From owner-emf-bio@net.bio.net Thu Feb 01 22:00:00 1996 Path: biosci!biosci!not-for-mail From: afrey@uunet.uu.net (Allan Frey) Newsgroups: bionet.emf-bio Subject: Access thru web Date: 2 Feb 1996 10:02:38 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 21 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: NNTP-Posting-Host: net.bio.net All BIOSCI/bionet newsgroups and their archives have been made accessible through the World Wide Web at URL http://www.bio.net/ Please click on the "Access the BIOSCI/bionet Newsgroups" hyperlink. One can both read and post to all full newsgroups in addition to doing WAIS searches on each group and browsing the archives through the new hypermail interface. This service avoids the need to subscribe by e-mail and also makes it possible to access the latest postings quickly if you have problems with your local news USENET system or have an unreliable newsfeed. Allan Allan H. Frey email afrey@uunet.uu.net 11049 Seven Hill Lane voice 301.299.5181 Potomac, MD 20854, USA From owner-emf-bio@net.bio.net Sun Feb 04 22:00:00 1996 Path: biosci!biosci!not-for-mail From: Bill Hickey Newsgroups: bionet.emf-bio Subject: Re: reply re tox assumption Date: 5 Feb 1996 06:35:37 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 75 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: NNTP-Posting-Host: net.bio.net Allan: > Date: Mon, 29 Jan 1996 10:52:29 -0500 > From: Allan Frey > To: nobody@net.bio.net > Newgroups: bionet.emf-bio > Subject: reply re tox assumption >...... > to nervous system function. To model how em fields affect living beings, > one might compare them to the radio we use to listen to music. If one wishes to use this "model" of em interactions, one must also be consistent with the other analogic observations as well. > The em signal the radio picks up and transduces into the sound of music is > almost unmeasureably weak. At the same time there are, in toto, strong > em fields impinging on the radio. We don't notice the stronger em signals > because they are not the appropriate frequency or modulation. Thus, they > don't disturb the music we hear. Not necessarily so. Especially at the lower frequencies (MF and lower), a strong _nearby_ signal can "swamp" the receiver and desensitize it significantly. In most receivers, this is a function of RF tuned circuit "Q" which can be readily calculated. It would give us a measure of how strong the field would have to be vs. the frequency offset in order to disturb or override the desired signal. Another analogy would be Television interference from nearby transmitters "close" in frequency, but within the tuning capability of the receiver because of poor design by the manufacturer. Since we cannot return our bodies to the manufacturer on warranty, we are pretty much stuck with the response systems we have. One other point. If the em signal the radio picked up was truly "almost immeasureably weak" -- then the radio wouldn't pick it up. By definition, it has to be able to "measure" the signal to detect it...either that or in more complex modulation schemes it must have some a priori notion of the sequence being used to bring the signal out of the noise. Besides, we routinely "measure" these RF fields all the time without converting them to "music." > However, if you impose on the radio an appropriately tuned em field > or harmonic, even if it is very weak, it will interfere with the music. You are reaching here. First, if the em field is AT the right frequency, then whether or not it interferes with the music will depend on the relative field strength of the undesireable field to that of the music carrying signal. If the undesireable field strength is low enough, you'll never know it was there. (Dose-Response maybe?) However, going further to say an appropriately tuned "harmonic" will interfere is to oversimplify the situation. Harmonics are a complex phenomenon, and I disagree that you can make that analogy safely with such simplicity. > Similarly, if we impose a very weak em signal > on a living being, it has the possibility of interfering with normal function > if it is properly tuned. This is the model that much biological data and > theory tell us to use, not a toxicology model. _POSSIBILITY_ .... _IF_ it is _PROPERLY_ tuned. How do you or anyone else propose to determine just exactly WHAT the proper frequency(ies) of concern is(are)? A number of researchers have taken data which suggest the problem comes as a part of VERY low frequency modulation, not the carrier itself...of course, there's a lot going on right now. I don't disagree with your hypothesis necessarily, I merely obvserve that it is inconsistent with your analogy. I think while you classically think of "dose-response" as a "strength-response" curve, you could also stretch that a bit and look at "frequency-response" before you start worrying about how low the strength has to go before the effect is negligible. Just some thoughts. Bill Hickey From owner-emf-bio@net.bio.net Sun Feb 04 22:00:00 1996 Path: biosci!biosci!not-for-mail From: "Kenneth R. Foster" Newsgroups: bionet.emf-bio Subject: Re: Item for discussion Date: 5 Feb 1996 13:23:40 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 138 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <2.2.16.19960205121520.2be7af42@Postoffice.seas.upenn.edu> NNTP-Posting-Host: net.bio.net Blackman and Blanchard wrote: >A. Sastre cites the various EMF interaction mechanisms developed by >Liboff, Blanchard-Blackman, Lednev, Walleczek, and Litovitz, and >says "None of the mechanisms have been proven for any reported >effect, and all need, before they can be accepted or rejected, to match >their predictions (including dose-response) to the experimental data >that may be collected." > >It would be interesting to explore in this forum what various >scientists believe are the pathways that lead to 'proof'. Although >mathematical formalism is often not available in the biological >sciences, the repeatability of experimental results one would expect >from such a proof is a useful standard to apply to biology. For >example, one approach has been to follow an experimental finding >reported by a research group, and see if that group can repeat their >results and extend them. This would constitute one step in the >process of 'proof'. > >Another step would be to wait for independent research groups to >essentially repeat the experiments of the first group and obtain the >same basic findings. There are several degrees of "independence" >that can be envisioned so this step has varying degrees of >importance. We might also note that lack of replication in an >independent lab can be, and often is, a function of how well the >second lab understands all the procedures of the first lab. The >replication process can and should be a learning process for both labs >as they search for factors that created the originally observed effect. > >Another step in the establishment of a proof is to demonstrate that >the model predictions are applicable to other biological systems and >endpoints. > >The last step empirically, is to have the experimental system so well >established the any competent research team can perform the >experiment and obtain the same basic result. > >Another aspect of the search for proof is to examine the theoretical >underpining supporting each of the models. Certainly the Free >Radical Pair Recombination model (presently being tested by >Walleczek, Grissom, Scaiano, and others) is on the strongest footing (it >is a chemical mechanism that is well established at high magnetic >field strengths, searching for a low level biologically important >effect). Litovitz's model is also well accepted because it depends on >well-known and widely accepted signal-to-noise models. Liboff's >model is incomplete because of its lack of a full 'dose-response' >function. Lednev's model has limited reports of results in chemical >changes (but also some non-replications) and a single reported set of >data from an outside group (Prato et al.) examining magnetic field >effects on snail behavior. Those tests only partially explored the >dose response predicted by the model, but they also explored the >importance of the relative orientation between ac and dc fields. Our >IPR model is supported by extensive dose-response tests, off >resonance tests, and a variety of other tests, each of which shows >results consistent with the predictions of the model over a wide >range of tested parameters. In fact, the IPR model's hypothesis >generation allowed us to consider hydrogen as a biologically >significant ion, and subsequent tests by Trillo and Ubeda confirmed >this prediction. > >However, all of these models are limited in their full theoretical >development. Part of this is due to fundamental uncertainties about >the microscopic biological environment and the nature of interactions >that might occur there. Just as lack of replication by an independent >lab cannot be taken as proof that the original results can never be >repeated, lack of clear understanding of the physical foundations of a >model for which there is extensive experimental support should not >deter us from tests to better understand the biological mechanisms >these models seem to be describing. > >It would be useful to have other scientists discuss this issue of >incremental 'proof' and the interplay between theory and >experimental results. > >Janie Blanchard >Carl Blackman I just finished writing a book that dealt, in part, with issues of scientific proof, and have spent more time with the philosophy of science than I care to admit. The question you asked -- what makes an acceptable proof of a theory -- is a deep one that nobody has any really good simple answer for. Moreover, theory and observation are closely linked, and in the short term the testing of a theory by experiment can be controversial because of experimenters' regress and other problems. Several authorities have given checklists for identifying a good theory, that take a much longer view than the issue of reproducibility of data that is mentioned by Blackman. For example, Philip Kitcher considered these attributes of a good theory: 1. Independent testability (ability "to test auxiliary hypotheses independently of the particular cases for which they are introduced") 2. unification ("the result of applying a small family of problem-solving strategies to a broad class of cases") 3. fecundity ("when a theory opens up new and profitable lines of investigation") Karl Popper listed various ways in which the validity of a theory can be judged: 1. By comparing the conclusions that can be deduced from the theory among themselves, to see whether they are internally consistent. 2. By investigating the logical form of the theory, to determine "whether it has the character of an empirical or scientific theory, or whether it is, for example, tautological." 3. By comparing the theory with other theories, "with the aim of determining whether the theory would constitute a scientific advance should it survive our various tests." 