Prestimulus Response Experiments?

[Joe_Black]

Has this topic been discussed on the board yet?!:

http://www.lfr.org/LFR/csl/media/vid...scoveryCA.html

[Ersby]

I don't think so.

The paper is on this page (it's the first one):

http://www.lfr.org/LFR/csl/academic/library.html

Personally, I've never sat down and read the papers that cover this phenomenon, but it seems pretty interesting.

ETA: Bah, that's just an abstract and a bit of the results. I'll have a look to see if I can find the paper somewhere.

[Kell]

Prestimulus Response...tingling

[Ersby]

Okay, I found May's first paper on the subject.

www.parapsych.org/papers/10.pdf

It's pretty dense in technical jargon, so I'd need to sit down and read it properly. This sentence caught my eye:

Quote:

The experimental result from the acoustic study gives the rate prior to acoustic stimuli as P1 = 0.091 and prior to controls as P0 = 0.053; therefore a response was a rather rare event. That is, on the average only one or two stimuli in each session might contain an anticipatory response.

Which is also what happened to the guy in the video in the opening post.

[roger]

edited:

I origianlly wrote that they were discarding data. Now, I'm not so sure.

I originally wrote:

Quote:

Read the paper carefully, specifically the bottom of page 116 and top of 117. Note that they start with 190 people, then "screen" them to select 100 people for the formal analysis of the data. I.e., as far as I can tell, they discard the data that doesn't fit.

Yawn.

But on 117 they do use data from 190 people. I guess the original paper discarded data, but this one is using data from all 190 to do the DAT analysis? I can't tell.


Are they using the subset of 100 people to conclude that "somethign" is happening, and then using the data from the full 190 people to analysis the DAT hypothesis?

[davidsmith73]

This is a fascinating psi topic. The best paper I've read on this is :

http://www.scientificexploration.org...18.2_radin.pdf

It's Dean Radin's latest set of experiments investigating the presentiment effect - a pre-stimulus response of the autonomic nervous system to future emotional stimuli, where the occurance of the future emotional stimulus cannot be predicted by the nervous system in any known way.

Can anyone find a problem with this study?

[roger]

Originally Posted by davidsmith73

This is a fascinating psi topic. The best paper I've read on this is :

http://www.scientificexploration.org...18.2_radin.pdf

It's Dean Radin's latest set of experiments investigating the presentiment effect - a pre-stimulus response of the autonomic nervous system to future emotional stimuli, where the occurance of the future emotional stimulus cannot be predicted by the nervous system in any known way.

Can anyone find a problem with this study?

I don't understand his argument on pages 270-271.

I don't understand why he selects 13 people out of the total number, based on their strong performance, and analyses only their data. The idea that he is testing is that perhaps the pattern of calm/exciting previous to the current trial influences the current excitment level. But then he examines only data from people who happened to do really well. By chance some people are going to do really well. That says nothing about whether the pool of people, as a whole, are influenced by previous trials.

Also, the independent reviews are meaningless, since once again Radin hides his data, and refuses to share either the reviewer's names or the reports that they wrote.

If I was to design the experiment, I would want a long time period between each trial; say, at least 10 minutes. This would hopefully eliminate the past trials from influencing the current trial.

[fuelair]

Are they possibly using Thiotimoline (per Isaac Asimov)

[Soapy Sam]

Originally Posted by davidsmith73

This is a fascinating psi topic. The best paper I've read on this is :

http://www.scientificexploration.org...18.2_radin.pdf

It's Dean Radin's latest set of experiments investigating the presentiment effect - a pre-stimulus response of the autonomic nervous system to future emotional stimuli, where the occurance of the future emotional stimulus cannot be predicted by the nervous system in any known way.

Can anyone find a problem with this study?

Don't have time to read the study just now, (at work)-but I find a problem with the phrase "where the occurance of the future emotional stimulus cannot be predicted by the nervous system in any known way."
There are only so many types of emotional stimulus. Unless there is one I have not , ever, experienced before, I suspect I could anticipate any of them. As with any psycho / neurological experiment, the observer effect is complicated by the fact that the subject is also an observer.

