From: Robert Sheaffer Subject: Re: Mars effect and induced births Message-ID: <9210300616.AA10499@lll-winken.llnl.gov> Date: Thu, 29 Oct 1992 09:33:05 PST > (Chip Denham writes:) > Can you clarify this point? In the vast majority of cases of induced labor > or c-section, the birth date of the infant would be only a matter of days > different from natural birth. Is this enough to change to supposed Mars > Effect? > Oh, indeed. It's worse than you think. The supposed "Mars sector" is based not on the position of Mars with respect to the constellations, but rather on the position of Mars with respect to the earth's horizon, at the location that the birth took place. Hence, even a change of a few *minutes* could easily change one's "Mars sector." Those doctors choosing to induce labor should read Gauquelin very carefully, to make certain that Mars is in the right position! :) -- Robert Sheaffer - Scepticus Maximus - sheaffer@netcom.com Past Chairman, The Bay Area Skeptics - for whom I speak only when authorized! "Beware when the great God lets loose a thinker on this planet. Then all things are at risk. It is as when a conflagration has broken out in a great city, and no man knows what is safe, or where it will end." - Emerson: Essay, "Circles" From: Chip Denman Subject: Mars effect and induced births Message-ID: <9210300504.AA07477@lll-winken.llnl.gov> Date: Thu, 29 Oct 1992 08:40:10 EST There's a paucity of good medical information on the effect of induction and c-section on length of gestation. It's harder than you might think to get a reliable estimate of the day of conception in a data set large enough to allow for good estimates. In a study published in 1869 with only 221 cases having information on date of conception, the normal duration for a first birth was estimated to be 284 days and 281 for subsequent births. Another data set of 1017 births from Munich in 1944-1948 reported a mean duration of 272.48 days, a rather different ballpark. An extensive data set collected at the University of Minnesota from 1935-1962 reported a mean of 277.9 days. Another 882 cases collected prior to 1930 showed a mean of 278.7. A few years ago I had a chance to analyze a more modern data set-- 460,530 births in Sweden from 1975-80. (A national health-care system sure does improve our ability to do statistics!) We came up with a mean of 280.9 days for normal singleton births and 274-275 days (there seemed to be a time trend) for c-sections. The c-section rate was a tad over 10%. Spontaneous and induced labor were not distinguished in the records. So what's the point? Looking for a differential Mars Effect in pre-1950 vs post-1950 data would be a really, really hard task even if the Mars Effect turns out to reflect some mysterious physiologic influence. Pre-1950 data gives a range of estimates of pregnancy duration that includes my more modern estimates for *both* natural and c-section births. I'm still a bit fuzzy on whether the effect is supposed to occur at the moment of birth or instead is supposed to reflect some kind of cumulative effect, but in any case it seems to me that poking around in data that does not specifically include info about intervention isn't going to resolve this kind of issue. And of course, it's a moot point if the "Effect" isn't really an effect at all. A final tidbit for thought: one intriguing finding in our Swedish data was an apparent seasonal effect. In the 5 years represented in our data there was a fairly clear pattern of shorter pregnancies and lower birthweights for births occuring in the winter for both natural and c-section births. If this finding were to hold up, would such a fluctuation in any way at all relate to the alleged Mars Effect? From: Suitbert Ertel Subject: Mars effect and induced births Message-ID: <9210290938.AA01183@lll-winken.llnl.gov> Date: Thu, 29 Oct 1992 10:26:41 MEZ Regarding Chip Denman's question: Lowered "Mars effects" with birth induction by obstetric drugs? ------------------------------------------------------------- From medical statistics we know that some years after World War II birth inductions by obstetric drugs increased rapidly in Western countries. Gauquelin had expected that correlations between birth frequencies and planetary positions would drop due to medical intervention, that is, that planetary effects would decrease and perhaps entirely disappear after 1950. He held that planetary effects were due to environmental (probably geomagnetic) stimulation, his prediction made sense in his physical model, he reported some empirical evidence for it. Gauquelin's physical model allows for a number of testable predictions. But my own attempts at helping him to pave that way more thoroughly failed entirely. I tested quite a few hypotheses derived from his model. For example, Mars effects should disappear with Sun-Mars conjunction (Mars is behind the Sun), but they don't, effects should oscillate with varying Mars-Earth distance, but I couldn't find any variation even though the range of Mars-Earth distance variation is large (1:7), etc.(published in CORRELATION,9.1,1989, "Purifying Gauquelin's 'grain of gold'"). So I also began doubting Gauquelin's contention regarding induction effects and I tested them. What I found has been sketched in a paper published in the Skeptical Inquirer, see below: ****************************************************************** From Ertel, S. "Update on the Mars effect" Skeptical Inquirer, Winter 1992, 16, p. 156 "A clue from induction? Gauquelin held that the Mars effect was diminished for births after 1950. He attributed this to the increased prevalence of induced births and surgical intervention, and concluded that planetary relationships apply only if the birth is natural, which of course also supported his physical explanation. In his view, subtle stimulation of the fetus by planets could be expected only for births occurring under natural conditions. However, his only published data are for 113 sports champions born in 1946 or later vs. 319 born earlier, so his sample size is very small (Gauquelin, 1979). Worse, I found that the difference between the 319 earlier births and the 113 later births exists only for 12-sector division. For 36-sector division the difference disappears - as it happens many of the later births have Mars in the initial key sectors cut off by 12-sector division. (See the outer ring in Figure 1 [Ertel 1989].) So Gauquelin's ideas about induction are greatly in need of support from an appropriate test on a large sample. But having found no evidence so far for any other physical link, I would almost bet that his ideas resting on physiological assumptions will not be supported." ****************************************************************** In that paper I suggested a comparative study of planetary effects with professionals from pre-war and post-war generations. I hope to be able to do this study before long. Its result would tell us at the crossroads where to go (physical or nonphysical explanation?). From: Suitbert Ertel Subject: Mars effect Message-ID: <9210282230.AA01154@lll-winken.llnl.gov> Date: Wed, 28 Oct 1992 22:28:11 MEZ ------------------------------------------------------------------- This letter to Dr. Nienhuys might have been posted directly to him, it is again technical stuff. Today it is about how to avoid wrong conclusions regarding the existence of a "Mars effect". Nevertheless by browsing through this correspondence bystanders might get a better feeling of how "Investigations of (certain) Claims of the Paranormal", on an empirical level, need to be conducted. I would like to encourage you to keep on raising general questions. I am collecting them and will gladly reply soon - no less readily than Dr. Nienhuys' whose replies to your messages now and then seem to require supplementary or emending comments. A hint: I published a report about the Mars effect controversy "UPDATE ON THE 'MARS EFFECT` in the Winter 1992 issue (Vol 16.2) of THE SKEPTICAL INQUIRER. You may find answers to some of your questions in that article. ------------------------------------------------------------------- Dear Dr. Nienhuys, the logic of your idea that year-wise shifts of CFEPP birth data would lead to G% repetition is not yet clear to me. Supposing you were right in contending that year-wise shifts would go along, in shifted samples, with astronomical repetitions of the "baseline" G% obtained from unshifted data. In that case inferential statistics based on year-wise shifts should result in erroneously higher instead of erroneously lower error probabilities. That is, affirmative conclusions regarding the existence of the Mars effect referring to conventional statistical error probabilties would be safer (more "conservative") rather than riskier. Since I performed, for statistical inference , year-wise shifts with the new CFEPP athletes data, I would not have to reconsider my conclusion at all - if you were right. An example may be helpful: We may compare genuine (=baseline) G% = 25.19 as obtained with CFEPP data with 50 G% values from year-wise shifted data. Let us assume, as you apparently do, that those 50 control G% would tend to maintain that high level of G% due to astronomical repetition. Chance effects might even tend to lift individual control G% above an elevated repetitive level, exceeding 25.19% of the genuine sample in some cases. I.e., by performing year-wise shifts we do not run the risk of falsely concluding that a Mars effect exists, on the contrary, we would run the risk of falsely concluding that a Mars effect, if real, does not exist. An argument such as yours would be more comprehensible if it would be brought up by some proponent of the Mars effect who might be afraid that my inferential results with CFEPP data would underestimate the evidence. Someone who is skeptic about it and who does not like to be surprised by opposing evidence should actually not be worried by my year-wise shift procedure. This is the difficulty I have with your argument, and you may solve it. Another point to discuss is that I would suggest to solve the divergence between your conjecture ("there are repetitive tendencies") and my conjecture ("if there are any, they are negligible") empirically. I might repeat the analysis of athletes' birth data using one experimental and 50 control samples altered by year-wise shifts - with one critical change of condition: That is, I would suggest to replace the experimental CFEPP-sample by a manipulated CFEPP-sample. The manipulation would consist of randomly deleting in this sample key sector cases. The G% level of the manipulated sample might be lowered down to, say, G = 20.5% (this is appreciably below chance expectation just as 25.19%, the unmanipulated value, is appreciably above chance expectation). Fifty control samples might then be formed by year-wise shifting birthdates of the manipulated sample which would thus serve as a 20.5% baseline sample comparable to the original unmanipulated 25.19% baseline sample. Do you understand what I am proposing? Now, what to predict? I think you would have to predict a significantly lower mean G% for the 50 control samples derived from the 20.5% mother sample as compared to the mean G% of 50 control samples derived from the 25.19% mother sample. Am I right? If we do not find the predicted difference between mean G% of the two samples (significance level may be set to p=.05) would you conclude that your argument does not hold and that my year-wise shift procedure is legitimate? On the other hand, if a significant difference would result I would certainly be ready to drop my presently preferred assumption ("repetitive effects are negligible"). I would even consider some change with my shift procedure - although not wholeheartedly. The change suggested by such result would require improved means to avoid false *conservative* conclusions, i.e., to avoid the conclusion that a Mars effect does not exist even though it actually exists (see above). Suspicious skeptics might then object that I changed the procedure with effect-boosting intentions. Your "playing around" argument taught me a respective lesson. However, that problem need not be solved now, it might turn out not to exist. It would not exist if your repetition argument would turn out to lack empirical evidence. Your comment? SE From: "James J. Lippard" Subject: Re: Mars effect and induced births Message-ID: <9210282117.AB25387@lll-winken.llnl.gov> Date: Wed, 28 Oct 1992 13:17:28 -0700 In reply to Chip Denman: Yes, a difference of a few days between natural birth and induced labor would make a difference to the "Mars effect." Gauquelin divides the zodiac into sectors, two of which are "key sectors." The "Mars effect" claim is that sports champions are born at times when Mars is in a key sector with greater frequency than those who are not sports champions. Jim From: Chip Denman Subject: Mars effect and induced births Message-ID: <9210281822.AA16734@lll-winken.llnl.gov> Date: Wed, 28 Oct 1992 10:31:52 EST James J. Lippard wrote: > One of the difficulties in taking a new sample is that Michel Gauquelin >specifically claimed that the "Mars Effect" does not show up for induced >births, only for natural births, which means you are more or less restricted >to births prior to the mid-1950s. Can you clarify this point? In the vast majority of cases of induced labor or c-section, the birth date of the infant would be only a matter of days different from natural birth. Is this enough to change to supposed Mars Effect? From: "James J. Lippard" Subject: Re: DUMB QUESTIONS Message-ID: <9210281530.AA08809@lll-winken.llnl.gov> Date: Wed, 28 Oct 1992 07:51:37 -0700 For Thomas Howe and anyone else who might be having trouble following the Mars Effect discussion, here's a brief summary posted by Jan Willem Nienhuys on sci.skeptic in response to the same complaint there. One of the difficulties in taking a new sample is that Michel Gauquelin specifically claimed that the "Mars Effect" does not show up for induced births, only for natural births, which means you are more or less restricted to births prior to the mid-1950s. Newsgroups: sci.skeptic Subject: Re: "Mars Effect": JWN replies Ertel's 23/10 post (pt 2a) Message-ID: <6055@tuegate.tue.nl> From: wsadjw@rw7.urc.tue.nl (Jan Willem Nienhuys) Date: 27 Oct 92 10:31:04 GMT Reply-To: wsadjw@urc.tue.nl Sender: root@tuegate.tue.nl References: <6049@tuegate.tue.nl> <6050@tuegate.tue.nl> <94708@netnews.upenn.edu > Organization: Eindhoven University of Technology, The Netherlands Lines: 69 In article <94708@netnews.upenn.edu> jmv@grip.cis.upenn.edu (Jean-Marc Vezien) w rites: > > >This discussion is IMHO interesting, but somewhat gets lost in details. >Could someone post a summary of experiments and what has >been found so far. Is there a Mars Effect ? Or is all this >debate solely on the impossibility to interpret the datas in >one coherent way ? >Isn't all the statistic involved based on lots of assumptions >as to the model used (variable distribution...). >It's not that I don't like maths, but I think plain english >with a few relevant figures would be better. The problem is in the details. The Mars Effect is at best a rather tiny deviation in the distribution of the positions of Mars in the sky at people's births. The Mars Effect is supposed to work with sports champions only. For other eminent professionals similar effects are claimed. The whole theory and the supporting data have been collected by Michel Gauquelin and his former wife Francoise Schneider-Gauquelin. The total amount of data (sportsmen, other professions, ordinary people) amounts to about 40,000 people's horoscopes. There have been two more or less independent tests: one Belgian (535 subjects) and one American (409 subjects). The Belgian test confirmed the Mars Effect, the American test disconfirmed it. An additional test, the socalled Zelen test (16,000 subjects), checked one type of naturalistic explanation. Basically it showed that Gauquelin's theory of what could be expected from "ordinary" people's horoscopes was correct. There has been endless discussions about (1) the quality of data collection by Gauquelin (2) the results of the Belgian test (3) the American test (3) the Zelen test. Ertel's contribution is (A) the discovery that among the sportsmen (oops, sportspersons) that Gauquelin had in his files (but never published about) there was an anti-Mars effect, which indicates some kind of bias in Gauquelin's procedure and (B) that there was nonetheless a trend that Gauquelin couldn't have faked, namely more famous athletes show a clearer Mars effect. All these discussions are about the details of the statistics. My position is as follows. An old proverbn says: you can't have your cake and eat it. In statistics: you can't use the same data to generate a hypothesis and prove it. I think that Gauquelin did something like that, thereby introducing a subtle bias that he was unaware of himself. More precisely, I think that Gauquelin might have determined the criteria for "championship" AFTER knowing the athlete's Mars sectors. Initially he was quite liberal in accepting someone as champion (there are hundreds of Italian aviators in his files), but gradually tightened the conditions: after the U.S. test he complained that only Olympic Gold Medal winners were good enough. Others have turned this complaint into a suspicion that the U.S. Skeptics are actually a kind of crypto-neo-astrologers, because they ruined the test on purpose by slipping in semi-cripples like mere Silver Medal winners (I hope you understand that I am exaggerating a little here). One development has been that Ertel and Mueller have found that among the extremely famous (sportsmen and otherwise) there is also a kind of anti-Mars effect. I hope the original poster will understand that a discussion on such tiny effects must involve some technicalities. JWN From: "James J. Lippard" Subject: Mars Effect: Nienhuys responds to Ertel Message-ID: <9210261938.AA19096@lll-winken.llnl.gov> Date: Mon, 26 Oct 1992 09:27:56 -0700 Newsgroups: sci.skeptic Subject: "Mars Effect": JWN replies Ertel's 23/10 post (pt 1) Message-ID: <6041@tuegate.tue.nl> From: wsadjw@rw7.urc.tue.nl (Jan Willem Nienhuys) Date: 26 Oct 92 12:34:04 GMT Reply-To: wsadjw@urc.tue.nl Sender: root@tuegate.tue.nl References: <24OCT199209243794@skyblu.ccit.arizona.edu> Organization: Eindhoven University of Technology, The Netherlands Lines: 153 In article <24OCT199209243794@skyblu.ccit.arizona.edu> lippard@skyblu.ccit.arizo na.edu (James J. Lippard) writes: #The following is from the BITNET SKEPTIC discussion list. # #Date: Fri, 23 Oct 1992 16:13:48 MEZ #From: Suitbert Ertel # #My rejoinder to Dr. Nienhuys (JWN, Oct 12) might appear too long #(514 lines). But, being quite explicit now may avoid requests for #more explicitness later. #------------------------------------------------------------------ I noticed that some of my arguments are misunderstood (and some were wrong). #collaboration among name collectors or plagiarism. Collaboration #between Comite and Gauquelin resulting in support for Gauquelin's #claim is very hard for me to conceive. If Dr. Nienhuys means by #"causal links" that effects favoring Gauquelin's claim might have #occurred inadvertently he should explain how #snooping into former Gauquelin results might have led Comite to #thwart their own intention. I know very little of what went on between Gauquelin and the Comit\'e Para. I can imagine G. proposing the "20 international games limit" for soccer players, *knowing* that a lower limit would decrease the G% (the percentage of athletes with Mars rising or culminating). Including many classes of athletes for which G. had already established optimal "goodness criteria" is OK, but then one should exclude the data on which these optimal bounds were based from a new independent test. If the 535 atheletes were good enough according to Gauquelin, then