The Tangled Methods of Quantum Entanglement Experiments

(Published 1999: "Accountability in Research", vol. 6, no. 4, pp 311-332 [1999])

Caroline H Thompson, Department of Computer Science, University of Wales, Aberystwyth, UK.

Key words: data adjustment, bias, peer review, quantum entanglement, EPR, Bell inequalities, photon

This paper concerns quantum theory, but you do not need to be familiar with the subject to appreciate the problems I discuss. These are matters more of our limitations as human beings - the conflict between our natural ways of doing things and the rigours of science, especially science that is beyond our everyday experience.

I became involved in the story of quantum entanglement in 1993, when I stumbled upon a statement in a book review that scientists had shown "instantaneous action at a distance", which was, to my way of thinking, impossible. I simply could not imagine how the claim could be taken seriously. A magician might make such a claim, but not a scientist! How could twiddling a knob here instantaneously - not just fast but in zero time - produce an effect over there? There had to be something wrong with the experiment. There had to be some built-in bias or artifact that they had not understood.

Acceptance of the idea that this kind of mysterious quantum effect really happens has wide implications. If you add to it Einstein's ideas on relativity, with his doubts on the concept of absolute time, you open the door to the paranormal, time-travel, whatever you wish, for you can no longer distinguish the rational from the irrational. The universe might not be rational!

I had good reason for taking a straightforward view of things. I had reached the age of 50 living in a world that seemed to behave entirely rationally, and had had a limited amount of experience of working with scientists. Moreover, I had not invested years of my life in the study of quantum theory. If I had been told that all its predictions were correct, I would have been frankly sceptical. It was only a man-made model: we mere mortals just could not know enough to make a model that perfect!

The scientists I had worked with were at an agricultural research station (East Malling, Kent, which dealt mainly with fruit crops), where I had been a statistician for about eight years. The system there was - or so it seemed from my vantage point - almost perfect. It did seem to produce valid science, but then, all the factors were in its favour, so why should it not? Our "science", our common sense, and our practical know-how were never in conflict. Was it really "unbiased"? Probably not, but it was perceived to be of practical use, so did it matter?

The part of the system of which I was most aware was the very rigid procedure whereby every single research project was supposed to have its own assigned statistician. The statisticians were as independent as they could be, all belonging to the Statistics Department. No project could be started without an experimental design, approved by the Head of Statistics! All results were supposed to be processed by the Statistics Department, who graciously marked the "significance levels" that the experimenter had reached. This rigid protocol guaranteed that we had at least done our best to ensure that experiments led to valid advice to our "members" - fruit growers, largely from the immediate vicinity. In addition to this procedure, there was a great deal of contact with growers, who had no inhibitions about telling us their problems, and there was in practice enough scope for established experimenters to just play with new ideas on a small scale, investigating anything that took their fancy.

Thus we were constantly aware that we were accountable to our local community. There was also a notable lack of theoretical models, other than the basic ones underlying the analysis of variance: empirical results were all that most experiments were seeking. All that was required was that the trials be conducted as fairly as possible, and reported in such a way as to enable the growers to draw useful conclusions. On the rare occasions when we did find ourselves constructing mathematical models, we would follow the obvious and necessary course, investigating their behaviour over as wide a range of parameter values as possible.

At the time, I must admit that I could not quite understand the need for rigid experimental protocol. Why could the experimenters not be trusted to do their own statistics? It seems that the answer lies in human nature. East Malling, though funded mainly by the Government, was answerable to its members, to whom the annual report was an important source of information. If we had shown benefits of x%, with standard error of y%, then the growers expected to be able to trust this in commercial decisions. Human nature, unmoderated either by commercial accountability and social responsibility or by a team of policing statisticians, is bound to be selective in publishing results (see for example (Matthews, 1998)). The subconscious cannot really avoid designing experiments in a manner that is biased towards pet theories. This tendency of ours, the finding of patterns given only the slightest hint, and the attachment to them, persuading others to join our school, has probably been of great value to us in the past. It has enabled progress in agriculture. Every now and again, someone would notice what they thought was an improvement, and tell their friends. However, the whole purpose of organised research is to speed the process up and make it more reliable: one well-designed experiment should be able to replace many individual judgements, but statistical analysis depends on us keeping to new rules. If we do not keep our natural ability to "leap to conclusions" in check, we may invalidate the experiment. Hence the need for that police force.