[Ersby]

It's odd that Radin should choose a measurement that previously had found no significant effect, and in fact showed a marginal effect in the opposite direction (with more change in pre-calm trials). His earlier paper is here:

http://www.boundaryinstitute.org/art...entiment99.pdf

Maybe he didn't have a choice with the equipment he had.

Plus, on page 266 he does a stouffer z calculation on the four trials that range in size from 240 to 2059 trials. That bothers me a little.

Here's another paper from Bierman that describe their findings as "marginally significant" but apart from that, I can't make head nor tail of it. Anyone know about brain scans?

http://www.quantumconsciousness.org/...esentiment.pdf

[roger]

Don't know a lot about brain scans, but used to date a college professor whose livlihood was doing and analysing fRMI studies. Doing studies in the time domain are problematic for reasons that I no longer recall. But basically the BOLD technique relies on analysizing blood oxygen levels in the brain, and this response is very slow (on the order of several seconds) compared to neuronal activities. In all the technique is highly debated, and she often found herself defending her science due to these concerns.

But the kicker is on page 8, paragraph 4.1. Isn't he basically saying that he didn't get a statistical correlation, but that if we imagine that we perform a data filtering that he didn't perform that the data would be better, and thus we can pretend (imagine) that the data supports the hypothesis.

That's a neat trick. My data doesn't support my hypothesis, but let's imagine that it does, if I would just perform an analysis that I can't be bothered to make.

[jj]

Hmm. Selecting the ones that "responded"...

Let's see, if we have random results, and we select the ones who guess right...

???? I'm not sure that happened here, but somehow selecting data after the experiment doesn't sound good. ????

[Mercutio]

"about once every 45 seconds, varying by about 20 seconds or so" (from memory, I won't guarantee absolute word-for-word), sessions lasting half an hour.

His subjective report is that he could not tell when the sound would be coming; this is not surprizing. There are some fairly predictable conditioning effects that do not reach "conscious awareness". (For example, in a list of words, one word is chosen for pairing with electric shock; subjects typically will learn the association enough to have a sympathetic nervous system response, but only about 50% will be able to name the target word.)

Two possibilities--if they are cherry-picking, like they are in the video, they can choose hits to keep and misses to toss. I can't believe that they would be that careless, although it would not be the first time such a thing has happened.

The other possibility is more intriguing, and has the advantage of being quite testable. Simple temporal conditioning would be enough to show an effect if A) there were sufficient trials to sum to see an effect, and B) the randomization was inadequate. Any random number generator will generate sequences that vary in their predictability in the short term. (Long vs. short term control sequences for random number generators are part of what messed with J. B. Rhine's results. One must compare strings of equal length--simple probability statistics!) If only some of the subjects have been able to demonstrate the precognitive effects, perhaps the subjects' random sequences were different. A search for short-term periodicity in the random sequences could show sufficient pattern to have given some subjects enough information for temporal conditioning (it has been X long since the last startle stimulus, it must be coming again) even if it was not something they were consciously aware of.

The experts in Radin's experiment did not include behaviorists (who might have been more apt to look for this artifact), and his discussion of "anticipatory strategies" did not sufficiently explore this possibility (IMO), although it was the closest of the potential artifacts. I remember Radin's experiment; a fellow behaviorist who read it when it was first out also came up with the same temporal conditioning potential artifact.

Fortunately, it is not only testable, but easily guarded against in future studies.

(and I wonder whether the 3.5 second precognitive spike is an artifact of the randomization schedule. This also could be tested; the VT (variable time) schedule could be lengthened or shortened from its 45 seconds, and/or the variance could be altered from its +/- 20 seconds. If such changes altered the 3.5 second spike (or eliminated it), it seems more clearly a schedule-induced artifact.

[davidsmith73]

Originally Posted by roger

I don't understand his argument on pages 270-271.

I don't understand why he selects 13 people out of the total number, based on their strong performance, and analyses only their data. The idea that he is testing is that perhaps the pattern of calm/exciting previous to the current trial influences the current excitment level. But then he examines only data from people who happened to do really well. By chance some people are going to do really well. That says nothing about whether the pool of people, as a whole, are influenced by previous trials.