4. By "testing of the theory by way of empirical applications of the conclusions which can be derived from it." By Popper's standards, the theories by Lednev and Liboff (for example) are nonstarters since they are open to devastating objections on theoretical grounds. My impression is that they do not do so well in the "fecundity" line either, since a lot of the "testing" that has gone on has the appearance of post-hoc fitting of noisy data to the theory, and some of even these observations cannot be independently confirmed. Only time will tell whether these theories are productive (as was, for example, the Hodgkin-Huxley model for excitable nerve membranes) or merely aberrations. Kenneth R Foster Department of Bioengineering University of Pennsylvania 220 S. 33rd St. Philadelphia PA 19104-6392 215-898-8534 fax 215-573-2071 From owner-emf-bio@net.bio.net Sun Feb 04 22:00:00 1996 Path: biosci!biosci!not-for-mail From: CFB@vaxtm1.rtpnc.epa.gov Newsgroups: bionet.emf-bio Subject: Item for discussion Date: 5 Feb 1996 06:32:28 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 77 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <01I0TMI4LA368X6LGE@epavax.rtpnc.epa.gov> NNTP-Posting-Host: net.bio.net A. Sastre cites the various EMF interaction mechanisms developed by Liboff, Blanchard-Blackman, Lednev, Walleczek, and Litovitz, and says "None of the mechanisms have been proven for any reported effect, and all need, before they can be accepted or rejected, to match their predictions (including dose-response) to the experimental data that may be collected." It would be interesting to explore in this forum what various scientists believe are the pathways that lead to 'proof'. Although mathematical formalism is often not available in the biological sciences, the repeatability of experimental results one would expect from such a proof is a useful standard to apply to biology. For example, one approach has been to follow an experimental finding reported by a research group, and see if that group can repeat their results and extend them. This would constitute one step in the process of 'proof'. Another step would be to wait for independent research groups to essentially repeat the experiments of the first group and obtain the same basic findings. There are several degrees of "independence" that can be envisioned so this step has varying degrees of importance. We might also note that lack of replication in an independent lab can be, and often is, a function of how well the second lab understands all the procedures of the first lab. The replication process can and should be a learning process for both labs as they search for factors that created the originally observed effect. Another step in the establishment of a proof is to demonstrate that the model predictions are applicable to other biological systems and endpoints. The last step empirically, is to have the experimental system so well established the any competent research team can perform the experiment and obtain the same basic result. Another aspect of the search for proof is to examine the theoretical underpining supporting each of the models. Certainly the Free Radical Pair Recombination model (presently being tested by Walleczek, Grissom, Scaiano, and others) is on the strongest footing (it is a chemical mechanism that is well established at high magnetic field strengths, searching for a low level biologically important effect). Litovitz's model is also well accepted because it depends on well-known and widely accepted signal-to-noise models. Liboff's model is incomplete because of its lack of a full 'dose-response' function. Lednev's model has limited reports of results in chemical changes (but also some non-replications) and a single reported set of data from an outside group (Prato et al.) examining magnetic field effects on snail behavior. Those tests only partially explored the dose response predicted by the model, but they also explored the importance of the relative orientation between ac and dc fields. Our IPR model is supported by extensive dose-response tests, off resonance tests, and a variety of other tests, each of which shows results consistent with the predictions of the model over a wide range of tested parameters. In fact, the IPR model's hypothesis generation allowed us to consider hydrogen as a biologically significant ion, and subsequent tests by Trillo and Ubeda confirmed this prediction. However, all of these models are limited in their full theoretical development. Part of this is due to fundamental uncertainties about the microscopic biological environment and the nature of interactions that might occur there. Just as lack of replication by an independent lab cannot be taken as proof that the original results can never be repeated, lack of clear understanding of the physical foundations of a model for which there is extensive experimental support should not deter us from tests to better understand the biological mechanisms these models seem to be describing. It would be useful to have other scientists discuss this issue of incremental 'proof' and the interplay between theory and experimental results. Janie Blanchard Carl Blackman From owner-emf-bio@net.bio.net Tue Feb 06 22:00:00 1996 Path: biosci!biosci!not-for-mail From: "Bowman, Joseph D." Newsgroups: bionet.emf-bio Subject: Re: Item for discussion Date: 7 Feb 1996 08:01:28 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 89 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <31184589@SmtpOut.em.cdc.gov> NNTP-Posting-Host: net.bio.net On February 04, 1996, Janie Blanchard and Carl Blackman posted: >A. Sastre cites the various EMF interaction mechanisms developed >by Liboff, Blanchard-Blackman, Lednev, Walleczek, and Litovitz, >and says "None of the mechanisms have been proven for any >reported effect, and all need, before they can be accepted or >rejected, to match their predictions (including dose-response) >to the experimental data that may be collected." >It would be interesting to explore in this forum what various >scientists believe are the pathways that lead to 'proof'. >Although mathematical formalism is often not available in the >biological sciences, the repeatability of experimental results >one would expect from such a proof is a useful standard to apply >to biology. The repetition / replication of a single experimental finding does not "prove" that the hypothesis leading to the experiment is correct. It only establishes a single experimental "fact" which the hypothesis or any alternatives must explain in order to be "proven" (i.e. accepted as an established theory by most of the scientific community). In order for an hypothesis to become a theory, we all know intuitively that the hypothesis must: * explain many experimental "facts" * not be contradicted by other experiments (or at least have a plausible explanation for discrepancies) * predict the outcome of new experiments * agree with other accepted theories This process holds whether the hypothesis is a mathematical model or the more qualitative forms that biological hypotheses usually take. The only aspects of a mathematical model which might be new for biologists are: * A model is built on mathematical postulates, which can often be compared to established theories and facts. If those postulates contradict other knowledge, the hypothesis faces an up-hill battle. * A mathematical model can easily predict the outcome of many different experiments. If some experiments contradict the model's predictions, the hypothesis is in trouble, and adjustments are needed. For any of the present EMF mechanistic hypotheses to be proven, a ton of experimental and theoretical progress is needed. Let's assume that the replication efforts now underway establishes as fact a biological effect of low-level EMF (e.g. ELF magnetic fields <100 mG), and that a mechanism had predicted this outcome. At the risk of being obvious, I offer a list of other steps needed to "prove" the mechanism's validity: For theoreticians: * State the model's postulates in forms that can be compared with established physics, chemistry and biology * Develop the mathematical model so that it predicts the results of other exposure conditions. * Demonstrate how the mechanism works (or why it fails to work) in well-established fields of biology and chemistry. For experimental biologists: * Test the mechanism's predictions, esp. for exposures that are qualitatively different from those already studied. * Identify experimentally which biological molecule(s) are the site of the EMF interaction mechanism. * Establish the biologic pathway from the EMF interaction site to the observed bioeffect. * Test the mechanism in other biologic systems, esp. well- understood systems which meet the model's postulates. * Find explanations for experiments that do not follow the mechanism's predictions. EMF biology clearly has a long ways to go. Joe Bowman National Institute for Occupational Safety and Health Cincinnati, Ohio, USA E-mail: jdb0@niobbs1.em.cdc.gov As always, these thoughts are my own, and do not necessarily reflect NIOSH policy. From owner-emf-bio@net.bio.net Wed Feb 07 22:00:00 1996 Path: biosci!biosci!not-for-mail From: Spadaroj@VAX.CS.HSCSYR.EDU (Joe Spadaro) Newsgroups: bionet.emf-bio Subject: mechanisms discussion Date: 8 Feb 1996 08:19:18 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 27 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4fd7q6$3oc@net.bio.net> NNTP-Posting-Host: net.bio.net In the spirit of the current discussion on establishing EMF interaction mechanisms, I pose the following question, which I don't think is trivial: If research demonstrated repeatable biological effects at higher magnetic field strengths (say, 0.1-10 G), perhaps with pulsed waveforms (high dB/dt), could we expect to extrapolate downward in intensities and expect a similar mechanism to be operative? Would it be fruitful to start where things may be more easily repeatable in relatively short exposure times, to determine the mechanism(s), and then using that information, design experiments to see if the same (or similar) mechanisms apply at "environmental" levels? Case in point: In bone cells and tissues, a number of effects of magnetic field effects have been found, and recently some hint of the sites of action have begun to emerge. Usually, these involve pulsing waveforms with rms or peak intensities in the 1-10 G range with exposures from minutes to days. Now, bone cells are not brain cells or leukocytes, but they are nice cells too. How do findings of this type bear on the 50-60Hz, <100 mG, sine-wave problem? Joe Spadaro, 2-7-96 Joseph A. Spadaro, Ph.D. Associate Professor - Orthopedic Research S.U.N.Y. Health Science Center - Syracuse spadaroj@vax.cs.hscsyr.edu From owner-emf-bio@net.bio.net Mon Feb 12 22:00:00 1996 Path: biosci!biosci!not-for-mail From: Bill Hickey Newsgroups: bionet.emf-bio Subject: Re: mechanisms discussion Date: 12 Feb 1996 18:31:26 