Tobias J. Osborne's research notes

“It’s better to pursue one bad idea to its logical conclusion than it is to start and not finish ten good ones,” Michael said.

I was sitting in Michael Nielsen’s office at The University of Queensland: it was early 2002 — a steamy Brisbane summer afternoon — and the air conditioner struggled to cool the room. I had just finished with a long despairing complaint about the disappointing lack of progress I’d been making on my PhD when he issued me with his advice. (I was beginning the third and final year of my PhD.)

I’d had an interesting ride so far: I began my PhD in the year 2000 in applied mathematics studying free-surface problems in fluid mechanics. Fluid dynamics is a challenging and mature research area and requires a lot of effort to get up to speed. Unfortunately, I am very lazy and it had taken me a very long time. Also, I quickly found out that I just wasn’t that interested in the motion of fluids (although, one of the papers I’m proudest of emerged from this period). I quickly became unmotivated and I had begun to distract myself by reading quantum field theory textbooks to procrastinate instead of finding that sneaky bug in my code…

Then everything changed. I think it was in late 2001 when Michael arrived at UQ and gave a series of talks on quantum computers. I was hooked and I immediately dropped everything and started working with Michael “in my free time” on quantum entanglement and condensed matter systems.

I once heard a definition of a golden age in science as a period when mediocre scientists could make great contributions. (I forget when and where I heard this and a cursory google search didn’t turn up anything.) The early 2000s were definitely a golden age for quantum information theory and I had the greatest luck to work with one of its architects. In practically no time whatsoever (in comparison with applied mathematics) we’d written a couple of papers on entanglement in quantum phase transitions.

It had been just so effortless. Now I’d finally found a research field that appealed to me: with an absolute minimum of effort one could write a paper that’d be read by more than two people. Wow! (Alas, this is no longer true…)

All this went to my head. I figured that if one could just stick two buzzwords together (entanglement and quantum phase transitions) and get a paper then why not do it again? I was skimming through texts on partial differential equations, algebraic topology, and stochastic calculus and seeing connections EVERYWHERE! I was discovering “deep” connections between entanglement and homotopy theory before breathlessly diving into an idea for a quantum algorithm to solve PDEs. I would spiral into hypnotic trances, staring distractedly into space while one amazing idea after the other flowed through mind. (This is the closest I ever got to the flow state so beloved of hackers.)

But at the same time frustration, edged with desperation, was growing. I was having all these amazing ideas but, somehow, when I started writing one of them down it started to seem just sooooo boring and I promptly had a better one. My hard drive filled with unfinished papers. I had less than a year until my money was gone and no new papers!

I was lost in the dark playground:

I then went to Michael and told him of my frustration. And it was this complaint that had prompted him to give me his advice. All at once, it was clear to me what I’d been doing wrong. So I threw my energies into a problem Micheal suggested might be interesting: proving the general Coffman-Kundu-Wootters inequality. This was a hugely satisfying time; although I didn’t end up proving the inequality during my PhD I managed to, mostly by myself, work out a generalisation of a formula for a mixed-state entanglement measure that I was convinced would be essential for a proof (this sort of thing was a big deal in those days, I guess not anymore). Every day I was tempted by new and more interesting ideas, but I now knew them for the temptation of procrastination that they were.

Michael’s advice has stuck with me ever since and has become one of my most cherished principles. These days I’m often heard giving the same advice to people suffering from the same temptation of the “better idea”.

Now “focus on one idea” is all very well, but which idea should you focus on? (You will have no doubt noticed that I was rather lucky Michael had the perspective to suggest what was actually a rather good one.) What do we do if we have lots and lots of good ideas, each one of them clamoring for attention? How do we break the symmetry? How can we best choose just one or two ideas to focus on? How should you split your most precious resource, your time, while balancing the riskiness of an idea against its potential return?

