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From: Robert Sheaffer <[e-mail]>
Subject:      Re: Mars effect and induced births
Message-ID: <[e-mail]>
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 - [e-mail]

 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 <[e-mail]>
Subject:      Mars effect and induced births
Message-ID: <[e-mail]>
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 <[e-mail]>
Subject:      Mars effect and induced births
Message-ID: <[e-mail]>
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 <[e-mail]>
Subject:      Mars effect
Message-ID: <[e-mail]>
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" <[e-mail]>
Subject:      Re: Mars effect and induced births
Message-ID: <[e-mail]>
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 <[e-mail]>
Subject:      Mars effect and induced births
Message-ID: <[e-mail]>
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" <[e-mail]>
Subject:      Re: DUMB QUESTIONS
Message-ID: <[e-mail]>
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: <[e-mail]>
From: [e-mail] (Jan Willem Nienhuys)
Date: 27 Oct 92 10:31:04 GMT
Reply-To: [e-mail]
Sender: [e-mail]
References: <[e-mail]> <[e-mail]>
<[e-mail]
   >
Organization: Eindhoven University of Technology, The Netherlands
Lines: 69

In article <[e-mail]> [e-mail] (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" <[e-mail]>
Subject:      Mars Effect: Nienhuys responds to Ertel
Message-ID: <[e-mail]>
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: <[e-mail]>
From: [e-mail] (Jan Willem Nienhuys)
Date: 26 Oct 92 12:34:04 GMT
Reply-To: [e-mail]
Sender: [e-mail]
References: <[e-mail]>
Organization: Eindhoven University of Technology, The Netherlands
Lines: 153

In article <[e-mail]>
[e-mail]
   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 <[e-mail]>
#
#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" <[e-mail]>
Subject:      "Mars Effect":  Nienhuys responds to Ertel, parts 2 and 2a
Message-ID: <[e-mail]>
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: <[e-mail]>
From: [e-mail] (Jan Willem Nienhuys)
Date: 26 Oct 92 15:49:13 GMT
Reply-To: [e-mail]
Sender: [e-mail]
References: <[e-mail]> <[e-mail]>
Organization: Eindhoven University of Technology, The Netherlands
Lines: 235

In article <[e-mail]>
[e-mail]
   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 <[e-mail]>
#Subject: JWN and MARS EFFECT
#Sender: SKEPTIC Discussion Group <[e-mail]>
#Reply-to: SKEPTIC Discussion Group <[e-mail]>
#Message-id: <[e-mail]>
#
#
#             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: <[e-mail]>
From: [e-mail] (Jan Willem Nienhuys)
Date: 26 Oct 92 16:59:32 GMT
Reply-To: [e-mail]
Sender: [e-mail]
References: <[e-mail]> <[e-mail]>
<6
   [e-mail]>
Organization: Eindhoven University of Technology, The Netherlands
Lines: 57

In article <[e-mail]> [e-mail] 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 <[e-mail]>
Subject:      JWN and MARS EFFECT
Message-ID: <[e-mail]>
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: [phone] email: [e-mail]





From: Suitbert Ertel <[e-mail]>
Subject:      JWN and MARS EFFECT
Message-ID: <[e-mail]>
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 <[e-mail]>
Subject:      Skeptics' focus
X-To:         [e-mail]
To:           Multiple recipients of list SKEPTIC <[e-mail]>
------------------------------------------------------------------
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: <[e-mail]>
From: [e-mail] (Jan Willem Nienhuys)
Date: 12 Oct 92 13:26:11 GMT
Reply-To: [e-mail]
Sender: [e-mail]
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: [e-mail]





From: Suitbert Ertel <[e-mail]>
Subject:      JWN and MARS effect
Message-ID: <[e-mail]>
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" <[e-mail]>
Subject:      Re: JWN and MARS effect
Message-ID: <[e-mail]>
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: <[e-mail]>
From: [e-mail] (Jan Willem Nienhuys)
Date: 7 Oct 92 17:29:06 GMT
Reply-To: [e-mail]
Sender: [e-mail]
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: <[e-mail]>
From: [e-mail] (York H. Dobyns)
Date: 7 Oct 92 22:00:30 GMT
Sender: [e-mail] (USENET News System)
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Originator: news@nimaster
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In article <[e-mail]> [e-mail] 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<p<1.  Call this H1.