I think he does this so that there are a sufficient number of sequential calm targets before an emotional one, in order to test the anticipatory strategy hypothesis. He says that he forms an arbitrary division of targets into calm and emotional ones based on where the targets lie in the order of emotionality ratings. Based on this target selection he then finds out that 13 individuals achieve significance. Why look for sequential effects in the other 90 when they don't even show a presentiment effect?

Quote:

If I was to design the experiment, I would want a long time period between each trial; say, at least 10 minutes. This would hopefully eliminate the past trials from influencing the current trial.

Stop them from influencing in what way? This will not eliminate anticipatory strategies and the hypothesis will certainly have to be tested even if you space out the trials in this way.

[davidsmith73]

Originally Posted by Ersby

It's odd that Radin should choose a measurement that previously had found no significant effect, and in fact showed a marginal effect in the opposite direction (with more change in pre-calm trials). His earlier paper is here:

http://www.boundaryinstitute.org/art...entiment99.pdf

Maybe he didn't have a choice with the equipment he had.

Maybe. He also may be simply trying to asses whether SCR is a good measure of this effect or not since experiments earlier than the one you linked gave positive results, as did experiments by other researchers using SCR. I think the experiment that did not give a significant effect using SCR is the odd one out so to speak.

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Plus, on page 266 he does a stouffer z calculation on the four trials that range in size from 240 to 2059 trials. That bothers me a little.

Why does it bother you?

Quote:

Here's another paper from Bierman that describe their findings as "marginally significant" but apart from that, I can't make head nor tail of it. Anyone know about brain scans?

BOLD technique is very prone to artifacts if you don't know what you're doing. The effect would have to be quite large to rule that out I think. Interesting that the same effect seems to show up though. Ideally, an MEG experiment should be done. Massively better in terms of temporal and spatial resolution. However, I think there's only a handful of MEG machines in the world. Not promising...

[Ersby]

Originally Posted by davidsmith73

Why does it bother you?

The problem is that the stouffer z doesn't take into account the size of the experiment. If you had a number of small scale experiments with high z-scores and one large scale experiment with a small z-score, a stouffer z would treat them equally. Of course, here there's only four experiments they're not too dissimilar in size and the second largest experiment is the most successful, which is why it only bothers me a little.

[roger]

Originally Posted by davidsmith73

I think he does this so that there are a sufficient number of sequential calm targets before an emotional one, in order to test the anticipatory strategy hypothesis. He says that he forms an arbitrary division of targets into calm and emotional ones based on where the targets lie in the order of emotionality ratings. Based on this target selection he then finds out that 13 individuals achieve significance. Why look for sequential effects in the other 90 when they don't even show a presentiment effect?

But you can't do that in science. Gather your data, and then decide how you are going to analyze it. That's called data mining. Suppose this hadn't worked out for him. Then he could have chosen a different way to analyze the data, and found a correlation.

But it's worse than that in this case. Here, he specifically chose 13 people where they show a lot of hits. Pretend for a second that this isn't real data from people doing the trial, but just simulated data created by a computer - so we know there is no effect to observe. Most of the random data is going to show no correlation, but a few data sets, maybe, oh, 13 or so, will show some strong hits. So you go and analyze those, and guess what? They probably aren't going to that anticipatory period over several calm sessions, merely because the strong performance means that the data shows calm before calm targets, and excitement before exciting targets. I.e. he preselected data that probably wasn't going to exhibit the patterns he was hoping to not find.

It also preassumes the conclusion - that psi is responsible for this.

That's my hypothesis. I'd actually like to see that experiment run. Generate random data for the human trials, and see if you can find similar correlations. If so, the experimental results are bunk.

Quote:

Stop them from influencing in what way? This will not eliminate anticipatory strategies and the hypothesis will certainly have to be tested even if you space out the trials in this way.

We are not talking about anticipatory strategies (if you mean that in a psi sense). If I jump out of a closet and scream at you you'd be quite startled. If I did it an hour later you'd be startled again. But if I did it 3 seconds later you wouldn't be startled at all. It takes time for your system to settle down after excitement.

