------- Forwarded Message Follows ------- Date: Sat, 27 Feb 1999 11:14:41 -0700 To: healthfraud@ssr.com From: Larry Sarner Subject: [healthfraud] Non-science at Philly Alt-Health Conference A few days ago, Becky Long posted to this list a press release from CSICOP that some new some "scientists" would reveal new research on Human Energy Fields (HEFs) at CSICOP's Alternative Health Conference in Philadelphia this weekend. I'm afraid the "research" turns out to be a bit of a bust. It is likely to be a non-starter, both with the press and those concerned with Therapeutic Touch (TT) and "energy medicine." For those on this list who fall in the latter category might read on. The principal problem with this study is that it has no reason to exist, much less to be presented at conference orlater published. It makes no contributions. It addresses no known problems. The study is, "Perception of Conventional Sensory Cues as an Alternative to the Postulated 'Human Energy Field' of Therapeutic Touch," by Rebecca Long herself, with Paul Bernhardt doing the statistics. Its stated objectives were: * To determine whether human subjects can "perceive" the presence of a human hand which they cannot see * To investigate the role of conventional sensory cues * To establish data and protocol baselines for future TT testing of the Perceptibility Postulate The conclusions related to these objectives were: "Subjects can 'perceive' the presence of the experimenter's hand over the distance range at which TT is practiced, 3 to 6 inches. Because we [the experimenters] were able to eliminate the effect by interposing glass, which does not transmit infrared efficiently, the most likely explanation for what subjects feel is body heat. The Burden of Proof is now on TT Practitioners to exceed this baseline." Actually, the data presented does not support these conclusions. Also, the methodology was quite poor for testing what was in reality a jumble of experimental hypotheses. But the more significant problem is that last sentence. It is likely to give TT proponents a field day on how "skeptics" cannot think critically. A brief description of what was reportedly done in this experiment: The protocol was similar to that of the Rosa experiment (JAMA, 1 Apr 1998), differing only in a number of unimportant procedural alterations. 27 non-practitioners of TT were tested; 14 in one group, using the hand of an 11-year-old female as a target; 13 in another group, using the hand of an adult female as a target. Trials were run at 3, 4, and 6 inches of separation, (inexplicably) in groups of 9 and 12. They included two sets of trials which introduced "negative cuing" in one and interposing a "glass" barrier in the other. Supposedly statistically significant results were reported for 3" (means=76% accuracy and 77%), 4" (mean=65%). Non-significance was reported for 6" (mean=58%), the negative cuing--also done at 6" (mean=39%), and the glass barrier at 3" (mean=52%). Since there is nothing conclusive in the statistics, that alone dismisses this study as unimportant. But since it is already being trumpeted around anyway, let's focus on the last conclusion ("Burden of Proof is now on TT Practitioners") as a lesson in critical thinking. The claim is that this experiment shows the ability of human subjects to sense radiant body heat through the hands. Such ability has already been investigated by Schwartz, Russek & Beltran in 1995. Because of the methodological problems in Long's study as study in perception of radiant body heat, her results even if statistically valid would add be questionable. Even if those problems were inconsequential (and they're not), she adds nothing to the body of knowledge that Schwartz et al. (even with all THEIR problems) were already contributing. At best, Long was engaged in a replication of Schwartz. So, are Schwartz and Long relevant to studies of the practice of TT, even when using (more or less) the Rosa protocol? Nope. A study of the ability a small number of non-practitioners to detect radiant body heat--EVEN IF WELL DONE AND VALID, WHICH THIS WASN'T--says nothing about the practice of TT by those who claim to practice TT. The fact is, the Rosa study (which has very little wrong with it, methodologically or epistomologically) said all that needed to be said: Plunk a bunch of trained practitioners in front of a "patient" and challenge them to detect the patient's energy field. They didn't. So why do a test, as Long has, to explain the practitioners' detection of the HEF, when they DIDN'T do so? There's no problem to solve here: practitioners have yet to demonstrate any real abilities; so why are you testing for POSSIBLE explanations for the day when they MAY do so? And in any event, you can't explain away practitioners' (even imagined) abilities when you aren't using any practitioners in your test! Even if one considers all this as intended as a refutation of Emily Rosa's protocol (as I think may be a sly subtext for Long's work), there are still epistomological problems. Emily Rosa tested 21 practitioners in 28 trials. Had Long successfully demonstrated that radiant heat is detectable by non-practitioners within the same testing range, it still says nothing about *practitioners* under the same testing conditions. Practitioners claim to go into an altered state of consciousness (called "centering") before going after the HEF. Perversely for them, perhaps centering psychologically cuts them off from more mundane cues such as body heat. Or there could be other explanations for failure. In short, Long's experiment is a non sequitor to TT practice and hence to Emily's experiment. Far from establishing a "baseline" for TT practitioners to somehow "exceed", Long's study conveys the impression that TT opponents are unfairly moving the goalposts. The Rosa study already set the bar at a point where practitioners have not cleared. There was no need for another study to raise the bar higher. It's like setting the bar higher for a pole vaulter after he misses at a lower height. It makes it difficult for those of us in the frontlines on TT to have someone like Long come along and muddy the waters, especially when it was so completely unnecessary. If someone at CSICOP, Prometheus, ScRAM, or even this list, had contacted us about this experiment and allowed us to comment privately, we could have saved them a lot of embarrassment, the health-fraud movement a lot of trouble, and this list a very long post. ************************************************************************* * Send mail to healthfraud-help@ssr.com for a list of available commands, * including help in UNSUBSCRIBING... * * DO NOT, NOT, NOT, SEND SUBSCRIBE/UNSUBSCRIBE REQUESTS TO THE LIST. ************************************************************************ ------- Forwarded Message Follows ------- Date: Sat, 27 Feb 99 23:34:00 -0700 From: Paul Bernhardt To: "Healthfraud" Subject: Re: [healthfraud] Non-science at Philly Alt-Health Conference Larry Sarner said on 2/27/99 11:14 AM: >A few days ago, Becky Long posted to this list a press release from CSICOP >that some new some "scientists" would reveal new research on Human Energy >Fields (HEFs) at CSICOP's Alternative Health Conference in Philadelphia >this weekend. I'm afraid the "research" turns out to be a bit of a bust. >It is likely to be a non-starter, both with the press and those concerned >with Therapeutic Touch (TT) and "energy medicine." For those on this list >who fall in the latter category might read on. > >The principal problem with this study is that it has no reason to exist, >much less to be presented at conference orlater published. It makes no >contributions. It addresses no known problems. You certainly have a right to your opinion, but in the opinion of the committee reviewing presentations for the CSICOP conference Ms Long's study does make a contribution which they feel should be publicly presented. If and when it is offered for publication to a journal the editors and reviewers of that journal will have the opportunity to make the same decision, regardless of your opinion. > >The study is, "Perception of Conventional Sensory Cues as an Alternative to >the Postulated 'Human Energy Field' of Therapeutic Touch," by Rebecca Long >herself, with Paul Bernhardt doing the statistics. Its stated objectives >were: > > * To determine whether human subjects can "perceive" the presence of a >human hand which they cannot see > * To investigate the role of conventional sensory cues > * To establish data and protocol baselines for future TT testing of the >Perceptibility Postulate > >The conclusions related to these objectives were: > >"Subjects can 'perceive' the presence of the experimenter's hand over the >distance range at which TT is practiced, 3 to 6 inches. Because we [the >experimenters] were able to eliminate the effect by interposing glass, >which does not transmit infrared efficiently, the most likely explanation >for what subjects feel is body heat. The Burden of Proof is now on TT >Practitioners to exceed this baseline." > >Actually, the data presented does not support these conclusions. Also, the >methodology was quite poor for testing what was in reality a jumble of >experimental hypotheses. But the more significant problem is that last >sentence. It is likely to give TT proponents a field day on how "skeptics" >cannot think critically. The methodology was virtually identical to yours in the Rosa, et al (1998; JAMA) study. So, to the extent that you consider Ms Long's methodology flawed, you should consider your own study flawed. Ms Long's deviations from the Rosa protocol were to facilitate examination of variables of importance for studying the HEF phenomena (that is, heat and voice cueing). > >A brief description of what was reportedly done in this experiment: > >The protocol was similar to that of the Rosa experiment (JAMA, 1 Apr 1998), >differing only in a number of unimportant procedural alterations. 27 >non-practitioners of TT were tested; 14 in one group, using the hand of an >11-year-old female as a target; 13 in another group, using the hand of an >adult female as a target. Trials were run at 3, 4, and 6 inches of >separation, (inexplicably) in groups of 9 and 12. They included two sets >of trials which introduced "negative cuing" in one and interposing a >"glass" barrier in the other. Supposedly statistically significant results >were reported for 3" (means=76% accuracy and 77%), 4" (mean=65%). >Non-significance was reported for 6" (mean=58%), the negative cuing--also >done at 6" (mean=39%), and the glass barrier at 3" (mean=52%). The results had not been made public at the time of your posting your message to Healthfraud. Ms Long will present her report in the AM on Sunday, Feb 28. Your posting was in the AM of Saturday Feb 27. The press release only barely mentioned that a TT study would be presented and there had been no public presentation of her findings. The only location that you could have gotten the above statistical values is from the password protected web site that Ms Long had posted a *draft* of the presentation. The draft clearly states: "THIS IS A PROPRIETARY DRAFT, COPYRIGHT REBECCA LONG, BEING MADE AVAILABLE FOR PEER REVIEW ONLY. IT IS ******NOT FOR DISSEMINATION******* " Your presentation of information and quoting from Ms Long's draft presentation is, IMO, ethically questionable. You don't indicate the probabilities associated with each finding. Incomplete revelation of findings is also, IMO, ethically questionable. But I have permission from Ms Long, so I can identify specifically which ones were significantly different from chance accuracy (50%): 3 inch (for each experimenter, no glass) probability < .0001, 4 inch probability = .01, 6 inch distance (no cueing) probability=.075 (marginal significance), 6 inch with negative cueing probability = .066 (marginal significance), 3 inches with glass probability = .53 (not significant). Not mentioned by you is the test of accuracy of detection between the 3 inch with and without glass. These conditions were significantly different at probability less than .0001. Not mentioned by you is the test of linear association between accuracy and distance which showed a significant linear regression equation where accuracy dropped off with distance. This is consistent with known radiative fields such as heat (actually a power equation is the likely best fit, but was not possible to develop with only 3 measurement points and regression methods). It may be consistent with the Human Energy Field, but the failure to sense through glass suggests heat was the cueing mode for these non-TT practitioners. All significances reported in Ms Long's study are 2-tailed significances. > >Since there is nothing conclusive in the statistics, that alone dismisses >this study as unimportant. But since it is already being trumpeted around >anyway, let's focus on the last conclusion ("Burden of Proof is now on TT >Practitioners") as a lesson in critical thinking. The burden of proof statement makes sense in the context that TT practitioners claim to be able to sense through common materials such as glass. Glass effectively removed the apparent cue of body heat. Therefore, TT practitioners do have a burden of proof to exceed these levels of accuracy. > >The claim is that this experiment shows the ability of human subjects to >sense radiant body heat through the hands. Such ability has already been >investigated by Schwartz, Russek & Beltran in 1995. Because of the >methodological problems in Long's study as study in perception of radiant >body heat, her results even if statistically valid would add be >questionable. Even if those problems were inconsequential (and they're >not), she adds nothing to the body of knowledge that Schwartz et al. (even >with all THEIR problems) were already contributing. At best, Long was >engaged in a replication of Schwartz. Replication is a fundamental process by which science advances. Therefore, replication is a valuable addition. Endless replication is not valuable. I don't know, have there been other replications of Schwartz, et al, if indeed her study is a replication (you don't provide sufficient details of the study to evaluate)? >Even if one considers all this as intended as a refutation of Emily Rosa's >protocol (as I think may be a sly subtext for Long's work), there are still >epistomological problems. You are reading things into Ms Long's draft report. She makes no statement as the relevance of her study to Rosa, except as a basis for methodology and reference for comparison. > Emily Rosa tested 21 practitioners in 28 trials. >Had Long successfully demonstrated that radiant heat is detectable by >non-practitioners within the same testing range, it still says nothing >about *practitioners* under the same testing conditions. Practitioners >claim to go into an altered state of consciousness (called "centering") >before going after the HEF. Perversely for them, perhaps centering >psychologically cuts them off from more mundane cues such as body heat. Or >there could be other explanations for failure. In short, Long's experiment >is a non sequitor to TT practice and hence to Emily's experiment. Therefore, let them do better than untrained persons in the same situation. The situation with untrained persons has been established, let the trained persons demonstrate their special skills. > >It makes it difficult for those of us in the frontlines on TT to have >someone like Long come along and muddy the waters, especially when it was >so completely unnecessary. If someone at CSICOP, Prometheus, ScRAM, or >even this list, had contacted us about this experiment and allowed us to >comment privately, we could have saved them a lot of embarrassment, the >health-fraud movement a lot of trouble, and this list a very long post. > Discussion of findings, challenging of findings, and resolving contrary findings is all part and parcel of all sciences. It is not personal and it is not about public image. Indeed, any science that has no internal disputes is automatically suspect in my book. It is about truth as best as we can ascertain it with the tools we have. About a week ago, one of the authors of the Rosa, et al (JAMA) study was given access to the draft copy (mentioned above) of Ms Long's presentation prior to it's public release. Therefore, your statement above about not being contacted is simply wrong. I don't think you'll see any embarrassment on Ms Long's part (or mine) regarding this presentation. What kind of trouble or embarrassment could have been saved, or how you would have gone about saving it is an outside issue. Science is what matters. Paul Bernhardt ************************************************************************* * Send mail to healthfraud-help@ssr.com for a list of available commands, * including help in UNSUBSCRIBING... * * DO NOT, NOT, NOT, SEND SUBSCRIBE/UNSUBSCRIBE REQUESTS TO THE LIST. ************************************************************************ ------- Forwarded Message Follows ------- Date: Sat, 27 Feb 1999 17:50:37 -0700 To: Robert Frick From: Larry Sarner Cc: healthfraud@ssr.com Subject: Re: [healthfraud] Non-science at Philly Alt-Health Conference Bob Frick wrote: > Your criticisms were not convincing. To the contrary, some of them >seemed reckless. (I claim expertise in methodology.) Why did you claim >that there was nothing conclusive in the statistics, when some of the >comparisons were statistically significant and the pattern supported >Long's hypotheses? I stated that there was nothing CONCLUSIVE in the statistics, not that there wasn't a claim to statistical significance about SOMETHING. If you re-read Long's objectives and *conclusions*, you will see that the (statistical) data does not support them. On top of it, Long's "objectives" were not her experimental hypotheses (which are quite a jumble). Just saying there is a "pattern" supporting the hypotheses doesn't count. At best, that's qualitative analysis. Moreover, the reported analysis is of experimental groups of 12 trials (9 in one case); it's hard to accept the conclusiveness of results based on such small samples, even if there is nominal significance reported. >Why did you criticize apparently irrelevant aspects >of the experimental procedure? (If you feel they posed an alternative >explanation, you should suggest that alternative explanation.) I confess I don't follow you here. To what " irrelevant aspects" do you refer as the target of my criticism? > I cannot find the Schwartz study in PubMed. Therefore, even if Long's >study was a replication of Schwartz's, it would still be useful. In any >case, science does not work by single studies answering a question. The reference is: Schwartz GE, Russek LG & Beltran J. Interpersonal hand-energy registration: Evidence for implicit performance and perception. in Subtle Energies, 1995; 6(3). To be scientifically useful, a "new" study should either confirm, contradict, or extend existing work. As a stretch, you might say Long "confirms" Schwartz et al. Even at that, there should be at least a statement to that effect. And to do a confirmation, you at least have to do something at least as well as the original; that isn't the case with Long vis a vis Schwartz. By the way, we did not mention Schwartz in our JAMA paper because it was irrelevant to the study of TT practitioners, with the concurrence of our reviewers and editors. Likewise is Long. (None of which is meant to imply that Schwartz is any GOOD, mind you.) > Similarly, you argued that the study somehow was unnecessary given the >study by Rosa (in which you were a co-author). I think not true. You >claimed to have put the bar at a level the TT people could not vault >over -- they couldn't detect a hand. However, if untrained practioners >could detect a hand, then sooner or later, trained practioners would. >So, from my perspective, you planted the bar at a height that, as Long >demonstrates, could be vaulted. Long plants the bar, not only at a >higher height, but also at a more appropriate height. I did not claim Emily put the bar at level that they COULD NOT vault over, but rather that they DID NOT vault over (and to date HAVE NOT vaulted over). And it was one of the earlier points in my prior post that specifically Long's study DOES NOT demonstrate that the bar has been vaulted, not even by non-practitioners. It was exactly because I feared reasonable people would reach the erroneous conclusion (that " Long plants the bar...at a more appropriate height") that I wrote my previous post. It was always the point of Emily's study that "if TT practitioners can practice TT, they should be able to feel my 'energy field' in a simple test where they couldn't see". Part of its *public* appeal was its obviousness; and part of its *scientific* appeal was its logical irrefutability. Long with her test has missed that point, and apparently so have you in her defense. It was never that the TT practitioners COULD have passed Emily's test, but that they DIDN'T. In all the months since the JAMA publication, no TTers have come forward with contradictory evidence to Emily's results (as Long and you suggest that they could *easily* do). You might ask yourself, *why not*--after 11 months? They are certainly motivated: "Alternative Medicine for Dummies" says Emily gave "all of alternative medicine" a black eye (though it goes on to say the black eye was "undeserved" apart from TT). > And finally, I can't even understand why you are mad at Long's study. Let's just say I'm Skeptical of it. (But it is a Mad, Mad, Mad, Mad World. I could well be Mad ;) You might re-read the last paragraph of my prior post to get my reasons for being at least Bothered by it. > And post-finally, Long should have demonstrated a statistically >significant interaction between hands at 3" and hands at 3" blocked by >glass. If they didn't, that would have been a criticism of the >methodology. But it is a common error and would not have warranted 1/10 >the criticism you gave. I specifically avoided discussing Long's poor methodology in testing "cueing by radiant body heat". The relevance of doing such testing at all to Emily's test or TT practice was the principal point I was trying to discuss. Larry Sarner Chairman, National Therapeutic Touch Study Group ************************************************************************* * Send mail to healthfraud-help@ssr.com for a list of available commands, * including help in UNSUBSCRIBING... * * DO NOT, NOT, NOT, SEND SUBSCRIBE/UNSUBSCRIBE REQUESTS TO THE LIST. ************************************************************************ ------- Forwarded Message Follows ------- Date: Sun, 28 Feb 99 22:23:33 -0700 From: Paul Bernhardt To: "Healthfraud" Subject: Re: [healthfraud] Non-science at Philly Alt-Health Conference Larry Sarner said on 2/27/99 5:50 PM: >I stated that there was nothing CONCLUSIVE in the statistics, not that >there wasn't a claim to statistical significance about SOMETHING. If you >re-read Long's objectives and *conclusions*, you will see that the >(statistical) data does not support them. On top of it, Long's >"objectives" were not her experimental hypotheses (which are quite a >jumble). Just saying there is a "pattern" supporting the hypotheses >doesn't count. At best, that's qualitative analysis. Moreover, the >reported analysis is of experimental groups of 12 trials (9 in one case); >it's hard to accept the conclusiveness of results based on such small >samples, even if there is nominal significance reported. Just to make it clear. All of your commentary has been based on a draft report for an oral presentation at a conference. You might have done well to wait until you had a summary from someone on scene (such as one of your co-authors) on what was actually said at the conference rather than assuming a draft version would be presented without revision. Finally, there were no groups of 12 or 9 subjects (I'm assuming 'trials' is a typo for subjects because clearly each subject did 10 trials of detecting a hand). Where did you get those numbers (12 and 9)? Paul Bernhardt ************************************************************************* * Send mail to healthfraud-help@ssr.com for a list of available commands, * including help in UNSUBSCRIBING... * * DO NOT, NOT, NOT, SEND SUBSCRIBE/UNSUBSCRIBE REQUESTS TO THE LIST. ************************************************************************ ------- Forwarded Message Follows ------- From: "Rebecca Long" To: healthfraud@ssr.com Date: Tue, 2 Mar 1999 19:41:08 +0000 Reply-to: arlong@netcom.com Priority: normal Subject: [healthfraud] Response to Sarner et al Before proceeding further with my response to Sarner, I would like to state that I feel I am owed an apology by the peer reviewer who violated the confidentiality and propriety of the peer review process by inappropriately providing to Larry Sarner the preliminary outline of my in-progress research paper. The preliminary draft which Sarner inappropriately obtained and improperly released was clearly marked (in red no less!) to indicate that it was not to be disseminated and that it was not to be seen by persons other than the approved peer reviewers. In fact, the draft was so preliminary and incomplete that it was still in outline rather than text form. Further, given Sarner's previous actions such as his August 1998 post to this list that I should expect to be "ill-served" by asking questions about the Rosa et al JAMA paper, I had