In any event, this is the system I was presented with, and it preconditioned me to expect all branches of science to at least give the semblance of impartiality! Scientists were trained, I thought, to accept experimental evidence as it stood, without reading more into it than was there. Even the authoritarian system at East Malling could doubtless be bypassed with sufficient determination, but why should anyone want to? We were not expecting to be able to confirm mathematical theories, only find out what happened. My limited experience had shown scientists to be happy to discuss their experiments with anyone who came up with queries on them, especially if those queries were relevant or led to testable hypotheses. As to publications, we naturally expected all valid results to be accepted, and if any result had later been found to be in error a published explanation would be a matter of course.

Now quantum theory is rather different from agriculture! It is not an area where we have as yet had the opportunity to develop "common sense" and indeed, its proponents will tell you unashamedly that nobody understands it. One might hope to be able to investigate its claims experimentally and thus come nearer to understanding, only something seems to happen to prevent this. Experiments seem to tell us less than the mathematics! What has gone wrong?

Quantum theory was invented around the beginning of this century when a few experimental facts emerged that seemed to demand it. Light seemed sometimes to behave not as waves but as if it were composed of particles - "photons" - which could not be divided. At first, this was just a different way of describing things, but then, in the mid 1920s, it was incorporated into a new mathematical theory: quantum mechanics (QM).

And QM turned out to have some very odd properties. First and foremost to my mind (and indeed, the subject of much dispute at the time) would have been that it made the understanding of some of the basic behaviour of light - interference effects - very difficult, where before it had been no problem. But, once they had decided that this was a necessary sacrifice, the problem that the scientists focused on was "entanglement". The theory said that two particles that had once interacted became somehow bound together so that what you did to one of them could instantaneously affect the other. In the everyday world, this is impossible, and in most areas of science it is taken for granted that this kind of "magic" cannot happen, that the aim of science is to find rational explanations for things in terms of cause and effect. Real causes cannot leap across space instantaneously. (QM not only disregarded "causality" but also invented its own rules of probability, thus starting an era in which it was impossible for statisticians to work comfortably with fundamental physicists.)

It did not look feasible to test this entanglement property, as the quantities concerned were too small and too easily destroyed, but Einstein, together with colleagues Podolsky and Rosen, led a rebellion, publishing their famous "EPR" paper (Einstein et al, 1935). No theory that allowed "spooky action at a distance" (Born, 1971) could be accepted as truly fundamental.

Niels Bohr argued that perhaps the quantum world obeyed different logic, and such was his prestige that this has become the official view. The fact that he organised congresses in Copenhagen that nobody would have liked to have missed may also have played a part, not to mention his reputation as a formidable adversary (Heisenberg, 1971)!

This situation continued for a few decades, and QM consolidated its position, being taught to the next generation despite its "conceptual difficulties". Eventually a method of testing entanglement experimentally was found. John Bell, in the mid 1960s, discovered what has become known as the "Bell inequality". This was intended to distinguish between QM and "local realist" alternatives. It was based on the fact that QM predicted correlations in "coincidence rates" (see Supplements A and B) that cause a certain test statistic to be greater than would otherwise have been possible. In certain simple situations, Bell's original rather complicated test is equivalent to the observation that QM predicts a sine curve that has a minimum of zero and "visibility" ((max - min)/(max + min)) of 1.0, whilst the local realist alternative predicts one with minimum definitely greater than zero and visibility 0.5. Observe a visibility of over 0.71 and you have evidence of something unexplainable under ordinary logic (but see later!). The literature does not make it easy for the general reader to see that the issue is really this simple.