Now, assume for a second there is no psi effect. None. Take an experiment where there are twice as many calm trials as excited trials, as Radin has done. This means that exciting trials are relatively few and far between. It is likely after an exciting trial that it will be followed by a calm trial or two because of that uneven distribution. So, you are presented an exciting picture, you show a response, and slowly start calming down. You are presented a calm picture and you remain calm. But then you start getting excitied because consciously or unconsciously you know something exciting is coming up. Sooner or later that exciting picture is shown, and lo and behold, prior to that picture you were showing excitement.

Hey, they admit that this happens. They've done tests and it does happen that way. So the burden on the experiementers is to show that the results are do to psi, and not this well known, verified behavior.

How does he do this? Performs post hoc analyses on a data subset that is likely to support the psi hypothesis. Bad science.

He did this, in a more blantent way, in an earlier paper. He gathered his data, found no effect, but found that some people performed negatively - ie worse than chance. What does he do? Presupposes his conclusion, decides that these people are exhibiting negative psi, and discards their data from the data sets. Now his statistical analysis shows a positive correlation, and he decides he has proven his hypothesis.

The problem with that is obvious. In uniformly distributed random data, some will show a negative correlation, some positive, some neutral. If you discard the negative, the rest of the data will show a slight positive correlation.

I can't find a link to that paper, but Paul started a thread on it a few years ago, and the paper was pretty much trashed. I've searched the archives and can't find it.

[davidsmith73]

Quote:

But it's worse than that in this case. Here, he specifically chose 13 people where they show a lot of hits. Pretend for a second that this isn't real data from people doing the trial, but just simulated data created by a computer - so we know there is no effect to observe. Most of the random data is going to show no correlation, but a few data sets, maybe, oh, 13 or so, will show some strong hits.

So we have data created to simulate SCR which is generated to form a random distribution of SCR values around a baseline value. Is that what you're essentially suggesting here? If so, yes, a small sample of trials will by chance show a significant difference between calm and emotional trials. With you so far.

Quote:

So you go and analyze those, and guess what? They probably aren't going to that anticipatory period over several calm sessions, merely because the strong performance means that the data shows calm before calm targets, and excitement before exciting targets. I.e. he preselected data that probably wasn't going to exhibit the patterns he was hoping to not find.

He selected data that had the highest chance of showing this effect, if it were present! Back to our computer generated data. Within our 13 significant samples, our data isn't going to show an anticipatory strategy because we know one is not present - its just random data. However, someone who did not know that the whole dataset was generated by random distribution would also find that our small sample does not show an anticipatory strategy. And that's all they could conclude. That's what is being tested after all - whether or not an anticipatory strategy can account for our selected data.

Now, considering that we need a sufficient length of calm trials before an emotional one in order to test the anticipatory hypothesis, and considering that the best case for such a strategy being present is within those trials that show a positive result, I see no problem with Radin's approach. If there is no anticipatory strategy observed in those 13 high scorers then what chance is there of finding one in the rest of the data! Indeed, if you're sceptical it seems a bit pointless trying to find anticipatory strategies in data that does not show a significant effect! What if he found such strategies in the 90 other non-significant individuals? Wouldn't that actually increase his confidence that such strategies are not responsible for the overall results because it would demonstrate that such strategies are not sufficient to get positive results.

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It also preassumes the conclusion - that psi is responsible for this.

Maybe. But it seems not to be anticipatory strategies!

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That's my hypothesis. I'd actually like to see that experiment run. Generate random data for the human trials, and see if you can find similar correlations. If so, the experimental results are bunk.

No not at all. You also have produce overall significant result from such random data. If you plan just to run your random data program and show that there is a significantly positive subset that shows no anticipatory strategy then that's all you can conclude. That's all that Radin is trying to show too - that anticipatory strategies are not present in his best data. Taken in isolation his selected subset could still be just a fluke (granted, he doesn't acknowledge this) but when they are put back in the overall data, the results remain significant.

Quote:

How does he do this? Performs post hoc analyses on a data subset that is likely to support the psi hypothesis. Bad science.

What? He performs the test on data that is most likely to show the anticipatory effect you talked about! The test is designed to demonstrate if such a strategy is responsible for the positive results.

Returning to the other issue, if you increase the interval between trials as you suggested, there will still be the possibility that anticipatory strategies can influence the results. The participant can still remember what the last trial was, regardless of how long its been since. The hypothesis will still have to be tested.