also the 535 minus the 203 were good enough. Ertel can easily look up in his files which percentage of the 535-203 were born in sectors 1,2,3, 10,11,12 (of the 36 sector division). I have even hinted that he would do so. But he has not reproted on the outcome. #The Dutch skeptics had tried "to find a naturalistic explanation #for Gauquelin's and Comite Para's findings", Dr. Nienhuys says. #Those findings had been positive (Mars G% above chance level). #Then, however, came the U.S. test which was negative. # #Careful reading of Nienhuys' passage will show that for the Dutch #this must have been good and bad news at the same time. Their #devising of a naturalistic explanation for positive deviations #will have nourished expectations that any test of Mars sector #frequencies for athletes, the U.S. test included, would yield G% #above chance expectation. Now G% of the U.S. test wasn't above #chance expectation, numerically it was even slightly below it. This is a good point. Ertel has remarked in his contributions to the EuroSkeptics III Proceedings (due to appear coming Friday!), that this naturalistic explanation would run into numerous problems, even if it had worked. But Ertel knows that what started the exploration was a model in which "spurious correlations" could give large more or less random deviations from expected values, and these might work just the opposite way in another geographical location. A second model presupposed a relation between athletic prowess and a diurnal-seasonal birth rhythm that might hold only in France, and not accross the ocean. # #But apparently, the Dutch skeptics' belief in their naturalistic #approach had not been very strong, since Dr. Nienhuys now says #"the U.S. test was quite convincing". I think there's a confusion here. I am not one of the four Dutch people that investigated the Mars effect. To be honest, I've thought this exercise a waste of time (wrongly, because something came out of it after all, even if it was not the result foreseen). So *my* evaluation afterwards cannot be interpreted as the point of view that this group of four had beforehand. # It is pertinent that Dennis Rawlins, one of the #astronomers who made computations for Kurtz' and Abell's study #of the U.S. athletes gave with "sTARBABY" an account of what #occurred behind the stage which would make it sensible if not #inevitable to suspect that the U.S. data had not been collected #without bias - Rawlins' probable exaggerations notwithstanding. I have spelled sTARBABY. Only on p. 76 Rawlins gives an insight of what happened behind the scenes of the U.S. test. Most of sTARBABY is about the interpretation of the ZELEN test, and what all those CSICOPs did to poor Rawlins when p.R. wanted to say that they made a mistake. #My own reanalysis of Kurtz'et al. data gave independent support: #In CSICOP members'U.S. sample average athletic success (citation #counts) was much lower than with another sample of U.S. athletes #that Gauquelin collected right after CSICOPian findings had been #published in THE SKEPTICAL INQUIRER ("Results of the U.S. test #of the "Mars Effect" are negative", 1979/80).That is, CSICOP #researchers had unquestionably violated - possibly on the fringe #between intention and inadvertence - Gauquelin's eminence #requirement. Here a very remarkable conjecture is made! CSICOP apparently believed so strongly in the Mars effect's reality, that they deviously selected about 300 weak-willed cripples from books listing the top people in several of America's favorite religions (baseball, football, basketball, boxing, ... ), just to thwart Gauquelin. That they really were weak willed cripples is of course clear from the fact that after M.& F. G. had done their selection of 192 true athletes, the G% of the remainder had dropped to 10% or so. # # # Re (2): Present test # -------------------- # 2.1 Selection bias. # #Dr. Nienhuys, having suspected biased data-selection by the #Belgian skeptics, now suspects that of the French skeptics. Bias Maybe I have not been clear enough about that. The possible (suspected) bias I am talking about is: [*the choice of eminency thresholds not independent from knowledge of the Mars sector distribution of part of the sample.*] As Benski has discussed with G. (as far as I know) which athletes should be included and which not, it is not absolutely clear that the bias source between [* and *] has been excluded. I haven't seen Benski's paper. I don't exactly know the content of his discussions with G. But unless bias source [*...*] is not provably excluded, the CFEPP experiment should be suspected. Also I don't know whether (and if so, how) Benski argues that bias source [*..*] is absent from his experiment as far as he is concerned. I hope he thought of it. It is clear from the writing of Francoise Gauquelin (see the EuroSkeptics proceedings) that she after 40 years in this research is not even aware that [*..*] can be a problem. I am not aware of any statement or proof of the Gauquelins that they ever controlled for bias source [*...*]. # 2.2 Control samples by year-wise shifts # #Dr. Nienhuys apparently rejects testing for planetary effects by #examining the effects of shifts by units of years. He points out #that fixed stars take the same positions in the sky every year at #the same time and by the same token, Mars is purported to recur #every year in similar positions. As the planet can only move #within the restricted limits of the belt of the ecliptic, #variations of position are deemed to be small. # Here I think Professor Ertel has not understood what I meant. I have been too vague (possibly in my desire to get the answer ready before my lunch break ended). I will provide more details in a next post. JWN From: "James J. Lippard" Subject: "Mars Effect": Nienhuys responds to Ertel, parts 2 and 2a Message-ID: <9210270021.AA03838@lll-winken.llnl.gov> Date: Mon, 26 Oct 1992 13:29:00 -0700 Newsgroups: sci.skeptic Subject: Re: "Mars Effect": JWN replies Ertel's 23/10 post (pt 2) Message-ID: <6049@tuegate.tue.nl> From: wsadjw@rw7.urc.tue.nl (Jan Willem Nienhuys) Date: 26 Oct 92 15:49:13 GMT Reply-To: wsadjw@urc.tue.nl Sender: root@tuegate.tue.nl References: <24OCT199209243794@skyblu.ccit.arizona.edu> <6041@tuegate.tue.nl> Organization: Eindhoven University of Technology, The Netherlands Lines: 235 In article <24OCT199209243794@skyblu.ccit.arizona.edu> lippard@skyblu.ccit.arizo na.edu (James J. Lippard) writes: #The following is from the BITNET SKEPTIC discussion list. # #Date: Fri, 23 Oct 1992 16:13:48 MEZ #From: Suitbert Ertel #Subject: JWN and MARS EFFECT #Sender: SKEPTIC Discussion Group #Reply-to: SKEPTIC Discussion Group #Message-id: <01GQAYA8T8SI8WVZHG@CCIT.ARIZONA.EDU> # # # 2.2 Control samples by year-wise shifts # #Dr. Nienhuys apparently rejects testing for planetary effects by #examining the effects of shifts by units of years. He points out #that fixed stars take the same positions in the sky every year at #the same time and by the same token, Mars is purported to recur #every year in similar positions. As the planet can only move #within the restricted limits of the belt of the ecliptic, #variations of position are deemed to be small. # As announced I will try to be more explicit now. When we shift back by exactly one year the apparent position of the ecliptica with regards to the observer will hard have changed. However, on this ecliptica Mars will be in another place. Where? Well, Mars takes 2.16 years to complete an orbit (between two conjunctions), if I'm not mistaken. If this apparent orbit would be traversed with uniform speed, then 1 year would mean that it is about 165 degrees advanced (or retarded). That is, in terms of houses or sectors, about 16 or 17 sectors (36 sector division). In other words, shifting all 1076 athletes one year back, would mean shifting all their Marses by the same amount over the ecliptic. The whole distribution over the 36 sectors is cyclically shifted by approximately 16 sectors. For other shifts the same thing holds, mutatis mutandis. Now I know of course that Mars does not move with apparent uniform speed: that speed is near opposition about 5 times quicker than near conjunction; moreover, Mars sectors have varying width depending on "Mars seasons". When Mars is in a wintry position on the ecliptic (wintry= where the sun is in winter), the relevant Mars sectors are short, and in a summer-like position they are long. On top of all this, Mars doesn't even move uniformly in its own real orbit, in connection with its excentricity. All the same, there is ample reason to believe that shifting birth years of athletes all by the same amount will for many athletes give about the same phase shift. Certain multiples of 1 year will give a better approximation to "exactly same phase shift for all athletes" than other multiples. For instance, a shift of 79 years will result in a phase shift of almost an integral number of 360 degrees for almost all athletes (I guess). Now the question: how many and which multiples will introduce such phase shifts that they may be considered as independent samples of size 1076 from a comparable universe of athletes? I don't know. I suggest: none, but I would be willing to believe 9: phase shifts that are for each athlete 40 degrees or more differing from each other phase shift, I would accept. The burden of proving that such shifts may be considered as independent samples is on the one who proposes this method. #I don't know whether Dr. Nienhuys begging a convincing gist #in his argument would accept my clarifying paraphrase of it: #"Time series consisting of G proportions obtained once every #year on the same day are autocorrelated, i.e. successive #measurements are not independent, therefore they cannot be #utilized, as Ertel did, as controls." That is not what I meant, at least not when "autocorrelated" is not very carefully described. Let's call two Mars sector distributions cyclically correlated when one can be obtained from the other by cyclically shifting all individuals by the same number of sectors plus or minus a few sectors. In that case that "same number of sectors" I propose to call the shift parameter. Obviously two cyclically correlated sector distributions can't be considered independent if the shift parameter is between -3 and +3 sectors, nor when it is bewteen 6 and 12 sectors or between -12 and -6 sectors. My argument is that I would be surprised if 50 yearly shifts would result in 50 mutually independent distributions (each pair either not cyclically correlated, or cyclically correlated with permitted shifts). # If that was his point and #if his premise were true his conclusion would be valid. His #objection might even hold empirically, for some reason or other, #irrespective of its erroneous deduction. # #Therefore I calculated an autocorrelation function across N = 51 #shifts of G% arranged in year-by-year order. I did not find any #significant signal, r's for lag = 1 and lag = 2 are -0.1 and .10, #respectively, both insignificant - autocorrelations should peak #with lag = 1 and 2 if events observed in t(i) depend on events #observed in t(i-1) and t(i-2). I don't see what this type of autocorrelation, where (1) cyclic shifts have not been considered and (2) only 1 and 2 years are looked at. One year would result according to my estimate in at worst 16 or 20 sector shifts, and two year in +4 or -4 cyclic shifts, that is, if for these periods the non-uniformity of Mars motion would not mix the results too bad. # At that time (1991) #in Holland optimism culminated. When the EUROSKEPTICS met in #Amsterdam one of the Dutch researchers, Mr. Koppeschaar, announced #an "unmasking" of Gauquelin's Mars effect; and the Dutch newspaper #VOLKSKRANT having obtained pertinent information through de Jager, #Koppeschaar, and Jongbloet, referred to the Mars effect as an #artefact due to biological rhythms. The "Gauquelin bastion" was #"crashing", one newspaper headline proclaimed. Such jumping to #conclusions and their public dissemination, was it necessary? One can't do much about newspapers getting hold of conference abstracts, and then interpreting them in such a way that maximizes reader interest. Fortunately, the practice of quoting daily newspapers in scientific disputes has not spread much (yet). On the other hand, taking isolated scientific findings (that have not been discussed fully) out of their context, and then overinterpreting them is what's going on all the time in circles that look for evidence in favor of homeopathy, astrology, E-rays and so on. But I don't think that any believer in astrology has wavered for a second: those results had been "found" by skeptics, which makes them suspect per se. Among astrologists it is inconceivable that one's a priori beliefs are not the prime determinant of the outcome of any investigation. So no damage is done to the tender souls of occultists. What other damage can have been done? [here the real JWN shines through the veneer, of course] # # 2.4 "Warning bell": recurrent values # #Dr. Nienhuys might have asked me whether I could explain #recurrence among the 51 percentages - but he preferred to #forget where the decimal numbers came from and to calculate an #10^-9 impossibility ending up in ringing the bell. # #I would have been pleased to point out to Dr. Nienhuys the #following: The total number of athletes is 1,076. The proportion #of athletes having Mars in key sectors varies between 25.19% and #21.10% across 51 samples (one genuine, 50 controls). That is, the #range of *absolute* frequencies span between 271 and 227. With 51 #observations ranging between 271 and 227, there are 45 possible #results: 271(1), 270(2), 269(3)... 227(45). Numbers must therefore #recur: First, of necessity, there are 6 more observations than #there are distinct possible results. [etc.] Touch'e. Stupid of me. I should have thought of that. Completely right. # # 2.5 Inferential statistics. # #Dr. Nienhuys came up with z = 1.23 as deviation of observed Mars- #born athletes (N = 271/1,076) from chance expectation which he #estimated as N = 247/1,076 (G% = 22.93%). "Not impressive", he #says. Error probability would be p = .11, so his statement could #be rephrased by "not significant" ,i.e., not reaching #p = .05, the conventional significance level. I protest. *I* will only use the word "significant" when it refers to the outcome of an experiment with a null hypothesis and an alternative hypothesis well formulated before the experiment, where the experiment should be designed in such a way that all necessary precautions have been taken to prevent experimental artifacts favoring one or the other hypothesis. And even then, a judgement is necessary on the probability P that the experimenter has overlooked a source of errors large enough to account for an important part of the observed effect. Only when that probability P is below the claimed significance level, the significance level means something. After all, any judgement like "well, let's believe there is something there" rests basically on a more general type of judgement: reject the implausible in favor of the more plausible. As Professor Ertel will recall, I estimated the standard deviation at about 14 absolute, no matter what the exact value was for G%. However, the z = 1.23 was computed not from the 22.93 estimate, but from another one, namely the middle value 23.6 of Ertel's shift simulations. (Which I told Ertel, on his request). I clearly stated (I think) that I don't know the "true" expected value. # #I thought he had taken them from Zelen's comprehensive canvass #because Zelen's large N = 16,756 consisted of "ordinary" controls #for French athletes. But I found that setting out from that study #(details published by Gauquelin, 1977) he must have come up with #an expected G% = 21.84% Mars (N = 235). How are the percentages compared to the 24,961 births of the general population of Gauquelin, 1972? Are there any theoretical computations (like the 16.67% -> 17.2% of earlier Gauquelin computations) of the expected values? # #I checked G% with another special file of ordinary people in my #archive, (N = 1,713), ordinary controls in that file have one #Gauquelin athlete each as "birth twin" (born on the same day or up #to 4 days earlier or later). For them G% is 21.72%, close to With a margin of 1% plus or minus, so 2 more decimals are meaningless. #Zelen's expectancy of 21.84%. Now, if we use as control 21.84% #obtained by unsuspected skeptics and essentially confirmed by my #"replication", the indicator z for CFEPP's Mars G% with athletes #(N = 271) goes up: z = 2.658 , p = 0.0039. That is, even if we #follow Dr. Nienhuys' statistical approach and do it correctly the #result strongly supports the Gauquelin hypothesis. # #Nevertheless, the Nienhuys "parametric" test, even though feasible #in principle, is second to what I have been proposing with using #controls from year-wise shifts. Here we do not need new data as #estimates for chance expectancy ("ordinary people") nor do we have #to rely on "parametric" assumptions. But the test relies heavily on unproven and implausible independence assumptions. So: first a theoretical independence proof, and after that (and Benski's final report, convincing us sufficiently that his chosen standards are independent from data colleted by him) we'll see. #A second addendum refers to Dr. Nienhuys' alleging a statistical #error on my part in another study: Let's drop that (even though I am convinced that the track record of a researcher has bearing on significance claims). JWN Newsgroups: sci.skeptic Subject: Re: "Mars Effect": JWN replies Ertel's 23/10 post (pt 2a) Message-ID: <6050@tuegate.tue.nl> From: wsadjw@rw7.urc.tue.nl (Jan Willem Nienhuys) Date: 26 Oct 92 16:59:32 GMT Reply-To: wsadjw@urc.tue.nl Sender: root@tuegate.tue.nl References: <24OCT199209243794@skyblu.ccit.arizona.edu> <6041@tuegate.tue.nl> <6 049@tuegate.tue.nl> Organization: Eindhoven University of Technology, The Netherlands Lines: 57 In article <6049@tuegate.tue.nl> wsadjw@urc.tue.nl writes: ># ># 2.5 Inferential statistics. ># >#Dr. Nienhuys came up with z = 1.23 as deviation of observed Mars- >#born athletes (N = 271/1,076) from chance expectation which he >#estimated as N = 247/1,076 (G% = 22.93%). "Not impressive", he >#says. Error probability would be p = .11, so his statement could >#be rephrased by "not significant" ,i.e., not reaching >#p = .05, the conventional significance level. I calculated from Gauquelin 1972 (or rather from a table quoted there) on the basis of the mentioned 24,961 "ordinary people" that 22.9% is correct. I interpolated the expected values given for the 12-sector distribution (with sectors 1,2,3 and 10,11,12 making up rising and culminating standard sectors) to values for sectors 36 and 9, and arrived at the 22.9%. Originally I had applied the ratio 17.2/16.67 to 8/36, giving about the same. It doesn't matter whether one does it with the theoretical values or the actual observed values in that table. >As Professor Ertel will recall, I estimated the standard deviation >at about 14 absolute, no matter what the exact value was for G%. > >However, the z = 1.23 was computed not from the 22.93 estimate, >but from another one, namely the middle value 23.6 of Ertel's shift >simulations. (Which I told Ertel, on his request). I clearly stated >(I think) that I don't know the "true" expected value. I guess the middle value (from a uniform distribution coming out of Ertel's method) should be discarded. If we believe 22.9%, then this gives z = 1.78. Interesting, unless you insist on two-sided tests. >#Zelen's expectancy of 21.84%. Now, if we use as control 21.84% >#obtained by unsuspected skeptics and essentially confirmed by my >#"replication", the indicator z for CFEPP's Mars G% with athletes >#(N = 271) goes up: z = 2.658 , p = 0.0039. That is, even if we >#follow Dr. Nienhuys' statistical approach and do it correctly the >#result strongly supports the Gauquelin hypothesis. Observe the interesting discrepancy between 21.8 and 22.9, both coming out of a tabulation of results of about 20,000 people. Statistical theory says that the uncertainty in the percentage should be around 0.3 percent. And now we have a difference of 3 times that. "Hurray, again something significant"? (Two-sided at the 0.05 level! Chi-squared = 4.1, 1 df, roughly) Certainly not. No prior hypothesis. No test to check especially that hypothesis. Just an indication that this type of data *might* have more scatter to it than those nice binomially distributed variables from probability theory. JWN BTW, is anybody really interested in this, except Ertel and me? I hate to think that this is degenerating into some kind of SS (siano-sheaffer) dispute. From: Suitbert Ertel Subject: JWN and MARS EFFECT Message-ID: <9210240518.AA10924@lll-winken.llnl.gov> Date: Fri, 23 Oct 1992 16:13:48 MEZ My rejoinder to Dr. Nienhuys (JWN, Oct 12) might appear too long (514 lines). But, being quite explicit now may avoid requests for more explicitness later. ------------------------------------------------------------------ JWN and Mars Effect: A REJOINDER TO JWN's MESSAGE OF 12 OCT. 1992 ------------------------------------------------------------------ Dr. Nienhuys (JWN) takes issue with (1) former skeptics' tests of Gauquelin's planetary claim ("Mars effect"), (2) with Ertel's and Mueller's present test based on CFEPP (French skeptics) data. Re (1): Former tests -------------------- 1.1 Comite Para (Belgian: result favorable for Mars-effect). 