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 29 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4fot5u$dtc@net.bio.net> NNTP-Posting-Host: net.bio.net On Wed, 7 Feb 1996, Joe Spadaro wrote: > I pose the following question, which I don't think is trivial: >... > expect a similar mechanism to be operative? Would it be fruitful to start > where things may be more easily repeatable in relatively short exposure > times, to determine the mechanism(s), and then using that information, > design experiments to see if the same (or similar) mechanisms apply at > "environmental" levels? This is a good question. Possibly because the effects would be expected to be nonlinear, I would expect this to be a rather complex relationship. line 1> of action have begun to emerge. Usually, these involve pulsing waveforms > with rms or peak intensities in the 1-10 G range with exposures from > minutes to days. Now, bone cells are not brain cells or leukocytes, but > they are nice cells too. How do findings of this type bear on the > 50-60Hz, <100 mG, sine-wave problem? An excellent question. Given the wavelength at 50-60 Hz, I would say that the microT/picoT field people would have a hard time explaining why the treatment you describe for bone cells would not adversely affect other parts of the body, and I don't think I've ever seen any indication that patients have been examined for deleterious effects therefrom. I would be interested if anyone else has anything relevant to this particular question. Bill From owner-emf-bio@net.bio.net Tue Feb 13 22:00:00 1996 Path: biosci!biosci!not-for-mail From: "Kenneth R. Foster" Newsgroups: bionet.emf-bio Subject: Re: "Proofs" and related follow-up Date: 14 Feb 1996 12:51:42 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 110 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4fti0u$6oh@net.bio.net> NNTP-Posting-Host: net.bio.net Who are you? I don't recognize your email address. Nice comments. Some small points: > This brings me to an important point: A candidate theory must be >"falsifiable" or "refutable." That is, the theory should not have so many >degrees of freedom (whether for fitting data or conceptually) that it cannot be >shown to be wrong. I believe it was Popper (Ken, am I wrong?) that stressed the line 1>falsifiability criterion Yes, Popper made big deal of it. He used it to define science -- he thought that Freud's theory was not falsifiable and thus not science, while Einstein's relativity was (because it made so many definite predictions about things such as the bending of starlight by the sun) and is. Popper's theory has been well examined by other philosophers of science, and there are lots of problems with it, mostly in applying the criterion in the way Popper intended.. But clearly anything that is so loose as to be unfalsifiable (eg. Chineses fortune cookies) is slippery indeed. This enters into EMF discussions in many ways. The view, often expressed by some people, that a critical issue is whether "effects" exist is too loose to be meaningful. If interpreted literally, it cannot be falsified -- it is demonstrably true, but the statement does not carry much meaning if interpreted so broadly. Nobody ever argued whether electric shocks were real phenomena. >and one way to interpret Thomas Kuhn's paradigm shifts >is to consider their coming at a time that a theory has had too many ad-hoc >revisions. Kuhn's theory is quite different from Popper's and I am not sure that the "falsifiability" criterion plays a role in his concept of paradigm shift. > In this context, the old ion cyclotron resonance was immediately a >candidate theory (one had the equations of motion and relatively few free >parameters, with none for field amplitude) and could also be *falsified* >quickly. (Carl Durney did it beautifully in 1988). Well said >This criterion essentially >formalizes the essence of a quote attributed to the 19th century mathematician >Cauchy: "Give me 5 free parameters and I will give you the equations for an >elephant, but give me a sixth free parameter and I will make the elephant wag >its tail." Too many free parameters and one can fit almost anything; such a >theory in the long run cannot be proven or disproven, and is therefore of little >use. > My bottom line for Carl and Janie: Your quest for reproducible findings >that are either predicted by or consistent with your IPR theory is admirable, >and to the extent that you add to the empirical data base, by urging others to >reproduce your results, it will result in a testing ground not only for IPR but >for other competing theories. This, in itself, does not help to "prove" IPR, >even if the findings are "predictions", because in the absence of the equations >of motion (yes, I know you are working on it !!!) there are too many free >parameters that allow for a fit. A prediction adds to the "proof" of a theory >only when there are no free parameters, so that a result can be unambiguously >interpreted as support or refutation. Science does not usually deal with "proofs" of theories -- in the short term, what constitutes proof is usually too controversial among investigators. A more pertinent criterion is usefulness. Unless others follow up the work and make something of it, it will be forgotten. The only test the success of the IPR theory is in the long run, if it can be successfully defended against challenge by people like Bob Adair and if other scientists find the theory line 70useful in organizing their own work. Science, as science commentator John Ziman wrote recently, is ruled not by the Invisible Hand but by the Royal Boot. > Such is the case of the Hodgkin-Huxley theory invoked by Ken. Once you >do the proper voltage-clamp experiments on a given cell (other than the squid >axon where the theory was derived) there are no free parameters. The equations >then predict how the action potential shape and time course will be. The >prediction either matches or it doesen't match the action potential of the cell. And H-H theory, despite its ad-hoc character (and lots of free parameters!), has been enormously fruitful in biology. So far, ion cyclotron resonance and other such theories have been embarrassing failures. If a theory conflicts with what is already well known, it can't be true. Kenneth R Foster Department of Bioengineering University of Pennsylvania line 92220 S. 33rd St. Philadelphia PA 19104-6392 215-898-8534 fax 215-573-2071 From owner-emf-bio@net.bio.net Tue Feb 13 22:00:00 1996 Path: biosci!biosci!not-for-mail From: "Kenneth R. Foster" Newsgroups: bionet.emf-bio Subject: Mechanisms, continued Date: 13 Feb 1996 18:27:31 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 43 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4frhaj$cdc@net.bio.net> NNTP-Posting-Host: net.bio.net >Date: Tue, 13 Feb 1996 08:43:43 >To: emf-bio@net.bio.net >From: "Kenneth R. Foster" > >On Wed, 7 Feb 1996, Joe Spadaro wrote: > >> I pose the following question, which I don't think is trivial: >>... >> expect a similar mechanism to be operative? Would it be fruitful to start >> where things may be more easily repeatable in relatively short exposure >> times, to determine the mechanism(s), and then using that information, >> design experiments to see if the same (or similar) mechanisms apply at >> "environmental" levels? > (and other discussion from others) There is actually a much simpler and more compelling need -- to make sure that the "effect" is real. The noise level in bioeffects research is incredible. The literature is filled with reports of effects that cannot be reproduced in other laboratories. Start where things are more reproducible? Many of the reports, it seems from reading the papers, were from SINGLE experiments that were never repeated, even by the same investigator. Many other effects seem to have been reported on the basis of post-hoc analysis of noisy data, and involve "effects" that are barely above the level of statistical uncertainty. Finding the "mechanism" for an effect would be wonderful, but a better reason to continue experiments is to first make sure that the facts are right! Some attempt to vary the parameters would help, if only to make sure that the original "effect" was not an artifact. Kenneth R Foster Department of Bioengineering University of Pennsylvania 220 S. 33rd St. Philadelphia PA 19104-6392 215-898-8534 fax 215-573-2071 From owner-emf-bio@net.bio.net Thu Feb 15 22:00:00 1996 Path: biosci!biosci!not-for-mail From: mmzsm@mmn2.med.nottingham.ac.uk (sasha mae) Newsgroups: bionet.emf-bio Subject: EMF and Radon Date: 16 Feb 1996 10:19:17 -0800 Organization: Rechenzentrum Universitaet Hohenheim Lines: 23 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4g2hr5$of1@net.bio.net> NNTP-Posting-Host: net.bio.net There has been quite a bit of publicity, here in the UK, over the last few days i.e. main TV news, radio, TV documentaries etc on a report that was published by Prof. D. Henshaw (Bristol Univ.) showing that EMF can act to attract Radon particles with the hypothesis being that that the increased cancers observed from some epidemiological studies (i.e. the recent Swedish study, Leepers original study etc) may be explained (in part) by the high LET alpha particles produced from the Radon particles. The EMF is therefore not inducing the carcinogenic process directly but via an indirect means by increasing the relative Radon concentrations. Radon has been shown to be extremely line 1carcinogenic in a number of both in vitro and in vivo studies. Anyone have any comments ?? I've tried doing a literature search to find the article but had no luck. Anyone know where the study was published ? Stewart G. Martin CRC Department of Clinical Oncology University of Nottingham stewart.martin@nott.ac.uk From owner-emf-bio@net.bio.net Thu Feb 15 22:00:00 1996 Path: biosci!biosci!not-for-mail From: Steven Belsky Newsgroups: bionet.emf-bio Subject: Re: mechanisms discussion Date: 16 Feb 1996 10:16:53 -0800 Organization: Balstarr Lines: 48 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4g2hml$o2q@net.bio.net> References: <4fot5u$dtc@net.bio.net> NNTP-Posting-Host: net.bio.net Bill Hickey wrote: > > On Wed, 7 Feb 1996, Joe Spadaro wrote: > > > I pose the following question, which I don't think is trivial: > >... line 1> > expect a similar mechanism to be operative? Would it be fruitful to start > > where things may be more easily repeatable in relatively short exposure > > times, to determine the mechanism(s), and then using that information, > > design experiments to see if the same (or similar) mechanisms apply at > > "environmental" levels? > > This is a good question. Possibly because the effects would be expected > to be nonlinear, I would expect this to be a rather complex relationship. > > line 1> of action have begun to emerge. Usually, these involve pulsing wavefo rms > > with rms or peak intensities in the 1-10 G range with exposures from > > minutes to days. Now, bone cells are not brain cells or leukocytes, but > > they are