Quote:

He did this, in a more blantent way, in an earlier paper...

...I can't find a link to that paper, but Paul started a thread on it a few years ago, and the paper was pretty much trashed. I've searched the archives and can't find it.

That's a pity because I'd like to check out this claim for myself. Paul if you reading, can you help?

[Paul C. Anagnostopoulos]

I remember this subject, but I can't find the old thread either. Here is a 2003 paper by Spottiswoode and May:

http://www.scientificexploration.org...swoode_may.pdf

Radin called it "presentiment." Here is a paper by Broughton on a failure to replicate:

http://72.14.207.104/search?q=cache:...s&ct=clnk&cd=2


~~ Paul

[roger]

Originally Posted by davidsmith73

He selected data that had the highest chance of showing this effect, if it were present!

He asserts that, but does not prove that, to my understanding. Could you explain why this would be true?

I offered a counterexample that suggests that it would be less likely to show this effect.

Quote:

Back to our computer generated data. Within our 13 significant samples, our data isn't going to show an anticipatory strategy because we know one is not present - its just random data.

Untrue. Uniform random data will show exactly that in some subsets. Other subsets will show nothing, and yet other subsets will show a negative correlation.

Quote:

Returning to the other issue, if you increase the interval between trials as you suggested, there will still be the possibility that anticipatory strategies can influence the results. The participant can still remember what the last trial was, regardless of how long its been since. The hypothesis will still have to be tested.

I see what you are saying. My test rules out some kinds of antipatory strategies, but not all of them. Agreed.


ETA:

Assume 4 trials, with random data. 4 so I can write out all the possibilities - obviously a real experiment will require more trials. I simplify by rating each trial as calm or excited, rather than the continuum that is actually measured.

With random data we generate (c = calm, e = excited):

CCCC
CCCE
CCEC
CCEE
...
EEEE

When matched against a specific picture series, some of those show no correlation, some positive correlation, and some negative. I'm sure we agree on that point. But, as far as the non-psi anticipatory strategy goes, some of those will show the anticipatory effect, and some won't. However, the better the match, the less of that effect it will show, I argue.

For example, suppose the picture series was CCCE. Take the data set CCCE. That will test low for the antipatory practices, because there is no build up from calm to excited. yet it is the highest possible performace possible for that picture series. Radin, by selecting the 13 highest performers, is quite probably selecting against the anticipatory strategy, not for it. The point being that the anticipatory strategy will only yield a modest positive correlation; random data can (and will) yield higher correlations, just by the law of large numbers.

[roger]

Originally Posted by Paul C. Anagnostopoulos

Here is a paper by Broughton on a failure to replicate:

(snip url)

~~ Paul

An interesting paper, perhaps. I haven't read it yet, but see in the abstract that they tackle the retest question. That's another issue with the papers above. They talk about strong performers, but never prove it. A person is a strong performer if they can show a positive correlation across multiple experiments. These papers are all taking the strong performers from a single experiment. The law of large numbers tells us there will always be strong performers within a single experiment. Any analysis that follows from those selected groups is immediately worthless. Another objection to the 13 person subset used to test the anticapatory strategy.

[davidsmith73]

Originally Posted by roger

He asserts that, but does not prove that, to my understanding. Could you explain why this would be true?

There is a specific hypothesis under test here - that an anticipatory strategy (just like the one you described previously) is the mechanism by which a significant difference in SCR between calm and emotional trials is generated. If his set of data is selected on the basis of a significant difference between calm and emotional trials then this dataset is the most likely one to display the anticipatory effect if it is present because such a strategy predicts such a significant difference, according to the hypothesis under test . I think its fair to say that no strategy was found to be present in his subset of data.

Quote:

I offered a counterexample that suggests that it would be less likely to show this effect.

I address this below

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Untrue. Uniform random data will show exactly that in some subsets. Other subsets will show nothing, and yet other subsets will show a negative correlation.

Yes, you are right. I'll address this below again.

Quote:

Assume 4 trials, with random data. 4 so I can write out all the possibilities - obviously a real experiment will require more trials. I simplify by rating each trial as calm or excited, rather than the continuum that is actually measured.

