One of the exciting things about condensed matter physics is that we are continually discovering exotic new phenomena. Many are unanticipated and understanding them presents a rich intellectual challenge. That is the nature of emergence.
Due to chemical complexity and the richness of quantum many-body physics it seems the frontier is endless.
Superfluid 3He, heavy fermions, sliding charge density waves, weak localisation, giant magnetoresistance, organic superconductors, quantum Hall effects, quantum point contacts, cuprate superconductors, non-Fermi liquids, buckyball superconductors, Luttinger liquids, colossal magnetoresistance, spin liquids, pseudogap, composite fermions, strontium ruthenate, topological order, quantum dots, sodium cobaltates, solid state quantum computing, fluctuating gauge fields, spinons, topological insulators, iron pnictide superconductors, ultracold atomic gases, quantum criticality, spin-charge separation, anomalous Hall effect, Majorana fermions, ....
Exotica are a blessing. They keep us excited and busy. The field will never die out or get boring.
However, I believe that exotica can also be a curse to the field.
Why?
1. The field can be too driven by fashions.
Every few years a new system is discovered which grabs attention. Lots of people work on it grabbing the "low-lying fruit" before jumping on the next band-wagon. Painstaking long term studies needed for a deep understanding are neglected.
The current fixation with citation metrics accentuates this problem. People want to publish quickly in a field in which lots of other people are working.
Twenty years ago Pantelides made this criticism.
2. Problems that are old, difficult and important get neglected: water, ice, metallic ferromagnetism, glasses, high-Tc superconductors, polarons, correlated two-dimensional electron gases, bad metals, fracture, enhanced thermoelectricity, multi-scale modelling, magnetite, high quality materials synthesis....
3. One can end up focusing on some exotic system or very specific material that is so finely tuned or rare or fragile or difficult to fabricate that it is not representative of any significant class of materials or phenomena.
4. One ends up with exotic theories in desperate search for a experiment, rather than constructing realistic theories that explain the many existing materials or phenomena waiting to be explained.
5. Students can get too narrow a training and perspective on the field.
6. We end up focusing too much on materials and devices that are so exotic and expensive to make that they will never be of any commercial use. This will ultimately diminish funding for the field.
A real challenge and struggle for me is for each new discovery to try and critically assess whether it is going to be important in the long term. I think the community could benefit from more critical reflection and self control.
What do you think?
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I welcome discussion on this point. I don't think it is as sensitive or as important a topic as the author order on papers. With rega...
I'll take exotica any day over the alternative. I think the problem is both citation metrics as well as the fickleness of funding in condensed matter in an overall sense. It is hard to get funding - or attention - to tackle a hard problem that is 'old, difficult and important'.
ReplyDeleteI will also take exotica over boring anyway. But I don't think the choice is so black and white.
DeleteI think the community needs to take responsibility for the funding decisions. If we unite around priorities (the balance of old vs. new) then the funding will follow. Astrophysics and Particle Physics communities unite and set priorities and the money is allocated accordingly.
I have very mixed feelings about this. I completely agree with you on 1. and 4. However, it seems to me that there are often good reasons for abandoning an "old, difficult" problem. For instance: 1. Often the physics is qualitatively understood and the details appear non-universal. One usually wants to start from well-defined anomalous features and then construct toy models that reproduce them. 2. Sometimes (as with the FQHE or the pseudogap) the problem has been reduced to deciding which one (or more) of several "good" candidate ground states is in fact realized in nature. This sort of question is great if you're an experimentalist; if not, not, as conceptually nothing depends on the answer. 3. Sometimes the community is legitimately stuck on something (e.g., turbulence), so that any real progress seems to demand a major breakthrough. _Some_ people should work on problems like this, but the optimal number is clearly not large, and it should be kept in mind that the breakthrough is as likely as not to come from somewhere else altogether (cf. critical phenomena). 4. Sometimes solving a problem demands extensive development of ad hoc methods that don't seem widely applicable. At some level I think it'd be a good thing if the field escaped from the dominant band-structure and field-theoretic paradigms, but there is also a sense (captured in Anderson's book, say) in which these paradigms unify the field, so working outside them isolates one's research from that of others, makes it harder to fit into a big picture, etc.
ReplyDeleteThanks for this comment. I largely agree.
DeletePerhaps I just disagree about the balance.
I think we would be better off if half the people worked on a new problem and worked on it for twice as long.
I agree that there are some very hard old problems that we should dedicate limited resources too. But I also think with many recent conceptual, computational, and experimental advances (e.g. ARPES and STM) more people working on some of these old important problems could make some progress.
The core of the problem is that the extraordinary richness of the fractional quantum Hall effect has permanently altered the tastes and values of a certain fraction of the theoretical community.
ReplyDeleteFractionalisation and exotic statistics are remarkable, but thirty years on these ideas have had no definitive second act. If one looks back at the early history of High Tc, it's clear that many of the early theories (e.g. anyon superconductivity!) were built in the image of the FQHE.
The usual defence is that one is exploring a space of possibilities that may be realised in Nature, but this must be underpinned by rigour (as in mathematics) or experiment. To proceed with neither is hubris. Moreover, it leads to an erosion of the problem solving base of theoretical physics, which has always been the most fruitful source of new concepts.
Of course, high energy physics is in the same boat.
Austen,
DeleteThanks for the comment.
I think your observation about the influence of the FQHE is an important insight.