For a little more detail on all these matters, the reader is referred to the various supplements to this article. Suffice it to say that from the late 1960s onwards, there have been various attempts at doing "EPR experiments" (see Fig. 1), testing for infringement of Bell inequalities. The vast majority of these have seemed to back QM, but every single one has needed many assumptions (see Appendix) in order to be interpreted at all, and closer inspection shows that these assumptions are unlikely to be true unless QM is true! It is possible that the whole argument is circular, as "realists" have been trying to point out for many years now (Marshall et al, 1983).

Not only do the reported EPR experiments rely on many assumptions, but there is absolutely no attempt to help the reader understand their implications. Some of the assumptions allow them to use tests that are, in my view, completely invalid. The best known is concerned with the so-called "detection loophole" (see Appendix), and this is generally mentioned, though in rather a casual manner. But there is another, often of great numerical importance, that is made regularly and yet never mentioned at all. It is that of the independence of the emission events, and it is used to justify a data adjustment - the "subtraction of accidentals" (see Supplement B) - that, in almost all cases, forces their test statistic up and over its limit. The subtraction changes results that can be explained realistically into ones that require quantum magic. There is no mention in published papers of the assumptions behind the adjustment, and insufficient information given for the reader to work out what the unadjusted data was.

And how big is this adjustment? Well, I have searched through Alain Aspect's thesis (Aspect, 1983), found some data (not a lot) and summarised it:

Angle between polarisers	0.0°	22.5°	45.0°	67.5°	90.0°	One polariser absent	Both absent
Raw coincidence rate	96	87	63	38	28	126	248
"Accidental" rate	23	23	23	23	23	46	90
Adjusted rate	73	64	40	16	5	81	158

The actual formula that is needed for the relevant "Bell test" involves all columns, but one can judge the significance of the adjustment just by looking at the first five. They show that the raw coincidence rate decreases as angle increases, and this follows a sinusoidal curve as expected. It does not, however, decrease to zero, as QM predicts. Its visibility is 0.55, not significantly above the expected realist value. Subtract the "accidentals", however, and you get 0.87, a very considerable change!

It is my belief that publication of the above would have meant the rejection of QM 20 years ago. A very few others (notably Marshall, Santos and Selleri, 1983) have realised that the subtraction is unjustified, but it has fallen to me, a complete outsider, to unearth the full extent of the bias (Thompson, 1997, 1998a, 1998b).

In 1993, as I said, I stumbled into the EPR story. It was a different world, as indeed the participants realise! They have recently published articles on entanglement with titles such as "Quantum Theory: still crazy after all these years" (Greenberger and Zeilinger, 1995).

I have been shocked by the whole approach, both the design of experiments and the way in which they are reported. Is this really a reasonable way of testing QM as a model, and are they reporting results in such as way as to leave the reader with a true picture? The strategy employed appears to be to use whatever methods necessary to coax the apparatus into producing the high correlations in the "coincidence counts" that will violate Bell's inequality. (Admittedly, this is a considerable technological achievement.) They do not probe too deeply for "realist" explanations, as they believe that infringement of Bell's inequality shows that none are possible. And they give the reader only the most gentle of reminders that maybe there are doubts, that the interpretation presented depends on assumptions that depend on the validity of QM.

Faith in theory has been supplemented by faith in authority. For example, Clauser and Shimony, in an otherwise excellent survey (Clauser and Shimony, 1978), mention the so-called "detection loophole" (see Appendix and published papers such as my own "Chaotic Ball" paper (Thompson, 1996)) but dismiss it as most unlikely to apply. They express the opinion that

and their word has been accepted. Within weeks of reading Aspect's papers, I knew this statement was misleading, something that was true only if QM was true.