supplemented my normal expectation of proper confidentiality in the peer review process by obtaining explicit promises that the pre-publication draft would not be turned over to Sarner or his wife Linda Rosa. Sarner has repeatedly declared, ex cathedra, that my test methodology was flawed. He did not provided specifics as to the nature of the alleged flaws. Further, his post misquoted, partially quoted, quoted out of context, and otherwise mischaracterized the information in the improperly-obtained preliminary outline of my article. Although I am more than willing to discuss questions regarding the talk I delivered in Philadelphia, I do not intend to spend a lot of time on this list explaining and justifying what I intend to write in my future article. Once the article has been written, peer-reviewed, and published, then I will WELCOME comments on it. There are a few comments by Sarner I would like to respond to, for the record, as follows: Sarner wrote: > I'm afraid the "research" turns out to be a bit of a bust. > It is likely to be a non-starter, both with the press Press attention for my experiment is a moot point. As one can surmise from the CSICOP press release, I was originally scheduled to be part of the press conference along with Paul Kurtz, Wally Sampson, and Lewis Vaughn. In fact, I was asked to change my flight reservations to an earlier day for this purpose. However, when I was informed of intense and sustained pressure from the authors of the 1998 JAMA paper to prevent me from presenting the talk at the conference, and upon learning of threats that the conference would be disrupted and SRAM discredited, I gladly agreed not to be part of the press conference. I care about science, not publicity. > The principal problem with this study is that it has no reason to exist, > much less to be presented at conference orlater published. It makes no > contributions. It addresses no known problems. > The protocol was similar to that of the Rosa experiment (JAMA, 1 Apr 1998), > differing only in a number of unimportant procedural alterations. Let me see if I understand what Sarner is implying. Both studies tested subjects at a stated hand distance of 3 to 4 inches. My test results at these hand distances were significantly above chance (e.g. mean of 7.5 out of 10 at 3 inch hand distance) whereas the Rosa study got average scores of less than 5 out of 10 (e.g. mean of 4.1 on the portion filmed by a television crew). If, as Sarner claims, the protocol of the two studies differs only in a number of unimportant procedural alterations, doesn't this beg the question of why the difference in the results? > The claim is that this experiment shows the ability of human subjects to > sense radiant body heat through the hands. Such ability has already been > investigated by Schwartz, Russek & Beltran in 1995. Because of the > methodological problems in Long's study as study in perception of radiant > body heat, her results even if statistically valid would add be > questionable. Even if those problems were inconsequential (and they're > not), she adds nothing to the body of knowledge that Schwartz et al. (even > with all THEIR problems) were already contributing. At best, Long was > engaged in a replication of Schwartz. Again, let me see if I have this straight. I gather from Sarner's post that Schwartz confirmed the ability of subjects to detect radiant body heat, but that Sarner considers it a bad experiment. If Schwartz et al performed a bad study, what then is the beef with a subsequent study of the same thing? The 1998 JAMA article published no control group data to demonstrate that the testing protocol contained no systematic error to bias the outcome, such as would occur with either positive or negative cuing. The article did state that some control data was informally collected with a few subjects, many of whom were children. On the basis of this informal pilot testing, the authors asserted that their apparatus was sufficient to prevent body heat from reaching the test subject. In August 1998, Larry Sarner issued to post to the Healthfraud list elaborating on the control group and stating that subjects in their pilot testing could detect body heat at 2 inches. He stated that Linda Rosa could consistently do so. Contrary to Sarner's assertion that my study "addresses no known problems", the information above represents some puzzling contradictions worthy of being addressed. By common experience we know that people can feel the body heat of others. Sarner tells us that Schwartz et al confirmed experimentally that subjects can detect body heat. Rosa et al found that subjects can CONSISTENTLY detect body heat at 2 inches. Yet according to the data from Rosa et al, subjects cannot detect body heat at 3-4 inches (e.g. the mean score of 4.1 out of 10 for the data taken for Scientific American Frontiers). Why? If I was "replicating" a prior experiment, or portion thereof, then one way to look at my experiment might be as a replication of the Rosa et al control group. > Even if one considers all this as intended as a refutation of Emily Rosa's > protocol (as I think may be a sly subtext for Long's work) What specifically about his experiment strikes you as a refutation of Linda Rosa et al's protocol? Why are you so quick to assume that any additional research in your area is aimed at refutation? > Had Long successfully demonstrated that radiant heat is detectable by > non-practitioners within the same testing range, it still says nothing > about *practitioners* under the same testing conditions. Practitioners > claim to go into an altered state of consciousness (called "centering") > before going after the HEF. Perversely for them, perhaps centering > psychologically cuts them off from more mundane cues such as body heat. Or > there could be other explanations for failure. In short, Long's experiment > is a non sequitor to TT practice and hence to Emily's experiment. The hypothesis you have proposed to explain the difference between my test results and Emily's looks to me to be a testable one. > so completely unnecessary. If someone at CSICOP, Prometheus, ScRAM, or > even this list, had contacted us about this experiment and allowed us to > comment privately, we could have saved them a lot of embarrassment, the > health-fraud movement a lot of trouble, and this list a very long post. Excuse me, but the editors of SRAM went so far to accomodate the authors of your paper as to give coauthor Stephen Barrett access to the draft for confidential comment. Your claim that you would not have released your attack on the draft of my talk if you had been "allowed" to "comment privately" is pretextual. Last Friday, I was told that on Wednesday evening you called an editor of SRAM with your comments on the surreptitiously-obtained draft of my paper. I was told the nature of your comments. Therefore I consider your claim that you would not have acted publicly if you had been given an opportunity to comment privately to be less than truthful. > separation, (inexplicably) in groups of 9 and 12. "Inexplicably" only to persons reading and criticizing a surreptitiously obtained sketchy outline of a future paper, and perhaps to someone who does not understand statistics. The values 9 and 12 were listed as df, which stands for "degrees of freedom". This is one less than the number of test subjects. >They included two > sets of trials which introduced "negative cuing" in one and > interposing a "glass" barrier in the other. I'm as puzzled and amused by the quotes around the word "glass" as I was by the reference to me as a "scientist". "glass" means glass. As it happens, the "glass" I used in the experiment was from my MS diploma from Georgia Tech. I'd like to hear Sarner's criteria for who is entitled to be called a scientist sans the scare quotes. Nurses? MDs? "Statisticians"? Persons with physics degrees and over twenty years professional experience designing, performing, and evaluating the adequacy of scientific testing? Oh me, Rebecca Long ************************************************************************* * Send mail to healthfraud-help@ssr.com for a list of available commands, * including help in UNSUBSCRIBING... * * DO NOT, NOT, NOT, SEND SUBSCRIBE/UNSUBSCRIBE REQUESTS TO THE LIST. ************************************************************************ ------- Forwarded Message Follows ------- Date: Sun, 28 Feb 99 17:59:17 -0700 From: Paul Bernhardt To: "Healthfraud" Subject: Re: [healthfraud] Re: Non-science at Philly Alt-Health Conference Larry Sarner said on 2/28/99 2:49 PM: >Paul Bernhardt said: > ... > >(That seems like more than just a "bare mention", but oh well.) Anyway, >even if Long's stated restriction applied to me (and perhaps it didn't) That restriction applied to anyone who read her draft report, even those given permission to read it. >, it >nonetheless seemed like the cat was out of the bag at 1 pm EST on Saturday. >I sent my message at 11:14 am MST (1:15 pm EST). It wasn't posted to the >list until about 1:25 (at least back to me). I didn't actually >"disseminate" it, just abstracted and reported the results which were >scheduled to be "announced" as I posted. I do admit that I wanted to beat >the press to the punch (on this list only). (I had visions of them running >from the press room, yelling into their cell phones "stop the >presses"--perhaps I live in a very Hollywood-filtered world. :) I doubt you will find many people here who will argue that you didn't "disseminate" when you did report details and quotes to an internationally distributed forum. Ms Long owns this work and until she presented the details publicly or gave you advance permission you exceeded your authority in presenting it anywhere to anyone. Quoting from your first post you described Ms Long's research as "...a non-starter, both with the press and those concerned with Therapeutic Touch..." It doesn't sound to me like you expected this mad rush of the press. This post-hoc explanation of your premature quoting of Ms Long's copyrighted work doesn't absolve you of your behavior. >From what you say above, it appears you wrote your post prior to the press conference, made assumptions about what would be presented at the press conference, didn't confirm the details of the presentation at the press conference, then posted copyrighted material from a *draft* of the formal presentation not yet released. > I wanted >the listers to hear it here before they got it in the media. Why? >I suppose >that may be "ethically questionable," but at the time I didn't think it a >problem. Come to think of it, I still don't. > >Where do you get the term "marginal significance"? I've heard some results >near BUT JUST BELOW .05 as "marginally significant", but never applied to >anything ABOVE .05. (I've even heard some people suggest that .05 is too >high these days.) I thought I had done Long's reputation a favor when I >omitted in my report her reference to these non-significant results as >"near significance, and likely represents a true effect." This is the kind >of commentary that TTers have printed in THEIR studies on TT which has made >them such a joke. It is conventional in the social and medical sciences, others can confirm this, that results at and below .05 are described as statistically significant and results above .05 to .10 can be described as marginally significant. There are countless examples of this and references to this practice in the literature of the sciences that usually use statistics and in statistics texts. Above, again, you quote from the *draft* report, not from the actual presentation. There are statisticians who loath the term 'marginal significance.' But there are similarly statisticians who have no problem with it. Pick your favorite statistician and be happy. > >>Not mentioned by you is the test of accuracy of detection between the 3 >>inch with and without glass. These conditions were significantly >>different at probability less than .0001. > >Well, you've mentioned them now. So let's look at it. You took one >SIGNIFICANT result, compared it with an especially NON-SIGNIFICANT result, >and came up with significance in the comparison? Well, I suppose that's >statistically possible (treating the glass trials as a placebo), but one of >the numbers used in that analysis (79%) did not jibe with the results >reported earlier (76% and 77%). In addition, the methodology used did not >support any conclusion on radiant heat. The glass could have acted as a >sneezeguard, preventing breezes or other cues, and not just as a >radiant-heat barrier. Certainly these other alternative explanations are possible. Nevertheless, the interposition of glass did reduce to near chance the accuracy of the subjects. The difference in the percentage accuracies is due to the fact that the summary of the 6 testing situations was broken down by experimenter and condition. The glass test used 2 subjects with one experimenter and 13 with the other experimenter. Since Ms Long was using a repeated measures design, the proper comparison was to combine the without glass data from 2 subjects from the one experimenter with the data for the 13 subjects from the other experimenter. This particular subset of the data is not summarized elsewhere because it was not germane to the other questions under consideration. > >>Not mentioned by you is the test of linear association between accuracy >>and distance which showed a significant linear regression equation where >>accuracy dropped off with distance. This is consistent with known >>radiative fields such as heat (actually a power equation is the likely >>best fit, but was not possible to develop with only 3 measurement points >>and regression methods). It may be consistent with the Human Energy >>Field, but the failure to sense through glass suggests heat was the >>cueing mode for these non-TT practitioners. > >Now that you've mentioned it, let's take a look at what you have. You have >just three measurement points. Two have reported significance, the other >one does not. You do a regression between all three (significant or not) >and report significance in the relationship (.022). You want to stand by >that? Yes. > Then on top of it, you admit that a power equation would be a proper >theoretical fit (accomodating inverse-square laws for energy), but bull >ahead with a *linear* analysis anyway. Sigh. Sigh all you want but I can't calculate what mathematics won't let me calculate. The statisticians here don't need me to explain this, but there are lots of non-statisticians here that might like to understand this kind of detail. The data we had only allowed me to estimate 2 parameters. Regression to a quadratic equation requires estimation of 3 parameters which means we needed 4 measurement points (distances). Note that I'm talking about regression here, estimation of a relationship accounting for uncertainty, not simply plotting a line through points in space. Of course, I was able to regress onto a power function with no linear term (Accuracy = A + B*distance*distance) since only 2 parameters (A & B) are estimated in that case, but it provided no improvement in the fit to the data. Most folks are better acquainted with linear relationships from regression (Accuracy = A + B*distance), therefore I decided the linear relationship would communicate the relationship more clearly to the anticipated audience. In a more complete written report a description of the power function would be appropriate to mention. Finally, inclusion of data in a regression analysis is not based on the significance of the deviation of the data at those points from chance guessing. These were different statistical analyses intended to answer different questions. (Ms Long did a more involved study that addressed several questions.) The significance of each of the specific subsets of data were simply tests to see if the accuracy was statistically different from chance accuracy at each distance and testing situation. The regression calculation was intended to answer the question: Does accuracy drop off as distance increases? The significant regression coefficient answers this question 'yes.' Different questions, different statistical approaches. >>The burden of proof statement makes sense in the context that TT >>practitioners claim to be able to sense through common materials such as >>glass. Glass effectively removed the apparent cue of body heat. > >Do you have a literature citation to back your statement that practitioners >claim to feel through glass? I know of none, and I'm pretty familiar with >their claims, but I'm willing to be shown. I do know that they claim to >feel through fabric and wood (e.g., clothes and some chairs), but glass is >a new one. Of course, there is no earthly reason why they should claim >glass is a problem, but I know Krieger claims *plastic* mutes or impedes >the HEF (possibly because it is an evil petrochemical product), so she >might demur that glass is another such