1.1.1 Dr. Nienhuys says: "No one contends that the Para test came out favorable for G.". I am somewhat confused. Para researchers themselves said: "The distribution of the actual frequencies of Mars [in our data] is far from uniform: they display the same general pattern found by M.M. Gauquelin with samples of other sports champions... The Comite Para therefore gives its agreement on this point with the results of M.M. Gauquelin" (1976). The Belgians had not expected replication of the Gauquelin pattern in their data, they then conjectured - without giving evidence - that this pattern must be due to some artefact. Addendum: Dr. Nienhuys in response to one of my direct messages says that "contends" was a slip of the tongue, his sentence should have read "No one contests that..." 1.1.2 Collecting names of eminent athletes within some country by two independent researchers should result in an overlap of names if the collections are done well. For instance, among any sample of the most eminent Dutch painters, names like Rembrandt, van Ruisdael, Vermeer van Delft, etc., should show up, otherwise the collector did bad work. The occurrence of overlapping names therefore does not of itself give sufficient reason to suspect collaboration among name collectors or plagiarism. Collaboration between Comite and Gauquelin resulting in support for Gauquelin's claim is very hard for me to conceive. If Dr. Nienhuys means by "causal links" that effects favoring Gauquelin's claim might have occurred inadvertently he should explain how snooping into former Gauquelin results might have led Comite to thwart their own intention. 1.2 Kurtz', Zelen, Abell's (U.S.: result unfavorable for Mars-effect). Glossary: Mars G% = percentage of individuals in a sample with Mars in rising or culminationg sectors (= "key sectors"). Mars effect = G% significantly greater than chance expectation. Eminence effect = G% for athletes' samples increase with average athletic success (G% for mediocre athletes may not yet deviate from the chance level) The Dutch skeptics had tried "to find a naturalistic explanation for Gauquelin's and Comite Para's findings", Dr. Nienhuys says. Those findings had been positive (Mars G% above chance level). Then, however, came the U.S. test which was negative. Careful reading of Nienhuys' passage will show that for the Dutch this must have been good and bad news at the same time. Their devising of a naturalistic explanation for positive deviations will have nourished expectations that any test of Mars sector frequencies for athletes, the U.S. test included, would yield G% above chance expectation. Now G% of the U.S. test wasn't above chance expectation, numerically it was even slightly below it. But apparently, the Dutch skeptics' belief in their naturalistic approach had not been very strong, since Dr. Nienhuys now says "the U.S. test was quite convincing". It is worth noting that the Dutch researchers failed to defend their naturalistic explanation against those *negative* U.S. results (G% not above chance level). They might have defended it by using the "biased selection" argument which Dr. Nienhuys is presently putting forward against the *positive* CFEPP result (G% above chance level). It is pertinent that Dennis Rawlins, one of the astronomers who made computations for Kurtz' and Abell's study of the U.S. athletes gave with "sTARBABY" an account of what occurred behind the stage which would make it sensible if not inevitable to suspect that the U.S. data had not been collected without bias - Rawlins' probable exaggerations notwithstanding. My own reanalysis of Kurtz'et al. data gave independent support: In CSICOP members'U.S. sample average athletic success (citation counts) was much lower than with another sample of U.S. athletes that Gauquelin collected right after CSICOPian findings had been published in THE SKEPTICAL INQUIRER ("Results of the U.S. test of the "Mars Effect" are negative", 1979/80).That is, CSICOP researchers had unquestionably violated - possibly on the fringe between intention and inadvertence - Gauquelin's eminence requirement. Re (2): Present test -------------------- 2.1 Selection bias. Dr. Nienhuys, having suspected biased data-selection by the Belgian skeptics, now suspects that of the French skeptics. Bias in the French sample cannot be excluded out of hand. However, we should also not exclude out of hand any possible answer to the question: If there is bias in CFEPP's sample would its effect be to favor or disfavor Gauquelin's Mars percentage? Let us try to find out. Benski (or CFEPP) drew their sample using Gauquelin's main biographical source: LEROY: Le Dictionnaire des Sports. Under optimal conditions the overlap between Benski and Gauquelin for that source should be 100%. In archival research, however, conditions are rarely optimal, for instance, registry offices may not have the data, or they just do not respond to data requests from researchers. They may provide data to a first request, but not to the second, or vice versa. Thus we find only 52.4% of published Gauquelin athletes in Benski's sample and 69.7% of Benski's athletes in Gauquelin's published sample. However, misses at registry offices are only one possible cause for divergence between samples in this field, another is subjectivity of judgment regarding athletic eminence. Gauquelin said he excluded low achievers by applying certain criteria (see Nienhuys). But here arbitrariness may enter, one of the reasons for CFEPP to redo the Gauquelin study with LEROY was to find proof for their suspicion that Gauquelin's Mars effect was due to deliberately selecting suitable cases. Now, Dr. Benski, bound to also consider Gauquelin's eminence requirement, said that he accounted for it by applying selection criteria of his own. Unfortunately his criteria are less precisely described than Gauquelin's - which were not precise enough either. Moreover, Benski's criteria are less strict, an athlete need only to have participated in some "competition on a national level" to be included in CFEPP's sample. That is, for CFEPP there was no less room for biased selections than for Gauquelin. An impartial assessment of both studies is required, let us compare Benski (BE) and Gauquelin (GQ) as follows: (A note first: We will deal with GQ's published (N = 809) and unpublished (N = 246) athletes taken from LEROY. As early as 1986, I had expected and in fact discovered unpublished birth data when I visited Gauquelin in his Laboratoire in Paris. For the CFEPP sample, we do not know whether any selected athletes were excluded from publication. But there is no reason to assume that anyone was excluded). To begin with we recollect that Mars G% for BE's for total sample is 25.19% (271/1076). Next we may ask: What is the Mars G% for those BE athletes who are also found in GQ's total sample comprising his published and unpublished data? Call it the overlap or "BE_GQ sample". The answer is: G% for BE_GQ = 26.27%, 234/925. That is, Mars G% for BE's "Gauquelin-also" athletes (overlap) is 1.08% above the G% for BE's total sample (25.19%, 271/1076). Whence this difference? BE listed 151 athletes who appeared neither in GQ's published nor in his unpublished sample, call them "BE-only" athletes. For them, G% is only 18.54% (28/151). (Note: "BE_only athletes"+ "BE_GQ athletes" = BE's total sample). This looks as though bias were at work. If so, it would add to our list of causes for GQ-BE divergence (3), sampling bias, in addition to causes (1) different responses from registry offices and (2) differing criteria of eminence. What is important to note here is that BE`s bias - if it was bias - went in the GQ-*unfavorable* direction. Any bias on GQ's part would have tended to the GQ-*favorable* direction. And indeed he collected 130 athletes that did not appear in BE`s sample ("GQ- only"). For them the G% is 31.54% (41/130). I think we can justifiably take 26.27%, the Mars G% for the sample common to both, BE and GQ, as closest to a "true" or bias-free G%- level for successful LEROY athletes. The "GQ-only" athletes deviate +5.27% from the "true" level, while "BE-only" athletes deviate -7.73 from the "true" level. That is, both, GQ and BE samples, appear to be biased, with BE's-bias not being smaller than the GQ's-bias. In an earlier paper published in the Journal of Scientific Exploration I scrutinized GQ-bias, so we know how it worked there (Ertel, 1987). How could BE's bias have worked? First, BE (or whoever did the sampling) might have discarded athletes, prior to own data collection after noticing positive Mars sectors in published Gauquelin data. This would have increased the numbers of athletes in the "GQ-only" subsample associated with above average G%, assuming that BE hoped to disprove GQ-claims. Indeed, G% is +5.27% above average in "GQ-only" data (see above). Second, BE's bias might also have led the data collector to readily include, when the sample was formed - i.e., without knowing Mars sector positions - mediocre athletes in the experimental sample. For less successful athletes lower G% levels had been predicted (Gauquelin, Ertel), so inasmuch as BE assumed that an eminence effect might exist and inasmuch as he did not like to have such effects in his data he might have tended to choose mediocre sportsmen. This would have increased the "BE-only" subsample associated with a reduction of G%. We found such reduction, the difference was -7.73% (see above). Effects of BE-bias and GQ-bias, however, cannot easily be disentangled without supplemetary analysis including eminence as a variable. This will not be done here. Suffice it to say that some BE-bias probably existed and that, if it existed, it had the right direction consistent with BE's skeptic expectation. The main conclusion from comparing BE's with GQ's numbers is this: Even allowing for an apparent BE-bias in CFEPP's data they do support the Mars effect hypothesis with an error probability of at least p = .01. 2.2 Control samples by year-wise shifts Dr. Nienhuys apparently rejects testing for planetary effects by examining the effects of shifts by units of years. He points out that fixed stars take the same positions in the sky every year at the same time and by the same token, Mars is purported to recur every year in similar positions. As the planet can only move within the restricted limits of the belt of the ecliptic, variations of position are deemed to be small. Three comments here: First, annually recurrent positions of fixed stars are unrelated to the positions of Mars sectors. Even if the universe were somehow to lapse into chaos while leaving the solar system intact nevertheless the diurnal rise, culmination and set of Mars, or more generally, sector positions defining the Mars G% would remain unaffected. Second, ecliptical constraints on the movements of Mars in the sky have again nothing to do with the diurnal positions of the Mars sectors. That is, the fact that the diurnal half or near-half Mars circle above the horizon, as seen from a fixed point on earth, does not vary much during the Martian year, is irrelevant. If the ecliptic were a line without leaving any room for variation instead of a belt Mars G% would not change. (The astronomically less informed reader may be reminded here of the more familiar seasonal variations in positions of the sun between summer (high) and winter (low) right ascension (= angle between culmination point and horizon). The positional variation of Mars during one Martian year ( = 2.14 solar years) resembles that of the sun during one solar year. I don't know whether Dr. Nienhuys begging a convincing gist in his argument would accept my clarifying paraphrase of it: "Time series consisting of G proportions obtained once every year on the same day are autocorrelated, i.e. successive measurements are not independent, therefore they cannot be utilized, as Ertel did, as controls." If that was his point and if his premise were true his conclusion would be valid. His objection might even hold empirically, for some reason or other, irrespective of its erroneous deduction. Therefore I calculated an autocorrelation function across N = 51 shifts of G% arranged in year-by-year order. I did not find any significant signal, r's for lag = 1 and lag = 2 are -0.1 and .10, respectively, both insignificant - autocorrelations should peak with lag = 1 and 2 if events observed in t(i) depend on events observed in t(i-1) and t(i-2). Thus, by adding to our time series of G% more observations with successive year-wise shifts beyond N = 51, as I suggested in my earlier message, the basis for statistical inference would unquestionably become safer. Another significance test with >50 control observations might have two possible outcomes: First, the probability of erroneously concluding that CFEPP data display the Mars effect might rise above .05, the present finding would thus become insignificant - which is what Dr. Nienhuys would probably welcome. However, second, he would also run the risk of witnessing the Mars effect boosting its success: error probability might drop below the present .01 level. I admit that my asking him in my earlier message whether I should go on with year-wise shifts was not meant as a serious question but as a kind of testing him at an impasse - perhaps we should test our subject matters only, not test each other. I apologize. 2.3 Playing around with data Dr. Nienhuys says I certainly played around with insignificant data until I hit upon a test that gave the desired effect. He refers to my recent report about an analysis of the same data at a conference in Munich (First European SSE-Meeting) where I presented results obtained by shifting the data by units of *hours* only. Dr. Nienhuys' comment, however, should also have referred to another bit of information about those shifts that I presented in Munich: the G- proportion obtained from the *correct* birth hours exceeded all those obtained with the birth hours shifted (as much as 24 shifts). I admit to having done some further playing when nobody was around: I tried shifting birth dates by *days*, too. Again, however, the Mars G% for *genuine* data surpassed all G% values calculated by shifting the data in units of days (N = 20). One of the reasons for our eventually preferring shifts by *years* was that with shifts by hours or days the G% are autocorrelated which prevents any straightforward calculation of error probabilities - Dr. Nienhuys objection above would have applied if we had disregarded autocorrelation for shifts by hours/days. With shifts by years we solved the problem (see Table 1). Table 1 --------------------------- autocorrelations --------------------------- lags: 1 2 --------------------------- {hour-wise .684 .255 shifts {day-wise .707 .390 {year-wise -.012 .099 --------------------------- Note: Considerable autocorrelations are observed with shifts by hours and days, not with shifts by years. Controls obtained by units of years have an additional advantage: They exclude, if present, possible contamination by diurnal or seasonal factors. Had we "played around" and hit upon the present technique earlier (shifts by years) the former Dutch attempts to explain positive G% excesses by naturalistic mechanisms could hardly have been launched with any optimism. At that time (1991) in Holland optimism culminated. When the EUROSKEPTICS met in Amsterdam one of the Dutch researchers, Mr. Koppeschaar, announced an "unmasking" of Gauquelin's Mars effect; and the Dutch newspaper VOLKSKRANT having obtained pertinent information through de Jager, Koppeschaar, and Jongbloet, referred to the Mars effect as an artefact due to biological rhythms. The "Gauquelin bastion" was "crashing", one newspaper headline proclaimed. Such jumping to conclusions and their public dissemination, was it necessary? 2.4 "Warning bell": recurrent values Dr. Nienhuys might have asked me whether I could explain recurrence among the 51 percentages - but he preferred to forget where the decimal numbers came from and to calculate an 10^-9 impossibility ending up in ringing the bell. I would have been pleased to point out to Dr. Nienhuys the following: The total number of athletes is 1,076. The proportion of athletes having Mars in key sectors varies between 25.19% and 21.10% across 51 samples (one genuine, 50 controls). That is, the range of *absolute* frequencies span between 271 and 227. With 51 observations ranging between 271 and 227, there are 45 possible results: 271(1), 270(2), 269(3)... 227(45). Numbers must therefore recur: First, of necessity, there are 6 more observations than there are distinct possible results. Second, chance effects will increase recurrences of numbers just as throwing a dice, say twelve times, results a non-uniform occurrence of the possible numbers - the one-dot side may turn up 4 times, the two-dots side may not show up at all in 12 trials etc.. Third and finally, we have to consider that very high and very low numbers among those 51 empirical observations would tend to be rarer than those in the central range of the distribution. 