere and the desired result of social engineering through media manipulation has been achieved. To note one recent example that may fall into such a category, there is the "Helena Heart Miracle" study by Drs. Sargent and Shepard. The heart attack rate in a small community was theoretically slashed in half purely as a result of the imposition of a widespread smoking ban. The implication that this effect was largely due to the reduction in secondary smoke exposure was made strongly in statements by such scientists as Richard Pasternak of Harvard who said "So when we have less people exposed to smoke as was the case in Helena it makes sense that the hospital admission rate will be decreased." and in a similar statement by Stanton Glantz of USC (a mechanical engineer who served as statistical consultant for this study), "This striking finding suggests that protecting people from the toxins in secondhand smoke not only makes life more pleasant -- it immediately starts saving lives" (UPI Science News. 04/01/03.) Stanton Glantz' associate, Cynthia Halett put it even more succinctly: "The bottom line is simple. Secondhand smoke kills." However, did the study actually show that? Or did it perhaps show nothing due to small sample size? Or did it perhaps show an effect due only to a reduction in primary smoking, having nothing to do with secondary smoke exposure? I tried to investigate this with some lack of success. Unfortunately a series of emails to Dr. Shepard produced fairly noncommittal responses in which he indicated that he was not permitted to discuss the details of the study (evidently such permission problems didn't apply during the initial press releases and TV interviews) and a promise that the study would eventually be published in an unnamed medical journal. Follow up emails from four months ago requesting details on when it might be published or what journal was involved produced no answers other than "you have what we are going to say until it is published," ... not an unusual response when dealing with public figures who prefer not to stand behind statements that have been made in this area, but an unfortunate one when dealing with scientific research. The last response Dr. Shepard made to me was on November 21st, 2003. Let me close with one very clear and simple example easily checked by anyone. In 1998 the WHO released a study on secondary smoke and lung cancer amidst a massive stir of publicity in which its results were questioned. The debate on overall result interpretation went back and forth, but there was one detail that particularly caught my eye. In looking at the abstract of the study itself it appeared that only one really statistically significant scientific finding had been made: children of smokers who were exposed to secondary smoke at home were 22% *less* likely to develop lung cancer later in life than matched children of nonsmokers. This was the *only* result where the confidence interval did not cross unity. Surely, if the result had been the other way around the WHO researchers and the Antismoking community would have secured headlines around the world proclaiming "CHILDREN OF SMOKERS GET LUNG CANCER!" Instead the finding was passed over in the official abstract with the simple observation that "no association" was found in the case of childhood exposure. The amazing thing is that this observation immediately followed the sentence in which the significant result was spelled out for all to see, and that this result was the *only* significant result of the entire study! (JNCI. Vol.90. pps 1440-1450). Does such interpretation and heralding of Antismoking results to the media suggest a bias that may be fully as strong and far more insidious than the simple force of tobacco company money? Does such publicity and increased opportunity for future lucrative grants and advances in position within the academic and research communities suggest a motivation far less pure than the simple advancement of scientific knowledge? I believe it does, and I believe the potential social effects may be as devastating or even more so in many ways than the medical effect of tobacco use itself. Michael J. McFadden Author of "Dissecting Antismokers' Brains" http://www.Antibrains.com Competing interests: I am a member of several Free Choice organizations, and have written a book titled "Dissecting Antismokers' Brains." I have absolutely no financial connections with Big Tobacco, Big Hospitality, or any other player in this arena other than as a customer. |
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Clifford G. Miller, English lawyer, graduate physicist, former examining lecturer on law, standards, ethics Beckenham Kent BR3
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Science can be legally unreliable for failing to take account of relevant evidence. Governments, courts and officials may be making a fundamental error in applying the wrong standard of proof when relying on that science to make public interest decisions. See the following BMJ Rapid Response article, which is unique in its field and in the way it explains the issues in a manner accessible to the non lawyer. See BMJ rapid response:- http://bmj.bmjjournals.com/cgi/eletters/328/7440/602-c#52948 Competing interests: Personal interest - close relative with life threatening food allergy. |
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Jeffrey Mann, Retired physician Salt Lake City, UT 84103
