## My biggest (scientific) mistake (so far)

Waterloo, Canada. It was early 2004. It was cold.

I was cocky and full of the naive self-satisfied arrogance of a young physicist convinced of his powers. Filled with dreams of glory I made my way onto the airport shuttle to return home to Bristol. I was returning from QIP 2004.

It had been an exciting week.

I had just enjoyed a string of inspiring talks on a variety of fascinating topics across the full spectrum of quantum information theory. There was a palpable buzz in the air: quantum computers were coming! We were all positioning ourselves for the game of the millennium. As far as I was concerned, the only game in town was quantum algorithms, and fame and fortune would be awarded to those lucky few who could find a quantum algorithm yielding the holy grail of the exponential speedup.

My mind was a ferment of ideas; I’d just seen a fabulous talk by Oded Regev on quantum complexity, cryptography, and lattice point problems. I was convinced this was where quantum computers would exhibit a speedup. Oded had presented a truly lovely result showing that if you could prepare a very special kind of quantum state, a superposition of gaussians centred on the points of an (unknown) lattice in $\mathbb{R}^n$, you could decide the shortest/closest vector in a lattice problem in polynomial time (in n). Wow! That would be a demonstrable exponential speedup over the best classical algorithm! What’s more, I had an “in”: I knew some quantum optics and I could see that the natural language to discuss this problem would be that of continuous quantum variables. It would be so simple: I’d find a quantum-optical circuit that naturally prepared this state, discretise it, and solve the problem. Along the way I’d introduce a totally new paradigm of continuous quantum algorithms!!

Thus began the worst year of my life.

The year 2003 had already been very difficult for me for a variety of reasons. I’d started my first two-year postdoc in 2003 and it had taken me a long long time to settle down. I had found moving countries to be so much more difficult than I imagined. This meant that my productivity had basically fallen to zero for a year (everything you see from me on the arXiv during this period, with one exception, are papers that had been developed during my PhD.) So there I was, at the beginning of 2004, resolved to write the big one: a paper that would one day become as famous as Shor’s algorithm. I figured they’d call it Osborne’s lattice algorithm. Of course, when giving a talk, I already knew I’d always modestly refer to it as “the quantum lattice point algorithm”. Awesome.

I worked tirelessly. I spent hours and hours in a row, day after day, completely focussed on this one problem. I dreamt about it.

To solve it, I deployed the full arsenal of my quantum optical tricks to annihilate this problem. And at the beginning it looked really promising. I had the basic idea clear (use a phase kickback trick and continuous-variable teleportation to create the superposition, then correct the phases afterward).

Slowly, but surely, a disturbing pattern emerged. I’d begin really inspired, convinced that I was finally on the right track. Then I’d carefully write up my latest version of the algorithm. Then I’d find the mistake, which always turned out to be that I’d simply misunderstood some aspect of the problem. Then I was right back at square one. There was simply nothing to be recovered because every damn time the mistake was that I’d misunderstood the problem and tried to solve the wrong thing. This ecstasy/agony cycle took, variously, one week to one month each time.

This lasted over 6 months. I was becoming exhausted. I didn’t work on anything else. My personal life was in a shambles.

But I persisted. Surely this time I would do it. Giving up was for losers.

Instead of giving up I doubled down and enlisted the help of Nick Jones, a PhD student at Bristol at the time. I am filled with admiration for Nick who, with limitless patience, worked with me at the board hour after hour on this wretched problem. But it was, alas, to no avail.

Finally, humiliated and defeated, I gave up. I think it was October 2004.

This was the worst feeling: nearly a whole year gone with absolutely nothing to show for it. Worse, I was wracked with guilt, feeling I’d totally wasted Nick’s time.

Things soon got better. By a miracle my postdoc had been extended for a while, so at least I wasn’t on the job market straight away. Secondly, at the end of 2004 I went to a truly inspiring conference at the Isaac Newton institute where I met up with Guifre Vidal who showed me something amazing: the Multiscale Entanglement Renormalisation Ansatz, and I realised that what I should do is focus on more my core skill set (quantum entanglement and many body quantum spin systems). I began working on tensor networks, read a fantastic paper of Hastings, and got into the Lieb-Robinson game.

If I had my time again what would I do differently? I don’t regret working on this problem. It was worth a try. My mistake was to keep working on it, to the exclusion of everything else, for too long. These days I am mindful of the advice of Wheeler: you should never do a calculation until you already know the answer. I also try to keep a portfolio of problems on the go, some risky ones, and some safe ones. (More on that in a future post.) Finally, upon reflection, I think my motivation for working on this problem was totally wrong. I was primarily interested in solving a famous problem and becoming famous rather than the problem itself. In the past decade I’ve learnt to be very critical of this kind of motivation, as I’ve seldom found it successful.

PS. I find the QIP 2004 conference photo rather striking: so many of the attendees have moved on to great success in quantum information theory and have now become household names. It was still a year before Scott Aaronson would start his famous blog. I never would have guessed at the time.