nice cells too. How do findings of this type bear on the > > 50-60Hz, <100 mG, sine-wave problem? > > An excellent question. Given the wavelength at 50-60 Hz, I would say > that the microT/picoT field people would have a hard time explaining why > the treatment you describe for bone cells would not adversely affect > other parts of the body, and I don't think I've ever seen any indication > that patients have been examined for deleterious effects therefrom. > > I would be interested if anyone else has anything relevant to this line 24> particular question. > > Bill Doctors use electric stimulation to heal broken bones, I think the japaness(?) also use electric current and/or magnets on the body. don't cycltrons use magnets to move atoms? I would think by know there would be enough proof that EMF does effect the body that there would be no need to talk about this any more AM I WRONG? next question: how much will it cost to bury the wires? STEVEN BELSKY From owner-emf-bio@net.bio.net Thu Feb 15 22:00:00 1996 Path: biosci!biosci!not-for-mail From: "Bowman, Joseph D." Newsgroups: bionet.emf-bio Subject: RE: brain cancer meta-analysis & other EMF epi reviews Date: 16 Feb 1996 10:29:06 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 111 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4g2idi$pi4@net.bio.net> NNTP-Posting-Host: net.bio.net The recent discussion on mechanisms in this newsgroup started with Allan Frey's posting: >Subject: brain cancer meta-analysis >Date: Monday, January 22, 1996 4:28PM >I understand that Leeka Kheifets... >of EPRI conducted a Meta-analysis of a number of brain cancer epi studies. >Has anyone read the report and have any thoughts on it? I gather that Allan was re-acting to a news story (like the Dec. 22 story in the Washington Post) which paraphrased the article's final sentence: Because of the lack of adequate exposure information and a clear dose-response pattern, it is not possible to conclude that EMF is causally associated with the observed excess of brain cancer in workers employed in electrical occupations. The original article is easily available (J. Occ. Environ. Med., 37: 1327-1341, 1995), and it's over-all conclusions are not as negative as the press reports make out: The body of epi evidence admits 3 possible interpretations..: (1) There is no association between occ. EMF and the risk of cancer. (2) There truly is a small effect and the inconsistencies among studies arise because of misclassification and bias... (3) The true EMF exposure effect is large, but affects a small number of individuals who are somehow preconditioned; alterenatively this could .. affect all individuals but require a rare .. simultaneous exposure to another factor or a magnetic field with yet-to-be identified charateristics. We believe that this meta-analysis provides some evidence against the hypotheis of no association ..., provides some ... support .. for a small pervasive effect, and provides no clues .. for the third hypothesis..... I completely agree with their logic, but the complexities of the scientific situation is lost on the media. (The convoluted prose in the Conclusion doesn't help reporters to understand things either.) Another recent review (Heath CW. EMF exposure and cancer: A review of epi evidence. CA -- A CancerJournal for Clinicians, 46:29-44, 1996) got even more biased coverage in a story in the Atlanta Journal-Constitution. The lead sentence was: A comprehensive scientific review has dealt another major blow to the hotly debated theory that EMF ... cause cancer and other ills. After reviewing all ..., Dr. Clark W Heath of the American Cancer Society concludes that the data suggesting a possible link are "weak, inconsistent and inconclusive." Dr. Heath does an admirable job of summarizing a large literature (the only major gap is the animal tumour promotion studies), and does conclude on a very sceptical note. His final proposal is: Should our research investment not lead to reproducible and cohesive results, the scientific should ... perhaps assign likely risk boundaries upon which practical guidance for community consensus can be reached. I've done such an exercise in the past for leukemia, and it could be done for brain cancers with the estimates from Kheifets et al. The outcome is not as reassuring as Dr. Heath might suspect because the numbers of workers exposed is massive. Using the magnetic field exposure measurements from Floderus (1993) whose controls are a nearly random sample of the male workforce, the Kheifets meta-analysis give the following bounds on the relative risk for brain cancer: TWA magnetic % male workforce # US men 95% CI field exposure (from Floderus) (1980 census) on RR <1.5 mG 25% 5,000,000 reference group 1.5 - 3 mG 50% 10,000,000 1.1 - 1.7 >3 mG 25% 5,000,000 1.3 - 2.0 I don't have the necessary cancer stats to finish the exercise. If memory serves, around 5,000 male deaths each year -- 0.5% of all deaths -- are due to brain cancer. But you don't need exact figures to see three things: 1) the lower bound on brain cancers attributable to occupational magnetic field exposures is not zero. 2) the upper bound gives us a non-trivial public health problem. 3) Not included is leukemia in working men and children. Nor have I gotten into breast cancer, other cancers in working women, Alzheimer's disease, and other diseases linked to occupational EMF by preliminary epi studies. The media coverage of these epi reviews focuses on their conclusion that the EMF-cancer hypothesis isn't proven. That 's old news to anyone who has been following this discussion group. Beneath the high-lighted quotes, these reviews are evidence that EMF could be a significant public health problem. Joe Bowman National Institute for Occupational Safety and Health line 93Cincinnati, OH, USA jdb0@niobbs1.em.cdc.gov As always, my thoughts are not necessarily NIOSH policy. From owner-emf-bio@net.bio.net Fri Feb 16 22:00:00 1996 Path: biosci!biosci!not-for-mail From: "John Moulder" Newsgroups: bionet.emf-bio Subject: Radon, Powerlines & Cancer Date: 17 Feb 1996 15:03:40 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 142 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4g5msc$k32@net.bio.net> NNTP-Posting-Host: net.bio.net British television has reported on a paper in the upcoming issue of the International Journal of Radiation Biology (Feb 1996 issue). The paper reports that the radioactive decay products of radon are attracted to power-frequency electric field sources. The authors indicate that they believe that this provides a mechanism for the alleged connection between powerlines and childhood leukemia. The report is: DL Henshaw, AN Ross, AP Fews, AW Preece: Enhanced Deposition of Radon Daughter Nuclei in the Vicinity of Power Frequency Electromagnetic Fields. Int J Rad Biol 69:25-38, Feb 1996. Further details can be found at the authors' web site. The journal article itself will not be widely available (at least not in the US) for another month or so). Authors URL: http://www.phy.bris.ac.uk/research/track_analysis/emf_radon.html >From Authors Abstract "We report the attraction of radon daughter nuclei in normal domestic room air to everyday sources of power frequency electromagnetic fields... We observed that wires carrying mains frequency potential attract radon daughter nuclei... The effects appear to be due to interactions of the electric component of the EM-field with both the ultrafine and attached fraction of radon daughter aerosols.... For larger aerosols the effect may be sufficient to allow electrically neutral aerosols to migrate up strong E-field gradients... Enhanced plateout on the skin is likely, increasing the dose to the basal layer... Increased local concentration in room air could lead to increased dose by inhalation... The authors believe that the observations may have implications for the apparent enigma that there is no persuasive biological evidence to show that power frequency electromagnetic fields can influence any of the accepted stages in carcinogenesis. On the contrary, the observations show that EM-fields can concentrate in their vicinity a cocktail of radon daughter nuclei, a known carcinogen, and presumably other potentially harmful agents." Commentary The basic observation is plausible; the extension to the powerline leukemia question, however, is quite a stretch. On the basic observation of increased radon-derived alpha exposure near strong electrical fields: 1) A large proportion of "radon daughters" attach to aerosols immediately after being formed by decay of the radon itself. These aerosols would be expected to be attracted to strong electrical fields (this is more or less how an electrostatic precipitator works). For example, it has been known for years in the radiation safety community that you can pick up radiologically significant quantities of radon daughters by swabbing a VDT screen. 2) The radon daughters and radon daughter containing aerosols are inhaled, and the dose to the various respiratory structures depends in part on whether the radon daughter is free or attached to an aerosol. So making bigger aerosols might matter. 3) Inhaling radon daughters at a high enough concentration causes lung cancer, particularly when combined with smoking (data from miners). The radon link with other types of cancer is highly speculative (and dosimetrically not very plausible). Thus it is not unreasonable to suggest that a person breathing air near a source of strong electrical fields might be exposed to a higher radon daughter concentration, and thus to higher alpha radiation doses to skin, oral mucosa, bronchus and lung. However, if the radon daughter containing aerosols plate out on the source of the electrical field, it would seem that they would then not be available for inhalation. The jump to a generalized power-frequency field cancer connection is a real stretch. There are particular problems with the suggestion that this could explain the alleged connection between residence near powerlines and increased childhood leukemia. 1) Residences along powerlines do not have elevated electrical fields (see Barnes et al, Bioelectromag 10:31-21, 1989; Kaune et al, Bioelectromag 8:315- 335, 1987; London et al, Amer J Epidem 134:923-937, 1991). 2) The residential epidemiological studies that have looked at both electrical and magnetic fields have found that the association (where there is any) is for the magnetic, not the electrical field (Savitz et al, Amer J Epidem 128:21-38, 1988; London et al, Amer J Epidem 134:923-937, 1991). 3) According to the theory being advanced by the authors, the strong powerline correlation should be with adult lung cancer (not reported in excess), not childhood leukemia. 4) Outdoors, under a powerline, the electrical fields might be strong enough to attract and concentrate radon daughter aerosols, but the outdoor concentrations of radon is generally very low. Since the half-life of the radon daughters is very short (30 minutes is the longest half-life in the decay chain), they are not going to "pile up". Using this as an explanation of the alleged cancer increase in some electrical occupations also has problems. 