This letter to Dr. Nienhuys might have been posted directly to him, it is again technical

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------------------------------------------------------------------- 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?


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