A somewhat better informed alternative hypothesis might be:
"Well, the Mars effect shouldn't be overwhelming, because if
astrological effects were huge and unvarying there wouldn't be any
debate about the validity of astrology. And a result *less* than
the chance level hardly counts as evidence for a 'Mars effect'--it
refutes astrological predictions as surely as a null result would.
So let's say the plausible range of values for p is 0.172 < p < 0.344,
from the chance level up to twice the chance level." Call this
informed alternative H2.

The next step is to calculate the relative likelihoods of these
hypotheses given the observation of 435 "hits" in 2087 attempts.
The absolute values aren't interesting, because the useful information
is in how much the evidence favors one hypothesis over another--this
is called an odds ratio, odds adjustment, or Bayes factor depending
on who you consult. My figures are probably a few percent off, because
I'm using a normal approximation to the likelihood rather than the
actual beta-function. (They're not far off, though, because the
normal is going to be a fairly good approximation for totals this
large.)

The comparison between H0 and H1 produces an odds ratio of 96 in favor
of H1. That is, however confident I was that there is no Mars effect,
I should be almost 100 times less confident after reading the figures
Jan has presented.

The comparison between H0 and the more plausible alternate H2 makes the
odds ratio 560 in favor of the alternate. Same meaning as above, but
with a bigger number to plug in.

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, etc., that JWN mentions with regard
to some other figures. But I certainly can't salvage my peace of mind
by flying in the face of statistical inference and claiming, along with
JWN, that the observation *as presented by him* doesn't constitute
evidence for an effect.

York H. Dobyns          [e-mail]




Newsgroups: sci.skeptic
Subject: Re: Statistical Evidence (was Re: Fwd: Astrology...)
Message-ID: <[e-mail]>
From: [e-mail] (Jan Willem Nienhuys)
Date: 8 Oct 92 16:02:10 GMT
Reply-To: [e-mail]
Sender: [e-mail]
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In article <[e-mail]> [e-mail]
(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 <[e-mail]>
Subject:      Re: JWN and MARS effect
Message-ID: <[e-mail]>
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 <[e-mail]>
Subject:      jwn and MARS effect
Message-ID: <[e-mail]>
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" <[e-mail]>
Subject:      Re: JWN on MARS effect
Message-ID: <[e-mail]>
Date:         Mon, 12 Oct 1992 08:14:41 -0700
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Newsgroups: sci.skeptic
Subject: Ertel's Error
Message-ID: <[e-mail]>
From: [e-mail] (Jan Willem Nienhuys)
Date: 12 Oct 92 13:26:11 GMT
Reply-To: [e-mail]
Sender: [e-mail]
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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: [e-mail]





From: "Mark, Phone 2404" <[e-mail]>
Subject:      RE: JWN and MARS effect
Message-ID: <[e-mail]>
Date:         Mon, 12 Oct 1992 18:01:35 MDT
Suitbert Ertel <sertel%dgogwdg1.bitnet>
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: [e-mail]                           |          |
Voice: 403-329-2404                                      \_       _\\
FAX:   [phone]                                         \\   / _
                                                              \  \/ |
                                                               ---^---




From: "James J. Lippard" <[e-mail]>
Subject:      Mars Effect: Nienhuys responds to Ertel
Message-ID: <[e-mail]>
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: <[e-mail]>
From: [e-mail] (Jan Willem Nienhuys)
Date: 26 Oct 92 12:34:04 GMT
Reply-To: [e-mail]
Sender: [e-mail]
References: <[e-mail]>
Organization: Eindhoven University of Technology, The Netherlands
Lines: 153

In article <[e-mail]>
[e-mail]
   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 <[e-mail]>
#
#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 <[e-mail]>
Subject:      Mars effect
Message-ID: <[e-mail]>
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 <[e-mail]>
Subject:      Proceedings aftermath
Message-ID: <[e-mail]>
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?