Friday, June 3, 2016

Functional electronic materials: I usually just don't get it

A hot area of research is that of functional electronic materials. The goal is to find new materials that can be used in new devices, ranging from solar cells to biosensors to catalysts to transistors.

Let me first concede some positive points.

Overall this is an important and exciting area of research which involves some interesting science and significant potential technological benefits.

There are some excellent people working in this challenging field and doing careful and valuable work.

History shows that going from a university lab to mass produced technology can take a long time. Who would have ever thought you could go from the first transistor to computer chips? Or from the first giant magnetoresistance materials to current computer memories?

Good science is hard.

However, I wonder if I am the only one who is underwhelmed by the average work in this field.

In a "typical" experiment someone might do something like the following. They get some large complicated organic molecules and they somehow get it to stick on the surface of some highly exotic material. The experiment is often done under extreme conditions such as low temperatures or ultrahigh vacuum. They then probe the system with some highly specialised probe such as STM (scanning tunnelling microscope) or a femtosecond laser. Maybe they make an actual device such as a photovoltaic cell. It may have terrible performance characteristics. They then produce some pretty coloured graphs. They might do some DFT (density functional theory) based calculations to produce some more pretty coloured graphs. The results are published in a baby Nature and claims are made about the technological promise. The authors then move on to a new system for their next paper...

First, the exotic factor worries me.

Is there any realistic hope of an economically competitive technology coming out of this, even on the time scale of 20-30 years?

The lack of reproducibility and control, the extreme conditions, the highly specialised and expensive materials raise concerns.
For solid state devices and solar cells it is going to be so hard to beat the well developed technologies, fabrication and cheap materials associated with silicon based devices.
We should certainly be trying but there is big difference between realistic optimism and scientific fantasy. This is my view on quantum computing with Majorana fermions.
For photovoltaics there has been a rigorous cost analysis of different competing materials, highlighting challenges of competing with plain old silicon. Note, those materials are nothing like the exotic ones I see in many studies.

Second, the lack of control and reproducibility worries me.
This relates more to the science than the technology.
There is great value in studying in detail some exotic material under extreme conditions if one can control the different variables in order to gain a good understanding of the fundamental science involved, e.g. of photo induced charge transfer between an organic molecule and a substrate. However, very rarely do I see this happening in these studies. There is just a bunch of data and some hand waving about what is going on....

I think all of this is compounded by the luxury journals and the pressures on people to justify funding and to claim dramatic economic benefits for their research.

But, to me much of what is going on isn't science and it isn't technology.

So, am I too harsh? too pessimistic? what do you think?


  1. As someone who works in this area (and will soon be leaving), I don't think you're being too harsh or pessimistic. In fact, I completely agree. Many scientists doing this work on functional materials don't seem to have an authentic desire to turn their science into technology. Too often the motivation for their work feels like lip service, without a serious considered analysis of the technological barriers.

    To be fair, I can sympathize with the view that labor specialization increases productivity, the idea being that having scientists worry about economic and technical hurdles might harm their scientific productivity with little benefit to show for it. Plus there is the argument that the future is unpredictable, so it's not worth worrying over apparent future hurdles when they might never actually occur. But I think those views are lazy cop outs.

    I wish scientists took technology development more seriously. Unfortunately, until grant agencies find a better way to identify and reward 'serious' research, we will be stuck with the 'less serious' research peddled by scientists who don't actually care about the path toward societal benefit.

    1. Thanks for the feedback.
      I agree that these views in the end seem to be lazy cop outs.

  2. If I were a betting person (and I am), I would bet on semiconductor transistors being the dominant computing technology for decades to come. Nothing else seems even close to touching it, especially when you consider that a successor technology needs to be at least an order of magnitude better to make up for the giant costs of switching and learning and ramping up a new technology. I hope I'm wrong, but I don't think I am.

  3. (like)

    From Dec. 1947 when Brattain demonstrated the 1st transistor prototype to the first devices rolling off a production line was not quite 4 years. And it was about 7 years from the demonstration of GMR in the late 80s to the first commercial devices. In all those cases - although there were obvious challenges - there was a clear path to commercialization from day zero.

