So-called "formative causation" - A hypothesis disconfirmed
Response to Rupert Sheldrake
Rivista di Biologia - Biology Forum 85 (3/4), 1992, 445-453;
by Steven Rose
Brain and Behaviour Research Group, The Open University, Milton Keynes, MK7 6AA, UK

Sheldrake's paper claims that the results of the experiment which we jointly planned, and which was conducted by myself and Ms Harrison, are in conformity with the hypothesis he describes as "formative causation". Before demonstrating that Sheldrake's interpretation of these results is invalid, and that they by no means confirm his hypothesis, I wish to comment briefly on the background to the experiment. His book A New Science of Life seemed when I first read it, and still seems, to propose an entirely empty hypothesis. The circumstances in which novel hypotheses (paradigms) become important in science have been well described by Thomas Kuhn; they emerge when there is an accumulation of observational anomalies which existing hypotheses cannot account for, or when a theory becomes excessively cumbersome and "inelegant" and the alternative seems to handle the same material more coherently. To Kuhn's account we can, at least in the particular context of the present discussion, add the well-worn view that to have utility, a hypothesis should be capable of disconfirmation.

The trouble with the Sheldrake hypothesis is that it fails on all of these criteria. First, there is no convincing evidence adduced in Sheldrake's books that there are any anomalous phenomena, in the biological or non-biological world, which require his explanation. Most of the somewhat random assemblage of phenomena he describes are better accounted for by existing, less grandiose, hypotheses - such as, in psychology especially, experimenter effects. And most of the rest seem anecdotal in the way that has bedevilled research into parapsychology for getting on a century. Second, so-called "formative causation" is an hypothesis of such astounding generality as to be virtually vacuous. And third, as I have always recognised as a danger in principle, but which the experience of this collaboration has convinced me in practice, Sheldrake is so committed to his hypothesis that it is very hard to envisage the circumstances in which he would accept its disconfirmation.

Granted its scientific and philosophical implausibility it is worth asking why the Sheldrake hypothesis has continued to receive any publicity. Partly this must be due to the tireless and ingenious advocacy of its author, who has encouraged regular public involvement in devising "tests" of his hypothesis, with prizes for the winners. Partly too, I believe it is in tune with a powerful anti-rational trend in these post-modern times, in which Nieztsche is more frequently cited than Voltaire. Along with parapsychology, corn circles, creationism, ley-lines and "deep ecology", "formative causation", or "morphic resonance" has many of the characteristics of such pseudosciences, well-discussed by a number of contemporary sociologists of science. For the inventors of such hypotheses the rewards include a degree of instant fame which is harder to achieve by the humdrum pursuit of more conventional science. For the non-scientific public, suspicious - and often rightly so - of the imperialising claims of orthodox science, anything which appears to spring the seemingly inevitable reductionist trap is seized upon. Morphic resonance, with its mixture of seemingly straight scientific concepts drawn from developmental biology and mysticism, offers to the 20th century something akin to what Hahnemann's homeopathy offered to the 19th.

So why did I offer to collaborate on the experiment Sheldrake describes? My original offer was made, as he points out, more than a decade ago, when his book first came out. As I am hostile to the fascist implications of book-burning, even when the suggestion is made in joke, I responded to the Nature Editorial to which Sheldrake refers by suggesting that he himself run some experiments in my laboratory. Sheldrake accepted but found it difficult to find time to conduct them. In 1988 he wrote a series of columns in The Guardian, a daily newspaper, in which he misquoted some experimental results from my own and other laboratories concerning the localisability of the memory trace for a simple learning task in chicks. In my response, I referred to my original offer of joint experiments, and this time he took the offer up as he describes.

As Sheldrake says, much of the work of my laboratory centres on elucidating the molecular and cellular cascade involved in the neuronal plasticity and synaptic remodelling that accompanies learning and memory formation, and which is argued to form the neural representation of such memories (for review see ROSE, 1991a; for more general account, ROSE, 1991b; 1992). Our standard model involves a passive avoidance protocol in which day-old chicks, which tend to peck at bright objects in their field of view, are offered a bitter-tasting bead. Having pecked once, the chicks remember the characteristics of the bead and avoid similar but dry beads subsequently. Incidentally, this paradigm has by now been in use for more than two decades and tens of thousands of chicks in three continents. Yet new-hatched day-old chicks offered the bright bead still peck at it within ten seconds of presentation. Not so much sign of morphic resonance here!