substance. Plus, as I've discussed >before, I'm unconvinced (as a knowledgeable observer) that statistically or >methodologically you've made the case for detecting radiant body-heat with >this experiment (as opposed to other cueing). If I'm right, then, the >"burden of proof" conclusion falls along with it. I don't know any literature to support my statement. I have relied on Ms Long for information on HEF and TT and got my information on that from her. I am simply the statistical consultant. You will need to address that question to her when she can return to posting on this forum in a few days. However, it occurs to me that if Krieger claims plastic impedes the HEF then how does she do it through the polyesters in clothing and sheets at hospitals? > >>Therefore, TT practitioners do have a burden of proof to exceed these >>levels of accuracy. > >NOW we're getting to the nub of the matter. Even if it is accepted, for >the sake of argument, that the test validly and plainly tested for >perception of radiant body heat, it is inconsequential and irrelevant to >the study of TT, as I've tried to state in previous posts. Rather than >repeat myself, let me add to my reasoning. By way of argument: (1) Let us >accept that human beings CAN feel radiant heat. (We probably don't need an >experiment for that, as there is much human experience to validate it.) >(2) Let us also accept that human beings are heat radiators (again, no >experimental data needed). (3) Finally, let us accept that Emily's >experimental protocol allows for someone to detect a hand through radiant >body heat at any given distance. What is the logic that flows from these >assumptions that allows one to establish ANY level of performance by >experimental means. Moreover, what is the logic that says that this one >experiment has done so? The real trick is to *control* for the >variables, not to raise the bar of significance. > One study is never enough to tell the whole story in science. >>Replication is a fundamental process by which science advances. >>Therefore, replication is a valuable addition. Endless replication is not >>valuable. I don't know, have there been other replications of Schwartz, >>et al, if indeed her study is a replication (you don't provide sufficient >>details of the study to evaluate)? > >Actually, replication is rarely a means of advancement, only confirmation >we are on the right track. But that's a niggle. You tell me--were you (or >rather Long) *intending* to replicate (or maybe extend) Schwartz? You (or >she) ARE aware of it, no? With our negative finding, we had to establish >with JAMA that we could distinguish Emily's experiment from theirs and >justify our lack of citation/recognition of it in our lit review. At the point of written versions of this report we will deal with these issues as may be required by reviewers. >>Therefore, let them do better than untrained persons in the same >>situation. The situation with untrained persons has been established, let >>the trained persons demonstrate their special skills. > >I'll wait to see if they can demonstrate ANYTHING...in Emily's test or any >other venue. I've nothing against refining the methodology with each >successive test of practitioners. (I can see putting in sneezeguards as >you all did, but there are probably better ways to control for heat.) You and I are in agreement here. I'd love to see cloth used as the control for heat because it would also simulate clothing that TT practitioners often measure fields through. But you make a lot of assumptions about the shape, size and positioning of the glass used in Ms Long's study. How do you know it was large enough to be effective as a 'sneezeguard'? >But >it's tests of PRACTITIONERS that we need. If any of them ever do show >something statistically significant in a straightforward test of ability, >we'll look to see if there is a non-HEF explanation for that set of >conditions. I don't agree that a test of non-practitioners changes the >standard that the claimants must meet. Testing of both practitioners and non-practitioners has value. If practitioners can do no better than non-practioners in detecting HEF then they've failed. Since ordinary people can detect hands through other cues, probably heat, then it stands to reason that if there is anything to the HEF, practitioners should be able to do even better. > >>I don't think you'll see >>any embarrassment on Ms Long's part (or mine) regarding this >>presentation. What kind of trouble or embarrassment could have been >>saved, or how you would have gone about saving it is an outside issue. >>Science is what matters. > >...And welcome to the court of public opinion. It can be brutal. Take it >from somebody who's been there. > Welcoming me to the court of public opinion at this point would be a bit after the fact. I've been praised and vilified in the press several times over the past year. But we are about science, so the court of public opinion doesn't matter. Paul Bernhardt ************************************************************************* * Send mail to healthfraud-help@ssr.com for a list of available commands, * including help in UNSUBSCRIBING... * * DO NOT, NOT, NOT, SEND SUBSCRIBE/UNSUBSCRIBE REQUESTS TO THE LIST. ************************************************************************ .com ------- Forwarded Message Follows ------- Date: Sun, 28 Feb 1999 14:49:40 -0700 To: healthfraud@ssr.com From: Larry Sarner Subject: [healthfraud] Re: Non-science at Philly Alt-Health Conference Paul Bernhardt said: >You certainly have a right to your opinion, but in the opinion of the >committee reviewing presentations for the CSICOP conference Ms Long's >study does make a contribution which they feel should be publicly >presented. But apparently not for scientific reasons or in an orderly manner. This wasn't a conference which had a "call for papers" and Ms. Long had not been on the agenda as a presenter. In fact, one of the announced presenters is giving her a part of his time so she could present. And usually conferences which might present astounding, controversial, or questionable results usually invite someone onto the program to cast a critical eye upon it. That wasn't done here, either. It all sounds very short-circuited at this level of "peer review." A similar rush job happened with Fleischmann and Pons on "cold fusion", to the embarrassment of everyone involved (including Fleischmann and Pons). >If and when it is offered for publication to a journal the >editors and reviewers of that journal will have the opportunity to make >the same decision, regardless of your opinion. Indeed. Having gone through that with JAMA, I trust that process to sort out the science. (Provided we're not talking about NURSING "journals" here.) It should have gone through that process first before becoming public, though. I do hope it is not "regardless" of my opinion, however, or at least of the same opinions expressed by someone else (say a reviewer). I wouldn't want someone to make a crappy editorial decision. Nonetheless, I do think I have some qualification to speak out on this particular topic, and to suggest rejection to any editor or reviewer--or author (and consultant)--who may be listening (perhaps not many on this list). >The methodology was virtually identical to yours in the Rosa, et al >(1998; JAMA) study. So, to the extent that you consider Ms Long's >methodology flawed, you should consider your own study flawed. Ms Long's >deviations from the Rosa protocol were to facilitate examination of >variables of importance for studying the HEF phenomena (that is, heat and >voice cueing). You have the wrong end of the stick. I criticize the USE of Emily's methodology as poor for the objective of determining the ability to detect radiant body heat. I also criticize Long's "deviations" as poor for those same purposes. Emily's protocol was demonstrably sufficient for testing claims of an ability to detect an HEF by TT practitioners. For the record, Emily's methodology is not claimed to be good for any OTHER purpose, such as testing for ability to sense electromagnetic fields, to detect human presence through gravitation, to detect the strong or weak nuclear forces, to feel the investigator blowing on the subjects' hands, or to detect the passage of neutrinos (which apparently have mass and hence should be ABLE to be felt). >The results had not been made public at the time of your posting your >message to Healthfraud. Ms Long will present her report in