1) No one appears to have reported an association of cancer with occupational exposure to electrical fields; and you can't assume that electrical field exposure is equivalent to magnetic field exposure, since the correlation between occupational electric and magnetic field exposure is not very strong (Savitz et al, Bioelectromag 15:193-204,1991; Theriault, Rec Res Cancer Res 120:166-180, 1990). 2) Increased exposure to radon would be expected to increase lung, skin and oral/throat cancer, none of which have generally been found in excess in "electrical occupations". 3) The construction and ventilation of most work places is such that high concentrations of radon would not be very common. The British National Radiation Protection Board has made the following comments (14-Feb-96) on the paper. "The authors indicate that electric fields increase plateout of radon daughters present in the air in a room... This is a well-known phenomena. The consequence of increased plateout is that fewer radon daughters will remain in the air to be breathed... The authors of the paper go on to speculate that there may be some mechanism by which electric fields cause radiation doses from the inhalation of radon daughters to be increased, but offer no credible explanation why this should occur. The theory is implausible: the weight of evidence would suggest that the presence of electric fields will, if any thing, slightly reduce human exposure to radon daughters" The NRPB goes on: "There is a well established causal link between exposure to radon daughters and lung cancer... It has not been established that radon daughters cause any other cancers. This reflects differences in doses between the lung and other internal body tissues" and "The position of the Board... is that there is no convincing evidence that the electric and magnetic fields generated by overhead powerlines or electrical apparatus are harmful to health... The paper, which is purely speculative in the issue of radon and EMFs, does not change the Board's view" From owner-emf-bio@net.bio.net Fri Feb 16 22:00:00 1996 Path: biosci!biosci!not-for-mail From: Bill Hickey Newsgroups: bionet.emf-bio Subject: EMF and Radon Date: 17 Feb 1996 15:07:08 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 73 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4g5n2s$koo@net.bio.net> NNTP-Posting-Host: net.bio.net On Friday, 16 Feb 1996 at 09:47:42 GMT, Stewart G. Martin wrote: > ...published by Prof. D. Henshaw (Bristol Univ.) showing that EMF can > act to attract Radon particles with the hypothesis being that the > increased cancers observed....may be explained by the high LET alpha > particles produced from the Radon particles. I would likewise be interested in seeing the original article. It sounds like what we are seeing is yet another trade press "translation" of some scientific work, which is fanning hysteria for no particularly good scientific purpose. As to the good professor's assertion that EMF acts to "attract" Radon atoms, I would like to observe that in high school chemistry, we are taught that the radon atom is chemically inert. Thus, all electron shells are completely filled. On further study, we also learn that the structural distribution of the electrons in the sub-shells is even, thus there is NO residual electron spin imparted to the atom at the quantum level, and thus NO paramagnetic tendency. Since ferro-magnetism is an exclusive property of metals, and diamagnetism (weakly repelling magnetic forces) exists as a natural property of all elements due to the distribution of the electron charge cloud, it would not seem likely that there is scientific or mathematical backing for the professor's theory -- at least on first examination. Since the professor's hypothesis would seem to rely on either ferro- or para-magnetism for the ability of EMF to "attract" radon atoms, I'm at a total loss to explain how he could rationalize this theory. Also, there is no particular "polarity" to the EMF field, since by definition it is a time-varying field, and one of VERY low energy (at power line frequencies) to boot. > ...increased cancers observed from some epidemiological studies...may be > explained (in part) by the high LET alpha particles produced from the > Radon Can we please try to define "high" here? High energy LET (Linear Energy Transfer) alpha particles are usually thought of as being around 30MEv. Natural radioactive decay energies associated with alpha degeneration of Radon are typically well under 10 MEv. In order for a single proton to be included in the LET calculations, it must exceed 30MEv (to produce a single event effect at the atomic level). > The EMF is therefore not inducing the carcinogenic process directly > but via an indirect means by increasing the relative Radon concentrations. The FIRST question we need to ask the good professor is just how the EMF is performing this increase in relative Radon concentration. It can't be magnetic, the atom is electrically and chemically neutral, and if anything is feebly diamagnetic, thus the expected phenomenology would be dispersal not concentration. Sadly, since Radon is itself a decay product, the relative increase in its concentration would more likely be caused by the presence of it's radioactive precursors rather than some other mechanism to increase the incidence of this particularly rare element. What we are finding here in the US is that increased Radon concentrations are being observed more and more as we insulate our houses and businesses better which reduces the air flow (fresh air exchange), thus leaving whatever Radon WAS present in place longer. As to where the study was published, I would probably recommend contacting the professor first, the university second, and the media last to determine where the source work was published. But it would certainly be desireable to examine the original article rather than relying on media hypists for accuracy. My fear is that we have someone who neither understands EMF phenomenology well nor quantum chemistry but who is making hypotheses without mathematical backing which are being simplified and perhaps misinterpreted by the media in an attempt to increase circulation. Sincerely, Bill Hickey bhickey@auc.trw.com From owner-emf-bio@net.bio.net Fri Feb 16 22:00:00 1996 Path: biosci!biosci!not-for-mail From: amarino@UNIXSRV1.LSUMC.EDU (Andrew A. Marino, Ph.D.) Newsgroups: bionet.emf-bio Subject: Mechanisms Date: 17 Feb 1996 14:59:19 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 65 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4g5mk7$jsd@net.bio.net> NNTP-Posting-Host: net.bio.net On February 13, 1996 Dr. Foster expressed doubt regarding the existence of EMF bioeffects, and urged that studies be repeated. His arguments, however, were vague and unreasonable. Dr. Foster asked that proof be furnished that effects are "real." What does that mean? In 1984, for example, Liboff described an effect of EMFs on DNA synthesis in cells. Does Dr. Foster think that the reported cause-and-effect relationship was not real? Or that Dr. Liboff should conduct the experiment again? Or that an independent investigator could obtain funds from, say, NIH, to reproduce the same experiment? Can Dr. Foster provide a specific example of a "real" cause-and-effect relationship in biology so that we could gain insight into his meaning? Dr. Foster said that some reported effects "are barely above the level of line 1statistical uncertainty." What does that mean? How is an investigator supposed to know when the results are more than "barely"? Isn't "barely" enough? Dr. Foster opined that "the noise levels in bioeffects research is incredible." Compared with what? What area of biological research involving cause-and-effect relationships contains studies that have a materially different "noise level"? What is Dr. Foster's objective means of assessing noise levels in various areas of biology? Dr. Foster expressed concern regarding the existence of "artifacts." Is there any reasonable level of scientific inquiry that would persuade Dr. Foster of the reality of observations that he cannot deduce from his knowledge of Maxwell's laws? Take, for example, the reported link between cancer and powerlines. Is not the number of such studies sufficient to establish that a link between the two actually exists? What purpose is served by criticizing studies that are being performed at a scientific level of competence equivalent to that of non-EMF epidemiological studies? Isn't it enough for EMF bioeffects studies to be as good as non-EMF bioeffects studies within the respective scientific disciplines, or is it actually the general state of biology that Dr. Foster deplores? When Dr. Foster applies his "real" meter to the evidence linking cigarettes and cancer, what does it register? If it reads in the "yes" zone, it would be wonderful to have specific citations so that we could see how to perform better studies. If Dr. Foster cannot point to specific studies, as I suspect, then it would be fair to take it as proof that his threshold regarding causality in biology is unreasonable. In the last analysis, Dr. Foster lives in an unrealistic world in which what is "real" is equated with what is deducible from equations, and decisions remain unmade until the level of certainty rises above 95%. That is not, however, how science interacts with society in non-EMF areas. With regard to neither the safety of chemicals in food, the efficacy of medicines, the toxicity of heavy metals in drinking water, nor any other area where society and biology interact, have the standards for reproducibility and certainty advocated by Dr. Foster been applied -- why has Dr. Foster singled out EMFs for such special attention? Regarding, generally, Dr. Foster's ruminations on biology and philosophy: having done essentially none of the former and only a modest, one-sided amount of the latter, should his naked opinion in these areas be accorded any respect? Andrew A. Marino, Ph.D. line 47Professor, Dept. of Orthopaedic Surgery LSU Medical Center - Shreveport P.O. Box 33932 Shreveport, LA 71130-3932 PH: 318-675-6180 FAX: 318-675-6186 From owner-emf-bio@net.bio.net Mon Feb 19 22:00:00 1996 Path: biosci!biosci!not-for-mail From: Bill Hickey Newsgroups: bionet.emf-bio Subject: Re: Radon, Powerlines & Cancer Date: 19 Feb 1996 16:31:35 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 27 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4gb4p7$auq@net.bio.net> NNTP-Posting-Host: net.bio.net On Fri, 16 Feb 1996, John Moulder wrote: > Commentary > ... > an electrostatic precipitator works). For example, it has been known for > years in the radiation safety community that you can pick up radiologically > significant quantities of radon daughters by swabbing a VDT screen. For what it's worth, the screen of a VDT