With random data we generate (c = calm, e = excited):

CCCC
CCCE
CCEC
CCEE
...
EEEE

When matched against a specific picture series, some of those show no correlation, some positive correlation, and some negative. I'm sure we agree on that point. But, as far as the non-psi anticipatory strategy goes, some of those will show the anticipatory effect, and some won't.

Agreed so far. ETA: apart from the last sentence!

Quote:

However, the better the match, the less of that effect it will show, I argue.
For example, suppose the picture series was CCCE. Take the data set CCCE. That will test low for the antipatory practices, because there is no build up from calm to excited. yet it is the highest possible performace possible for that picture series.

Your example can't show any form of anticipatory strategy because you are forcing the SCR dataset into only two discrete responses - C or E. The anticipatory strategy hypothesis predicts a gradual increase in SCR along calm trials, culminating in a maximum SCR at the emotional trial, after which the level of SCR response is then "re-set". I'm still a little unsure of what you are trying to show in your counter example.

Quote:

Radin, by selecting the 13 highest performers, is quite probably selecting against the anticipatory strategy, not for it.

I don't see how this is the case at all. Your random data example is not a valid model for what the anticipatory hypothesis predicts, ie, it is not possible for your example to show such a strategy at all because you only have two discrete reponses.

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The point being that the anticipatory strategy will only yield a modest positive correlation; random data can (and will) yield higher correlations, just by the law of large numbers.

I don't understand. A modest correlation between what?

[roger]

Quote:

I don't see how this is the case at all. Your random data example is not a valid model for what the anticipatory hypothesis predicts, ie, it is not possible for your example to show such a strategy at all because you only have two discrete reponses.

As I said, I simplified the notation just so I could easily write it down. Infer for each C and E in my notation a continuous, analog signal. After all, to judge the results the experimenter has to decide if the multisecond, analog measurement corresponds to a calm or exciting picture.

My point is that one can posit an analog data set where it shows high correlation with the pictures, but doesn't show the anticipatory response.
I.e. for the CCCE picture sequence, assume an analog signal with remains pretty much at baseline, with no significant rises, until 3 seconds before the fourth picture, where it shows a stong spike. And assume a second analog signal with slowly rises from baseline until it reaches it's maximum, at 3 seconds before the fourth picture. Both show positive correlation to the CCCE picture sequence, however the first data set is a stronger correlation because it does not have that rising slope. The first data set also does not show the anticipatory response, because it doesn't have a rising slope prior to the fourth picture.

And that's the point. Random data can and will produce a stronger correlation than can the well documented anticipatory response, and it will not show the anticipatory response.

By choosing the top 13 performers, we risk selecting random data that fits that criteria. That it doesn't show evidence for the anticipatory response is not proof that the data is due to PSI, since we would expect exactly that result if the data was random anyway.

Originally Posted by davidsmith73

I don't understand. A modest correlation between what?

Between the recorded data and the picture sequence.

[davidsmith73]

[quote=roger;1676436]

Quote:

My point is that one can posit an analog data set where it shows high correlation with the pictures, but doesn't show the anticipatory response.
I.e. for the CCCE picture sequence, assume an analog signal with remains pretty much at baseline, with no significant rises, until 3 seconds before the fourth picture, where it shows a stong spike. And assume a second analog signal with slowly rises from baseline until it reaches it's maximum, at 3 seconds before the fourth picture. Both show positive correlation to the CCCE picture sequence, however the first data set is a stronger correlation because it does not have that rising slope. The first data set also does not show the anticipatory response, because it doesn't have a rising slope prior to the fourth picture.

I see what you mean now. That's a good point. But I'm still a little sceptical over this because he did analyse all his participants that achieved significance (according to his arbitrary emotional/calm picture rating of course). I would expect that some of these individuals would show an anticipatory strategy if such a strategy was responsible for the overall experimental results.

So would it be possible that the remaining 90 individuals in Radins showed an anticipatory strategy? It's not clear how Radin did his analysis. I think its implied that the remainder didn't achieve a significant difference between calm and emotional taken individually. However, would it be possible for an anticipatory effect to be present in the difference between calm and emotional trials when you average everyones response in some way. Seems quite over complicated.