In our joint experiment, described by Sheldrake, we chose a slightly different paradigm, that of conditioned taste aversion (GARCIA et al 1966). In this situation, the chick is offered and pecks at a dry, coloured bead and half an hour later is made mildly sick by intraperitoneal injection of lithium chloride. Chicks which have been treated in this way will subsequently tend to avoid pecking at beads resembling those they first pecked. The implications of conditioned taste aversion for learning theory are quite interesting, as they imply that the animal must form and retain, for at least half an hour, some type of neural representation of the bead even although it is non explicitly paired during this period with either an aversive or rewarding experience. Conditioned taste aversion is thus a form of learning which does not conform to conventional Hebbian or associationist criteria, and for this reason I have been interested to explore the extent to which it involves similar neural mechanisms to those involved in clearly associationist learning (BARBER et al., 1989; ROSE, 1991b).

The reasons for choosing this model to test the Sheldrake hypothesis were that the experimental design would allow chicks to demonstrate morphic resonance, if it occurred, at the time of their training experience and without any actual test manipulation. By training the chicks in a novel and hopefully unique environment (a brightly coloured and patterned pen) and using a "bead" - actually a yellow LED - of a colour that previous generations had not specifically experienced, at least in our laboratory, Sheldrake and I agreed that we would maximise the chance of finding any effect. The actual experimental design was as Sheldrake describes it in his paper, and the hypothesis that we were testing was also clearly understood between us; that if any effect which might be attributable to morphic resonance occurred, there should be an increasing reluctance of successive hatches to peck at the neural yellow LED which previous generations had come to associate with sensations of sickness. This increasing reluctance should be expressed in a cumulative increase in the latency to peck at the yellow LED by successive hatches when offered it during the "training" period of 30 s, whereas there should be no such increase in the latency to peck at the chrome bead. In addition to measuring latencies to peck during the training period it was also important to show that the chicks which had pecked the yellow bead and were then injected with LiCI did develop an aversion to it and therefore avoided the bead on test.

There are two constraints on these measures, imposed by the design of the experiment. First, there is always going to be an absolute minimum latency to approach and peck at the LED or the chrome bead. This minimum is partly dependent on experimenter variables, such as the moment from which the experimenter decides that the chick has observed the bead and therefore begins timing, and partly on the relative attractiveness of the yellow LED or the chrome bead to the chick. In practice in turned out that the beads were not equally attractive to the chicks from the very beginning of the testing sequence, so latencies for the two beads were always somewhat different. These differences were in part due to the chicks' ontogenetic colour preferences, in part to the fact that the yellow LED was differently shaped from the chrome bead, its stem thicker and not so easy for the experimenter to manipulate.

The second constraint is the converse of the first; because the test cut-off point is thirty seconds, this imposes a cut-off point to the timing; birds which do not peck within the period are conventionally either scored at the maximum - i.e. at 30 sec latency - or in our case as nor pecking at all (see Sheldrake's Fig. 1). These contraints ("ceiling" and "floor" or "basement" effects) inevitably skew the latency data, and must be taken into account in any statistical analysis, in addition to the possible practice effect as the initially naive and always blind experimenter works through the repetitive day-by-day experimental sequence.

With these constraints in mind, let me turn to the data. Firstly, as Figs. la and b show, chicks trained on the yellow LED and then made sick with lithium chloride tended to avoid the LED on test, whilst continuing to peck at the chrome bead. These figures show the data both for latencies and number of pecks, in the form of weekly medians. (In this and the next set of figures I show the full data set rather than omit the first few days as Sheldrake does). Thus throughout the period of the experiment, the "Garcia" effect, in terms of conditioned taste aversion, could be observed on testing the yellow-trained birds.

The important question however is not what happens on testing the birds but whether there are any secular differencies in the pecking or latencies during training. If morphic resonance were to be occurring, the latencies to peck at the yellow LED during training should steadily increase, and the ceiling effect would ensure a decrease in the number of birds successfully trained on yellow over the period of the experiment. As Sheldrake's Fig. I shows, that this did not occur, although he fails to refer to this, which is the most significant feature of the data.

fig 1a

fig 1b

At the beginning of the experiment, the number of birds successfully trained (yellow or chrome) was relatively low, reflecting the inexperience of the experimenter. The figures rapidly improved however, and by the end of the experimental series virtually all birds were being trained successfully. Nor were there any differences in the success rate of yellow-trained compared with chrome-trained birds. This in itself tends to disconfirm Sheldrake's hypothesis.