is STATICALLY charged due to the high DC potentials in use. It is NOT an EMF field, per se. Thus, the attraction of any particles is most likely due to the static field, not any residual EMF field. Further, on "reduced radiation" monitors, the powerline magnetic fields are significantly reduced, but you will find line 1that high frequency RF signals are generated galore by these monitors...sufficiently strong enough to cause interference to nearby TV sets on the lower channels. > The jump to a generalized power-frequency field cancer connection is a real > stretch. Agreed. My thanks to John for providing other information and comments on the paper. Bill Hickey Boulder, CO From owner-emf-bio@net.bio.net Mon Feb 19 22:00:00 1996 Path: biosci!biosci!not-for-mail From: Bill Hickey Newsgroups: bionet.emf-bio Subject: Re: Mechanisms Date: 19 Feb 1996 16:34:15 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 39 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4gb4u7$b2e@net.bio.net> NNTP-Posting-Host: net.bio.net On Fri, 16 Feb 1996, Steven Belsky wrote: > Doctors use electric stimulation to heal broken bones, I think the > japaness(?) also use electric current and/or magnets on the body. Let's not confuse electric fields with electric potential, magnetic fields generated by electricity with static magnetic fields, and electromagnetic fields with any of the above. > don't cycltrons use magnets to move atoms? In cyclotrons, positively charged particles are accelerated in a spiral path within dees in a vacuum between poles of a magnet (confinement field), the energy (required for "acceleration") being provided by a high frequency voltage across the dees. There are many ways to move atoms (more properly nuclei or ions), this is but one of them. > I would think by know there would be enough proof that EMF does > effect the body that there would be no need to talk about this > any more If there were enough PROOF, there would indeed be no need to talk about it anymore...since the discussion continues, does that not imply insufficient proof at this point? > AM I WRONG? Quite possibly. > next question: how much will it cost to bury the wires? Someone got into that some time back. I think here in Boulder, the utility company quoted $3 Million to bury a 275kV line for about a mile and a half. Even if that is not a correct or even nearly correct number, the cost is high, and in the vernacular, "a million here and a million there, and pretty soon you're talking about some REAL money." Bill Hickey Boulder, CO From owner-emf-bio@net.bio.net Mon Feb 19 22:00:00 1996 Path: biosci!biosci!not-for-mail From: afrey@uunet.uu.net (Allan Frey) Newsgroups: bionet.emf-bio Subject: replication? Not in biology. Date: 20 Feb 1996 10:08:08 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 59 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4gd2m8$sg2@net.bio.net> NNTP-Posting-Host: net.bio.net A thread running through the current discussion is the notion of "replication". There is no such thing as replication in biology. Replication is a procedure used in the simpler sciences such as physics, but is inappropriate to apply in biology. The problem is that the notion of replication is based upon the implicit assumption that essentially all variables are known. In physics and engineering there are relatively few variables that need to be controlled in an experiment and they are generally known. Thus, replication of the experimental conditions is possible. In contrast, in biological systems there are scores, if not hundreds, of interacting variables and feedback loops, most of which are as yet unknown or poorly understood. Biologists recognize this and, in general, don't use inappropriate notions like "replication" from other sciences . That is why there are rarely any funds applied for or granted in biology for replication. To do so is to engage in fantasy. If there is an interesting finding, biologists design related experiments to build on the finding. After enough such experiments, the interacting variables start getting identified and we have an advance in knowledge; this puts the original observation in a context and makes it interpretable. The misapplication of the notion of replication simply illustrates the fact that the emf-bio area is unusual in biology. It initially evolved out of the engineering and physics communities concern about hazards and they continue to be deeply involved. As a consequence, the biological research has been encumbered with inappropriate (for biology) notions. This has hindered, distorted and delayed the development of the biological science (1-3). Though understandable, this has unfortunate consequences for biology, policy makers and the companies that sell products that emit emf For the companies, the distortion and delays in the development of the biological science expose them to the specter of financial disaster such as that which overwhelmed the asbestos companies and appears to be overtaking the tobacco companies. 1. Frey, A.H. Overview and perspective. Chapter in On the nature of electromagnetic field interactions with biological systems. A. H. Frey, (ed.), R. G. Landes Co., Austin, 1994 2. Frey, A.H. The evolution and more significant results of biological research with low intensity non-ionizing radiation. Chapter in Modern Bioelectricity, A. Marino, (ed.), Marcel Dekker, NYC, 1988. 3. Frey, A.H. From the laboratory to the courtroom: Science, scientists, and the regulatory process. Chapter in Risk/Benefit Analysis: The Microwave Case, N.H. Steneck (ed.) , San Francisco Press, 1982. Allan Allan H. Frey email afrey@uunet.uu.net 11049 Seven Hill Lane voice 301.299.5181 Potomac, MD 20854, USA From owner-emf-bio@net.bio.net Tue Feb 20 22:00:00 1996 Path: biosci!biosci!not-for-mail From: "Kenneth R. Foster" Newsgroups: bionet.emf-bio Subject: Replication in biology, cont'd Date: 21 Feb 1996 09:38:09 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 46 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4gfla1$4fu@net.bio.net> NNTP-Posting-Host: net.bio.net Frey wrote: >A thread running through the current discussion is the notion of >"replication". There is no such thing as replication in biology. >Replication is a procedure used in the simpler sciences such as physics, >but is inappropriate to apply in biology. The problem is that the notion of >replication is based upon the implicit assumption that essentially all >variables are known. Actually, there is no replication in any experimental science. Nothing can be replicated. Moreover, philosophers have long talked about "experimenter's regress". One can always argue that the failure to confirm someone else's experiment is the result of some subtle mistake on the part of the second investigator. Thus, if investigator A says "cats can fly", and investigator B says "I couldn't observe the effect", investigator A can reply "you didn't kick it hard enough" or "the effect only occurs on a witches' sabbath." But science progresses in spite of this philosophical problem,. It progresses by other scientists making use of the results and building on them. Scientists are still arguing whether the unsuccessful attempts to confirm cold fusion were replications of Pons and Fleischmann's experiments. Those arguments can go on forever. Cold fusion is dead nevertheless. A chronic problem in EMF bioeffects research is much more elementary. Investigator A does a quick-and-dirty experiment and reports an effect. Investigator B does a more carefully controlled series of experiments to follow up the previous work, and finds no effct. Moreover he/she finds all sorts of potential artifacts that might have led to the first investigator into error. Whether or not the original study was "replicated" or not is hardly the point. Unless investigators (collectively) can come to some agreement about the experimental conditions under which a phenomenon can be observed AND MOVE FORWARD in studying it, nothing will have been accomplished. As John Ziman observed, science is ruled by the Royal Boot, and unsuccessful attempts at following up other studies is the Royal Boot in action. Kenneth R Foster Department of Bioengineering University of Pennsylvania 220 S. 33rd St. Philadelphia PA 19104-6392 215-898-8534 fax 215-573-2071 From owner-emf-bio@net.bio.net Tue Feb 20 22:00:00 1996 Path: biosci!biosci!not-for-mail From: armins@asiaonline.net (Armin Schon) Newsgroups: bionet.emf-bio Subject: Re: mechanisms discussion Date: 21 Feb 1996 09:34:46 -0800 Organization: Asia On-Line Limited, Wanchai, Hong Kong. Lines: 31 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4gfl3m$3vu@net.bio.net> References: <4fd7q6$3oc@net.bio.net> Reply-To: armins@asiaonline.net NNTP-Posting-Host: net.bio.net Spadaroj@VAX.CS.HSCSYR.EDU (Joe Spadaro) wrote: > Case in point: In bone cells and tissues, a number of effects of >magnetic field effects have been found, and recently some hint of the sites >of action have begun to emerge. Usually, these involve pulsing waveforms >with rms or peak intensities in the 1-10 G range with exposures from >minutes to days. Now, bone cells are not brain cells or leukocytes, but line 1>they are nice cells too. How do findings of this type bear on the >50-60Hz, <100 mG, sine-wave problem? The most reasonable mechanism I heard of recently is the magnetic field related suppression of Melatonin synthesis, which serves as a natural cancer drug by neutralizing free radicals. A recent study (not yet published in English, I think) by a group of the University of Hannover, Germany, showed a linear correlation between breast cancer in rats and magnetic field exposure. They induced the cancer by cancerous chemicals and studied histologically how often the cancer broke out and how severe it became after a couple of month. An increase in cancer onset and severeness was observed in rats with a permanent exposure to fields as little as 1 uT (10 mG)! I would be very interested in those findings concerning the mechanisms in bone cells that you mentioned - could you elaborate a little on that? Concerning your question: I don't think one can make a general rule here about the "scale-invariance" of a mechanism. You really have to understand exactly how a mechanism works in order to make extrapolations from high fields to low fields. Threshold behavior and non-linearities could just ruin the nice concept totally. From owner-emf-bio@net.bio.net Tue Feb 20 22:00:00 1996 Path: biosci!biosci!not-for-mail From: liboff@oakland.edu (A.R. Liboff) Newsgroups: bionet.emf-bio Subject: mechanisms discussion Date: 20 Feb 1996 19:35:05 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 50 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4ge3t9$m6o@net.bio.net> NNTP-Posting-Host: net.bio.net Ken Foster suggests that it is more important to determine if the "effects" are "real" rather than worry about mechanisms. I do not understand this distinction. Part of the process of determining whether an experimental result is real is to establish