In praise of failure

“In 2004, Kim and Chan (KC) carried out torsional oscillator (TO) measurements of solid helium confined in porous Vycor glass and found an abrupt drop in the resonant period below 200 mK. The period drop was interpreted as probable experimental evidence of nonclassical rotational inertia (NCRI). This experiment sparked considerable activities in the studies of superfluidity in solid helium”.

Thus begins the abstract of a manuscript recently uploaded to ArXiv. One of its authors is Moses H. W. Chan, namely the senior author of the original article that “sparked considerable activities in the studies of superfluidity in solid helium”.
The abstract goes on to state that “More recent ultrasound and TO studies, however, found evidence that shear modulus stiffening is responsible for at least a fraction of the period drop found in bulk solid helium samples [...] We report here the results of a new helium in Vycor experiment with a design that is completely free from any bulk solid shear modulus stiffening effect. We found no measureable period drop that can be attributed to NCRI” [0].
So, basically here we have a report of the same experiment carried out eight years ago, which started the whole business of a possible supersolid phase of helium, performed in slightly different conditions, apparently yielding diametrically opposite results, pointing to the non-existence of such a phase.

Uh-oh…

Readers of my blog know that I have from the beginning been rather skeptical about the interpretation of Kim and Chan’s (KC) original findings in terms of supersolid behaviour of helium (see this post).
I am therefore scarcely surprised by this recent finding which I expect to end the whole discussion. It appears now very likely that the anomaly observed at low temperature (by other groups as well, following the first KC experiment), which has intrigued and kept busy for the past eight years a number of theorists and experimentalists, is not connected to the transition of the helium crystal to a new, yet unobserved phase of matter (the “supersolid”), but rather is a spurious effect due to the unexpected and unpredicted stiffening of the crystal itself [1], which in turn affects the quantity that is measured in the experiment, namely the moment of inertia of a solid helium sample.

I could be wrong, but I think that this is the conclusion to which the community is converging. Let us assume for the sake of argument that this is indeed what eventually ends up happening. If that were the case, should this be considered a “fiasco” ? A scientific “failure” ?
Did KC make a “mistake”, when they reported the (probable) observation of a supersolid phase of helium in the first place ? Did they act in haste, based on data that were inconclusive or insufficient ? Is this occurrence in the same category as the cold fusion embarrassment of the late 80s, for example ?
If that initial claim had been confirmed, this would have inarguably been a discovery worthy of a physics Nobel prize. Should instead one regard the past eight years, the time and money that went into this research, as a “waste” ?
The above are questions that I am often asked by friends, family, and in general people who are themselves not scientists; while I try to answer to the best of my knowledge, I consistently find that when it comes to assessing what constitutes a “failure”, a “fiasco”, or an “embarrassment”, in the context of scientific research, many hold views reflecting overall lack of clarity on how science works, and what the long term objectives of a scientist are. This in turn helps explain how misconceptions and downright falsehood about science (for instance, how it would allegedly be plagued by confirmation bias) can be spread and perpetuated so easily.

Mistakes ? Which mistakes ?

Let us begin by outlining the major differences between the report of Helium supersolidity by KC, and claims of major scientific breakthroughs that turned out to be bogus. The fundamental problem with bogus claims, such as that of room temperature muon-catalyzed fusion made in 1989 by Pons and Fleischmann, is generally that the key findings, the crucial piece of experimental evidence, cannot be independently reproduced.
This has never been the issue with “Supersolid” Helium, in that the key experimental finding by KC, namely the occurrence of an anomalous, non-classical moment of inertia at low temperature, has been independently observed by several groups. To be sure, quantitative differences in the magnitude of the effect, the temperature at which it occurs, as well as unexplained dependences on the geometry of the apparatus and other puzzling features were reported by different groups — but that something was indeed happening was quickly, and overwhelmingly accepted by the community. That lent at least some credibility to KC’s claim.

When Pons and Fleischmann first made their announcement, the reaction on the part of the community was of shock, and disbelief. How could what they were claiming be possible ? Why had no one observed anything like that before ? How could something like nuclear fusion, believed to require temperatures only achieved in the core of the Sun, occur on a table top at room temperature ?
Was the interpretation initially proposed by KC of their findings, namely that solid helium might be turning superfluid, equally far-fetched, dubious or outlandish ? Were there simpler, more obvious explanations ? Not really. The notion that solid helium could turn superfluid had been entertained for decades. Indeed, a superfluid transition of the crystal is the simplest, most plausible scenario accounting for the sudden drop of the period of the torsional oscillator reported by KC. This is why it was taken seriously by many and worthy of further investigation by many more. In fact, I am quite sure that some remain convinced of the correctness of that scenario even now, after the above-mentioned preprint has come out.
If it turns out that indeed the stiffening of the crystal is what causes the anomaly observed at low temperature, rather than a partial superfluid response of the bulk sample, this would be a remarkably subtle, unexpected, unpredictable scenario — it is no accident that it would have taken eight years of intense experimentation and theoretical work in order to arrive at this conclusion.
Thus, in no case would KC have anything to feel embarrassed about, and their reputation will be untarnished — in some respects even enhanced.
The fact that one of them (Chan) has now come to the conclusion, after repeating the same initial experiment, that upon removing the crystal stiffening effect no low temperature anomaly can be seen, does not mean that the initial experiment was wrong — simply that the physical system is more complicated than one thought, or knew.

It’s all good

The fact of the matter is, this is how science works. One sets out to discover something, to explore and find something novel — and for the most part one does not succeed.
It is like treasure hunting. If one were 100% that something would be found, then it would not be called “research” (maybe “nanotechnology”… kidding !). Those who spend a significant portion of their lives trying to gain insight into a particular, yet unexplained phenomenon, make a valuable contribution to scientific progress and by extension to society, regardless of whatever it is that motivates them in the first place. These individuals are to be commended, even if in the end the goal that they initially set out for themselves remains elusive. Of course, in those rare instances in which a discovery is made, the payoff is immense; but even if no breakthrough is achieved, incremental, valuable new knowledge is generated, from which many others benefit.
Exploring novel phases of matter is a worthwhile scientific endeavour. Belittling the effort of those who undertake this kind of “risky” investigation, requiring as it does a long term commitment with no promise of final success, calling it a “waste” if no discovery is made in the end, much less ridiculing them, is doing a disservice to science and to human progress.

Notes

[0] Without going into details, Non-Classical Rotational Inertia (NCRI) is believed to be one of the most important hallmarks of Supersolidity.

[1] First observed at University of Alberta — not to brag or anything.

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6 Responses to “In praise of failure”

  1. Schlupp Says:

    I raise my ( largely nonexistent) hat to Chan. The inability to even consider changing one’s mind upon further evidence is in my opinion one of the biggest issues in high-Tc superconductivity.

  2. James Says:

    I [2] think Moses should be applauded for his willingness to go with the evidence.

    [2] The one to have made the stiffening observation – not to brag or anything ;)

  3. Lior Says:

    Thanks for the interesting story. It now made the latest Physicshttp://physics.aps.org/articles/v5/111

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