2.5 Inferential statistics. Dr. Nienhuys came up with z = 1.23 as deviation of observed Mars- born athletes (N = 271/1,076) from chance expectation which he estimated as N = 247/1,076 (G% = 22.93%). "Not impressive", he says. Error probability would be p = .11, so his statement could be rephrased by "not significant" ,i.e., not reaching p = .05, the conventional significance level. First, I recalculated Nienhuys' numbers. Upon my request he had kindly described what he had done , but his calculations were apparently homespun, z must be obtained by normal approximation to the binomial (or "Critical Ratio" - C.R., as it was once called). Approximated z for Nienhuys' estimates is 1.740, p = 0.041. According to conventions ------------------------------------------------------------------ z = ( x - x')/sqrt(n * p * q ), inserting Nienhuys' numbers: z = (271-247)/sqrt(1076*.2293*(1-.2293) = 1.740. ------------------------------------------------------------------ this is significant (Consult, e.g., W.L.Hays: Statistics, NY: Holt 1988 4th ed., p. 286 ff). Dr. Nienhuys also kindly provided some information about how he had estimated chance expectancy of 22.93% which he had entered in his formula. He said the data were taken from ordinary people serving as a control group. Ordinary people as controls, o.k. But from which study were they taken? I thought he had taken them from Zelen's comprehensive canvass because Zelen's large N = 16,756 consisted of "ordinary" controls for French athletes. But I found that setting out from that study (details published by Gauquelin, 1977) he must have come up with an expected G% = 21.84% Mars (N = 235). I checked G% with another special file of ordinary people in my archive, (N = 1,713), ordinary controls in that file have one Gauquelin athlete each as "birth twin" (born on the same day or up to 4 days earlier or later). For them G% is 21.72%, close to Zelen's expectancy of 21.84%. Now, if we use as control 21.84% obtained by unsuspected skeptics and essentially confirmed by my "replication", the indicator z for CFEPP's Mars G% with athletes (N = 271) goes up: z = 2.658 , p = 0.0039. That is, even if we follow Dr. Nienhuys' statistical approach and do it correctly the result strongly supports the Gauquelin hypothesis. Nevertheless, the Nienhuys "parametric" test, even though feasible in principle, is second to what I have been proposing with using controls from year-wise shifts. Here we do not need new data as estimates for chance expectancy ("ordinary people") nor do we have to rely on "parametric" assumptions. This procedure is "distribution-free",i.e., the question of fit to model distributions such as the normal or binomial function does not arise. The test is "exact", it is as unlikely that erroneous expectations would gain invalid support as it is unlikely that substantial expectations would fail to obtain warranted support. Summarizing from the opposite perspective Let me summarize by giving my paraphrase of Dr. Nienhuys' arguments: 1. BENSKI'S DATA MIGHT BE BIASED. (It is true - argues JWN - that the direction of Benski's bias effect, as I (JWN) understand it, is inconsistent with Benski's expectation in view of his skeptical viewpoint. I (JWN) also admit that such Benski bias would oppose bias effects underlying Gauquelin's data selections where the effects were *consistent* with the researcher's expectation (Ertel's result). Nevertheless,... ) ...POWERFUL SUBCONSCIOUS *CAUSAL CONNECTIONS* WITH GAUQUELIN'S EARLIER ANALYSES MIGHT ALWAYS EXIST. (My -JWN's- suspicion regarding proper sampling by the French skeptics and its effect on G% may be considered absurd, even offensive, but such possiblilities must be considered in case Ertel's data analysis is correct. If I could safely assume Ertel's analysis to be flawed I would not have to risk such - admittedly weird - speculations. Nevertheless, I should better contend, without expressing any doubt:...) 2. ... ERTEL'S ANALYSIS OF BENSKI'S DATA IS FLAWED. APPARENTLY HE PLAYED WITH THIS DATA UNTIL THE RESULTS WERE "SIGNIFICANT". (If he played with the data, the significance test itself that he applied may be correct since his having played with data with no one else around invalidates any statistical conclusions. Unfortunately, I cannot be sure that he played with data. Therefore it is safer to contend that...) ... ERTEL'S TEST OF SIGNIFICANCE IS WRONG: HIS CONTROLS OBTAINED FROM YEAR-WISE SHIFTS ARE NOT INDEPENDENT. REMEMBER YOUR NIGHTLY LOOKING AT THE SKY: THE FIXED STARS REAPPEAR EVERY YEAR AT THE SAME LOCATIONS, SO MUST THE PLANETS, EXCEPT FOR SOME MINOR VARIATIONS. (I couldn't give any astronomical proof for that offhand - but doesn't that sounds very plausible? ...). THE PROOF IS RIGHT HERE: LOOK AT RECURRING NUMBERS IN ERTEL'S TABLE. THEY CLEARLY MIRROR AN ANNUAL RECURRENCE OF MARS POSITIONS. ERTEL IGNORED THE WARNING BELL. LET HIM PERISH. Back to my (Ertel's) own perspective: Dr. Nienhuys' run of breakneck leaps in this discussion could have been avoided had he considered another way out of the dilemma between Scylla (Benski) and Charybdis (Ertel), namely: The Mars effect might virtually exist. ------ Three addenda ----------- An addendum referring to Dr. Nienhuys' report about F. Gauquelin "refusing data" etc.: This refers to Francoise Gauquelin, Michel Gauquelin's first spouse who assisted him with data collection etc. for 30 years. I probably should say that Mrs. Gauquelin does not have facilities to communicate electronically and might want the chance to defend herself against Dr. Nienhuys' accusation. A second addendum refers to Dr. Nienhuys' alleging a statistical error on my part in another study: Objections of GWUP published recently will be replied in due course, but an error there, if it occurred at all, would not be relevant to the analysis here. Apparently, Nienhuys' reference to this incidence wasn't meant as a contribution to scientific discourse but as seizing what appeared to him as an opportunity for strategic advantage. Addendum # 3 refers to a misplaced metaphor: Dr. Nienhuys wants to see that "dubious type of ..." research on the Mars effect "nipped in the bud." If Dr. Nienhuys' plea to "nip" this approach would result in continued research by competent disbelievers, his metaphor would have served a good purpose. But will it really encourage more research? I am afraid not, it lacks power. "Bud" doesn't suit as a metaphor for a line of research looking back at 40 years of history with more than 200 technical publications. Nor does "nip" fit considering the energy spent by four different skeptic groups from four different countries with four astronomers involved to make an end, by empirical weapons, to Gauquelin's offence against scientific credos. One of these groups' recent attempt - the best one regarding care of data collection and numbers of observations - ended up, as I have shown in my earlier message, with unbending support for Gauquelin's survival. A "bud"? No, a "rock on the road of science"- that metaphor by Arno Mueller is proper. The effort needed to move that "rock" away from everyday scientific traffic should no longer be underrated. Suitbert Ertel Institut fuer Psychologie Gosslerstrasse 14 3400 Goettingen FAX: 0551-393662 email: SERTEL@DGOGWDG1.BITNET From: Suitbert Ertel Subject: JWN and MARS EFFECT Message-ID: <9210240517.AA10862@lll-winken.llnl.gov> Date: Fri, 23 Oct 1992 16:12:37 MEZ Rick Moen recently complained about too much advocacy and social policy, philosophy... together with lack of discussion about claims of fringe science in this circle. My reply to Dr. Nienhuys' objections ------------------------------------------------------------------ From: Rick Moen Subject: Skeptics' focus X-To: skeptic@vm1.yorku.ca To: Multiple recipients of list SKEPTIC ------------------------------------------------------------------ against my analysis of athletes data collected by French skeptics and its result (Mars effect supported) may ameliorate that state of affairs. For those who would like to have Dr. Nienhuys' contribution at hand - I will refer to it - I am posting it here. My reply to this is a seperate posting right after this one. S.E. ------------------------------------------------------------------- --------------- JWN's contribution of Monday 12 Oct --------------- Newsgroups: sci.skeptic Subject: Ertel's Error Message-ID: <5910@tuegate.tue.nl> From: wsadjw@rw7.urc.tue.nl (Jan Willem Nienhuys) Date: 12 Oct 92 13:26:11 GMT Reply-To: wsadjw@urc.tue.nl Sender: root@tuegate.tue.nl Organization: Eindhoven University of Technology, The Netherlands I'm sorry that this post is so long, but I have to include almost all of Ertel's remarks. Moreover, the explanation of why something is wrong takes up more space than the committing of the error itself. There goes my lunch break.... Ertel writes: # #My reply is short. only 5530 characters, compared to JWN's long exposition of 5300 characters :-) # #The main question to be kept in mind is this: # # IS THERE A MARS EFFECT? # I prefer: is there convincing evidence in favor of the Mars effect? #The Belgian skeptics (Comite Para) tried to refute Gauquelin's claim #by collecting N=535 new athletes data (published in 1976). # #Apparently, they couldn't refute G's claim. Otherwise U.S. #skepticts (Paul Kurtz et al.) would hardly have tried the #laborious Zelen test consisting of collecting birth data of #N=16,000 French ordinary people (control group) (1977). No one contends that the Para test came out favorable for G. The Zelen test was a test to examine one particular naturalistic explanation for the test result. It was a rather superfluous exercise, but at the time Zelen and others were not convinced that the Gauquelins had adequately corrected for demographic/astronomical factors (but he had). The disconcerting thing about the Para test for me is that the 535 athletes contained 203 athletes whose Mars sectors were known already by Gauquelin. It is not clear how many causal links there are between Gauquelin's knowledge of the Mars sectors of these 203 athletes and the choice of proficiency levels by the comit\'e Para. It seems clear (again from Ertel's own researches) that Gauquelin knew very well that Belgian soccer players with less than 20 international games would give a poorer result than the case of 20 games as minimum level. # #The results of the Zelen test apparently did not shake #Gauquelin's claim either, otherwise the same researchers would #hardly have tried another test consisting of collecting birth #data of N=408 U.S. athletes (1979/80). # #Again, the U.S. athletes test was apparently unconvincing. #Otherwise the Dutch skeptics would hardly have dived into that #matter again, they did it twice. I think I may speak for Dutch skeptics (D.S.). Of course the U.S. test is quite convincing - as far as any single test can be convincing. The D.S. tried to find a naturalistic explanation for the findings before the U.S. test. Especially because the U.S. test was negative, the problem remained: what was the explanation for the other results? # First their idea was: Birth #excess of Gauquelin athletes with Mars in G-zones exists, but it #can be explained by diurnal and/or seasonal association (published #in 1991). On closer look (and computation) they abandoned this #idea. Next they explained Mars birth excess for Gauquelin #athletes by Gauquelin's selection bias (in print) - they had #become aware of my detailed account of the Gauquelin bias effect #in the Journal of Scientific Exploration (1988). One skeptic (Koppeschaar) gave up also because F. Gauquelin would not give him the data he asked for. He had received from Ertel many data just after he asked. F.G. blamed Ertel for this, and refused to give more data, unless Koppeschaar would sign all kinds of documents declaring his intent and purpose (and one might suspect that F.G. would be fully prepared start legal battles when K. would say something she didn't like.) # #There is another skeptics group, the French CFEPP, which #apparently remained unconvinced by the Belgian and the two #American approaches. They started collecting new French athletes #birth data in 1983 and gave a report (unpublished) about their #procedure in 1990 adding an appendix providing birth data of #1076 athletes (Dr. Benski). Results of an analysis of CFEPP's #data have not been published until today. Therefore, Arno #Mueller and myself did an analysis of CFEPP's data (we informed #Dr. Benski in advance). We computed, first, the main indicator: #G percentage, i.e., the percentage of French athletes born with #Mars in key sectors), the result is 25.19%. This is probably the sum over sectors 36, 1, 2, 3, 9, 10, 11, 12 in the 36-sector division. I don't know what is exactly the expectation for these sectors, I guess something like 22.9%, taking into account astro/demographic factors. So expected: 247 +/- 14, and actually found 271. From the table below, it seems that 23.6% is a better estimate for the "expected average", so that would mean 254 +/- 14, and hence the actual 271 is 1.23 Standard Deviations away from the mean, which is not too impressive. The important question is again: how independent of Gauquelin's knowledge of the athletes's sectors is this result? I know for certain that Benski conferred extensively with M. Gauquelin. Were all the 1076 athletes "new", or are there again a lot of old ones from previous researches mixed in? # #Then we shifted the birth dates by one year. An athlete born on, #say, Jan 25 1938, at 3 a.m., was attributed the birth date and #time Jan 25 1939, at 3 a.m. We calculated G% for shifted birth #data. Then we shifted by two years and calculated G% again. The #same procedure was repeated by stepwise yearly shifts up to 25 years. #The same shifts were applied in the opposite direction (-1, -2 #.. -25 years). # #(Stepwise yearly shifts are applied here for the #first time as an improved test for a planetary #effect. The improvement consists of relating the experimental #group of genuine individuals to control groups of dummy #individuals whose "births" occurred under exactly the #same diurnal and seasonal conditions as those present at #the births of the experimental individuals.) # #What might Dr. Benski and Dr. Nienhuis (JWN) hypothesize here? Nienhuys if you please. #I guess they might expect both that the genuine #G% value of 25.19% does not deviate significantly from the #distribution of 50 G% values obtained from the dummy controls. # #The result, however, does not confirm this hypothesis. I am #appending a table showing 51 G% values in descending rank order. #The value on top is G% obtained from the genuine birth data. The #error probability of finding the genuine value on top is p=.01 #which is generally regarded as very significant (allowing for a #one-tailed test which is here called for). # #Now I would like to ask JWN how confident he is, on inspecting #these results, that the Mars effect does not exist. This would be all a lot more convincing when (1) I knew more about the degree to which the criteria for inclusion and exclusion in the 1076 athletes has been independent of Gauquelin's knowledge of their birth times/Mars sectors, (this I cannot answer, only Benski can,.... possibly) and (2) this were not so much post-hoc. We cannot know the number of analogous tests that there is nothing special about these results. If I *assume* that he would have given up only after trying 20 different tests, then finding a single test at the p=0.01 level is not that striking. I definitely got the impression this summer in M\"unchen, that he had tried shifting by multiples of half an hour. It should not be necessary that scientists have to speculate about what other scientists have been playing around with the data when nobody else was looking. This gives rise to all kinds of unpleasant insinuations. THAT is the reason why I think post-hoc analysis is distasteful. There is also a statistical error in the above argumentation of Ertel. He apparently assumes that computing a one-year shift will result in a sample that can be considered a random sample. But different shifts are not independent. To understand that I reason as follows. Shifting the time back by an integral number of years will give you for the same time almost exactly the same configuration of fixed stars at birth. The sky with fixed stars (and hence the ecliptica) will have shifted by at most a degree (because of leap days). A degree is little, compared to the width of 40 degrees of the Ertel G-zones (36+1+2+3 and 9+10+11+12). The fifty years represent therefore more or less randomly distributed positions of Mars on that same ecliptic. On average, these positions will be about 7 degrees apart. But positions 7 degrees apart will give highly correlated answers. Only when you shift by 40 degrees you get something approaching a mimick of an independent sample. (I've pointed out something similar to Ertel related to his half hour time shifts.) Moreover, a shift of 100 degrees will bring an overlap of zone 36+1+2+3 with 9+10+11+12, so again a correlation. In other words, what looks like 50 independent results only represents a much smaller number of independent results. Say about 8, then the Benski result again has a one-sided p-value of 0.12. Not significant, especially not because of the unknown bias introduced in the manner I described. At a previous occasion (see latest issue of GWUP's Skeptiker) Ertel has also found a "result" by a combination of a complicated statistical detour, combined with a rather elementary error. In that case too, if he had avoided the error, he would have found about the same result as the simple argument without the detour. In that case the detour consisted of a complicated and artificial way of computing an average, here it is a tricky way to artificially inflate the number of independent samples. Even for somebody who could not think of the above argument him/herself, the data that Ertel presents below (his own data) should have warned him that they cannot represent independent draws from random variable: the distribution of percentages is nearly uniform (between 21, 22, 23, 24 and 25 there are respectively 10, 13, 13, 14 year shifts). Moreover, the fact that in the interval from 21 to 25 there are 3 values that are repeated 4 or more times with an accuracy of <=0.01 should also have rung a warning bell. The chance that of 50 random numbers in that interval there should be 4 that round up to two decimals to the same value is roughly 0.003, and for 5 it's a tiny fraction of that. That there should be 3 such values is very improbable (10^-9) IF these values represented independent draws from some distribution. # #Second - assuming he is not yet confident enough about #the nonexistence of a Mars effect - how many additional yearly #shifts he wants us to calculate in order to improve his #confidence that the Mars effect actually does not exist. Or #else, what he would suggest should be done now to put his #conclusion and that of other critics of the Mars effect on firmer #ground. [ironic remark. What about just doing all shifts again, ten times. This will give 500 shifts, and a p-value of 0.002 ! There is hardly any difference between adding in the results of 450 more shifts, or just repeating the same 50 shifts over and over again.] I don't want any more post-hoc calculations. I want data that are collected (in this case birth data of eminent sportsmen and -women) in such a way that it can be PROVED that the decision to include or exclude CANNOT be related to knowledge of that person's Mars sector. This means: any athlete whose birth time has ever been known to Gauquelin should not be in the sample, because that birth time may have contributed to setting a criterion for inclusion or exclusion. The only test in which this condition was (almost) fulfilled was the U.S. test. Even that test was not perfect, because the decision to go on collecting data was based on knowledge of the data of the first 128 athletes. And the CSICOP probably has come to regret that error. ... I hope I have not been boring my audience with these technical discussions, but it's better that this dubious type of post-hoc statistics gets nipped in the bud. J.W. Nienhuys, Research Group Discrete Mathematics Dept. of Mathematics and Computing Science Eindhoven University of Technology P.O. BOX 513, 5600 MB Eindhoven The Netherlands e-mail: wsadjw@urc.tue.nl From: Suitbert Ertel Subject: JWN and MARS effect Message-ID: <9210112343.AA10905@lll-winken.llnl.gov> Date: Mon, 12 Oct 1992 00:33:52 MEZ JWN's contribution to the MARS effect debate is meticulous, but long. My reply is short. The main question to be kept in mind is this: IS THERE A MARS EFFECT? The Belgian skeptics (Comite Para) tried to refute Gauquelin's claim by collecting N=535 new athletes data (published in 1976). Apparently, they couldn't refute G's claim. Otherwise U.S. skepticts (Paul Kurtz et al.) would hardly have tried the laborious Zelen test consisting of collecting birth data of N=16,000 French ordinary people (control group) (1977). The results of the Zelen test apparently did not shake Gauquelin's claim either, otherwise the same researchers would hardly have tried another test consisting