    1. Peter,
      Thanks for the positive feedback and another helpful expert comment.

  4. Just to be fair, it probably took 50 years for low Tc superconductors to find a commercial application. And in this case we were really talking about "highly specialized, extreme conditions" research.

    1. Rolando,
      Thanks for the comment.
      I would argue superconductivity is a case study supporting my concerns.
      It was mostly studied for a long time, purely for scientific reasons, in careful well controlled studies. There was little hype. This is very different to the type of research I am criticising.
      There are now a few commercial applications. But, I wonder if they have really paid for all that basic science over 50 years. This highlights the problem of trying to use economic arguments to justify basic science.

  5. Hi Ross,
    I'm generally in agreement with the need to minimize technological hype. I wanted to make two comments about your post.

    1) Calling "typical experiments" such as you described "not science" is a bit harsh and leads us down a restrictive path where "curiosity-driven" research is disregarded. While I can see that most of the work you are talking about is "not technology" (and prpbably never will be) we need to have a very broad definition of what choices of topic count as science. Maybe I misunderstood what you meant by this?

    2) I want to also comment (as a UHV surface scientist) that UHV is not necessarily an extreme condition (though it is also not necessarily always totally realistic to make a connection to operating devices). For example, our best way to measure surface and interface electronic structure is photoemission spectroscopy. This simply doesn't work without UHV because the photoelectrons can't travel through air and physisorbed ambient residues (e.g. H2O and/or hydrocarbons) may attenuate photoelectrons that originate from an interface. So in many cases to get reproducible data that gives fundamental insights into interfaces in question absolutely requires this condition.

    Thanks for leading an interesting discussion as usual!

    1. Dan,
      Thanks for the thoughtful comment.

      1) I should have said the "typical experiment" is "poor science" rather than not "science". By definition anything published is "science" on some level.

      2) I should have been clearer. When it comes to science I am all for "extreme conditions" and highly specialised and expensive kit, such as UHV and photoemission. In fact, I worry about people who don't do this. My problem is with investigating effects and devices that only occur under "extreme conditions" and claiming a miracle is going to happen and this is going to be scaleable to some economically competitive technology.

  6. I think you are mistaking two complementary drives in functional materials research as being in conflict. Once a new material is synthesised, the (technological) drive to prove it in a working device, proceeds in parallel with the (scientific) drive to understand it fully. Of course, there is no such clean distinction between the two areas, the technological and scientific are inextricably linked.
    This is a fairly standard view of the technological world (i.e. see Ziman 'Public Knowledge' 1968), but they are messily and closely overlayed in functional materials.

    In terms of publications, there are a lot of them! A new material is just that, new. All of the characterisation needs to be done from scratch, building bridges of analogy and models from other similar systems. The short, but complete and certain, description of Si or GaAs in a textbook belies the decades of effort it took to understand them.

    I quite agree that there is a lot of miss-selling of studies into luxury journals, and totally spurious 'introductions' trying to spin the peer-reviewed hype-machine ever faster. It is most lamentable.

    I think a key problem is that peer review does not work well in this domain. A given paper typically has too many experimental techniques for the reviewers to have expert knowledge in them all. Due to the publication volume, there is enormous demand for peer review. Reading reviewer comments, you often wonder whether they bother to more than skim read.

    You are quite right that these technologies are extremely unlikely to replace the state of the art. In the area of Photovoltaics, Silicon has a 60 years engineering head start on anything developed today. The engineers have done some amazing things. It is openly understood that to displace Silicon & it's head start, a new technology must be 50% more efficient.

    1. Jarvist,
      Thanks for the helpful and thoughtful comment.
      I may not have expressed myself well.
      I don't think the scientific and technological drive are in conflict in functional materials.
      Perhaps my provocative phrase "it isn't science and it isn't technology" should be expanded to something like "technology hype is being used to justify poor science".
      I agree that luxury journals and weak poor review is compounding the problem.