Ultimately I do not have an answer, but I do have a decision tool that can help you to make your mind up. The idea is to regard research ideas as investments, i.e. assets, and to evaluate their potential return and their risk. In this language we have reduced the problem to that of investing some capital, your time, amongst several assets. This is an old problem in portfolio management and there is a very nice tool to help you work out the best strategy: the risk-return plane. The idea is pretty simple. In the case of portfolio management you have some capital you want to split amongst a portfolio of assets which are characterised by two numbers, their average return and their risk, i.e., the standard deviation of their return. Take a two-dimensional plane and label the x-axis with the word “risk” and the y-axis with the word “return”. Each asset is plotted as a point on the risk-return plane:

Now something should be obvious: you should never invest in an asset with the same return but higher risk, nor should you ever invest in an asset with the same risk but lower return. This picks out a thin set of assets living on the “boundary” of (basically the convex hull of) all the assets, called the efficient frontier. You should only ever invest in assets on the efficient frontier.

For a joke I once suggested using the risk-return plane to work out what research idea you should work on. However, it quickly became apparent that some people found it a useful tool. Here’s one way to do things: first write down all your research ideas. Then, after some honest reflection on what you think the most likely outcome of a successful result from the project would be, associate a “return” to each idea. (Just ask yourself: if everything worked out how happy would you be? How much would the completed idea contribute to science? Insert your own metric here.) The way I did this was, somewhat flippantly, to label each idea with a journal that I thought would accept the idea. Thus I created a list:

1. Journal of publish anything
2. Physical Review
3. New Journal of Physics
4. Physical Review Letters
5. Science, Nature, Annals of Mathematics, etc.

It is totally silly but it has just sort of stuck since then. Next, you have to assess the risk of each project. I think a reasonable way to do this is to quantify each research idea according to what you think is required to solve it, e.g., according to

1. Trivial calculation
2. Longer calculation
3. Some missing steps
4. Needs a new technique
5. I don’t know anything of what’s required

For an example let’s just take a look at my top twelve research ideas for the last year:

1. Chern-Weil theory applied to classification of quantum phases via quasi-adiabatic continuation.
2. Reaction kinetics for ultracold chemistry.
3. Continuous limits for quantum lattice systems.
4. Tensor networks for lattice gauge theory.
5. The scattering problem for local excitations in lattice systems.
6. Prove the quantum PCP conjecture.
7. Improve the gap for adiabatic quantum computation.
8. K-theory for the MREGS problem.
9. Classify topological order in higher dimensions.
10. A compact formula for the distillable entanglement of two qubits.
11. Calculate the entanglement of the 2-rotor rotor model.
12. Prove the quantum version of the KKL inequality.

Here’s my risk-return plane:

Looking at the results it quickly became apparent that I shouldn’t really invest my energy in a formula for the 2-qubit distillable entanglement (shame! I would be interested in solving that one, but I just can’t see how it would be useful to anyone, including to myself!!!) Also, I should steer clear of the quantum KKL inequality, the quantum PCP conjecture, and K-theory for MREGS.

Note that all of this is completely and utterly subjective! You might well argue that a proof of the quantum PCP conjecture would be a tremendously impactful result on par with the quantisation of quantum gravity. But my purely subjective assessment at the time was that it would not be of the same level of impact (for me) as, say, classifying topological order in all dimensions.

Thus, out of the top 12 ideas floating around my head only 5 remained. This is still way too many! To winnow down the list it is helpful to use an investment strategy employed in portfolio management which is, roughly speaking, to invest a more of your capital in less risky assets than riskier assets (i.e., don’t put all your eggs in one risky basket!!!!) Thus I dropped the riskiest idea and I also dropped the most trivial one as not really giving much personal reward. I was left with three ideas. This was just about enough for me, and I spent most of my available energies on those.

I find it helpful to keep this risk return plane around and to periodically update it as I get more information, or when I get new ideas. Looking at it today I figure I’ll move the adiabatic gap, Chern-Weil theory, and the scattering problem ideas up a bit. Maybe I’ll work on them soon…