of collecting birth data of N=408 U.S. athletes (1979/80). Again, the U.S. athletes test was apparently unconvincing. Otherwise the Dutch skeptics would hardly have dived into that matter again, they did it twice. First their idea was: Birth excess of Gauquelin athletes with Mars in G-zones exists, but it can be explained by diurnal and/or seasonal association (published in 1991). On closer look (and computation) they abandoned this idea. Next they explained Mars birth excess for Gauquelin athletes by Gauquelin's selection bias (in print) - they had become aware of my detailed account of the Gauquelin bias effect in the Journal of Scientific Exploration (1988). There is another skeptics group, the French CFEPP, which apparently remained unconvinced by the Belgian and the two American approaches. They started collecting new French athletes birth data in 1983 and gave a report (unpublished) about their procedure in 1990 adding an appendix providing birth data of 1076 athletes (Dr. Benski). Results of an analysis of CFEPP's data have not been published until today. Therefore, Arno Mueller and myself did an analysis of CFEPP's data (we informed Dr. Benski in advance). We computed, first, the main indicator: G percentage, i.e., the percentage of French athletes born with Mars in key sectors), the result is 25.19%. Then we shifted the birth dates by one year. An athlete born on, say, Jan 25 1938, at 3 a.m., was attributed the birth date and time Jan 25 1939, at 3 a.m. We calculated G% for shifted birth data. Then we shifted by two years and calculated G% again. The same procedure was repeated by stepwise yearly shifts up to 25 years. The same shifts were applied in the opposite direction (-1, -2 ... -25 years). (Stepwise yearly shifts are applied here for the first time as an improved test for a planetary effect. The improvement consists of relating the experimental group of genuine individuals to control groups of dummy individuals whose "births" occurred under exactly the same diurnal and seasonal conditions as those present at the births of the experimental individuals.) What might Dr. Benski and Dr. Nienhuis (JWN) hypothesize here? I guess they might expect both that the genuine G% value of 25.19% does not deviate significantly from the distribution of 50 G% values obtained from the dummy controls. The result, however, does not confirm this hypothesis. I am appending a table showing 51 G% values in descending rank order. The value on top is G% obtained from the genuine birth data. The error probability of finding the genuine value on top is p=.01 which is generally regarded as very significant (allowing for a one-tailed test which is here called for). Now I would like to ask JWN how confident he is, on inspecting these results, that the Mars effect does not exist. Second - assuming he is not yet confident enough about the nonexistence of a Mars effect - how many additional yearly shifts he wants us to calculate in order to improve his confidence that the Mars effect actually does not exist. Or else, what he would suggest should be done now to put his conclusion and that of other critics of the Mars effect on firmer ground. Suitbert Ertel ---------- APPENDIX ---------------------------------------------- Results of testing for a Mars effect using the stepwise yearly shift procedure Data: CFEPP French athletes (N=1,076) ------------------------- rank shift by by size years G% ------------------------- 1 0 25.19 genuine ------------------------- 2 -10 25.00 dummyes 3 -25 24.54 dummy 4 -14 24.54 ... 5 -6 24.54 6 6 24.54 7 8 24.54 8 17 24.44 9 -12 24.35 10 -11 24.35 11 21 24.35 12 22 24.26 13 11 24.07 14 20 24.07 15 -9 24.07 16 -8 23.98 17 -13 23.88 18 2 23.88 19 4 23.88 20 -20 23.88 21 -3 23.79 22 3 23.79 23 18 23.70 24 5 23.70 25 23 23.70 26 -23 23.61 27 -21 23.42 28 24 23.23 29 25 22.86 30 -4 22.86 31 -18 22.77 32 14 22.68 33 10 22.58 34 -7 22.40 35 -17 22.30 36 -22 22.30 37 -19 22.30 38 -24 22.30 39 15 22.21 40 12 22.12 41 -5 22.03 42 7 21.93 43 1 21.93 44 13 21.84 45 -15 21.75 46 19 21.56 47 16 21.47 48 9 21.47 49 -2 21.38 50 -16 21.28 51 -1 21.10 ------------------------------------------ From: "James J. Lippard" Subject: Re: JWN and MARS effect Message-ID: <9210120113.AA14530@lll-winken.llnl.gov> Date: Sun, 11 Oct 1992 18:10:44 -0700 In case anyone is puzzled by Suitbert Ertel's recent message, it was prompted by my forwarding him the following three messages from the sci.skeptic newsgroup. These messages are an exchange between Jan Willem Nienhuys and York Dobyns which occurred as a result of an earlier crossposting from alt.astrology. I will be posting Prof. Ertel's reply to sci.skeptic. Newsgroups: sci.skeptic Subject: Re: Fwd: Astrology: Scientific Research (Was Re: Doubters Of Astrology) Message-ID: <5874@tuegate.tue.nl> From: wsadjw@rw7.urc.tue.nl (Jan Willem Nienhuys) Date: 7 Oct 92 17:29:06 GMT Reply-To: wsadjw@urc.tue.nl Sender: root@tuegate.tue.nl Organization: Eindhoven University of Technology, The Netherlands Lines: 122 >Anyone want to comment? Yes but only to parts. The whole piece is too long. > >The so-called "Mars effect" is that *champion* athletes (not >athletes in general) have Mars above the ascendant (i.e., just >risen) or just past culmination (i.e., just past the planet's >highest point in the sky) with a frequency greater than expected >by chance. > >This Mars effect has been replicated now by two skeptics' >organisations, one in Belgium (Belgian Committee for the >Scientific Study of Paranormal Phenomena) and one in America. In >the latter case, the group providing the replication was CSICOP >(Committee for the Scientific Investigation of Claims of the >Paranormal). They originally published tainted results which A lie. >seemed to represent a failure to replicate, but after years of >controversy they admitted to adding into the sample non-champion A lie. >athletes to dilute the originally positive result that they had >obtained. In a recent issue of the Skeptical Inquirer (their >mouthpiece), they published an article by Suitbert Ertel which >showed that the American sample used in the CSICOP study does >indeed show the Mars effect. As a result of the controversy A lie. >resulting from their cover-up of the originally positive finding >in the Mars/athlete study, CSICOP has ceased conducting >scientific investigations (and so their name is no longer >appropriate). Not a lie, at least when you equate "scientific" with "astrological". The story is as follows. Originally 128 champs showed a nonsignificant Mars excess. CSICOP and Gauquelin agreed that this was not enough. The CSICOP has been (to my opinion) imprudent by adding more athletes without consulting Gauquelin. As they had started to select the very top from the available data (but were unable to obtain all birth times because of privacy regulations) they were caught in a double bind. If the results had turned out favorable the Gauquelins would have applauded their results. In the other case they were prepared to cry "dilution!". Actually the second case happened. The basic reason was that the Gauquelins never bothered to explain how good a champion must be to be considered really good. Their original sample included 268 Italian aviators. Not quite a strenuous sport for the millions, more something for viscounts and dukes that can afford private airplanes. Later Gauquelin collected data about 600 Italian first division soccer players. No result. He then raised the norms: the 98 ones that had played at least once in an international game "showed the Mars effect". In the Belgian test the norm was raised to 20 international games. What not many people know (but Ertel, who has found this, does) is that *prior* to the Belgian test the Gauquelins already had collected data about Belgian soccer players; their files contained 76 ones that fell just below the "20 internationals norm", and that showed a Mars effect of only 10 percent (17.2 expected). I don't know how the Belgians got the idea that "20 internationals" had to be the limit of excellency. From the enormous number (198) of Belgian cyclists in the Belgian test it might be concluded that even during the Belgian test the Gauquelins were not too strict about how excellent a champion must be. But *after* the American test they raised the standards. They complained that the data base for basketball players was too large (1000 U.S. champions). The reason? In their own data they had 33 basketball players of whom only 3 were born in the appropriate Mars sector. So they thought they had reason to distrust basketball players. After the test they suggested that only "Olympic gold medal winners" were champion level. The results of Ertel clearly show that the Gauquelins biased their data. (I don't think the bias was deliberate, because probably both of the Gauquelins did not understand the difference between exploratory research and testing. Otherwise they would have been ashamed to commit their post-hoc data selection after the American test). Ertel's position is that the Gauquelin data still show a Mars effect, in the sense that the effect is stronger in groups of more excellent athletes. However, Ertel's analysis is poor. I have reanalysed it, and (a) the effect is absent if one only looks at the French champions (b) the effect is present if one does not distinguish between champions whose result were and weren't published by the Gauquelins. As Ertel's sources were partly used by the Gauqelins themselves to establish who was good and who was not (which gave a bias in their results) the Ertel eminence effect is very dubious. (c) Moreover, Ertel himself has since "discovered" that this eminence effect is "reversed" among the very high top (after some more results I expect him to find a sinusoidal behavior...). And even though Ertel knows the Gauquelin data are biased, he keeps forgetting the importance of the fact that the Gauquelins never bothered to formulate what was a champion. All along the Gauquelin's idea has been that the effect only shows up if you take your champions good enough. The story about "cover up" refers to the treatment of the outcome of the Zelen test. Originally this was a test to find a demographic explanation for Gauquelin's results. The test came out as expected (by Gauquelin), namely that this explanation didn't work. No results were "covered up", but responsible CSICOP people were kind of slow in recognizing the results. The way Ertel gets "results" is by very carefully redefining what he means by "key Mars sector". There are many slightly different definitions possible, and he takes the one that gives the best answers. All this is post hoc. Gauquelin's data originally comprised 2087 athletes. Expected number of Mars athletes was 359, with a standard error of 17. Lots of physicists don't think a deviation of less than 5 sigma merits serious investigation. That would mean that an experimental finding of over 446 Mars athletes starts to be interesting. Initially Gauqulin found 452, but after recomputation (Correlation 4, 1983) there were only 435. The whole effect is therefore so much at the border of significance that it hardly woth so much effort. Ertel thinks different. For him is 1.65 sigma already significant. In a recent publication he even translates that into "It is highly probable that there exists a relation between the two phenomena" (in that same publication it turns out to be a silly computational mistake, but subtle or not so subtle errors in computation or experimental design apparently have no place in the minds of significance-fetishists). More about this in the forthcoming Proceedings of the Third EuroSkeptics Congress (Amsterdam 1991). JWN Newsgroups: sci.skeptic Subject: Statistical Evidence (was Re: Fwd: Astrology...) Message-ID: <1992Oct7.220030.3484@Princeton.EDU> From: ydobyns@phoenix.Princeton.EDU (York H. Dobyns) Date: 7 Oct 92 22:00:30 GMT Sender: news@Princeton.EDU (USENET News System) References: <5874@tuegate.tue.nl> Organization: Princeton University Originator: news@nimaster Nntp-Posting-Host: phoenix.princeton.edu Lines: 89 In article <5874@tuegate.tue.nl> wsadjw@urc.tue.nl writes: [...accusations by JWN of lies in the original posting, and of bias on the part of Ertel and the Gauquelins, deleted; my concern is only with some numeric, statistical assertions:] >Gauquelin's data originally comprised 2087 athletes. Expected number >of Mars athletes was 359, with a standard error of 17. Lots of physicists >don't think a deviation of less than 5 sigma merits serious investigation. (!!!) Maybe "lots" of physicists don't, but this physicist hasn't met many of them. I *certainly* would not put up with someone who handed me a piece of apparatus and said "Oh, by the way, we tested the output and in terms of our measurement uncertainty it was only 4 sigma out of spec, so we figured it must be OK and didn't bother doing any more measurements." The overwhelming majority of papers I've seen in physics are content to use at most 95% error bars or the equivalent: that happens to be about 2 sigma for a one-dimensional parameter measurement. Sometimes the conservative researcher reports a 99% confidence interval instead, that's about 2.6 sigma. I find this statement of JWN's utterly outrageous. >That would mean that an experimental finding of over 446 Mars athletes >starts to be interesting. Initially Gauqulin found 452, but after >recomputation (Correlation 4, 1983) there were only 435. The whole >effect is therefore so much at the border of significance that it hardly >woth so much effort. [...JWN concludes with snide remarks directed at Ertel's use of 1.65 sigma--the standard 95% one-tailed confidence level--as a significance criterion, and with a sneer against "significance-fetishists."] Significance-fetishists, eh? Well, let's apply a proper Bayesian approach to the numbers that Jan finds so unimpressive--statistical significance is a concept that doesn't even appear in that formalism. The data in JWN's posting reproduced above report a set of 2087 Bernoulli trials in which the theoretical expectation is that 359 should fit a given criterion. In fact 435 cases fitting the criterion are observed. What can we say about p, the probability that one of these random trials fits the criterion (i.e., the probability that one of these outstanding athletes has Mars in a "meaningful" position by astrological standards)? The null hypothesis ("There is no Mars effect") is that p=0.1720. Call this H0. A completely uninformed alternative ("There might be a Mars effect, but there is no information we can use to predict its magnitude in advance of the experiment") is simply 0 From: wsadjw@rw7.urc.tue.nl (Jan Willem Nienhuys) Date: 8 Oct 92 16:02:10 GMT Reply-To: wsadjw@urc.tue.nl Sender: root@tuegate.tue.nl References: <5874@tuegate.tue.nl> <1992Oct7.220030.3484@Princeton.EDU> Organization: Eindhoven University of Technology, The Netherlands Lines: 71 In article <1992Oct7.220030.3484@Princeton.EDU> ydobyns@phoenix.Princeton.EDU (Y ork H. Dobyns) writes: [Finally something worthwhile discussing in this newsgroup] > >>Gauquelin's data originally comprised 2087 athletes. Expected number >>of Mars athletes was 359, with a standard error of 17. Lots of physicists >>don't think a deviation of less than 5 sigma merits serious investigation. > > (!!!) >Maybe "lots" of physicists don't, but this physicist hasn't met many of >them. I should qualify my statement. When one is measuring something as a confirmation of a theoretical prediction (the workings of a self-designed apparatus ceratinly qualifies as such) then physicists are much less demnanding. But here we have the situation of `naturally produced data' that have no theoretical prediction. It resembles the situation of counting neutrinos, detecting gamma rays from an otherwise unknown celestial source; many examples of measurements of naturally occurring phenomena come to mind. In that case I still maintain that physicists are very wary of attaching theoretical importance to a 3 sigma peak in the noise. (I just quote an astronomer I know.) I *certainly* would not put up with someone who handed me a piece of >apparatus and said "Oh, by the way, we tested the output and in terms of >our measurement uncertainty it was only 4 sigma out of spec, so we figured it >must be OK and didn't bother doing any more measurements." The overwhelming >majority of papers I've seen in physics are content to use at most 95% >error bars or the equivalent: that happens to be about 2 sigma for a >one-dimensional parameter measurement. Sometimes the conservative researcher How many of those papers report an utterly unknown and ununderstood new phenomenon on the strength of it exceeding the random noise level by 2 sigma? >reports a 99% confidence interval instead, that's about 2.6 sigma. I find >this statement of JWN's utterly outrageous. > >Significance-fetishists, eh? Well, let's apply a proper Bayesian >approach to the numbers that Jan finds so unimpressive--statistical [statistics lesson deleted. Flame war about bayesian pseudo-science forestalled] >Now I, personally, don't believe in astrology, and I have to admit that >those numbers I've just calculated give me a sinking feeling in the >pit of my stomach. So maybe the 2087/435/359 figures are also susceptible >to the accusations of data selection, Well, IF this was a perfect 2087-fold Bernoulli experiment. But at these numbers there are some problems. The 17.2 percent refers to long-time averages, and I don't know if the "binomial variance" really is reliable in this case. Secondly, the effect size is small, (about 4%) and we have to ask ourselves how much certainty we have that the researcher collecting the data cannot have made systematic errors of that size. He collected his data in batches of 20-100 over the course of 20 years, and nobody knows exactly how he determined who was a good athlete and who not. But among the ones that he thought "not good enough" there were significantly less than 17.2 Martians. This brings me back to the above discussion about 5 sigma/ 3 sigma. One can't predict how large one's systematic errors will be from knowledge of the random errors. But if the aggregate of all your measurements with a given method seems off by only 3 sigma, I wish you much luck with tracking down what caused it: a genuine effect, some kind of bias or a fluke or an erroneous estimate of the size of sigma. From what I know of observations of natural phenomena, variances are very often underestimated. JWN From: Jon Bell Subject: Re: JWN and MARS effect Message-ID: <9210120141.AA15601@lll-winken.llnl.gov> Date: Sun, 11 Oct 1992 21:37:40 -0400 I can verify that in experimental particle physics, at least, the accepted standard for the significance of a possible "new" (i.e. not-looked-for originally) result is indeed five standard deviations above background. When I was a graduate student, another group in our collaboration produced a histogram with an unexpected "bump" in it at the three-sigma level, and there was much speculation about what it might be... a Nobel prize for us, maybe? But when more data was added to the sample, the "bump" disappeared into the background. That's life! Jon Bell / Physics & Comp. Sci. / Presbyterian College / Clinton SC USA From: suitbert ertel Subject: jwn and MARS effect Message-ID: <9210121339.AA10266@lll-winken.llnl.gov> Date: Mon, 12 Oct 1992 13:22:05 MEZ Re Dave Gombergs comment: > No wonder nobody believes these claims. Five short comments: (1) Some people believe in them including members of skeptics groups - after thoroughly examining the literature. So "nobody believes ..." seems to be wrong. (2) The significance test was one-tailed as I said in the message, i.e., the test was done on the basis of previous results showing positive G% deviations (Gauquelin, Comite Para). In that case error probabilities of claiming positive deviations are called for, an error p=.02 for a two-tailed test becomes