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I have noticed that no responder has challenged the opinions expressed by this author, so I have decided to personally respond to his incompletely informed opinions. Clifford Miller is critical of medical science, but I think that he does not really understand how medical science works, and he does not seemingly understand the foundational basis of evidence-based medicine. 1) The author states -: “The main reason medical science is potentially to be considered flawed, such as in the legal arena is because, it intentionally, necessarily (for its own purposes) and systemically fails to take account of evidence which is fundamental to the deliberations of a court. Reliable evidence is that which is authentic, accurate and complete. In short, scientific evidence is incomplete if used for purposes outside the strict confines of science because it fails to take account of evidence of lay witnesses of the facts and is hence only applicable to the narrow and specific confines of scientific enquiry and not the broader ones found in other fields of human endeavour.” This series of sentences seems to be the central tenet of the author’s critical attack on medical science. He seemingly believes that evidence-based medicine (EBM) does not consider anecdotal evidence from individual lay witnesses (or individual physicians). He is obviously in error, because all textbooks on evidence-based medicine discuss the issue of the apparent reliability of scientific evidence, and they all recommend using a grading system (classification system) to assess the scientific reliability of the EBM evidence. The highest level of evidence is evidence from multiple randomised controlled trials that have consistently positive results. The EBM evidence is deemed less reliable if there is inconsistency in the results of multiple randomised clinical trials, or if the trials have a low signal/noise ratio. Case control studies are accorded a lower level of evidence, and the lowest level of evidence is the evidence obtained from single case reports (anecdotal evidence). Although single anecdotal case reports are regarded as a lower level of evidence, it does not therefore imply that the field of EBM ignores anecdotal reports. It simply means that EBM will not regard anecdotal evidence as being totally reliable if it is not proven to be “authentic, accurate and complete” (author’s words). 2) The author writes-: “Science treats evidence of lay witnesses of fact as inadmissible (as ‘anecdotal’ only) for reasons which are inapplicable in Court, but science does so for two main reasons. The higher scientific standard of proof (in effect, irrefutability) only admits evidence which can be tested scientifically for reliability. Oral witness evidence is discounted by medical science because medical scientific method does not currently have or recognise a mechanism for testing oral evidence to the scientific standard and so, for the sake of rigour, excludes it. Neither of these propositions apply in Court. Evidence of the direct witness of the fact, whether oral, or more frequently now, by way of written statement, is always admissible and is, in fact, the keystone of the trial system of evidence and the primary source of information a court uses to make decisions of fact. The Court has and applies its own mechanisms for testing witness evidence (eg. cross-examination). Further, the Court applies a far lower standard of proof, namely a balance of probability and not the unnecessarily high one of irrefutability applied by science.” The author seemingly suggests that the science of evidence-based medicine is faulty because it does not utilise the same common sense standards that are applicable to a courtroom — where all types of anecdotal evidence are permissible and where the testing of the evidence occurs through the process of cross-examination, and where the jury’s final opinion is based on the balance of probability (preponderance of the evidence). Again, I think that the author does not understand how unbiased EBM practioners view the font of EBM evidence. I think that sensible physicians view the EBM evidence (all levels of evidence) by utilising the same simple common sense principles of probability. If the EBM evidence is only based on a series of anecdotal reports, a sensible, but unbiased, physician does not totally discount the evidence. He simply accords it a lower level of evidence, which can run through the entire gamut from possible-to-probable. If the EBM evidence is only “possible”, then a sensible physician — in contrast to a jury in a court of law, which may feel obliged to come to a definitive final opinion based on less than substantial evidence — simply assumes an agnostic position with respect to the anecdotal evidence while awaiting further suggestive evidence. A EBM practioner does not feel impelled to come to a definitive conclusion (either for, or against a particular position) if the evidence is inconclusive. EBM is like completing a crossword. EBM evidence is only deemed solid when all the clues are solved and when all the interlinking answers are consonantly linked together in an incontrovertible (unfalsifiable) fashion. If only some of the clues are answered, and one cannot perfectly interlink all the answers in a satisfactory manner, then a prudent physician simply adopts an agnostic position while awaiting further clue-solving attempts. A prudent physician does not feel impelled to come to a definitive conclusion based on inadequate, or contradictory, evidence. The author seemingly argues that one should come to a defintive conclusion even if the anecdotal evidence is unsubstantial, or otherwise incomplete. 3) The author states-: “Hence, the evidence of 1000 plus sets of parents in the MMR cases backed by before and after video, photographs and medical records, ought to be considered by a court in preference to the science. However, it seems that is not happening as it should. Whilst scientific opinion evidence ought to play second fiddle to the oral witness evidence, it takes pride of place and forces the oral witness evidence into the shadows.” The author seemingly suggests that anecdotal evidence from 1,000 individual case reports ought to be considered in preference to the results of medical science (EBM evidence). Again, he seemingly implies that those 1,000 case reports exist in a separate “universe” outside the field of EBM evidence, and he even believes that the “anecdotal evidence” should be given preferential treatment to other forms of EBM evidence. I think that this opinion reflects the author’s bias, and that it represents a misunderstanding of what constitutes EBM evidence. Those 1,000 case reports are part-and-parcel of what constitutes “EBM evidence”, and the “EBM evidence” they provide should be weighted according to simple common sense principles of probability (likelihood). Individual EBM practioners may weigh the evidence from those 1,000 case reports differently, and they may harbor varying degrees of agnosticism (scepticism) with respect to the evidence, but no responsible EBM practioner would ignore, or totally discount, the anecdotal evidence. 