After a few months in the library checking my facts (and finding that I was not alone) I started to circulate a paper showing primarily that the detection loophole can never be ignored in two-channel experiments, as you cannot prove it is not there and, if present, it is almost certain to bias the results in favour of QM. I realised that it would take time to publish, so I wrote directly to some of the experimenters, trying to warn them that they had been misleading themselves: their experiments could not legitimately be reported as "excluding the possibility of a local causal explanation", for I could produce one. I explained the matter as simply as possible, for it seemed evident that there had been a breakdown of communications. The "detection loophole" was "well known", yet it seemed to me that it was not understood, or it would not be ignored so freely. (The material of this early paper is now covered in my "Chaotic Ball" paper and various others.)

Alain Aspect (whose EPR experiments have won him world acclaim) never replied, either to this first or to subsequent letters. Others listened, sometimes even praised my work. Alan Duncan, from Stirling, said he was sorry but his department had been closed down. When I wrote a second time he said (Duncan, 1994):

He and his associates all continued to publish with no change, reporting results as if the possibility of QM being wrong was almost out of the question.

Looking back now at Rarity's first message, I can see that he raised all the arguments that are still confronting my ideas: "Why are the assumptions you use ... any better than those of [QM]?". Whether I agreed with his assumptions or not was just my own opinion. He argued that he was justified in presenting results as "evidence in support of" QM, as this was not the same as claiming to have proved it incontrovertibly.

The "realists" I contacted were on the whole enthusiastic about my ideas. Franco Selleri responded to my first paper with "[It] is incredibly good: who are you?" (Selleri, 1995a). But perhaps from the practical point of view my early ideas were not in fact very important - their expected numerical consequences were small.

More recently, however, as mentioned above, I have [re-]discovered another "loophole", a small matter of a data adjustment, that has large numerical consequences in many experiments. In many EPR experiments the data is adjusted by "subtracting accidentals" before the Bell test is calculated. But are there really any accidentals to be subtracted?

I have made sure that people are aware of the problem through emails and the Los Alamos Quantum Physics archive. In October 1997 I sent a message to Rarity asking very specific questions regarding his 1994 paper with Tapster. The most important question was what was the accidental rate. (I had on a previous occasion asked another question that might be vital for understanding the actual physics of parametric down-conversion: "Had he ever done the experiment he intended that altered both settings at once?" I had no replies. If he had not altered both settings - and I suspect that nobody else these days has either - then it is quite possible there is an area of theory here that has never been tested. But that is another story.)

Partly as a result of circulating early editions of this paper, I am now corresponding again with Rarity and am hopeful that the discussion will be fruitful.

I have now met a few of the people concerned at conferences. They have shown very little interest in the experimental details. They prefer talking about the applications of entanglement in quantum computing, or devising yet more devious ways of persuading Nature to demonstrate quantum magic. It seems to me that the idea of gently posing questions so as to find out how Nature really works has been lost. Niels Bohr had declared that we could not hope to find this out, that how it "really works" was one of the meaningless questions that we should not ask. But why did they accept this so meekly? In these optical experiments, at least, the actual mechanism did not look too difficult to me - it was something I could hope to simulate, though I would have been hard put to it to come up with a neat formula.

To give concrete examples: in July 1997 news of the experiment in Geneva came out in the popular press (even before publication in the scientific journals!). This was supposed to show instantaneous influences acting over distances of about 10 k. When details were available in the Los Alamos archive (Tittel, 1997), I contacted Nicolas Gisin and Wolfgang Tittel, two of the workers concerned. They said that yes, they were interested in realist explanations. When I met Gisin at a conference in Hull later that year, though, he did not appear to have understood the importance of my objections to the paper, which included the apparently casual subtraction of accidentals (see Supplement B). He did say that he would investigate some of my points, and I am now hopeful that some progress will be made: he confirmed in March, 1998, that they are "working on further experiments" (Gisin, 1998). Hopefully these include various critical tests, such as varying settings on both sides at once and (as promised in 1997) investigations at lower emission rates.