an error p=.01 in a one-tailed test.Are there statisticians out there who would disagree? (3) Even if p were .02 the result obtained from CFEPP data would have to considered as confirming the claim ofect a MARS effect. (4) Gomberg's comment above seems to imply that an error like stating p=.01 instead of p=.02 would be sufficient to dismiss 1) the whole study, 2) all previous studies showing support for the MARS effect. This may be considered as an overgeneralization. (5) Gauquelin and others who worked in this area confirming his basic claim are not responsible for disbeliefs of others based on overgeneralization or similar features of processing scientific information. Suitbert Ertel From: "James J. Lippard" Subject: Re: JWN on MARS effect Message-ID: <9210121525.AA14468@lll-winken.llnl.gov> Date: Mon, 12 Oct 1992 08:14:41 -0700 Relay-Version: VMS News - V6.0-3 14/03/90 VAX/VMS V5.5; site arizona.edu Path: arizona.edu!arizona!noao!ncar!destroyer!uunet!mcsun!sun4nl!tuegate.tue.nl! rw7.urc.tue.nl!wsadjw Newsgroups: sci.skeptic Subject: Ertel's Error Message-ID: <5910@tuegate.tue.nl> From: wsadjw@rw7.urc.tue.nl (Jan Willem Nienhuys) Date: 12 Oct 92 13:26:11 GMT Reply-To: wsadjw@urc.tue.nl Sender: root@tuegate.tue.nl Organization: Eindhoven University of Technology, The Netherlands Lines: 321 I'm sorry that this post is so long, but I have to include almost all of Ertel's remarks. Moreover, the explanation of why something is wrong takes up more space than the committing of the error itself. There goes my lunch break.... Ertel writes: # #My reply is short. only 5530 characters, compared to JWN's long exposition of 5300 characters :-) # #The main question to be kept in mind is this: # # IS THERE A MARS EFFECT? # I prefer: is there convincing evidence in favor of the Mars effect? #The Belgian skeptics (Comite Para) tried to refute Gauquelin's claim #by collecting N=535 new athletes data (published in 1976). # #Apparently, they couldn't refute G's claim. Otherwise U.S. #skepticts (Paul Kurtz et al.) would hardly have tried the #laborious Zelen test consisting of collecting birth data of #N=16,000 French ordinary people (control group) (1977). No one contends that the Para test came out favorable for G. The Zelen test was a test to examine one particular naturalistic explanation for the test result. It was a rather superfluous exercise, but at the time Zelen and others were not convinced that the Gauquelins had adequately corrected for demographic/astronomical factors (but he had). The disconcerting thing about the Para test for me is that the 535 athletes contained 203 athletes whose Mars sectors were known already by Gauquelin. It is not clear how many causal links there are between Gauquelin's knowledge of the Mars sectors of these 203 athletes and the choice of proficiency levels by the comit\'e Para. It seems clear (again from Ertel's own researches) that Gauquelin knew very well that Belgian soccer players with less than 20 international games would give a poorer result than the case of 20 games as minimum level. # #The results of the Zelen test apparently did not shake #Gauquelin's claim either, otherwise the same researchers would #hardly have tried another test consisting of collecting birth #data of N=408 U.S. athletes (1979/80). # #Again, the U.S. athletes test was apparently unconvincing. #Otherwise the Dutch skeptics would hardly have dived into that #matter again, they did it twice. I think I may speak for Dutch skeptics (D.S.). Of course the U.S. test is quite convincing - as far as any single test can be convincing. The D.S. tried to find a naturalistic explanation for the findings before the U.S. test. Especially because the U.S. test was negative, the problem remained: what was the explanation for the other results? # First their idea was: Birth #excess of Gauquelin athletes with Mars in G-zones exists, but it #can be explained by diurnal and/or seasonal association (published #in 1991). On closer look (and computation) they abandoned this #idea. Next they explained Mars birth excess for Gauquelin #athletes by Gauquelin's selection bias (in print) - they had #become aware of my detailed account of the Gauquelin bias effect #in the Journal of Scientific Exploration (1988). One skeptic (Koppeschaar) gave up also because F. Gauquelin would not give him the data he asked for. He had received from Ertel many data just after he asked. F.G. blamed Ertel for this, and refused to give more data, unless Koppeschaar would sign all kinds of documents declaring his intent and purpose (and one might suspect that F.G. would be fully prepared start legal battles when K. would say something she didn't like.) # #There is another skeptics group, the French CFEPP, which #apparently remained unconvinced by the Belgian and the two #American approaches. They started collecting new French athletes #birth data in 1983 and gave a report (unpublished) about their #procedure in 1990 adding an appendix providing birth data of #1076 athletes (Dr. Benski). Results of an analysis of CFEPP's #data have not been published until today. Therefore, Arno #Mueller and myself did an analysis of CFEPP's data (we informed #Dr. Benski in advance). We computed, first, the main indicator: #G percentage, i.e., the percentage of French athletes born with #Mars in key sectors), the result is 25.19%. This is probably the sum over sectors 36, 1, 2, 3, 9, 10, 11, 12 in the 36-sector division. I don't know what is exactly the expectation for these sectors, I guess something like 22.9%, taking into account astro/demographic factors. So expected: 247 +/- 14, and actually found 271. From the table below, it seems that 23.6% is a better estimate for the "expected average", so that would mean 254 +/- 14, and hence the actual 271 is 1.23 Standard Deviations away from the mean, which is not too impressive. The important question is again: how independent of Gauquelin's knowledge of the athletes's sectors is this result? I know for certain that Benski conferred extensively with M. Gauquelin. Were all the 1076 athletes "new", or are there again a lot of old ones from previous researches mixed in? # #Then we shifted the birth dates by one year. An athlete born on, #say, Jan 25 1938, at 3 a.m., was attributed the birth date and #time Jan 25 1939, at 3 a.m. We calculated G% for shifted birth #data. Then we shifted by two years and calculated G% again. The #same procedure was repeated by stepwise yearly shifts up to 25 years. #The same shifts were applied in the opposite direction (-1, -2 #.. -25 years). # #(Stepwise yearly shifts are applied here for the #first time as an improved test for a planetary #effect. The improvement consists of relating the experimental #group of genuine individuals to control groups of dummy #individuals whose "births" occurred under exactly the #same diurnal and seasonal conditions as those present at #the births of the experimental individuals.) # #What might Dr. Benski and Dr. Nienhuis (JWN) hypothesize here? Nienhuys if you please. #I guess they might expect both that the genuine #G% value of 25.19% does not deviate significantly from the #distribution of 50 G% values obtained from the dummy controls. # #The result, however, does not confirm this hypothesis. I am #appending a table showing 51 G% values in descending rank order. #The value on top is G% obtained from the genuine birth data. The #error probability of finding the genuine value on top is p=.01 #which is generally regarded as very significant (allowing for a #one-tailed test which is here called for). # #Now I would like to ask JWN how confident he is, on inspecting #these results, that the Mars effect does not exist. This would be all a lot more convincing when (1) I knew more about the degree to which the criteria for inclusion and exclusion in the 1076 athletes has been independent of Gauquelin's knowledge of their birth times/Mars sectors, (this I cannot answer, only Benski can,.... possibly) and (2) this were not so much post-hoc. We cannot know the number of analogous tests that there is nothing special about these results. If I *assume* that he would have given up only after trying 20 different tests, then finding a single test at the p=0.01 level is not that striking. I definitely got the impression this summer in M\"unchen, that he had tried shifting by multiples of half an hour. It should not be necessary that scientists have to speculate about what other scientists have been playing around with the data when nobody else was looking. This gives rise to all kinds of unpleasant insinuations. THAT is the reason why I think post-hoc analysis is distasteful. There is also a statistical error in the above argumentation of Ertel. He apparently assumes that computing a one-year shift will result in a sample that can be considered a random sample. But different shifts are not independent. To understand that I reason as follows. Shifting the time back by an integral number of years will give you for the same time almost exactly the same configuration of fixed stars at birth. The sky with fixed stars (and hence the ecliptica) will have shifted by at most a degree (because of leap days). A degree is little, compared to the width of 40 degrees of the Ertel G-zones (36+1+2+3 and 9+10+11+12). The fifty years represent therefore more or less randomly distributed positions of Mars on that same ecliptic. On average, these positions will be about 7 degrees apart. But positions 7 degrees apart will give highly correlated answers. Only when you shift by 40 degrees you get something approaching a mimick of an independent sample. (I've pointed out something similar to Ertel related to his half hour time shifts.) Moreover, a shift of 100 degrees will bring an overlap of zone 36+1+2+3 with 9+10+11+12, so again a correlation. In other words, what looks like 50 independent results only represents a much smaller number of independent results. Say about 8, then the Benski result again has a one-sided p-value of 0.12. Not significant, especially not because of the unknown bias introduced in the manner I described. At a previous occasion (see latest issue of GWUP's Skeptiker) Ertel has also found a "result" by a combination of a complicated statistical detour, combined with a rather elementary error. In that case too, if he had avoided the error, he would have found about the same result as the simple argument without the detour. In that case the detour consisted of a complicated and artificial way of computing an average, here it is a tricky way to artificially inflate the number of independent samples. Even for somebody who could not think of the above argument him/herself, the data that Ertel presents below (his own data) should have warned him that they cannot represent independent draws from random variable: the distribution of percentages is nearly uniform (between 21, 22, 23, 24 and 25 there are respectively 10, 13, 13, 14 year shifts). Moreover, the fact that in the interval from 21 to 25 there are 3 values that are repeated 4 or more times with an accuracy of <=0.01 should also have rung a warning bell. The chance that of 50 random numbers in that interval there should be 4 that round up to two decimals to the same value is roughly 0.003, and for 5 it's a tiny fraction of that. That there should be 3 such values is very improbable (10^-9) IF these values represented independent draws from some distribution. # #Second - assuming he is not yet confident enough about #the nonexistence of a Mars effect - how many additional yearly #shifts he wants us to calculate in order to improve his #confidence that the Mars effect actually does not exist. Or #else, what he would suggest should be done now to put his #conclusion and that of other critics of the Mars effect on firmer #ground. [ironic remark. What about just doing all shifts again, ten times. This will give 500 shifts, and a p-value of 0.002 ! There is hardly any difference between adding in the results of 450 more shifts, or just repeating the same 50 shifts over and over again.] I don't want any more post-hoc calculations. I want data that are collected (in this case birth data of eminent sportsmen and -women) in such a way that it can be PROVED that the decision to include or exclude CANNOT be related to knowledge of that person's Mars sector. This means: any athlete whose birth time has ever been known to Gauquelin should not be in the sample, because that birth time may have contributed to setting a criterion for inclusion or exclusion. The only test in which this condition was (almost) fulfilled was the U.S. test. Even that test was not perfect, because the decision to go on collecting data was based on knowledge of the data of the first 128 athletes. And the CSICOP probably has come to regret that error. # #Suitbert Ertel # #---------- APPENDIX ---------------------------------------------- # # Results of testing # for a Mars effect # using the stepwise yearly # shift procedure # # Data: CFEPP #French athletes (N=1,076) #------------------------- # rank shift # by by # size years G% #------------------------- # 1 0 25.19 genuine #------------------------- # 2 -10 25.00 dummyes # 3 -25 24.54 dummy # 4 -14 24.54 ... # 5 -6 24.54 # 6 6 24.54 # 7 8 24.54 # 8 17 24.44 # 9 -12 24.35 # 10 -11 24.35 # 11 21 24.35 # 12 22 24.26 # 13 11 24.07 # 14 20 24.07 # 15 -9 24.07 # 16 -8 23.98 # 17 -13 23.88 # 18 2 23.88 # 19 4 23.88 # 20 -20 23.88 # 21 -3 23.79 # 22 3 23.79 # 23 18 23.70 # 24 5 23.70 # 25 23 23.70 # 26 -23 23.61 # 27 -21 23.42 # 28 24 23.23 # 29 25 22.86 # 30 -4 22.86 # 31 -18 22.77 # 32 14 22.68 # 33 10 22.58 # 34 -7 22.40 # 35 -17 22.30 # 36 -22 22.30 # 37 -19 22.30 # 38 -24 22.30 # 39 15 22.21 # 40 12 22.12 # 41 -5 22.03 # 42 7 21.93 # 43 1 21.93 # 44 13 21.84 # 45 -15 21.75 # 46 19 21.56 # 47 16 21.47 # 48 9 21.47 # 49 -2 21.38 # 50 -16 21.28 # 51 -1 21.10 #------------------------------------------ # # I hope I have not been boring my audience with these technical discussions, but it's better that this dubious type of post-hoc statistics gets nipped in the bud. J.W. Nienhuys, Research Group Discrete Mathematics Dept. of Mathematics and Computing Science Eindhoven University of Technology P.O. BOX 513, 5600 MB Eindhoven The Netherlands e-mail: wsadjw@urc.tue.nl From: "Mark, Phone 2404" Subject: RE: JWN and MARS effect Message-ID: <9210130003.AA09087@lll-winken.llnl.gov> Date: Mon, 12 Oct 1992 18:01:35 MDT Suitbert Ertel says, >JWN's contribution to the MARS effect debate is meticulous, >but long. > >My reply is short. > >The main question to be kept in mind is this: > > IS THERE A MARS EFFECT? > > (Stuff deleted) > > >Then we shifted the birth dates by one year. An athlete born on, >say, Jan 25 1938, at 3 a.m., was attributed the birth date and >time Jan 25 1939, at 3 a.m. We calculated G% for shifted birth >data. Then we shifted by two years and calculated G% again. The >same procedure was repeated by stepwise yearly shifts up to 25 years. >The same shifts were applied in the opposite direction (-1, -2 >... -25 years). > I missed the original posting, but from the above quote it seems that they are talking about a phenomenon that has been investigated here and elsewhere regarding the birthdate of top athletes. In the National Hockey League and in other top leagues, there are many more players with birthdays in January and February than would be expected if they were drawn from the population at random. Obviously they are not drawn at random, but what birthdate has to do with it is not astrological sign, but the policies of the feeder-leagues. Young players are categorized by age and often it is their age as of December 31. So a player who is, say, 13 on January 15 is considered 12 for the whole season and gets to play with the 11-12 year-olds. Because of his larger size and greater maturity he gets more playing time and gets placed on elite teams and then gets more and better coaching. On the other hand the player whose birthday is in December is in the hole w.r.t. this. He might be just over 12, but playing in the 13-14 league with those 15 year-olds who turned 15 in January. Roger Barnsley has investigated this and some of his work is published in the Canadian Journal of Behavioural Science. Mid- 1980s but, sorry, I do not have the exact date or volume. _______________ _ Mark Sandilands --\____/ \ ___ Dept of Psychology / | | | University of Lethbridge / __ [_> - Lethbridge, Alberta---------------\ \ <| Canada, T1K 3M4 ----------------> \ * / e-mail: Sandilands@hg.uleth.ca | | Voice: 403-329-2404 \_ _\\ FAX: 403-329-2057 \\ / _ \ \/ | ---^--- From: "James J. Lippard" Subject: Mars Effect: Nienhuys responds to Ertel Message-ID: <9210261938.AA19096@lll-winken.llnl.gov> Date: Mon, 26 Oct 1992 09:27:56 -0700 Newsgroups: sci.skeptic Subject: "Mars Effect": JWN replies Ertel's 23/10 post (pt 1) Message-ID: <6041@tuegate.tue.nl> From: wsadjw@rw7.urc.tue.nl (Jan Willem Nienhuys) Date: 26 Oct 92 12:34:04 GMT Reply-To: wsadjw@urc.tue.nl Sender: root@tuegate.tue.nl References: <24OCT199209243794@skyblu.ccit.arizona.edu> Organization: Eindhoven University of Technology, The Netherlands Lines: 153 In article <24OCT199209243794@skyblu.ccit.arizona.edu> lippard@skyblu.ccit.arizo na.edu (James J. Lippard) writes: #The following is from the BITNET SKEPTIC discussion list. # #Date: Fri, 23 Oct 1992 16:13:48 MEZ #From: Suitbert Ertel # #My rejoinder to Dr. Nienhuys (JWN, Oct 12) might appear too long #(514 lines). But, being quite explicit now may avoid requests for #more explicitness later. #------------------------------------------------------------------ I noticed that some of my arguments are misunderstood (and some were wrong). #collaboration among name collectors or plagiarism. Collaboration #between Comite and Gauquelin resulting in support for Gauquelin's #claim is very hard for me to conceive. If Dr. Nienhuys means by #"causal links" that effects favoring Gauquelin's claim might have #occurred inadvertently he should explain how #snooping into former Gauquelin results might have led Comite to #thwart their own intention. I know very little of what went on between Gauquelin and the Comit\'e Para. I can imagine G. proposing the "20 international games limit" for soccer players, *knowing* that a lower limit would decrease the G% (the percentage of athletes with Mars rising or culminating). Including many classes of athletes for which G. had already established optimal "goodness criteria" is OK, but then one should exclude the data on which these optimal bounds were based from a new independent test. If the 535 atheletes were good enough according to Gauquelin, then also the 535 minus the 203 were good enough. Ertel can easily look up in his files which percentage of the 535-203 were born in sectors 1,2,3, 10,11,12 (of the 36 sector division). I have even hinted that he would do so. But he has not reproted on the outcome. #The Dutch skeptics had tried "to find a naturalistic explanation #for Gauquelin's and Comite Para's findings", Dr. Nienhuys says. #Those findings had been positive (Mars G% above chance level). #Then, however, came the U.S. test which was negative. # #Careful reading of Nienhuys' passage will show that for the Dutch #this must have been good and bad news at the same time. Their #devising of a naturalistic explanation for positive deviations #will have nourished expectations that any test of Mars sector #frequencies for athletes, the U.S. test included, would yield G% #above chance expectation. Now G% of the U.S. test wasn't above #chance expectation, numerically it was even slightly below it. This is a good point. Ertel has remarked in his contributions to the EuroSkeptics III Proceedings (due to appear coming Friday!), that this naturalistic explanation would run into numerous problems, even if it had worked. But Ertel knows that what started the exploration was a model in which "spurious correlations" could give large more or less random deviations from expected values, and these might work just the opposite way in another geographical location. A second model presupposed a relation between athletic prowess and a diurnal-seasonal birth rhythm that might hold only in France, and not accross the ocean. # #But apparently, the Dutch skeptics' belief in their naturalistic #approach had not been very strong, since Dr. Nienhuys now says #"the U.S. test was quite convincing". I think there's a confusion here. I am not one of the four Dutch people that investigated the Mars effect. To be honest, I've thought this exercise a waste of time (wrongly, because something came out of it after all, even if it was not the result foreseen). So *my* evaluation afterwards cannot be interpreted as the point of view that this group of four had beforehand. # It is pertinent that Dennis Rawlins, one of the #astronomers who made computations for Kurtz' and Abell's study #of the U.S. athletes gave with "sTARBABY" an account of what #occurred behind the stage which would make it sensible if not #inevitable to suspect that the U.S. data had not been collected #without bias - Rawlins' probable exaggerations notwithstanding. I have spelled sTARBABY. Only on p. 76 Rawlins gives an insight of what happened behind the scenes of the U.S. test. Most of sTARBABY is about the interpretation of the ZELEN test, and what all those CSICOPs did to poor Rawlins when p.R. wanted to say that they made a mistake. #My own reanalysis of Kurtz'et al. data gave independent support: #In CSICOP members'U.S. sample average athletic success (citation #counts) was much lower than with another sample of U.S. athletes #that Gauquelin collected right after CSICOPian findings had been #published in THE SKEPTICAL INQUIRER ("Results of the U.S. test #of the "Mars Effect" are negative", 1979/80).That is, CSICOP #researchers had unquestionably violated - possibly on the fringe #between intention and inadvertence - Gauquelin's eminence #requirement. Here a very remarkable conjecture is made! CSICOP apparently believed so strongly in the Mars effect's reality, that they deviously selected about 300 weak-willed cripples from books listing the top people in several of America's favorite religions (baseball, football, basketball, boxing, ... ), just to thwart Gauquelin. That they really were weak willed cripples is of course clear from the fact that after M.