Re: Aberrant Anthropology

Karl Kluge (
09 Jan 1995 06:13:45 GMT

We had a discussion about this line of work on not too long
ago. Here is a post of mine from that thread which should give interested
individuals pointers off to more stuff:

From: (Karl Kluge)
Subject: Re: On Lamark...get set...GO!
Date: 20 Dec 1994 05:52:53 GMT
In-reply-to:'s message of 19 Dec 1994 05:59:06 GMT

In article <3d37fa$> (Walter D Morris) writes:

> Thanks for your thoughts on this matter, Karl. I was not aware
> of some of the more recent papers cited by you. While I would
> agree with much of what you wrote, I would offer the following
> thoughts:

> With regards to your statement: "Ev seems to be more than mildly
> exaggerating when he claims that 'McConnell's results were confirmed
> and expanded in numerous different animals, from fish to mice, and
> in hundreds of different laboratories.'"
> Actually, I was not exaggerating at all. McConnell's results
> have been confirmed in numerous different animals and in
> hundreds of different laboratories. Here's the introductory
> paragraph from a paper entitled "Chemical transfer of learned
> information in Mammals and Fish," by Ejnar Fjerdingstad (in W.
> Byrne, "Molecular Approaches to Learning and Memory," 1970):
> "....There are by now more than 100 positive reports of the
> transfer effect in vertebrates alone. Although there are also a
> considerable number of reports of negative or unclear results,
> it would seem that the overall evidence heavily favors the
> existence of the phenomenon." (p. 430)

While in '70-'71 the number of positive *experiments* may have been in
the 100-135 range, the number of *labs* (as claimed by Malin, Golub,
and McConnell in NATURE 233:211-2) was on the order of "at least twenty
others" (as far as they were aware -- I'm not inclined to trace all 3
articles back to a full set of primary references to see if MG&M were
unaware of some of the work Dyal & E. F. were including). O(20+) and
O(100's) are not the same.

Regarding the claim that the number of positive reports increased
faster than negative reports post-1971...I couldn't find the
proceedings with the Travis paper, so I don't know what he
cites. Looking in PsycINFO with the query "k=rna and transfer and
(memory or avoidance or condition?)" only pulls 18 items from 1971 or
later, none of them after 1983. That doesn't add very many experiments
to the database one way or another.

> With regards to your statement: "Keep in mind that negative results rarely
> get published. As has already been suggested, it is likely that McConnell's
> work has not been ignored. Rather, it was merely in error, and there is a
> limited interest in publishing or reading papers which report a failure to
> find an effect."
> One should also keep in mind that positive results also get suppressed for
> fear of generating the same kind of controversy that McConnell's researches
> did. I know for a fact that this happened in the case of the memory-transfer
> experiments. It is also true that McConnell's grant money dried up as a
> result of the controversy (personal communication). Thus, as a supplement
> to your perfectly valid generalization, I would offer one of my own: There
> is limited interest in publishing or reading papers which result in
> ostracization, loss of grants, and/or loss of academic position.

This finesses the issue of whether the loss of grants, position,
etc. are a consequence of being controversial, or a consequence of
being sloppy methodologically. In another post you gave the quote "[In
the wake of McConnell's suggestion that memory-transfer was possible]
There followed a rash of attempts to replicate the phenomenon, many of
which failed. Later, more positive results began to emerge, and by
1970 the 'hit score' in terms of experiments was 133 for, 115 against,
and 15 equivocal. (Dyal, 1971) Since then the number of positive
reports has increased much more rapidly than the negative." (David
Travis, "Constructing Creativity: The Memory Transfer Phenomenon...,"
Paper read at the conference on the Social Processes of Scientific
Investigation, June 17-19th, 1979, p. 4.) Recapping that data:

* in 1962 McConnell published his first paper claiming memory
transfer in planaria
* between '62 and '70 there are ***263*** published experiments
in the area

If this work was being suppressed, there was sure as hell no sign of it in
the first 8 years after the initial result. However...