its connection to the body of knowledge. Would Foster have as much problem with the experimental results if they agreed with what he expected? Indeed this question of the missing mechanism is really at the heart of the difficulty that Foster and others have with the existing data. Their problem has less to do with reproducibility and signal-to-noise than it has to do with making the results reasonable. On the day that a credible mechanism emerges,the bulk of such criticism will cease. Part of the problem in this research area relates to the distinction between science and engineering. I like to believe that I am involved in scientific exploration, that is, trying to explain some things that are difficult to explain. It is the very fact that these things are difficult to explain that makes them worthwhile investigating, that makes this field so exciting. I fear that some do not share this sense of excitement. Perhaps they tend to look at this area of research in terms of what they already know, and not in terms of what may be learned. There have been many times in the history of science where new discoveries came out of experimentation that gave barely discernible results, seen by some observers and not by others. A good example is found in the beginning of the 20th century, in the decade before the discovery of cosmic radiation. There were bitter remarks directed at those who claimed to be detecting extra ionization in the air, even in the absence of radioactive substances. Some investigators saw these effects and others did not. Critics (some quite prominent) ascribed this extra ionization to experimental error due to leakage on electroscope surfaces. Not until Victor Hess flew a balloon with an electroscope was the source of this ionization properly identified. Of course criticism is as much a part of science as is observation and theory. At what point, however, does scientific criticism change from constructive to obstructive? I believe that weak-field biological interactions have been adequately demonstrated, beyond the point where it is reasonable to argue about their existence. There may be specific experiments that are suspect, but the general body of work is presently too strong to ignore. It seems pointless and out-of-step to continue this type of criticism, when the rest of us are seeking credible physical mechanisms to explain what we observe in the laboratory. A.R. Liboff liboff@oakland.edu Dept of Physics Oakland Univ Rochester, MI 48309 From owner-emf-bio@net.bio.net Tue Feb 20 22:00:00 1996 Path: biosci!biosci!not-for-mail From: liboff@oakland.edu (A.R. Liboff) Newsgroups: bionet.emf-bio Subject: mechanisms discussion Date: 20 Feb 1996 19:33:11 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 95 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4ge3pn$m34@net.bio.net> NNTP-Posting-Host: net.bio.net A recent statements by Joe Spadaro suggested that it may be worthwhile to "start" examining the "mechanisms" issue by looking at the results in bone, where "higher field strengths" and "pulsed waveforms" are employed. Some critical comments: As I have pointed out on other occasions, there has been too much emphasis on the 50/60 Hz cancer problem, and not nearly enough on the more basic laboratory-oriented research dealing with weak-field interactions in cells and simple systems. Contrary to what is often claimed, this lab work is on firm ground, with an extensive literature, [see, e.g. Norden and Ramel, Interaction Mechanisms of Low-Level EM Fields, 1992; Blank,E & M in Biology and Medicine, 1992; Polk and Postow, Handbook of Biological Effects of EM Fields..., 1996.] The cancer problem is merely the tip of the iceberg, one small aspect of a much larger, weak-field biointeractions problem. My opinion is that, for the most part,laboratory findings tend to support an ion cyclotron resonance [ICR] mechanism. Related approaches include terms such as combined magnetic fields, ion parametric resonance, ion precessional resonance, gyromagnetic resonance, etc. All such approaches are characterized by a signature for which tuning the magnetic field combination to the charge-to-mass ratio of specific biological ions, notably calcium, results in extrema in the biological response.This ICR approach has been incorporated into an FDA-approved bone repair device [Orthologic] that apparently is as effective, (if not more so), than the pulsed, high field strength devices mentioned by Spadaro. This, despite the fact that the ICR device uses sine waves at field strengths well below one Gauss, implying that one need not "start" with high pulsed fields. A series of recent articles related to this ICR device has been published by a group in the VA Hospital in Loma Linda; [see, Fitzsimmons et al, "Combined magnetic fields increased net calcium flux in bone cells, Calc Tissue Int (1994) 55:376-380; Combined magnetic fields increase insulin-like growth factor-II in TE-85 human ostreosarcoma bone cell cultures, Endocrinology (1995) 136:3100-3106; IGF-II Receptor number is increased in TE-85 osteosarcoma cells by combined magnetic fields, J of Bone and Mineral Research (1995) 10:812-819.] The development of this ICR bone device followed years of research, dating back to 1984. This research continues unabated, despite the many reasons proffered as to why any interaction of this type is unlikely. There are too many ICR reports to listevery one, but among my favorites are: Thomas et al, Low-intensity magnetic fields alter operant behavior in rats, BEMS,7: 349-357 (1986). This was the first experimental report published. The effect of ICR exposures on rat learning has now been augmented by Battelle PNL (Lovely et al in BEMS abstracts), and by Lyskov in St. Petersburg. Smith et al, Calcium cyclotron resonance and diatom motility, BEMS 8: 215-227 (1987). Rozek et al, Nifedipene is an antagonist to cyclotron resonance enhancement of 45Ca incorporation in human lymphocytes, Cell Calcium 8:413-427, (1987). Ross, Combined DC and ELF magnetic fields can alter cell proliferation, BEMS 11: 27-36, (1990). Lerchl et al, Evidence of an ion-cyclotron-resonance effect on pineal melatonin synthesis in vitro, Neuroscience Lett 124: 213-215 (1991). Yost and Liburdy, Time-varying andstatic magnetic fields act in combination to alter calcium signal transduction in the lymphocyte. FEBS Lett 296:117-122 (1992). Diebert et al, Ion resonance electromagnetic field stimulation of fracture healing in rabbits with a fibular ostectomy, J of Orthopedic Research 12: 878-885 (1994) Jenrow et al, Weak ELF fields and regeneration in the planarian Dugesia tigrina, BEMS 16: 106-112 (1995) Smith et al, Effects of CR-tuned 60 Hz magnetic fields on sprouting and early growth of Raphanus sativus. Bioelectrochemistry and Bioenergetics 32:67-76 (1993). These papers (and those reported by Fitzsimmons et al above) are a fraction of all the reports on ICR. Further, the total of all ICR reports constitute only a fraction of all the reports on weak magnetic and electric field bioeffects. Many, if not most of these works, do not include studies dealing specifically with cancer. Thus when I read statements about weak magnetic field "mechanisms". my mind jumps not to cancer, but rather to this large body of experimental work. For me, the critical question is how to theoretically explain these effects, that is, how to make them physically credible.I have concluded that the only option is to examine the existing body of work and use this knowledge to design new better experiments, and to continue this process until there are enough clues to propose a reasonable explanation(s). A.R. Liboff liboff@oakland.edu Dept of Physics Oakland Univ Rochester, MI 48309 From owner-emf-bio@net.bio.net Thu Feb 22 22:00:00 1996 Path: biosci!biosci!not-for-mail From: "Robert M. Patterson" Newsgroups: bionet.emf-bio Subject: Re: Replication in biology, cont'd Date: 22 Feb 1996 18:20:50 -0800 Organization: Temple University, Academic Computer Services Lines: 59 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4gj8a2$1rq@net.bio.net> References: <199602211738.JAA04618@net.bio.net> NNTP-Posting-Host: net.bio.net The following short excert from a commencement address by Richard Feynman seems quite appropriate in light of this discussion. The full text on "Cargo Cult Science" appears in the book, "Surely You're Joking Mr. Feynman!" Robert M. Patterson Temple University For example, there have been many experiments running rats through all kinds of mazes, and so on--with little clear result. But in 1937 a man named Young did a very interesting one. He had a long corridor with doors all along one side where the rats came in, and doors along the other side where the food was. He wanted to see if he could train the rats to go in at the third door down from wherever he started them off. No. The rats went immediately to the door where the food had been the time before. The question was, how did the rats know, because the corridor was so beautifully built and so uniform, that this was the same door as before? Obviously there was something about the door that was different from the other doors. So he painted the doors very carefully, arranging the textures on the faces of the doors exactly the same. Still the rats could tell. Then he thought maybe the rats were smelling the food, so he used chemicals to change the smell after each run. Still the rats could tell. Then he realized the rats might be able to tell by seeing the lights and the arrangement in the laboratory like any commonsense person. So he covered the corridor, and still the rats could tell. He finally found that they could tell by the way the floor sounded when they ran over it. And he could only fix that by putting his corridor in sand. So he covered one after another of all possible clues and finally was able to fool the rats so that they had to learn to go in the third door. If he relaxed any of his conditions, the rats could tell. Now, from a scientific standpoint, that is an A-number-one experiment. That is the experiment that makes rat-running experiments sensible, because it uncovers that clues that the rat is really using-- not what you think it's using. And that is the experiment that tells exactly what conditions you have to use in order to be careful and control everything in an experiment with rat-running. I looked up the subsequent history of this research. The next experiment, and the one after that, never referred to Mr. Young. They never used any of his criteria of putting the corridor on sand, or being very careful. They just went right on running the rats in the same old way, and paid no attention to the great discoveries of Mr. Young, and his papers are not referred to, because he didn't discover anything about the rats. In fact, he discovered all the things you have to do to discover something about rats. But not paying attention to experiments like that is a characteristic example of cargo cult science. Another example is the ESP experiments of Mr. Rhine, and