& F. G. had done their selection of 192 true athletes, the G% of the remainder had dropped to 10% or so. # # # Re (2): Present test # -------------------- # 2.1 Selection bias. # #Dr. Nienhuys, having suspected biased data-selection by the #Belgian skeptics, now suspects that of the French skeptics. Bias Maybe I have not been clear enough about that. The possible (suspected) bias I am talking about is: [*the choice of eminency thresholds not independent from knowledge of the Mars sector distribution of part of the sample.*] As Benski has discussed with G. (as far as I know) which athletes should be included and which not, it is not absolutely clear that the bias source between [* and *] has been excluded. I haven't seen Benski's paper. I don't exactly know the content of his discussions with G. But unless bias source [*...*] is not provably excluded, the CFEPP experiment should be suspected. Also I don't know whether (and if so, how) Benski argues that bias source [*..*] is absent from his experiment as far as he is concerned. I hope he thought of it. It is clear from the writing of Francoise Gauquelin (see the EuroSkeptics proceedings) that she after 40 years in this research is not even aware that [*..*] can be a problem. I am not aware of any statement or proof of the Gauquelins that they ever controlled for bias source [*...*]. # 2.2 Control samples by year-wise shifts # #Dr. Nienhuys apparently rejects testing for planetary effects by #examining the effects of shifts by units of years. He points out #that fixed stars take the same positions in the sky every year at #the same time and by the same token, Mars is purported to recur #every year in similar positions. As the planet can only move #within the restricted limits of the belt of the ecliptic, #variations of position are deemed to be small. # Here I think Professor Ertel has not understood what I meant. I have been too vague (possibly in my desire to get the answer ready before my lunch break ended). I will provide more details in a next post. JWN From: Suitbert Ertel Subject: Mars effect Message-ID: <9211060902.AA02037@lll-winken.llnl.gov> Date: Thu, 5 Nov 1992 21:29:04 MEZ In both, the listserv and the newsgroup skeptics circles, members seem to be interested in the Mars effect debate. So I am sending this message to the listserv group while asking Jim Lippard to kindly transfer a copy of this message to sci-skeptics (newsgroup) (he did transfers earlier, I am still at a loss for techniques of file transfer to newsgroups). ---------------------- Message --------------------------------- York H. Dobyns says (Oct 30, '92): "I'm no fan of the Mars effect: the evidence is questionable due to methodological flaws." Nevertheless he then dwells meticulously on consequences that would arise if the Mars effect were shown to be real. Apparently, the evidence is not questionable enough to remain aloof from it. My business today is to question the evidence for "methodological-flaws" arguments abounding in discussions here about the Mars effect. Most of these arguments have been brought forward by Jan Nienhuys. Newsgroup members seem to readily take his views as their own. What I would like to suggest is to read his messages more skeptically (should not be difficult in this circle). I am going to tell you why. ---------------------------- 1 ------------------------------------- J.N. Nienhuys 28 Oct 1992 > Later more "effects" were found with different professions. > But (to me) the main point is that Lasson already emphasized > one should take "famous" professionals. It's quite natural > that if the reality of this effect was suspected, they (both > Gauquelins) would try to determine how famous or good the professional > had to be. It is also conceivable that a psychologist receiving > his statistics training in the early '50's would not be aware of > artifacts resulting from cumulative biases introduced by this type > of exploration. News-readers, not being familiar with Gauquelin's procedure in detail will take it for granted that Nienhuys justifiably refers to some actual bias connected per se with collecting birth data of famous people. They will find it plausible that artefacts did accumulate due to poor statistical knowledge of the Gauquelins in the Fifties. "It wasn't their fault (how considerate we are), researchers at that time were not as sophisticated as we are today (how excellent we are)". The verdict is done. I feel obliged to defend Michel Gauquelin (he died last year and thus cannot defend himself) one of the most admirable figures (admirable regarding methodological conscientiousness) in frontier science fields. First, there is no bias at all associated with collecting birth data with preference for eminent people. On the contrary, collecting birth data without considering eminence must be considered as severely biased. As soon as Gauquelin had reported that planetary effects were stronger with famous than with average athletes (his first observation) any subsequent study testing the replicability of planetary effect was bound to select more excellent individuals from professional samples. Both, the American and the French skeptics did gravely (CSICOP) or appreciably (CFEPP) violate the eminence requirement. A study aiming at refuting some purported effect must show its absence despite having established most favorable conditions for the purported effect to occur. CSICOP/CFEPP apparently did not set up such conditions. They collected data in a way as if they feared the Mars effect might emerge (see data below). ---------------------------- 2 ------------------------------------- J.N. Nienhuys 28 Oct 1992 > Given the rampant habit of reporting "significance" without > model or hypothesis prior to the experiment (rampant at least > in social science and medicine), there is absolutely nothing special > or fraudulent about one psychologist not making the proper > distinction between exploration and testing. Jan Nienhuys here claims that the Gauquelins did not make proper distinction between exploration and testing. The facts tell a totally different story: M. Gauquelin published results of an exploratory study in 1955 based on French data. Since then most of his publications were of the hypothesis-testing kind. In 1960 he published his first hypothesis-testing study based on Italian, German, Belgian, and Dutch data. The book gives answers to the question: "Do previous French results replicate with non-French data? The chapters provide reports on hypotheses, subjects, methods of analysis, results, discussions as to whether the hypotheses had or had not been supported (etc.). On reading statements as those made by Nienhuys turning the facts upside down and on having to witness their acclamation by the majority of responding readers ("Congratulations, Jan!") I just feel sad, and doubts arise as to whether justice and fairness has any better chance to prosper in our science community than elsewhere in this foul world. ---------------------------- 3 ------------------------------------- How eminent were athletes selected by the skeptics research groups as compared to athletes selected by Gauquelin? Here we exclude athletes common in both samples, i.e., we only consider athletes listed either in the skeptics ("CSICOP-only", "CFEPP-only") or in Gauquelin's sample ("Gauquelin-only"). The eminence of an athlete is defined by the occurrence of his/her name in 18 reference sources. The CSICOP-only sample of U.S. athletes is compared with a Gauquelin-only sample of U.S. athletes (which G. collected later), the CFEPP-only sample of French athletes is compared with the Gauquelin-only sample of French athletes (which G. had collected earlier) (see Table 1). Table 1: Numbers of American and French athletes in skeptics and Gauquelin samples. American: Kurtz et al. (CSICOP) N = 216 American: Gauquelin .......... N = 162 French: CFEPP ............... N = 398 French: Gauquelin ........... N = 130 Table 2 shows citation counts in percentages of respective Ns for the skeptics' and Gauquelin's citation subsamples, as well as the differences "Gauquelin - skeptics." Table 2: Citation counts (percentages) --------------------------------------------------------------- CSICOP Gauquelin Difference GAUQ-CSICOP --------------------------------------------------------------- citations = 0 72.5 25.9 -46.6 citations = 1 24.9 22.8 - 2.1 citations = 2 2.6 29.1 26.5 citations = >2 0.9 22.2 22.2 --------------------------------------------------------------- 100.0 100.0 --------------------------------------------------------------- --------------------------------------------------------------- CFEPP Gauquelin Difference GAUQ-CFEPP --------------------------------------------------------------- citations = 0 71.9 36.9 -35.0 citations = 1 18.1 20.8 2.7 citations = 2 3.8 23.1 19.3 citations = 3 4.3 11.5 7.2 citations > 3 2.0 8.7 6.7 --------------------------------------------------------------- 100.0 100.0 --------------------------------------------------------------- Results 1) The majority of CSICOP-only athletes is much less eminent than Gauquelin-only athletes. 2) The majority of CFEPP-only athletes is much less eminent than Gauquelin-only athletes. Considering this difference alone the skeptics' studies cannot be taken as appropriate for testing Gauquelin's claim of a Mars effect. However, despite unfavorable preconditions a significant overall Mars G% deviation was observed at least for the French skeptics' sample. (This has been reported earlier). ---------------------------- 4 ------------------------------------- Another way of testing the presence of a Mars effect consists of calculating G% for each eminence subsample separately and to test for monotonic trend i.e., to test for the claim that G% increases with athletic fame. Results from such trend test is independent of the general G% level of the entire sample (=citation subsamples pooled) and may be considered as an alternative test of planet-birth relationships. Table 3 shows G% values for the skeptics and the Gauquelin samples, first U.S., then French athletes, entire samples, broken down by citation frequencies. Table 3: G% (key sector percentages) for the skeptics' and Gauquelin athletes' samples. ---------------------------------------------- CSICOP Gauquelin N=408 N=349 ---------------------------------------------- citations = 0 18.1 21.4 citations = 1 21.5 21.3 citations > 1 25.9 30.2 ---------------------------------------------------- CFEPP Gauquelin N=1076 N=2040 (publ. and unpubl.) ---------------------------------------------------- citations = 0 22.8 26.1 citations = 1 28.6 25.1 citations = 2 24.6 27.6 citations = 3 27.9 26.4 citations > 3 28.5 31.1 ---------------------------------------------------- Note: Less famous athletes (less citations) are much greater in number than famous athletes. Therefore, for small total samples of athletes famous subsample will be sufficiently large only by pooling individuals from a greater range of citation frequencies. Results: 1) A monotonic increase of G% with citation counts is present in the Gauquelin data, both samples. 2) A monotonic increase of G% with citation counts is present in CSICP's data (Kurtz et al.) 2) A monotonic increase of G% with citation counts is present in CFEPP's data (Benski) ---------------------------- 5 ------------------------------------- J.N. Nienhuys 29 Oct 1992 > There may be a file drawer effect. When Ertel asked Gauquelin > in detail *all* his data, not only the ones he had published, > he found that in the file drawer there were many athletes (unpublished) > that did collectively *not* have a Mars Effect (namely around 22% > born `under Mars'), and even did not conform to the average number > of people (17.2%), but that were collectively born `under Mars' > in a much smaller fraction. Their distribution over the sectors was > a kind of mirror image of the distribution of the published athletes. > Details: > French published athletes: 1357 of which born `under Mars' :306 > French unpublished : 683 89 > Nonfrench published : 1531 322 > Nonfrench unpublished : 820 133 > Readers with calculators (and knowing just a smattering of statistics) > are invited to draw their own conclusions. > JWN Jan Nienhuys here gives a partial summary of my published report about Gauquelin's selection procedure. His summary is partial for three reasons: First, Nienhuys would like to make his readers believe that discarding and not publishing cases must be regarded per se as bias. I discussed this point in my paper from which he took the information so he should know - and should have told his readers - that not publishing cases in Gauquelin's study was not at all bias per se. Gauquelin was not merely entitled, he even HAD to exclude from his athletes sample individuals of lower eminence rank after having found in 1955 that the Mars effect increased with eminence. He was no less bound to throw mediocre figures out of his sample than the skeptics in their replications were bound to do just that (as discussed above). Comparing unpublished with published Gauquelin atheletes regarding c i t a t i o n c o u n t s (see Table 3) we do find that the numbers of citations is considerably lower for unpublished as compared to published athletes. Gauquelin thus actually SUCCEEDED, by discarding cases, to improve the general level of success in his sample. Table 3. Citation percentages for published and unpublished Gauquelin athletes citations Published Unpublished Difference (N=2888) (N=1503) ----------------------------------------------- 0 46.1% 62.5% 16.4% 1 18.9% 29.4% 10.5% 2 16.0% 4.9% -11.1% 3 7.3% 2.9% -4.4% 4 3.3% 0.2% -3.1% 5 2.7% 0.0% -2.7% 6 1.1% 0.0% -1.1% 7 0.6% 0.0% -0.6% 8 0.1% 0.0% -0.1% --------------------------------------- 100.0% 100.0% --------------------------------------- Nevertheless, Gauquelin should have done this discarding (and not publishing) athletes with greater care. He should have discarded low achievers prior to collecting their birthdates. Or else, after having obtained their birth data, he should have asked some naive assistant to check biographical information and to discard low achievers by applying some reasonable criteria of success. Gauquelin did such selections himself, obviously overestimating his ability to base his judgment solely on the athletes record of successes without considering, at the moment of decision, his possibly knowing/remembering the respective person's planetary positions. I searched for this inflating bias and I found and published the result. When Gauquelin heard of my citation counts he welcomed this procedure as an objective alternative to what he was used to apply. He gladly opened his "drawers" to let me take all athletes data and do a reanalysis based on published plus unpublished athletes. In this study subsamples of athletes differing in numbers of citations were analysed seperately (similarly to what was shown above with Tables 2 and 3). A pronounced eminence correlation emerged. Secondly, Nienhuys informed sci-skeptics about the low overall G% of Gauquelin's unpublished sample as compared to his published sample inviting the readers to draw their own conclusions - and he could only expect his readers to draw wrong conclusions (which he apparently wants to see spread) with not informing them about essential details needed to draw correct conclusions (which he probably deters). Nienhuys did not inform readers about the UNPUBLISHED athletes' LOWER LEVEL OF SUCCESS. G% difference between unpublished (=less eminent) versus published (=more eminent) athletes MUST be obtained, if Gauquelin's Mars + eminence hypothesis holds. The observed difference is NOT CREATED but only INFLATED by Gauquelin's above mentioned seductions. A third neglect by Nienhuys must be set straight: He never informed readers about the effects on eminence correlation by my pooling Gauquelin's published with unpublished athletes. I just quote from my paper (with some linguistic amendments): "The crucial question remaining is as follows: Could the kind of bias noted in Gauquelin's procedure invalidate the outcome of the present study? Could an artefact carried over from original meterials raise the risk for wrong conclusions? ... [Gauquelin's] omission of athletes from experimental samples had two effects: (a) It served to inflate the level of kS-proportions [G%] overall. But also, (b), it weakened the eminence effect. Our merging of unpublished with published data did repair (i.e. lowered) the overall eminence level. But at the same time it served to repair the eminence slope, i.e., to make it steeper. Gauquelin's selection bias, therefore, does not weaken the conclusion that Mars'position and the athletes'births are statistically related. Paradoxical though it may seem, this claim has been corroborated due to this bias: Correcting for selection bias by pooling all data INCREASED empirical support for the stronger version of this claim: the data have overcome, IN SPITE OF DISTURBING EFFECTS OF BIAS, the higher methodological hurdle." ---------------------------- 6 ------------------------------------- Before carelessly attributing to Gauquelin's (and my own) work "methodological flaws", "file drawer effects", "rampant significance reporting", significance fetism", "lots of tests - one was significant", "no prior hypothesis", "post hoc interpretations", "anomaly-mongering" - look at the above Tables notably Tables 2 and 3. If you are suspicious of what is in the right columns, keep to the left columns with the skeptics results. This, hopefully, will foster