Are we scientists or quantum engineers?

I have taught my students about emergent physics, and that every level is fundamental. Condensed matter physics is just as fundamental as particle physics. This was true when the giants like Landau and Anderson opened up this field years ago.

However, so many years have passed, the basic interactions and effective interactions are known, although the problem or material could be complicated. They just manifest the same basic physics once and once again.

What we are doing is when the new materials are created, we try to solve the problem and figure out how these basic physical ingredients work together in a delicate way. We have encountered many surprises, and after we figure them out, it is more or less the same physics, once, twice, and again.

For example, after we figure out the iron-based superconductors, its mechanism is very similar to that of cuprates, while its correlation is similar to that of the manganites. We can have more classes of materials, such as the yet to be solved heavy fermion superconductors. But the truth is that our main endeavor is to understand how these basic rules work. Since it is a many body problem, one cannot exactly solve. As a result, no one can claim we made it, even though we already understand the problem in a qualitative way. When we talk about cuprate superconductivity, there are always details and subtleness, such as the CDW competing order. But these are just noises, since we already understand it. When someone asks me what is the fundamental problem left in cuprate and what will be the smoking gun experiment to answer that? My answer is No and No.

Then this makes me to think that we are more like dealing a quantum complexity, and like a back-tracking engineer of the quantum world. Since there are so many materials, and we have just studied the tip of the iceberg. Fortunately, there will be more and more “surprises”, and we will not lose our job as an engineer. We can even design new interfaces and materials, like the engineers in the semiconductor business. As quantum engineers, we are very successful. But we might have lost our job as a scientist, not even noticed!

It is likely at this stage of the condensed matter physics research, the fundamental side of it, which needs to be thought through. We need to find or create brand new phases of matter or create new concepts, or go to biological (more complex) level of condensed matter, or ................... Well, think hard! Otherwise we are just repeating ourselves, which is like a kid repeatedly working on exercises. We had fun solving puzzles, but they are alike. I am a bit shocked and frustrated about this findings.

The "comforting" news is the particle physicists of today are no better than us, if they just keep colliding. Maybe the true frontier of fundamental physics is on dark matter, dark energy and string theory (a doomed failure in my personal view, but honorable trial though), but how far they can go is questionable, which maybe fundamentally limited by our space and human capability.

Is it possible that physics will be fully matured and there will be nothing left to do after another 100 years ? The pessimistic answer is Yes.

Over 100 years ago, Sir Kelvin had the same frustration as mine... So on the positive side, we will have the next revolution and the next Einstein coming.

Notes added on Oct.12, 2014: This year’s Nobel physics prize is awarded to the blue LED, see, engineers ! In that sense, they fully deserve it. No one should moan about it and complain there is not enough physics!

What if you succeed ?!



为了做成一件事情,我们一定会付出很多精力、时间、物质等等,这就是所谓的opportunity cost.你做一件事,必然放弃了许许多多的其它选择。在科研中也是如是。比如利用ARPES测量一个新样品,当然可以轻松发一篇论文。However, just look for new samples and publish one more paper is just not going to work, you will lose your interest and get bored eventually, and it's simply pretty low level easy meal. 我们需要把有限的时间和资源用于研究重要的问题。

怎么做呢?Ask a clean and sharp question!!

需要思考解决关键的问题(就是外行也会有兴趣的问题,是你自己几句话就能说出重要性的问题,很啰嗦地描述往往说明问题本身比较细节)好的问题往往具有Elegance, Generality,直接和当前领域仍然存在的fundamental issues 相关. 比如



    我们已具有很好的条件,有了好的平台,有条件去回答重要的问题。那么就更需要多思考,多到室外去。江湾校园空旷、开阔、优美。那时自然会:心如浮云云卷云舒,意如流水任意东西。好的创新想法就来了。当然这也不是要去不着边际的空想,往往这个过程是passion driven, 也就是当你真的想知道一个具体问题是what's really going on的时候,会深入思考下去,想去把该问题中基本的东西都搞清楚,想达到定性完全理解的程度。这时候往往重要的问题会pop out in your mind.

    • 当科研做到一定火候,你终会明白:TASTE is EVERYTHING!
    • 所以在同学们的科研学习中,应一开始就要提醒自己要建立品味!当然,这要一步步来,Study more, read more, and most importantly, think more!