4) The author states-: “For issues of public safety, such as medicines like MMR or vaccines in the Gulf War, or the BSE crisis, the risk standard ought to be applied.” The author seeminly wants to use the same standards of probability (preponderance of evidence) as is applicable to a court of law, to public policy. He therefore argues that a risk assessment should be made regarding the use of MMR vaccination based on the preponderance of the evidence. I partially agree with the author on this point. I think that EBM practioners should weigh the “known” EBM evidence regarding the harms of MMR vaccination (using the standard EBM “level of evidence” weighting system) and balance the potential harms of MMR vaccination against the potential harms of not vaccinating the entire population (decrease in herd immunity to measles, mumps, rubella). The EBM practioner’s final, but tentative, conclusion would be equivalent to a tentative completion of a crossword. If a EBM practioner is unsure of his conclusion, he would simply pencil in his answers, and he would only use indelible ink if his final conclusion (final crossword solution) is deemed incontrovertible. Many people may be convinced that their risk assessment regarding the risks/benefits of MMR vaccination is worthy of a definitive conclusion and they may feel that it is appropriate to use indelible ink when pronouncing their opinions, but I think that they are wrong to condemn other EBM practioners who choose to only pencil in their opinions because they have come to a more tentative conclusion. I think that when the EBM evidence is incomplete, that further scientific evidence should be actively sought by performing more research studies eg. allowing a subsegment of the population to choose not to have MMR vaccination and then assessing whether there is a subsequent decreased incidence of autism (or allergies) in that sample population compared to the control population of MMR vaccinated individuals (during a finite period of time). Such case control studies may allow the EBM evidence regarding MMR vaccination to reach a higher level of EBM evidence, so that it may hopefully one day merit the designation “reliably accurate”. In the meantime, I think that people should avoid positing polarising opinions that are based on an inadequate understanding of what constitutes EBM evidence. Competing interests: None declared |
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Clifford G. Miller, Lawyer, graduate physicist, former examining university lecturer on law standards ethics Beckenham, Kent, BR3 England
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I am grateful to Jeffrey Mann, Retired physician, Salt Lake City, UT 84103 for his comments. I too had noticed no one else has taken me to task on what I am saying. What Dr Mann says is said with conviction, passion and fervour. I hope he does not mind the observation that his views, in my reading, do not detract in any way from what I say. I would, however, welcome further informed comment from others should they disagree. The rationale for my intervention with this item was a concern and, to some degree, an irritation, with the oft quoted 'there is no scientific evidence' and 'no scientific proof' for this or that, and stated by scientists or government officials, when it was simply unclear whether those making such statements had a clear conceptual grasp of what constitutes 'evidence', 'scientific evidence', or 'scientific proof', nor of what a standard of proof is or how to apply it. In this regard, I would refer anyone interested to another rapid response:- TIME FOR POLITICIANS TO ACT RESPONSIBLY AND ADDRESS THE ISSUES - at http://bmj.bmjjournals.com/cgi/eletters/328/7442/726-a#54697 which summarises the problem in relation to a topical issue and also to:- CLARIFICATION SOUGHT FROM AUTHORS TO ESTABLISH EVIDENTIAL VALIDITY OF THIS PAPER found at http://bmj.bmjjournals.com/cgi/eletters/322/7284/460#56882 which relates to a paper in which the authors state 'The data provide evidence that no correlation exists between the prevalence of MMR vaccination and the rapid increase in the risk of autism over time.' without explaining what they mean by their use of the term 'evidence'. Competing interests: Close relative with life threatening food allergy. |
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Ron Law, Risk Analyst Beyond Alternative Solutions
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Whilst it is often said that "Absence of evidence is not evidence of absence," this is a patently untrue statement. Absence of evidence may not be proof of absence, but it certainly is evidence of absence. For example, the last known natural case of small pox was in Somalia in 1977. Since then, the only known cases were caused by a laboratory accident in 1978 in Birmingham, England, which killed one person and caused a limited outbreak. Because of the absence of evidence of small pox disease, smallpox was officially declared eradicated in 1979.[1] Inother words, the WHO declared that not only was absence of evidence evidence of absense, but in the case of small pox, absence of evidence was PROOF of absence. If medicine wants the public to accept that it is practicing evidence -based medicine then it needs to understand that the continued use of the cliche, "Absence of evidence is not evidence of absence" has no scientific basis. The absence of evidence is, in fact, the only scientific basis for claiming evidence of absence. It's only a matter of certainty that determines whether absence of evidence is proof of absence. [1] WHO, http://www.who.int/csr/disease/smallpox/en/ Competing interests: Member of New Zealand Ministry of Health working party advising on the management of medical injuries within the health system |