the AM on >Sunday, Feb 28. Your posting was in the AM of Saturday Feb 27. The press >release only barely mentioned that a TT study would be presented and >there had been no public presentation of her findings. The only location >that you could have gotten the above statistical values is from the >password protected web site that Ms Long had posted a *draft* of the >presentation. The draft clearly states: "THIS IS A PROPRIETARY DRAFT, >COPYRIGHT REBECCA LONG, BEING MADE AVAILABLE FOR PEER REVIEW ONLY. IT IS >******NOT FOR DISSEMINATION******* " Your presentation of information and >quoting from Ms Long's draft presentation is, IMO, ethically questionable. Mea culpa...sort of. As I understood from the press release on Wednesday, Long was announcing her results at the press conference (which the release called a 'briefing') which was taking place Saturday at 1 pm EST. Indeed, here is exactly what it said: "In addition, scientists at the briefing will announce results of a new study examining the ability of therapeutic touch (TT) practitioners to detect a 'human energy field.' The research promises to be an improvement over previous scientific protocols used to evaluate this controversial technique. TT is being used by thousands of practitioners (most of them nurses) and promoted by its supporters--even though it has not been backed by any credible scientific evidence." (That seems like more than just a "bare mention", but oh well.) Anyway, even if Long's stated restriction applied to me (and perhaps it didn't), it nonetheless seemed like the cat was out of the bag at 1 pm EST on Saturday. I sent my message at 11:14 am MST (1:15 pm EST). It wasn't posted to the list until about 1:25 (at least back to me). I didn't actually "disseminate" it, just abstracted and reported the results which were scheduled to be "announced" as I posted. I do admit that I wanted to beat the press to the punch (on this list only). (I had visions of them running from the press room, yelling into their cell phones "stop the presses"--perhaps I live in a very Hollywood-filtered world. :) I wanted the listers to hear it here before they got it in the media. I suppose that may be "ethically questionable," but at the time I didn't think it a problem. Come to think of it, I still don't. >You don't indicate the probabilities associated with each finding. >Incomplete revelation of findings is also, IMO, ethically questionable. Whoa. I did say which ones you reported as significant. I thought for clarity of presentation that it was best just to report the percentages of right/wrong, label them as significant or not, and get on with the discussion. That MAY have been a bad editorial judgment (though I still don't think so), but not an ethical lapse by my lights. Still, if that's your standard... >But I have permission from Ms Long, so I can identify specifically which >ones were significantly different from chance accuracy (50%): 3 inch (for >each experimenter, no glass) probability < .0001, 4 inch probability = >.01, 6 inch distance (no cueing) probability=.075 (marginal >significance), 6 inch with negative cueing probability = .066 (marginal >significance), 3 inches with glass probability = .53 (not significant). Where do you get the term "marginal significance"? I've heard some results near BUT JUST BELOW .05 as "marginally significant", but never applied to anything ABOVE .05. (I've even heard some people suggest that .05 is too high these days.) I thought I had done Long's reputation a favor when I omitted in my report her reference to these non-significant results as "near significance, and likely represents a true effect." This is the kind of commentary that TTers have printed in THEIR studies on TT which has made them such a joke. >Not mentioned by you is the test of accuracy of detection between the 3 >inch with and without glass. These conditions were significantly >different at probability less than .0001. Well, you've mentioned them now. So let's look at it. You took one SIGNIFICANT result, compared it with an especially NON-SIGNIFICANT result, and came up with significance in the comparison? Well, I suppose that's statistically possible (treating the glass trials as a placebo), but one of the numbers used in that analysis (79%) did not jibe with the results reported earlier (76% and 77%). In addition, the methodology used did not support any conclusion on radiant heat. The glass could have acted as a sneezeguard, preventing breezes or other cues, and not just as a radiant-heat barrier. >Not mentioned by you is the test of linear association between accuracy >and distance which showed a significant linear regression equation where >accuracy dropped off with distance. This is consistent with known >radiative fields such as heat (actually a power equation is the likely >best fit, but was not possible to develop with only 3 measurement points >and regression methods). It may be consistent with the Human Energy >Field, but the failure to sense through glass suggests heat was the >cueing mode for these non-TT practitioners. Now that you've mentioned it, let's take a look at what you have. You have just three measurement points. Two have reported significance, the other one does not. You do a regression between all three (significant or not) and report significance in the relationship (.022). You want to stand by that? Then on top of it, you admit that a power equation would be a proper theoretical fit (accomodating inverse-square laws for energy), but bull ahead with a *linear* analysis anyway. Sigh. >All significances reported in Ms Long's study are 2-tailed significances. One-tailed would have been better, given that the hypothesis would push expectations to the high side, but this is of little note either way. >The burden of proof statement makes sense in the context that TT >practitioners claim to be able to sense through common materials such as >glass. Glass effectively removed the apparent cue of body heat. Do you have a literature citation to back your statement that practitioners claim to feel through glass? I know of none, and I'm pretty familiar with their claims, but I'm willing to be shown. I do know that they claim to feel through fabric and wood (e.g., clothes and some chairs), but glass is a new one. Of course, there is no earthly reason why they should claim glass is a problem, but I know Krieger claims *plastic* mutes or impedes the HEF (possibly because it is an evil petrochemical product), so she might demur that glass is another such substance. Plus, as I've discussed before, I'm unconvinced (as a knowledgeable observer) that statistically or methodologically you've made the case for detecting radiant body-heat with this experiment (as opposed to other cueing). If I'm right, then, the "burden of proof" conclusion falls along with it. >Therefore, TT practitioners do have a burden of proof to exceed these >levels of accuracy. NOW we're getting to the nub of the matter. Even if it is accepted, for the sake of argument, that the test validly and plainly tested for perception of radiant body heat, it is inconsequential and irrelevant to the study of TT, as I've tried to state in previous posts. Rather than repeat myself, let me add to my reasoning. By way of argument: (1) Let us accept that human beings CAN feel radiant heat. (We probably don't need an experiment for that, as there is much human experience to validate it.) (2) Let us also accept that human beings are heat radiators (again, no experimental data needed). (3) Finally, let us accept that Emily's experimental protocol allows for someone to detect a hand through radiant body heat at any given distance. What is the logic that flows from these assumptions that allows one to establish ANY level of performance by experimental means. Moreover, what is the logic that says that this one experiment has done so? The real trick is to *control* for the variables, not to raise the bar of significance. >Replication is a fundamental process by which science advances. >Therefore, replication is a valuable addition. Endless replication is not >valuable. I don't know, have there been other replications of Schwartz, >et al, if indeed her study is a replication (you don't provide sufficient >details of the study to evaluate)? Actually, replication is rarely a means of advancement, only confirmation we are on the right track. But that's a niggle. You tell me--were you (or rather Long) *intending* to replicate (or maybe extend) Schwartz? You (or she) ARE