thoughtfulness. Those scientists among ourselves calling themselves 'skeptics' should be more inclined than the remainder of us to reconsider skeptically, when faced with unexpected evidence, their own views. Once observational data demand it they should be ready to admit that they were wrong, at least as ready as "ordinary" scientists like Gauquelin who found and unearthed, with utmost rigor, in a dust heap despised by the community what might be considered - by an advanced posterity - as a real grain of gold. Gauquelin was faced one day with unexpected evidence, he was surprised by a replication failure in his "heredity" research (he could not replicate G% similarities between parents and their children), and he had this to say: "The samples [my former and my recent sample] seemed identical in every way, yet the first gave results strongly in support of the hypothesis while the second gave results almost as strongly contradicting the hypothesis ... Despite the disappointments, I am pleased about one thing: If my latest work has created doubt, then this is the best that can happen in science. As Bertrand Russell has written, "Not to be absolutely certain is, I think, one of the essential things about rationality". (Gauquelin's heredity hypothesis did not find empirical support in my studies either. His basic finding, however, (the one now replicated by CFEPP) is totally independent of the heredity construct which was part of Gauquelin's explanatoty model). The Dutch skeptics (de Jager, Koppeschaar) had already proclaimed in public to be able to "unmask" (as they said) the Mars effect as an unrecognized artefact caused by seasonal/ diurnal priodicities. It happened that they failed entirely. If they had stated their failure frankly and if Jan Nienhuys had reported about their failure in frank manner for us electronic readers I would compare him/them, regarding sincerity, with Michel Gauquelin. I am still ready to do so and to withdraw my suggestion to read Jan Nienhuys' messages more skeptically as soon as he would refrain from wrongly reporting about Gauquelin data and procedures and if he would show himself, instead, convincing signs of skepticism regarding his own stand. From: Suitbert Ertel Subject: Proceedings aftermath Message-ID: <9211211551.AA07752@lll-winken.llnl.gov> Date: Fri, 20 Nov 1992 20:04:51 MEZ Comments by Ertel on comments by Nienhuys on a post by Ertel (Nienhuys` post is unabridged.) ------------------------------------------------------------------- Comments on a post by Suitbert Ertel (note. Ertel has three different posts all titled `Mars effect'; this is an answer to the first. No need to look up the first, because the full text is here too. Sorry guys for the length.) # BACKSTAGE NEWS ABOUT THE EUROSKEPTICS PROCEEDINGS # #I would like to invite interested readers of this post to give #comments and Dr. Nienhuys to answer a number of questions at the #end of my message: # # #------- (1/5) Proceedings just published ------------------------ # ...... #I did not receive any pages of those papers neither did I #receive Dr. Nienhuys' "summary". NIENHUYS: First Comment Professor Ertel may recall that I wrote to him: I have received your letter. The 75 pages I refer to consist of 16 pages JJ, 12 pages Jongbloet, 20 pages Koppeschaar, 17 pages Ertel, (that makes 65, which you have seen) and an unknown number of pages from F. Gauquelin, which I estimate at between 10 and 15 pages, and which consist of a completely new comment on all papers above. I will send them to you when I receive them.... ERTEL's comment: Dr. Nienhuys sent me F. Gauquelin's pages, not those of the Dutch authors. NIENHUYS: I don't see much point in sending you my comments prior to publication; ... ERTEL's comment: But he should have known that *I* see much point, I had indicated that in my letter. NIENHUYS: ... as soon as my introduction is finished, I will bring the stuff to the printer, and collect the printed Proceedings one week later. If madame Gauquelin is not too tardy, I can get this over and done with before August. NOTE: actually the number of pages went up a bit because of changes in layout. I was rather optimistic about the time schedule, though. ERTEL's comment: Anyone interested in numbers of pages? A red-herring. N. should have explained here why he did not see much point to send me his alleged summary and why he thought that that wasn't much point for *me*. I would not care had Dr. Nienhuys behaved as predicted in a letter by Prof. de Jager to me in which he said that "he (Dr. N.) not being party in the dispute, is an excellent person to weigh the various pros and cons and thus to come to a balanced conclusion". Prof. de Jager's predictions contributed to my surprise later. # #---------- (3/5) Startling discoveries in the Proceedings ------------- ..... #J&J's insertion in their paper is an attempt to undo the #criticized neglect.... NIENHUYS: As far as I knew Ertel had obtained all his information about J&J's paper by direct correspondence with J&J long before February 4 (when I received the corrections to the first version); Ertel's contribution was sent on February 18. By the beginning of May it escaped me that Ertel might not have seen these corrections. De Jager had talked to Koppeschaar and others, and wanted to be a little more clear about what he thought were weak points in Gauquelin's work. There is no question of De Jager changing his paper after reading what Ertel sent to me.... ERTEL's comment: Jan : Dr. N. receives J&J's first version of his paper. Jan : Ertel receives J&J's first version of his paper. Jan : Ertel receives CORRECTIONS #1 of J's first version. Feb 4 : Dr. N. receives CORRECTIONS #1 of J's first version. (With Nienhuys' word "correction" above readers are totally mislead. They will understand that J&J sent the belated CORRECTIONS THAT I AM RESENTING quite on time, i.e. Feb. 4, before J&J sent THEIR paper on Feb 18. The "corrections" which Nienhuys refers to, however, are some earlier corrections which are irrelevant here. Dr. Nienhuys should not have brought in CORRECTIONS #1 at all, even I myself misunderstood his passage believing that I made an error until checking the correspondence once again. How could readers understand that passage correctly?) Feb 18 : N. receives Ertel's contribution to the Proceedings. April : Ertel has correspondence with Koppeschaar May : J&J talk to Koppeschaar ("and others"?) --------------------------------------------------------------------------- May : Nienhys receives CORRECTIONS #2 of J's paper --------------------------------------------------------------------------- May-Nov : Ertel does not receive CORRECTIONS #2 In his CORRECTIONS #2 J&J removed weak points OF HIS OWN PAPER. I did not receive J&J`s CORRECTIONS #2 and I am at a loss to understand (1) that J&J did not send me them (2) that Dr. Nienhuys was mistaken (in MAY !) that J&J's belated changes had been agreed upon by correspondence between J&J and Ertel. Dr. Nienhuys should have realized that his neglect is hard to understand, so he should have provided ample reasons to make us believe that it "escaped him" inadvertently. NIENHUYS: ...For a general reader it seems not so much of a contradiction: De Jager apparently thinks the Eminence Effect not very important, whereas Ertel thinks it is a replication of the Mars Effect.... ERTEL's comment: I don't see the logic. The contradiction is that I criticize de Jager for not considering the eminence issue. But J&J dealt with it (IN THEIR ADDITIONS). This contradiction is independent of the fact that J&J`s and my views on this issue differ. The reader cannot take the difference of views as something that might lessen the contradiction. NIENHUYS: ...But yes, the very astute reader, might wonder what caused Ertel's optimism that merely reading 1988 exposition (quoted in the original version as well) would convince J&J of the fact that the eminence effect replicated the Mars effect, especially in view of the dismissive remark "In view of the very small margins involved it seems questionable to us if this benefit [i.e. the benefit of the doubt extended to Gauquelin] is permissable." ... ERTEL's comment: J&J's not taking the eminence issue serious isn't what I criticize. I criticize that J&J did not say a word about this in their paper. Nienhuys here continues his red-herring strategy by criticizing me ("optimism" etc) instead of explaining J&J's and his own lack of informing me about changes in the Proceedings which were made 3 months after I had submitted my paper. # # I---------------------------I-----I-----I-------------------I # N = I 2,088 I 450 I 350 I N=1,503 I # I---------------------------I-----I-----I-------------------I #correct: I published I unpublished I # I---------------------------I-----------I-------------------I #wrong (J&J):I "published" I "unpublished" I # I---------------------------I-------------------------------I # # Figure 1: Gauquelin data, correct and wrong (J&J) divisions # .... #J&J's concise "This is not true" sounds as if that statement were #true. But it is wrong. J&J's error is to mistake the N = 2,088 #sample as the only published Gauquelin sample. The remainder of #the published sample (450+350=800) and the unpublished sample #are erroneously pooled. This error is hardly excusable. All #information regarding source of data and eminence counts are on #the file I posted them for analysis and in my 1988 paper minute #descriptions of that information is provided. #References to #"2,888 published" and "1,503 unpublished" #athletes (not "2,303") are made nine times and five times, #respectively, the samples #are listed in two tables. NIENHUYS: >From J&J's paper it is clear that they divide the total data set into two parts: published in 1972 by the Gauquelins and the remainder, which for two thirds consist of unpublished data. That remainder they denote by `Ertel Specific' and `unpublished'; the latter name for this is a rather unfortunate choice. The main impact of that section is to argue that the 2088 champions published by the Gauquelins in 1970 showed the Mars Effect (if it exists) most clearly. ERTEL's comment: (1) The choice is not "unfortunate", it is wrong. (2) The main impact is NOT that the 2,088 sample of champions "showed the Mars effect most clearly" (that isn't what skeptics J&J wanted to say). J&J said that the "unpublished" sample (actually a mixed-up sample) did not differ from the published (N=2,088) sample regarding citations. Here is an error and Dr. Nienhuys should help removing, not fogging it. # #Now, let us have a look at how J&J should have compared #the eminence (citation frequencies) of published and unpublished #samples (see Tabel 1): # # Table 1 # # Published All published Unpublished # N N = N = N = % N = % #Cit 2,088 450+350 2,888 100 1,503 100 #------------------------------------------------------------------ # # 0 1,178 153 1,331 46.1 940 62.5 # 1 431 226 657 22.7 443 29.5 # 2 271 191 462 16.0 73 4.9 # 3 115 95 210 7.3 43 2.9 # 4 39 57 96 3.3 4 0.3 # 5 43 35 78 2.7 0 0 # 6 10 23 33 1.1 0 0 # 7 1 17 18 0.6 0 0 # 8 0 3 3 0.1 0 0 #------------------------------------------------------------------- # #As can be seen, numbers of citations are considerably less for #unpublished as compared to published athletes. J&J having based #their conclusion on wrong sample divisions said there is no #difference. Their final conclusion based on this wrong #statement must therefore be rejected. # NIENHUYS: All these figures can be found in Koppeschaar's contribution. If one starts to divide data into groups, one may have differences of opinion about what constitutes a `natural' division. But one of the conclusions of J&J, namely `the difference between published and unpublished parts of Gauquelin's material ... remains a serious problem' doesn't have to be rejected: the percentage of athletes born in kS in the `unpublished' stuff is even below that of `ordinary people. ERTEL's comment: Dr. Nienhuys doesn't say "Ertel is right with pointing at J&J's error." He says "J&J's conclusion is correct anyway". #----------- (4/5) Another surprise ------------------------ # # The model (shape of the #relationship) is a precise claim totally different from #Nienhuys' derogatory simile with clouds and camels (my paper #will be published in the Journal of Scientific Exploration). NIENHUYS: Professor Ertel might consult Act 3, Scene 2 of Hamlet and find that camel detectors are in good company (but not those who believe them). This discussion must be continued in the Journal for Scientific Exploration. Nonetheless, in a nutshell, Ertel's new hypothesis is that the eminence effect follows a kind of sine curve on [0,pi], which enables him to fit almost any experimental data into his new model. ERTEL's comment: This is not correct. The way Dr. Nienhuys "informs" readers is not only vague, it is deficient. Th curvilinear eminence hypothesis (not "sine wave) is precise and unifies previous seemingly diverging results. (see forthcoming paper in The Journal of Scientific Exploration). # Nienhuys did not refer to that information even #though I had indicated in my Amsterdam rebuttal that it would #soon be available: "... final agreement should be expected, at #the latest from pending discussions with the French group #(CFEPP)". In a footnote I provided details about that important #study. NIENHUYS: I have not seen the CFEPP article, and I don't like to announce any opinions on it, before I've studied the paper of Benski (which isn't published yet), and before I've read what Benski himself has to say about it. #--------- (5/5) Questions ---------------------------------------- # #Postponing final conclusions I would like to consider, dear Dr. #Nienhuys, your answers to six questions: # #(1) Did you send a copy of my rebuttal to J&J before publication? I think so, but not before you had corrected the proofs, I think. ERTEL's comment: The question of whether my paper was sent before I had corrected the proofs or later is irrelevant. #(2) If yes, did you accept the revised version of J&J's paper # *after* having provided them a copy of my paper? No. I received J&J's revisions (and prepared the paper for final typesetting) two weeks before I received yours. ERTEL's comment: This fogs the issue. Dr. Nienhuys here refers to REVISION #1, the red-herring revision. My question (2) is directed solely at revision #2 which was done in May. In his reply to question (2) Dr. N. should have explained what actually "escaped him" in May (see above:" By the beginning of May it escaped me that Ertel might not have CORRECTIONS #2---> seen these corrections. De Jager had talked to Koppeschaar and others, and wanted to be a little more clear about what he thought were weak points in Gauquelin's work. There is no question of De Jager changing his paper after reading what Ertel sent to me....". (THAT IS, J&J CHANGED THEIR PAPER, "NO QUESTION", AND DR. NIENHUYS ACCEPTED THEIR CHANGES) #(3) Were you aware of their having changed their paper? Yes. I inserted carefully all the changes they indicated on their proofs into the definitive version, which was ready, warts and all, on February 9 (or earlier). ERTEL's comment: How did I understand that sentence on first and second reading and how will everyone else have understood it: That Dr. Nienhuys inserted changes before February 9. But Dr. Nienhuys did actually not say that he did the insertions before February 9, he said that the definite version was ready, "warts and all", on February 9. He doesn't say anything about the date of his insertions (which was in May). #(4) If yes, did you consider informing me about these changes # and if yes, why did you decide not to inform me about these # changes? As your paper arrived two weeks after their revision and as your paper ERTEL's comment: Dr. N is talking about the red-herring revision. apparently was based on direct communication between you and De Jager, it did not occur to me that there was any need to inform you; also because I was at that stage merely handling the typesetting part, and apart from details of spelling and formulation not familiar with the ERTEL's comment: There is no need to talk about revision #1. My question doesn't address this one. contents. That came only after Koppeschaar's paper. That's my explanation for not noticing the contradiction; if I had noticed the misleading term `unpublished' I would not have permitted them to change their paper. ERTEL's comment: Here Dr. Nienhuys refers to the belated changes brought in with REVISION #2. They were done in May at the time when Koppeschaar finished his paper. Dr. Nienhuys implies by what he says that he did not realize that J&J had made changes which contradicted my rejoinder. THIS, I think, is believable. But he might have asked ME to make sure. #(5) Why did you decide not to send me your own contribution # ("Summary") despite my having requested for it? You received the summary as soon as it came from the printer. ERTEL's comment: A driver defending himself after being accused to have caused an accident: "We stopped as soon as you were run over". With most of it you were familiar, because apart from last minute touch ups it is what I told in Munchen. ERTEL's comment: Dr. Nienhuys did not tell me in Munich what he would publish in the Proceedings. #(6) If you hold that replication trials of the Mars effect with # independent data are important why didn't you add while # referring to my Munich report in your "summary" my information # about Mars effect-supporting results with CFEPP? Professor Ertel, I heard your talk from yourself; that's something different from hearing a report on research of Benski from you. I have received some information (but not a complete paper) from Benski directly, but he made me promise not to say anything about it until it was published. Should I then go ahead, and print what I've ERTEL's comment: That strategy (to say nothing until it is published) seems to be practiced in Paris no less than in Eindhoven. heard other people say about it? This whole business of getting prior information on the contents of papers and running discussions about their contents (between people who hold more or less antagonistic points of view) even before the stuff is submitted, is somewhat distasteful to me. If a reader reads piece A by author X, and then ERTEL's comment: Distasteful? Would you include here the long correspondence I had with Koppeschaar (five postings of mine, 13 pages) his paper improved with every new critique and he expressed satisfaction, at least in his letter of Apr. 28 ("I am very happy with your comments and I will indeed change the respective sections in my paper wherever the comments are appropriate"). Inadvertantly, perhaps, he did not refer to my comments on previous versions in his acknowledgments, there he mentions the help of Dr. Nienhuys who, after it is done, finds his correspondence with me "distateful"). comment B by author Y, s/he cannot get a clear view on the discussion if actually X and Y have been exchanging many versions and comments already. In other words, readers (such as myself) want a real discussion, not some rehearsed play on a theatre stage. ERTEL's comment: The common practice of exchanging views about papers, critique by friends or referees, does this give rise to a "play on a theatre stage"? #I am looking forward to your replies. I am also looking forward to some spare time in which I can answer your proposals of tests of the CFEPP data. (Some of my time goes into other things, like teaching or providing information about Transcendental Meditation, Earth Ray witching, Homeopathy and Getting Things from Printers, reading UFO-manuscripts, and editing Congress contributions). Also not the time this has been sent. ERTEL's comment: More sincerity would have saved us time. The most deplorable result of this communication is indeed: LOSS OF TIME. Is anyone out there who would say: It payed?