The most sensitive measure of any morphic resonance effect should however be the training latencies and pecking behaviour. Figs 2a and b shows these data for the .chrome and the yellow bead day by day for the duration of the experiment. There is no secular trend for a reduction in the number of pecks on the yellow bead, nor for an increase in the latency, again disconfirming Sheldrake's prediction. Indeed, there is an increase in the number of pecks on the yellow bead (regression slope y=4.98 + 0.105, R=0.43) and a decrease in the latency (y=5.908 - 0.114x, R=0.30) - precisely the reverse of what Sheldrake would predict.

Sheldrake's response is to ignore the first few days of the experiment, on the grounds that this is where the "experimenter effect" of Ms Harrison learning how to train might be most apparent. Even if we do this, however, there is still a slight, though non-significant decline in latency for the yellow bead over the remaining days of the experiment (R=O. 14 for yellow, 0.07 for chrome). There are thus no significant differences between the secular trends in either yellow or chrome beads, even with the "correction" of omitting the first days of the experiment. Thus the crucial prediction made by the hypothesis, which Sheldrake agreed before the experiment began, is also disconfirmed. How then to explain the apparently miraculous emergence of significant differences between the chrome and yellow groups in Sheldrake's handling of this data? This is partly because he has ignored the issue of basement and ceiling effects of the experimental design, hence enabling him to argue about residual differences in latency between yellow and chrome irrespective of the fact that the yellow latencies shift, if at all, in precisely the reverse direction to that he would predict, and partly because he has chosen to omit some of the data.

Although Sheldrake and I disagreed on our interpretation of the data, we did agree that he should also send his analysis to Professor P.P.G. Bateson at Cambridge. Bateson is an experienced ethologist and pioneer of imprinting studies in the chick, who originally initiated me into the world of avian learning in the late 1960s (see ROSE, 1992a for discussion) and who has (like me) acted as a judge for some of the competitions Sheldrake has run to "test" morphic resonance.

fig 2a

fig 2b

Bateson reanalysed our data, and has given me permission to quote his conclusions (letter dated 9th May 1992, the contents of which Sheldrake has also seen):

"If we take all the data and use non-parametric tests, as I think we must, the median latency in the chromes is 6 seconds (N=415) whereas it is only 3 seconds (N=434) in the yellows, and this difference is statistically significant (Mann-Whitney U, z=2.605, p=.009). Most of this difference, however, is in the 8 - 14 day block [of trials] (Mann-Whitney U, z=3,12, p=.002). The difference in the next block of 7 days borders on significance, but otherwise there are no differences.
The medians (seconds) for the latency data from each individual (sample sizes in brackets) are:


1 - 7

8 - 14

15 - 21

22 - 28

29 - 37 (days)













It is factually correct to say that after starting at the same point the latency for the yellow group dropped and was followed subsequently by a drop in the control group. [Sheldrake's] technique of looking at differences (and excluding the first week) is potentially misleading. Indeed it is actually misleading, in my opinion, to describe the latencies of the yellows as moving up relative to the controls.

Common ground is that the latency to peck dropped across the period of the experiment (unexplained but unsurprising). My interpretation of the difference between the groups is that the yellow light caught the attention of the chicks to a greater extent than the chrome bead so that, other things being equal, they pecked at it more quickly. At the beginning of the experiment, the tester's lack of experience ... contributed to a floor effect (ie no difference between the groups) and by the end of the experiment, a difference between the groups was no longer detected because of an obvious ceiling effect.

As far as I can tell, the evidence that, overall, the chicks pecked more quickly at the yellow bead than at the chrome bead runs counter to the prediction from the morphic resonance hypothesis, and [Sheldrake's] analysis obscures this fact".

I concur with Bateson; this experiment reveals no phenomenon which the hypothesis of morphic resonance might be called upon to explain, and in strict terms, Sheldrake's postulate of formative causation is therefore disconfirmed.


BARBER A.J., GILBERT D.D., ROSE S.P.R., 1989 - Glycoprotein synthesis is necessary for memory of sickness-induced learning in chicks. Eur. J. Neurosci. 1, 673-677

GARCIA J ERVIN F.R., KF.OLLINO R., 1966 - Learning with prolonged delay of reinforcement. Psychonom. Sci. 5, 121- 122

ROSE S.P.R., 1991a - How chicks make memories: the molecular cascade from c-fos to dendritic remodelling. Trends Neurosci. 14, 390-397

ROSE S.P.R., 1991b - Memory- the brain's Rosetta stone? Concepts Neurosci. 2, 43-64

ROSE S.P.R., 1992 - The making of memory. Bantam Books, Uxbridge