other people. As various people have made criticisms--and they themselves have made criticisms of their own experiements--they improve the techniques so that the effects are smaller, and smaller, and smaller until they gradually disappear. All the para-psychologists are looking for some experiment that can be repeated--that you can do again and get the same effect--statistically, even. They run a million rats--no, it's people this time--they do a lot of things are get a certain statistical effect. Next time they try it they don't get it any more. And now you find a man saying that is is an irrelevant demand to expect a repeatable experiment. This is science? From owner-emf-bio@net.bio.net Thu Feb 22 22:00:00 1996 Path: biosci!biosci!not-for-mail From: Michael Kolios Newsgroups: bionet.emf-bio Subject: Re: replication? Not in biology. Date: 23 Feb 1996 11:14:27 -0800 Organization: University of Toronto / Ontario Cancer Institute Lines: 75 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4gl3mj$bga@net.bio.net> References: <4gd2m8$sg2@net.bio.net> NNTP-Posting-Host: net.bio.net Allan Frey wrote: > but is inappropriate to apply in biology. The problem is that the notion of > replication is based upon the implicit assumption that essentially all > variables are known. I do not think this is truly the case. There is no doubt that in biological systems there are many parameters that interact in a non-linear way to give some end result. However, this end result should be fairly reproducible. If someone irradiates a population of cells, the surviving fraction as a function of the dose is reproducible. This extends to animal systems too. The data from these experiments has been used to define guidelines as to which exposures are considered dangerous or not. In the case of low doses of radiation, extrapolations have been made based on available data. I am sure that the actual process by which this happens, while fairly well understood now, at some point i t was not. However, people knew that irradiation can have harmful effects, even though they did not know the exact mechanism. > understood. Biologists recognize this and, in general, don't use > inappropriate notions like "replication" from other sciences . That is why > there are rarely any funds applied for or granted in biology for replication. > To do so is to engage in fantasy. If there is an interesting finding, > biologists design related experiments to build on the finding. After enough > such experiments, the interacting variables start getting identified and > we have an advance in knowledge; this puts the original observation in a > context and makes it interpretable. This is not the way science should be done in my opinion. If you cannot show tha t an experiment can be done again (or show consistency in an epidemiological finding), you should be wary of the conclusions. If the cold fusion experiment was not attempted to be repeated, we would all believe in it. To go to biologica l examples, if I irradiated a population of mice with 100Gy and all died but in another experiment by another group none did, then I would be very skeptical about my experiments, much more about my conclusions. And if I wanted to implement protective measures, this end point is important and should not be disputed. I could not care less about the mechasisms at this point. They might take eons to figure out (even though when they do, we could make much better regulations). > The misapplication of the notion of replication simply illustrates the fact > that the emf-bio area is unusual in biology. It initially evolved out of the > engineering and physics communities concern about hazards and they > continue to be deeply involved. As a consequence, the biological research > has been encumbered with inappropriate (for biology) notions. This has > hindered, distorted and delayed the development of the biological science > (1-3). Though understandable, this has unfortunate consequences for > biology, policy makers and the companies that sell products that emit emf > For the companies, the distortion and delays in the development of the > biological science expose them to the specter of financial disaster such > as that which overwhelmed the asbestos companies and appears to be > overtaking the tobacco companies. The emf-bio area is unusual because we do not understand it. So was radiation. No doubt that if it can be shown that there is some cause-effect relationship, even if it is not understood, protective measures should be taken. However, one must first establish this. It is my limited understanding, not being in the fiel d and by occasionally glancing at reports of well respected scientific bodies, tha t this is very much disputed, and there are conflicting reports. If such, the protective measures should be delayed until harmful effects are shown, especiall y if those measures will cost dearly to society as a whole. Mike ----------------- Michael C. Kolios Dept. Medical Biophysics / Hyperthermia group mkolios@oci.utoronto.ca University of Toronto (416) 946-2000 x5767 "Pan Metron Ariston" From owner-emf-bio@net.bio.net Thu Feb 22 22:00:00 1996 Path: biosci!biosci!not-for-mail From: jmoulder@its.mcw.edu (John E. Moulder) Newsgroups: bionet.emf-bio Subject: Re: mechanisms discussion Date: 23 Feb 1996 11:17:00 -0800 Organization: Medical College of Wisconsin Lines: 64 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4gl3rc$bt2@net.bio.net> References: <4ge3pn$m34@net.bio.net> NNTP-Posting-Host: net.bio.net In article <4gfl3m$3vu@net.bio.net>, armins@asiaonline.net (Armin Schon) writes: > The most reasonable mechanism I heard of recently is the magnetic > field related suppression of Melatonin synthesis, which serves as > a natural cancer drug by neutralizing free radicals. At the moment, that mechanism has some real problems. First, the evidence that power-frequency magnetic fields actually suppress melatonin is very weak. Most of the supporting data is for ELF electric fields, static magnetic fields and pulsed static magnetic fields, none of which have any real relevance for residential exposure to powerline fields. Actually they don't have much relevance for most exposure in "electrical occupations" either. In humans, the best evidence is that power-frequency fields don't suppress melatonin [Graham et al, Contracter's meeting, 93,94,95]). Similarly, no effects have been seen in sheep exposed to 4 microT fields [Lee et al, Bioelectromag, 95], and no reproducible effects were seen in Siberian hamsters at 100 microT [Yellon, J Pineal Res, 94]. In rats AC magnetic field effects on melatonin are erratic, occur mostly for field intensities well above those found in residences, and do not result in increased cancer [Kato et al, Neurosci Let, 93, 94; Loscher et al, Oncology, 94]. The notion that melatonin has anti-carcinogenesis properties is on pretty thin grounds also. Reiter et al [Neuroendicrin Lett, 93] published some in vitro data supporting this idea in 1993, but I haven't seen anything since. There does not appear to be any peer-reviewed data suggesting that melatonin has anti-carcinogenesis properties in humans. There is animal data suggesting that melatonin has both anti-cancer and anti-carcinogenesis properties for breast cancer, but this could be explained by the fact that it is a weak anti-estrogen. A recent study (not yet published in English, I think) by a group of > the University of Hannover, Germany, showed a linear correlation > between breast cancer in rats and magnetic field exposure. They > induced the cancer by cancerous chemicals and studied histologically > how often the cancer broke out and how severe it became after a couple > of month. It is published: W Loscher & M Mevissen: Linear relationship between flux density and tumor co-promoting effect of prolonged magnetic field exposure in a breast cancer model. Cancer Letters 96:175-180, 1995. > An increase in cancer onset and severeness was observed in rats with > a permanent exposure to fields as little as 1 uT (10 mG)! No. They found no effect at all at 0.3-1 or 10 microT (91 days of continuous exposure), and had to go to 50 microT to find an effect that they considered statistically significant. Even the significance of their observation at 50 and 100 microT is open to question (see letters in the Nov/Dec issue of the BEMS newsletter). The problem is that they used a very high doses of their chemical carcinogen (DMBA) so that the rate of cancer in the shams was very high (51%), and highly variable (35-61%) between groups. The above debate cannot be resolved without knowing the tumor incidence in each arm, and this raw data is not included in the Cancer Letters publication. Their data is compatible with a linear relationship between field intensity and promotion, but it is also compatible with a threshold substantially above 10 microT. From owner-emf-bio@net.bio.net Thu Feb 22 22:00:00 1996 Path: biosci!biosci!not-for-mail From: Bill Hickey Newsgroups: bionet.emf-bio Subject: Re: Replication in biology, cont'd Date: 23 Feb 1996 11:12:49 -0800 Organization: BIOSCI International Newsgroups for Molecular Biology Lines: 35 Sender: daemon@net.bio.net Approved: afrey@uunet.uu.net Distribution: world Message-ID: <4gl3jh$bau@net.bio.net> NNTP-Posting-Host: net.bio.net On Thu, 22 Feb 1996, Robert M. Patterson wrote: > And now you find a man saying that is is an irrelevant demand to expect > a repeatable experiment. This is science? No it is not. A fundamental precept of science is that any experiment MUST be repeatable (certainly within reasonable bounds of error) for confirmation purposes. Last time I checked, Biologists called themselves scientists. If they wish to use that title, they must follow the same rules for other sciences, or they are nothing but artists. If they choose to be artists, then we will NEVER end the arguments about whether something (like EMF) is (biologically) active or not. The term "science" means more than just a collection of facts or knowledge. Science is a body of models and generalizations that allow us to systematize and correlate observed facts which allow us to make predictions which will agree with subsequent observations or experiments. >From my college physics text, a definition of the scientific method which appears to be pretty consistent with those I've seen in other basic texts: "The scientific method is the systematic attempt to construct theories that correlate wide groups of observed facts and are capable of predicting the results of future observations. Such theories are tested by controlled experimentation and are accepted only so long as they are consistent with all observed facts." The fact that biological systems are more, less, or equally complex as any those in other scientific disciplines has no bearing whatsoever on the requirement that experiments be repeatable. It merely means the biologist must be all the more careful in constructing the experiment and any validating studies. Bill Hickey Boulder, CO