Six Things I Believe

These six beliefs are the source of everything else we do. For how they play out day to day, see How the Day-to-Day Works.

1. Most ideas won’t work, but we’re not afraid to try and to debug

What we work on is often something nobody has attempted or done before. So here, a failed short-term result is a work product, not a total failure.

We hit walls often, but we learn together how to get past them:

• We keep a shared failure log. The ideas we tried, why they didn’t work, and how we got past the wall — it all goes in, so that others can dodge the dead ends earlier, or climb over them, when they hit something similar.
• Group meetings reserve time for failed results, so we can seriously discuss the causes and the fixes together.

2. Use toy examples to attack existing methods, and to give new ideas a fast debugging path

I believe the most expensive cost is not how much compute you spent — it’s how much time you spent before finding out the method was wrong.

So my habit is: for any new idea, run it first on a small-scale toy example, and see whether it behaves the way you expected.

We start from the point where existing methods do poorly, and design a toy example that they can’t solve well. That way, once our new idea passes it, we have some confidence and experience with the idea — and a basis for finding suitable benchmarks that show the new method’s advantages in realistic settings.

3. A problem worth doing must be both important and within reach

Even if a problem is important, if you have no idea at all how to start on it, it may not be the best problem for you right now.

Of course, we also try to avoid the kind of problem where you already know almost exactly what to do — that one may not be important enough, or may be too easy.

What we’re looking for is the balance point in between. We’ll think through these together:

Is this an important, worthwhile problem? Is it representative of a whole class of problems? Is it broadly applicable? Or does it genuinely solve a pain point in a specific field?

What advantages, tools, or ideas do we have to approach it with?

Roughly how long will it take to finish? How should we set the stop-loss point?

Who will cite it in five years? Can we name a plausible community specifically?

If a project keeps failing to answer these questions, we can discuss together whether to shelve it for now. Shelving isn’t a failure or a loss — it gives the time back to work that’s more worthwhile and more impactful.

I’m not saying you can’t try anything until you have an idea. I just don’t want us stuck for a long time in a direction that doesn’t suit us — especially when we have no clear advantage there.

4. We prefer fewer and deeper

Three or four papers a year that nobody reads are worth less than one paper that people will still read in ten years.

This is not about doing less — it’s about putting the effort you save into more meaningful, harder problems. “Will anyone still be reading this in five or ten years?” is a question we actually weigh when choosing problems. I’ll also give input on a topic’s potential as early as the ideation stage, offering my own view to help everyone decide whether it’s worth putting time and energy into the research in front of us.

5. Build intuitive, everyday thinking, and learn to connect different experiences

When I do research, what I value most is using intuition and everyday examples to understand and think about problems. Because no matter how complex a theory is, if you can translate it into a familiar everyday situation, it becomes far easier to build a solid, clear understanding — and easier to discover the true essence of the problem. This way of thinking not only helps you build clear research intuition, it also lets you explain your ideas to others in plain, accessible terms.

More importantly, we don’t stop at the intuitive level. We learn how to gradually abstract, from these everyday examples, the underlying mathematical models, engineering problems, and scientific principles — and to build connections across different fields. When you can move comfortably back and forth between intuition and abstraction, it becomes much easier to apply the experience you’ve accumulated to entirely new research problems, shaping and strengthening your capacity for cross-disciplinary thinking and innovation.

6. Discuss more, express more — the quality of an idea has nothing to do with seniority

In the short term, people who work behind closed doors may produce more.

But in the long term, the people willing to discuss and articulate their own ideas are the ones who come to know which problems are worth doing — and who, in the process of discussing and persuading others, find their own blind spots and spark better ideas. Everyone’s suggestions, regardless of seniority, deserve to be seen and respected.

I’ll encourage you to attend courses or talks outside your field, have coffee chats with people from other areas, and discuss and exchange your work. This seemingly inefficient time is a major source of our problem-selection quality and of pushing research forward.