Sunday, June 17, 2007

Grand challenges

As a condensed matter blogger, I am obligated to comment on the new report out from the National Research Council, titled "Condensed-Matter and Materials Physics: the Science of the World Around Us". This report is intended to list grand challenges for the discipline in the coming decade(s). I agree with the title, of course. As I wrote when I started this blog, while high energy physics and astrophysics grab much of the cachet and popular attention, it's very hard to dispute that condensed matter physics has had a much more direct impact on the daily lives of people living in developed societies. The transistor, the solid-state laser, and magnetic data storage are three prime examples of technologies that originated from condensed matter physics.

I haven't read the full report yet, but I had read the interim report and know several of the people who put this thing together. I think the substance is definitely there, though I do wonder if the summary suffers because of the decision to write the grand challenges in language for the consumption of the lay public. The challenges are:
  1. How do complex phenomena emerge from simple ingredients? Phrased this way this challenge sounds rather naive; the whole point of condensed matter physics is that rich phenomena can be emergent from systems with many (simply) interacting degrees of freedom. Still, this gets to the heart of the discipline and many outstanding questions. Why can one material system exhibit metallic behavior, superconductivity, and antiferromagnetic insulating order with only minor tweaks in composition? Figure that one out, and win a trip to Stockholm.
  2. How will the energy demands of future generations be met? This is clearly not the purview of condensed matter alone, but there is little doubt that our discipline can contribute here. Photovoltaic materials, supercapacitor and battery electrodes, catalytically active materials, light/strong composites, novel superconductors for transmission.... There are any number of reasons why investing in CMMP is an intelligent component of a sound energy policy.
  3. What is the physics of life? This is really a biophysics question, though certainly condensed matter physics is closely relevant. At the very least, the principles and methods of condensed matter physics are highly likely to play roles in unraveling some of the basic questions in living systems (e.g., How does the chemical energy released in the conversion of ATP to ADP actually get translated into mechanical motion in the protein motor that turns the flagellum of a bacterium?).
  4. What happens far from equilibrium and why? This is a good one. Equilibrium statistical mechanics and its quantum form are tremendously useful, but nonequilibrium problems are very important and there exists no general formulation for treating them. Heck, any electronic transport measurement is a nonequilibrium experiment, and beyond linear response theory life can get very complicated. Add in strong electronic correlations, and you are at the frontiers of some of the most interesting work (to me, anyway) going on right now.
  5. What new discoveries await us in the nanoworld? Wow - this one really sounds like a sixth-grade filmstrip title. I would've preferred something like, "What new physics will be found when we control materials on the nanoscale?" The ability to manipulate and engineer systems with precision approaching the atomic scale lets us examine systems (e.g., single quantum impurities; candidate qubits) that can reveal rich physics as well as possible applications to technology.
  6. How will the information technology revolution be extended? I don't know.... While this is certainly a useful goal of CMMP, and this point clearly encompasses exciting physics relevant in quantum computation as well as things like plasmonics and nanophotonics, I'm not sure that this is really a physics grand challenge per se - more of an engineering challenge.
So, what's missing? Well, I'm sure people will make suggestions in the comments, but here's one from me (though I'm sure that the NRC panelists consider this to be subsumed under point 1 above): Is there an efficient and exact general computational method for finding the ground state of the general strongly-interacting, strongly correlated many-electron problem? Basically I want something better than DFT that handles strong correlations. That would definitely be a grand challenge, though it's way too detailed ("physicsy") to fit the structure used in the above list.

The report also emphasizes the fact that research funding in the physical sciences, particularly CMMP, is lagging that in other nations these days, and that this is probably not to our competitive advantage. The demise of long-term industrial R&D in the US has not helped matters. None of this is news, really, but one major purpose of reports like this one is to send a message to Congress. Hence the use of non-physicsy language for the challenges, I'm sure.


Anonymous said...

Ab initio calculations based on DFT can be broadly used to analyze electronic band structures and phonon dispersions of materials now.However,whether such a calculation method can give us any chance to understand the fundamental properties(metallic behavior, superconductivity...) of the matetials eventually,I would doubt. Can the nature of complex phenomena be only explained by performing a large amounts of calculation or just so simple as the mass energy conversion formula? These are so interesting in fact.

NONE said...

the advantage of condensed matter over something like high energy physics is that it is so vast and spans so many different directions. But it is also one of key disadvantages - it has no clear face, no clear single goal and often people in one field don't have a single idea about what goes on in even somewhat related sub-fields.

The lists like these are a good idea. High energy folks can capture a lot of imagination with "How did universe start" and "multidimensional/stringy" stuff.

Condensed matter, nanoscience and biophysics have this huge advantage over any other field of physics, in that almost any discovery eventually trickles down to better electronic materials, better materials, or even life-saving medical devices and medicine. But very few common folks realize it.

Looming energy crisis is a good example, but to a lot of people it seems a matter of engineering solutions, rather than basic physics.

On the other hand, making a point about sweat-wicking coolmax fabric, stain-resistant pants and carbon fiber bikes seems to dilute the point to mundane claims. I get the same reaction when someone demonstrates a cool fundamental experiment on spintronics or some other amazing stuff, and then follows it up with "imagine a computer that boots up instantly". What? It may be nice to have a computer that boots up instantly, but it's not even on top 100 list of things I'd like to see done first. Same goes for levitating trains.

Even with better magnetic storage devices or faster computers - you cannot easily motivate a lot of people with this stuff, especially older generation.

It's hard to come up with "top 10" lists, but I would definitely mention self-assembly (both chemical and biological), creating new nanosized devices and materials with new properties - and on more fundamental level talk about phases and phase transitions - this gets across disciplines, from people working on polymers, alloys and glasses to strongly correlated systems to quantum criticality.

Maybe a good way to engage people's imagination is to keep bringing up "quantum physics". A lot of novel condensed matter physics is closely tied to quantum mechanics anyways.

Anonymous said...

Here's a grand challenge for you: how can more ordinary physics geeks like us end up making $900,000 per year?

Anonymous said...

Why can one material system exhibit metallic behavior, superconductivity, and antiferromagnetic insulating order with only minor tweaks in composition? Figure that one out, and win a trip to Stockholm.

Uh, the system has a Hamiltonian with several terms of opposite sign whose coefficients are similar? Do I win?

To me the most important Grand Challenge has to do with spanning many orders of magnitude both experimentally and theoretically. Experimentally, we would like to be able to pick-and-place and make contacts to nanometer-scale objects that we have newly found ways to fabricate. Theoretically, we would like to be able to calculate results using "atomistic methods" whose utility spans many orders of magnitude both in time and size. We are far away from being able to do either of these.

The most exciting possibility in CMP right now is that the new methods of atomic physics (trapping and cooling) will be used to make solids. But this speculation is too far distant to be a "Grand Challenge."

NONE said...

Alison, I don't see how AMO methods will help us make solids per se, but creating "toy models" of solids with tunable potentials where atoms replace electrons may help us understand superconductivity, quantum criticality etc.

On the other hand, I am always pessimistic about "toy model" systems - often they tell us more about "toy models" than the systems they are supposed to model.