Theory says that if you reduce the emission rate you should be able to reduce estimated "accidentals" faster than you reduce the counts you are interested in. There ought, therefore, to be no practical reason why the experiments should not be repeated at lower rates, so that accidentals are negligible, as they have been in at least one experiment. This is the obvious step that should be taken. The findings of a reduced-rate experiment would be of great interest, whether or not they conform to QM expectations.

At this same Hull conference I met (not for the first time) Lucien Hardy. He presented results from his "Ladder" experiment (see Boschi et al, 1997). The matter of the subtraction of accidentals was discussed (Hardy, 1997), and Hardy agreed that it was not justifiable and he had not done it. He had, however, relied on being able to ignore the "detection loophole". This I simply cannot understand! He is one of the first people to whom I showed my Chaotic Ball model, in early 1995 when the late Euan Squires invited me to Durham for the purpose. Hardy knew that this was a real weakness, but he did not seem to think that it mattered! He said he thought I would be able to see a realist explanation, as indeed I can. There is a glaring assumption that all "photons" go to the + or - channels, and none disappear, at least not until the detection stage, when a fixed proportion do. How, in the circumstances, can his statement in the abstract - "The experimental results violate locality (modulo, the efficiency loophole)" - be classed as "science"?

One of my concerns has been the difficulty of extracting supplementary information from individual experimenters. Perhaps their reluctance to release information can be explained by the fact that I am a private individual, with no PhD, but I have reason to think not. Profs Franco Selleri (Selleri, 1995b) and Emilio Santos (Santos, 1995) have had no more success. With experimenters such as Alain Aspect, one can understand that he would not have time to sift through all the mad-cap papers that must come his way. I am confident that my ideas are not in this category, having presented them at several conferences now and argued my case in the sci.physics newsgroup on the Internet. In other cases, such as that of Alan Duncan, the problem has been that the department has been closed down and the data effectively lost.

The major concern, though, is the evidence I have found of apparent lack of interest in how Nature really works, and this, I realise, is built into the very philosophical basis of quantum theory. Niels Bohr decreed that certain questions should not be asked. Others, such as Werner Heisenberg, said (Heisenberg, 1971):

He added, incidentally: "And that being the case, their number is unimportant." I fear that he was wrong: the number of people who challenge taboos is important, as the lone rebel will be crushed by the establishment.

In addition to problems with individuals, I have had first hand experience now with the editor and referees of Physical Review Letters (PRL). Foundations of Physics Letters, whose editor, Alwyn van der Merwe, is a friend of Selleri's and a supporter of realism, was happy to publish my Chaotic Ball paper, but it does not seem to have been seen by many. I have yet to see it cited, and the journal is not viewed by magazines such as New Scientist to be of sufficient repute for them to take into consideration. I felt that PRL was the correct place for my next ideas, as the majority of the papers I am concerned with are published there and because, if the referees never see my work, they are going to continue for ever, it seems, to publish with scarcely a question every paper submitted that "confirms" quantum entanglement.

Anyway, I submitted my "Timing and Other Artifacts" paper (the title did not at that stage include "accidentals") in April, 1997, and its progress has not been straightforward. At first they sent it in error to the Divisional Area Editor (incidentally exceedingly well qualified, having been involved with Aspect's experiment personally), because they thought it exceeded the required four pages. He read it, and proclaimed that "scientifically, it looks basically sound". Regarding my coverage of the detection loophole, he said (PRL, 1997a):

Of course, the main purpose of my "letter" was other matters - timing problems and "accidentals". He went on to condemn my ideas on the latter as ad hoc. In his opinion "Generally speaking inventing ad hoc models is not, it seems to me, how physics makes real progress." It did not occur to him that perhaps it was the QM model that was ad hoc! He concluded, after making a few reasonable points about my style, that "this text has too little chance to be eventually accepted and my advice to the author would not be to submit a new version."