aware of it, no? With our negative finding, we had to establish with JAMA that we could distinguish Emily's experiment from theirs and justify our lack of citation/recognition of it in our lit review. >You are reading things into Ms Long's draft report. She makes no >statement as the relevance of her study to Rosa, except as a basis for >methodology and reference for comparison. Granted. >Therefore, let them do better than untrained persons in the same >situation. The situation with untrained persons has been established, let >the trained persons demonstrate their special skills. I'll wait to see if they can demonstrate ANYTHING...in Emily's test or any other venue. I've nothing against refining the methodology with each successive test of practitioners. (I can see putting in sneezeguards as you all did, but there are probably better ways to control for heat.) But it's tests of PRACTITIONERS that we need. If any of them ever do show something statistically significant in a straightforward test of ability, we'll look to see if there is a non-HEF explanation for that set of conditions. I don't agree that a test of non-practitioners changes the standard that the claimants must meet. >Discussion of findings, challenging of findings, and resolving contrary >findings is all part and parcel of all sciences. It is not personal and >it is not about public image. Indeed, any science that has no internal >disputes is automatically suspect in my book. It is about truth as best >as we can ascertain it with the tools we have. Not much to quibble with there. As long as we recognize that science is a human enterprise and that much of the process is in place in order to keep from fooling ourselves.... >About a week ago, one of the authors of the Rosa, et al (JAMA) study was >given access to the draft copy (mentioned above) of Ms Long's >presentation prior to it's public release. Therefore, your statement >above about not being contacted is simply wrong. Well, that wasn't me, Linda, and certainly not Emily. We were first learned of it with the press release mentioned earlier. That leaves just Steve Barrett. Was it given to him with the intent that he/we review it? Maybe he felt obligated by (or agreed to) Long's restriction on it and didn't let us know. In any event, he seemed surprised when WE informed HIM of the contents of the press release. I do know he was, to put it mildly, rather opinionated on whether this study had any scientific merit, so I guess he must have been aware of it before we were. I would be surprised that he didn't convey this to you if he was invited to (and Steve rarely needs an invitation). Linda and I were given a grand total of 30 minutes to relay any "problems" we had with the paper before it was declared "too late" to do so. Football is a game of inches, science a game of minutes, I guess. >I don't think you'll see >any embarrassment on Ms Long's part (or mine) regarding this >presentation. What kind of trouble or embarrassment could have been >saved, or how you would have gone about saving it is an outside issue. >Science is what matters. ...And welcome to the court of public opinion. It can be brutal. Take it from somebody who's been there. ************************************************************************* * Send mail to healthfraud-help@ssr.com for a list of available commands, * including help in UNSUBSCRIBING... * * DO NOT, NOT, NOT, SEND SUBSCRIBE/UNSUBSCRIBE REQUESTS TO THE LIST. ************************************************************************ Note from Becky - The successful test subjects specifically stated that they were feeling body heat. This fact wasn't in the draft outline purloined by Sarner. Becky ------- Forwarded Message Follows ------- Date: Sun, 28 Feb 99 23:43:45 -0700 From: Paul Bernhardt To: "Healthfraud" Subject: Re: [healthfraud] Re: Non-science at Philly Alt-Health Conference Robert Frick said on 2/28/99 10:32 PM: >Larry Sarner said: >Correct me if I am wrong, Paul, but >couldn't you have used 9, 16, and 36 instead of 3, 4, and 6? I did that regression which is (Accuracy = A + B*Distance*Distance). The equation was: Accuracy = 7.90 - .062 * Distance*Distance Adjusted R-square = .131 Test of 'slope' parameter: t (37) = -2.59, p = .014 The linear regression (Accuracy = A + B * Distance) was: Accuracy = 9.16 - .582 * Distance Adjusted R-square = .139 Test of slope parameter: t (37) = -2.68, p = .011 Both have comparable adjusted R-square and tests of the slope parameter. The main reason for using the linear equation was it is easier to describe to our anticipated audience. If the power equation had been a demonstrably better fit then it would have been presented regardless. Another reason for not presenting the distance-squared (power) equation was it made less common sense. The intercept for that equation is 7.9 suggesting accuracy of near 8 for the hands in contact (zero distance) where we would actually expect perfect accuracy (10). Also 10 is not even within 3 standard errors of the intercept for the power equation (SE = .56). The linear equation intercept was 9.16. While still not 10, it is a better approximation. And 10 is within that intercept's standard error (.98). Finally, the power equation parameter for the squared term is negative where we would expect a positive parameter to generate a curve that asymptotically approaches chance accuracy at large distances. Therefore, it appears that another measurement point is necessary so that a linear term can be added to the power term. Don't get me wrong. I'm pretty sure a power equation will prove to be best, but we need more data to find it and it may not be worth the trouble. >> In addition, the methodology used did not support any conclusion on >> radiant heat. > >Again, Larry is correct on this. The inference of radiant heat depends >on ruling out other alternatives as implausible, and this has nothing to >do with the methodology of the study. Let's examine the possible modes of sensing that could be used. *Vision is blocked by the wall and the cloth over the subject's arms so that he/she couldn't see any light through the hand holes. If there were vision cuing we wouldn't expect the observed drop off with distance or the glass dropping the accuracy to chance. *Sound cueing was controlled by using a signal light to indicate that the experimenter was ready. The sound of the hand being positioned was controlled by not allowing the experimenter to bear any weight on her arms, which could cause joint 'creaking' and the sound of the arm rubbing against the table. In any case, if there were sound cueing we wouldn't expect the observed drop off in accuracy with distance or the glass dropping the accuracy to chance. *Tactile sensations of air movement. One way this could happen would be if the experimenter breathed (sneezed?) so that the air moved over one or the other hand either increasing or decreasing accuracy. If this were the case we wouldn't expect the observed drop off in accuracy as the distance increased. Another way this could happen would be if the experimenter positioned her hand so swiftly that it caused perceptible air currents on the subject's hands. However, as reported at the conference, pilot testing found that subjects reported 'cooling' of the hand or 'air movement' in certain ways of moving the experimenter's hand into position. Therefore, hand positioning methods where subjects didn't report air movement in pilot testing were used. Taste? Smell? You tell me how and then we can talk. Therefore, the finding that accuracy dropped off due to increased distance appears to argue against the other offered competing hypothesis leaving only radiant heat. Radiant heat is, IMO, the simplest explanation that accounts for all the Long data: the high accuracy of detection at close distance, dropping to lower accuracy at farther distance, and dropping to chance with the addition of glass. I welcome other readers offering their alternative explanations because this is a core issue that needs to be understood. If there are alternative modes of detection, we need to ferret them out so that future designs of this protocol can control for them. Paul Bernhardt ************************************************************************* * Send mail to healthfraud-help@ssr.com for a list of available commands, * including help in UNSUBSCRIBING... * * DO NOT, NOT, NOT, SEND SUBSCRIBE/UNSUBSCRIBE REQUESTS TO THE LIST. ************************************************************************