* of those 263 experiments, only 50.57% could replicate the effect

* reviews of the literature frequently complain about problems with
reproducibility or adequacy of controls (e.g., "Often investigators
cannot confirm their own findings." McGaugh, Proc. Am. Philosophical
Society 111(6):347-51 (1967); "In studies of the molecular basis
of memory, the evidence is conflicting because most experiments
are poorly designed and controlled, and are not directly
comparable." Wenman, J. Behavioural Science 1(1):6-12 (1969);
"Evaluated studies which have investigated the effects of RNA
and RNA synthesizers on memory and/or learning. It is concluded
that findings failed to support the notion that RNA functions
as a memory template or encoder." Sweet, Psychological Record
19(4):629-644 (1969)

Here's the abstract from one of McConnell's papers (NATURE 233:212
(1971)):"''RNA-rich extracts were obtained from the brains of trained
animals, untrained controls, and yoked-shock controls . . . . \Ss)
receiving injections of extract from these 3 sources were compared on
rate of acquisition of a jump-up avoidance task.'' Ss were 43 100-150
day old male albino rats. ''The mean number of avoidances during the 18
trials was 6.25 for animals receiving control group RNA, 5.83 for
animals receiving yoked-shock control group RNA, and 10.5 for animals
receiving experimental group extract.'' Results indicate that avoidance
was enhanced by extracts from trained donor brains.". Looking at the
paper, one notices the following methodological problems:

1) Inadequate controls -- "The enhancement of avoidance by
extracts from trained donor brains is open to several
interpretations. The chemical changes in trained animals
responsible for this effect might reflect learning, or
they might simply reflect general stimulation such as
shock trauma, violent activity, of [sic] mere exposure to
the experimental apparatus. The total ineffectivity of
extracts from yoked-shock donors argues against the latter
conclusion. But we did not control for all conceivable
sources of stimulation, such as being pushed off the
platform." Nor, I would add dryly, such as being subject
to recent classical conditioning.

2) Ambiguous data -- the difference in mean shock avoidance
between the experimental group (receieved extracts from
trained Ss) and the two control groups (no extracts given
and extract from yoked-shocked Ss given) only kicks in
on day 3 after the injections. Is this evidence of skill
transfer or facilitation of conditioning?

Note that in 1971 it was entirely possible to be doing better work than
this in this area. In particular, Braud, Laird, and collegues at U.
Houston, and the group at U. Dusseldorf's Institute of Psychology were
doing experiments that addressed these issues. Here are the cites and
abstracts of the Houston work (the second one is '74, but the similar
experiment at Dusseldorf was in '71).

AUTHOR: Braud, William G.; Laird, Porter V.; Richards, Steven J.
TITLE: Facilitation of avoidance behavior in goldfish by injection of brain
materials from trained donors: Effect of injection-testing interval.
SOURCE: Journal of Biological Psychology 1971 Dec Vol. 13(2) 6-8
Notes that previous studies of the ''biochemical transfer'' effect
have used within-S time course determinations which have been
confounded with practice effects. In this study, 6 independent groups
of 10 goldfish each were injected with brain extracts (RNA-protein)
from either trained (n = 48) or control (n = 48) donors. Recipients
were tested only once either 1, 2, or 3 days after injection. Although
recipients of ''trained'' extract consistently outperformed recipients
of ''untrained'' extract at all 3 nonreinforced test sessions, the
effect was maximal and significant (p < .02) at 3 days following
injection. The ''relatively permanent'' nature of the biochemical
transfer effect is discussed.

AUTHOR: Laird, Porter V.; Braud, William G.; Meador, Steven T.;
Galvan, Louis M.
TITLE: Biochemical transfer of a classical conditioning effect revealed
through reinstatement and reinforced learning procedures.
SOURCE: Journal of Biological Psychology 1974 Vol 16(2) 19-22
Conducted 2 experiments in which reinstatement and reinforced
learning procedures were used to detect the behavioral activity of
brain extracts from classically conditioned donor goldfish. In Exp I,
24 goldfish were given differential classical conditioning training in
which a green light signaled shock. In Exp II, blue light signaled
shock in a similar classical paradigm. Naive donor groups provided
control brain material. Extracts rich in both RNA and protein were
extracted from donor brains and injected intracranially into naive
recipient goldfish which were tested for color avoidance 72 hrs after
injection. At 48 hrs after injection, all recipient groups had been
given reinstatement or reminder trials consistent with the training of
their appropriate donors. Recipients of control extract learned blue-
and green-avoidance tasks equally (as predicted). However, recipients
of trained brain extracts learned the task homologous to that of their
appropriate donors significantly better than they did an antagonistic
task. Results suggest that reinstatement and reinforced testing may
make dramatically evident a classical conditioning transfer effect to
which previously used recipient test procedures were insensitive.