It would be much better for this experiment if such a strategy could be ruled out in the experimental design. The only way I can think of is to keep the participants naive to the fact that an emotional trial will appear. Perhaps let them think they are involved in an experiment looking at normal responses to calm stimuli, give them a sequence of calm pictures, then place an emotional one in there without them knowing. Probably wouldn't be allowed for eithical reasons here in UK! We're a bit soft.

[roger]

Originally Posted by davidsmith73

It would be much better for this experiment if such a strategy could be ruled out in the experimental design. The only way I can think of is to keep the participants naive to the fact that an emotional trial will appear.

Well, that's where I was going with the long periods between individual trials, though you rightly pointed out a limitation with that strategy.

How about this? It'd take a long time to generate a meaningful data set, but I think it would work.

Each experiment shows 4 pictures. The first 3 are the same for all testees, and are rated as 'calm'. The last picture is randomly selected as either calm or stimulating. The only data analysed for each experiment is the 3-4 seconds prior to the fourth picture. The subgroup where the 4th picture is calm is your control group, and the excited picture is your experimental group. All people are blinded to the purpose of the experiment. Data analysis method is chosen prior to the data collection, and no post hoc reasoning, data analysis, etc., is allowed. (of course you can do that to decide what you want your next experiment is, but you can't draw conclusions from those post poc decisions). All collected data and analsysis methods are published and/or made available to researchers - nothing is hidden from "negative sceptics", or whatever term you want to use. The papers are peer reviewed in an open environment.

If they can repeatedly show statistical significance in that scenerio, I'd tenatively agree that there was something going on (tenative because I'm no experimental scientist, and I've probably missed something that needs to be tightened up).

[davidsmith73]

Originally Posted by roger

How about this? It'd take a long time to generate a meaningful data set, but I think it would work.

Each experiment shows 4 pictures. The first 3 are the same for all testees, and are rated as 'calm'. The last picture is randomly selected as either calm or stimulating. The only data analysed for each experiment is the 3-4 seconds prior to the fourth picture. The subgroup where the 4th picture is calm is your control group, and the excited picture is your experimental group. All people are blinded to the purpose of the experiment. Data analysis method is chosen prior to the data collection, and no post hoc reasoning, data analysis, etc., is allowed. (of course you can do that to decide what you want your next experiment is, but you can't draw conclusions from those post poc decisions). All collected data and analsysis methods are published and/or made available to researchers - nothing is hidden from "negative sceptics", or whatever term you want to use. The papers are peer reviewed in an open environment.

Good suggestion. Only Dick Biermann has done something similar to this. He was performing a presentiment experiment like the one from Radin's paper but he added an extra experiment before the main one. Participants were told they would be shown only a series of about 10 calm pictures in order to calclulate a baseline reading, but he slipped in an emotional picture too. All participants got at least 3 calm pictures, just like your suggestion, with the only essential difference that he sequentially randomised the placement of the emotional picture after the 3 calm ones. So the emotional one could be 4th or 6th or 9th etc, up to a limit of 10th place. I think he did this to further test the sequential anticipatory strategy even though the participants were naive (so we assume) to the rogue emotional picure. Obviously participants could only have one trial so he didn't have a large n number. He did not get a significant result but there was a visible rise in SCR before the emotional picure. Interesting and definately worth a replication attempt.

Found the experiment. See Study 2.

http://m0134.fmg.uva.nl/publications...al_tucson3.pdf

Quote:

If they can repeatedly show statistical significance in that scenerio, I'd tenatively agree that there was something going on

I agree

[Ersby]

I'd say that of all parapsychology's claims, this one seems the most promising. The idea of people remote viewing and describing locations that are distant in both space and time? Forget it. The idea we subconsciously react to a stimuli in the immediate vicinity and in the immediate future is simply more plausible. To me, anyway.

Unfortunately, the results are not easily described to a layman, and tend to rely on statistics and technical details to a level beyond most people's understanding. Plus, I think it suffers from a certain "unsexiness" that things like remote viewing or the Global Consciousness Project don't have. They can talk about spies or our collective soul crying out at some disaster. The prestimulus response work doesn't have that option - it's pretty dry stuff, which is perhaps why there's not been a huge amount of work on the subject, despite its relative ease.