I objected, on the grounds that my work had not even been seen by a single referee, saying with regard to my pet subject:

I requested them to send my explanatory letter with the paper, but they chose not to. As expected, the one referee who commented rejected it. He did not appear to have realised that it did more than re-open the detection loophole debate. He said, among other things (PRL, 1997b):

(This, I have reason to think, is wishful thinking. As I try and explain in Supplement B, there is no future in experiments using "photons", as high "detection efficiency" is not possible without unacceptable side-effects. I see little prospect either for other kinds of "particles". For example, a recent experiment (Hagley et al, 1997) claims to have produced entangled pairs of atoms, but these produce a "modulation depth" (visibility) of only 25%, not the 100% predicted. Further, the paper shows little sign that the authors understand the assumptions behind Bell tests: unless these are met, even 100% would not necessarily "violate locality".)

(It seems that John Bell made the same mistake as Clauser and Shimony, in thinking that because various imperfections made QM less likely to violate his inequality, they must also make the real coincidence rates less likely to violate the modified inequality used in practice!)

I waited till after the Hull conference - my meeting with Gisin - before submitting a revised version, including a reference to the Geneva experiment as well as my original ones, which were mainly from Aspect's work. (I had hoped at one point that the resubmission could be a joint effort with the Geneva team!)

They have, as expected, treated my resubmission as an appeal. I have now heard (June 2, 1998) that the appeal has failed. This had been preceded by a ridiculous farce in which the paper was sent to another referee, who totally misconstrued it. It seems that I had no right of reply. The Editor decided (PRL, 1998), on the basis of the new review and on his "own understanding", that the manuscript was "not appropriate for PRL". He added that:

I should dearly love to know what this is supposed to mean! What it amounts to is that no new idea is ever going to be accepted, because all referees and editors will react against them and the author never even gets a chance to try and persuade them to change their minds. Be that as it may, the Editor-in-Chief confirmed the rejection, on the basis that he considered that the correct procedures had been followed. My final letter (email) had not been passed to him in time, and would probably have made no difference.

PRL has been rejecting papers like mine for a long time. This is surely, as Bryan Wallace has explained so clearly (Wallace, 1993), not in keeping with the official policy of the American Physical Society of "unfettered communication at the Society's meetings or in its sponsored journals of all scientific ideas and knowledge that has not been classified." Emilio Santos, who co-authored in 1983 the important paper with Marshall and Santos that did manage to gain acceptance in Physics Letters A, has been trying ever since to get one into PRL - preferably an uncensored one, giving all the facts. Indeed, in 1985 he submitted one specifically on the subtraction of accidentals. This was later published in some conference proceedings, where it quietly gathers dust. As he told me two years ago, he has grown tired, wasted too much time in this battle. He encourages me, but for himself has turned mainly to other more constructive things. I have in front of me a copy of the rejection notice for one of his papers (Santos, 1997). It could have been mine! The very same Divisional Area Editor refers to the same belief of John Bell:

Twice in the notice he gives his own opinion, that it is a "matter of personal taste" if you choose to query assumptions and hence "escape" from the consequences of the observed inequality violations! Though, as he says "colleagues point out that, rigorously speaking, a violation has not been proved", at the end of the day he does not think the material sufficiently original and also decides that it is "more appropriate for private correspondence than publication". Why?

Another realist, Al Kracklauer, said his papers had been rejected "for reasons and with arguments that are a disgrace to the profession" (Kracklauer, 1998). They appear to be rejecting papers that endanger the accepted dogma even when, as in my case, they are viewed as scientifically sound. There is no discussion of such papers with referees, who thus remain ignorant of the strength of the opposition - or the importance of those "small loopholes".

This system has grave consequences for science. New theories are not being considered, the experiments that would force re-assessment of the old ones not being done. For some of my own ideas on suppressed ideas, see Supplement C.