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John P Heptonstall, Director of The Morley Acupuncture Clinic and Complementary Therapy Centre LS27 8EG
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Sir An interesting observation and, if correct, would certainly add the weight required to eliminate Darwinism - amongst many other theories for which evidence is absent - as a viable theory. Regards John H. Competing interests: None declared |
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Clifford G. Miller, Lawyer, graduate physicist & former University examining lecturer in law (notably here, evidence) Beckenham, Kent, England, BR3 3LA
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An opportunity to clarify this phrase is kindly provided by Ron Law, Risk Analyst, of Beyond Alternative Solutions and Member of New Zealand Ministry of Health working party advising on the management of medical injuries within the health system. It is true that if someone is not in their house, that is evidence they are absent, just as it is true that if there are no cases of smallpox, that is evidence there are no cases of smallpox. However, that is not the point of this expression, as a careful re reading of the original editorial will reveal. My best wishes to the New Zealand Ministry of Health in the endeavours of its working party. Competing interests: Close relative with life threatening food allergy. |
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Richard M Lindley, SpR Paediatric Surgery Sheffield Children's Hospital, Sheffield, S11 7AX
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Dear Editor, "...if correct, would certainly add the weight required to eliminate Darwinism..." Where you get these people from? I can put up with the anti- vaccination protesters and (barely) the anti-child protection league, but to give space to Creationist theory within the BMJ website seems to be stretching the bounds of credibility and plausability. For the (fossil) record, there is a wealth of evidence that Darwinian natural selection and evolution has produced the biological world we live in today. If any readers are in doubt, I would recommend the Blind Watchmaker and the Selfish Gene by Richard Dawkins. If any people out there still refuse to believe in one of the greatest scientific theories ever produced by humankind, may I remind them that they all owe me £20. Competing interests: None declared |
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Sam Lewis, GP / Medical Adviser Surgery, Newport, Pembrokeshire, SA42 0TJ
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To further clarify - Ron Law is cheekily correct, as Clifford Miller would agree, that not finding me at home is evidence of my absence ! But the point of the statement is that someone should have taken the trouble to look .. Clearly John Heptonstall may be looking straight at the evidence for Darwinism, but with his eyes (or mind) firmly closed. Competing interests: None declared |
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Robert A. Da Prato, Physician Portland OR 97229
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Chiasmus is the transposition of words in parallel phrases for a literary effect ("First I had the wine, then the wine had me"). More recently, in our ongoing and interminable presidential election season one of the candidates intoned "I don't want God to be on my side; I want to be on God's side." Got a thundering ovation for that, but I suspect if each member of the audience were grilled individually as to the actual meaning of that sentence -- specifically how the second part actually differed operationally from the first -- there would be an embarrased silence. "Absence of evidence is not evidence of absence" falls into this entertaining but usually ambiguous syntactical exercise and I suppose it is usually employed for a manipulative purpose when a prediction fails for a pet hypothesis. In such cases ambiguity can be your friend. For example, does "absence of evidence" means no observations or data are available, or does it mean the observations and data are available but insufficiently robust or irrelevant by (unavoidably) subjective criteria to falsify the hypothesis, or are they available, robust and do not support the hypothesis? Here's a hypothesis: the room light periodically going off and on in a specific room in a specific house is caused by a person in that house flipping the light switch in that room. If I tell you to test that hypothesis from a thousand miles away, your absence of evidence is not evidence of absence. If I take you outside the house and you base your assessment of a person flipping the switch on hearing footsteps through the wall, failure to hear footsteps -- absence of evidence -- may be evidence of absence, but one could argue over its robustness. If I take you to the house and have you stand by the room's light switch and the light goes on and off without anyone being present then your "absence of evidence" of a person flipping that switch is definitely evidence of absence. Now this is a simple and relatively clear cut hypothesis without requiring extravagent statistical manipulations and the gray magic of molecular biology, and there are no vast sums of money or ideology at stake. In other words, this is not an accurate represention of the complex world of medicine. My suggestion: strive for accurate data and unambiguous testing of hypotheses. And ditch the phrase. Competing interests: None declared |
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