[In passing, at least one of the Dusseldorf experiments would seem to
offer some support for the "mere facilitation" view, although I don't
know that the authors interpretted it that way:
AUTHOR: Bisping, R., et al.
TITLE: The effects of nucleic acid concentration on biochemical memory
SOURCE: Journal of Biological Psychology 1971 Dec Vol. 13(2) 32-35
An RNA-fraction extracted by a ''hot phenol method'' from 45 goldfish
trained in a shock avoidance task was injected intracranially into 4
groups of recipient Ss (n = 124). The concentration of the extract was
either 1, l0, 30, or 200 mg. 4 other groups (n = 128) were similarly
injected with RNA-fraction extracted from 45 untrained Ss. 24 hr. later
all recipient groups were trained in the same avoidance learning task
for 40 trials. The performance of all injected groups was superior to
that of the uninjected donor Ss. Only at the lowest concentration were
the ''trained-RNA'' (T-RNA) Ss superior to the ''untrained-RNA''
(C-RNA) Ss. The performance of the T-RNA groups showed an ordered
decline with concentration while the C-RNA groups performed essentially
at the same level over all concentrations. The combined T-RNA groups
were superior to the C-RNA groups during the early phases of the test
trials while during the later stages the C-RNA groups performed at a
higher level.

Some funny things about that experiment, though: they see an effect
after 24 hrs (other positives only see an effect after ~3 days); and
they see an effect from injections of extracts from "naive" (i.e.,
untrained) subjects.]

What it boils down to is this:
1) research funds are a scarce resource;
2) the people who administer them have a fiduciary duty to the people from
whose pockets the money comes (whether taxpayers or shareholders) to
spend those limited funds judiciously;
3) they therefore have to make judgement calls based on the available data
as to what constitutes promising lines of work vs. what constitutes
unpromising line;
4) the decisions these folks make are not always *correct* -- they are just
as human as venture capitalists or bank loan officers (if you want
infallibility, talk to the Pope ex cathedra) -- but decisions *do* have
to be made about what is worth funding, and those decisions do not
constitute *suppression* in any meaningful sense of the word;
5) given a line of research where many of the positive results have
methodological problems, and the reproducibility rate is barely
over 50%, that would seem to be a good line of research to stop funding
after 8 years of work in the area;
6) whose fault is it that in 1971 (9 years after his initial paper) McConnell
is doing work that suffers from notable methodological deficiencies?;
7) McConnell and collegues were perfectly free to try and convince private
donors that their work was worth financing -- being the guy who ponied
up private money to prove a revolutionary discovery is a good way to
get famous (and, in the right circumstances, rich or richer);
8) why the heck are there more recent published reports that ALSO fail to
control for these issues (I'm thinking in particular of the Holt papers)?
whose fault is *that*?

> With regards to your statement: "Even if the evidence did support some
> sort of RNA-based memory storage, there would still be a huge gulf
> between that and establishing the heritability of memories encoded in
> such a way. To the best of my knowledge, no one did any work in that
> area. Such experiments would have to be very careful to control for
> potential effects involving heritable variability of learning rates on
> a task or tasks."
> Agreed. When and if such experiments are performed, however, I have
> little doubt that positive results of an inheritance of the effects of
> learning will be generated. This was the opinion of McConnell as well,
> who actually set out to perform such an experiment only to shut it down
> for fear of the professional repercussions (personal communication).

It would be interesting to know what his experimental design was. I'd want
to use cloned subjects.