As a statistician, I was taught that you should always present sufficient information so that readers could check the significance of the results for themselves. This means that all assumptions should be clearly stated, together with discussion of their importance and what attempts have been made to check their validity. In order to assess the EPR experiments, one also really needs to know what happened when parameters were set differently.

Now, in a subject such as particle physics, I fully understand that this is not feasible in a published paper, as there is simply too much data, but in these "entanglement" experiments there is relatively little. At the very least, supplementary information should be available on request, but some should be in the original report. It is clearly bad practice to publish adjusted data without making clear both the assumptions behind the adjustment and its size. In the case of a major adjustment, it would not go amiss to publish the effect on the final test statistic!

If the referees of the early reports had insisted on minimum standards, this would have helped, though in point of fact the faults in those days were obscure. The moral really is that there should never be any relaxation of standards. The doubts are known. They should be re-iterated in every report until they are resolved.

It seems reasonable to suppose that the reason for this poor standard is two-fold. There is the incomprehensibility of the subject, together with the lack of accountability to the world at large. There is beginning to be a degree of accountability now, in that computing firms and governments have become interested in possible applications, but in the early days there was no purpose other than academic interest. Hopefully this new accountability will help, but given the aura of mysticism surrounding the subject it may be hard to break the spell!

Thus there are improvements that could be made - improvements of access to the experimental facts, an obligation, perhaps, on the experimenter to answer legitimate queries - but incomprehensibility seems to be an insurmountable barrier to the conduct of science. What does not seem to have been realised is that it affects not only the accessibility of the subject to the general reader but also the referees and editors, who have no choice but to appeal to authority! One can, I believe, query the usefulness of the whole enterprise.

Aspect, A. (1983) Trois tests expérimentaux des inégalités de Bell par mesure de corrélation de polarisation de photons. PhD thesis No. 2674, Université de Paris-Sud, Centre D'Orsay.

Einstein, A., Podolsky, B. and Rosen, N. (1935) Can Quantum-Mechanical Description of Physical Reality be Considered Complete? Physical Review 47, 777.

Gisin, N. (1998) Private communication, March 31, 1998. [Corrected, 7:12:98, from 1997]

Greenberger, D. and Zeilinger, A. (1995) Quantum Theory: still crazy after all these years. Physics World, September, p 33.

Hardy, L. J. (1997) General discussion at the 6th UK Conference on Conceptual and Mathematical Foundations of Modern Physics, University of Hull, UK, September 8-12, 1997.

PRL (1997a) Communication from Divisional Area Editor, Physical Review Letters, May 23, 1997.

Santos, E. (1995) Private discussion, University of Cantabria, Santander, Spain, June 1995.

Thompson, C. H. (1996) The Chaotic Ball: An Intuitive Model for EPR Experiments. Foundations of Physics Letters 9, 357. Available at http://arXiv.org/abs/quant-ph/9611037

Thompson (1997) Timing, "accidentals" and other artifacts in EPR experiments. Submitted to Physical Review Letters, April 1997; re-submitted November 1997; rejected, June 1998. Available at http://arXiv.org/abs/quant-ph/9711044

Thompson (1998a) Behind the Scenes at the EPR Magic Show. In Open questions in relativistic physics. Franco Selleri (ed.). Apeiron, Montreal. (Proceedings of Athens conference, June 25-28, 1997, on "Relativistic Physics and some of its Applications"). pp 351-359.

Thompson, C H (1998b) EPR, Magic and the Nature of Light. In Causality and Locality in Modern Physics, G. Hunter, J-P. Vigier and S. Jeffers (eds.). Kluwer. pp 209-218.

Tittel, W., Brendel, J., Gisin, B., Herzog, T. and Gisin, N. (1997) Experimental demonstration of quantum-correlations over more than 10 kilometers. Physical Review A 57, 3229. Available at http://arXiv.org/abs/quant-ph/9707042