This letter to Dr. Nienhuys might have been posted directly to him, it is again technical
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
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.
E-Mail Fredric L. Rice / The Skeptic Tank