Selecting a Good Problem to Work On

What problem should you work on?

At first, it doesn’t matter. Just work on any toy problem that interests you so that you can build technical skills and gain domain knowledge. It doesn’t matter if you solve it or not, whether it’s been solved before, or how impactful it is.

But once you start getting into problems that require many years of full-time work, selecting a good problem becomes very important. This is the land of startups and research labs, many of whose inhabitants regret that all the time and effort they invested did not yield a commensurate reward.

Personally, most of the toy problems I worked on were bad problems. That’s okay because I learned a lot and gained a lot of skills – which is the whole point of a toy problem – but it made me painfully aware of two failure modes that can make a problem bad.

Failure Mode 1: You don't have an implementable vision of what the solution is. In particular, some of the resources you need (e.g. data, algorithms, compute power) do not actually exist yet and you don't have a good plan for obtaining them.

This means the problem is too hard and you probably won’t be able to solve it. In my experience, many complex systems modeling problems lie here, e.g. creating useful predictive models of the human brain or macroeconomy.

For instance, there was a time when I was interested in modeling the human brain. I framed it as a regression problem on a time-series data set containing the activities and connection weights of all the individual neurons in brain. It took me a while to realize that the data set I wanted did not exist, and creating it would require multiple lifetimes and revolutionary breakthroughs in wet-lab neuroscience (and I was not interested in wet-lab work).

It’s worth noting that sometimes, failure mode 1 is an indication that you’re not actually interested in the thing that you think you’re interested in.

In my case, I thought I was interested in neuroscience, but it turned out that I was interested in a lot of stuff that just happened to show up in neuroscience: multiscale modeling, connectionism, human learning/intelligence, etc.

The most obvious thing that encapsulates all of those interests is building a model of the biological brain, but it’s not the only thing. What I’m doing now, developing the AI system that powers Math Academy’s fully automated and personalized online learning system, encapsulates all of those interests I listed and does not require any wet-lab work. (I did still have to get my hands dirty with teaching and content writing, but those were things that I enjoyed.)

Failure Mode 2: People don't care about the problem. They are not willing to pay for a solution with whatever currency you're interested in (money, citations, their time, etc).

This means that you’re not going to experience any reward for solving the problem. In my experience, theoretical modeling problems can fall victim to this when the problem framing abstracts away details that make the problem intractable but are important for application to real life.

It’s possible to argue that failure mode 2 doesn’t apply to you if you’re ahead of your time. However, there are two issues with that:

  1. You're probably not ahead of your time. Being ahead of one's time is rare, unverifiable, and tempting to believe. Talk about a recipe for flawed judgement!
  2. Even if it's true that you are ahead of your time, if you are too ahead of your time, then the reward will come too late in your life to feel worth the sacrifice. You might not even live to experience it.

That being said, I have met some people who are entirely satisfied by exploring their intellectual curiosity without the prospect of receiving an external reward or making an external impact in their lifetime, if at all. These people might be legitimate exceptions to failure mode 2. But for the vast majority of people, exploring intellectual curiosity is not enough.

How do you find find a problem that avoids both failure modes?

You need to find (or create) an intersection between your own interests/talents, the realm of what’s feasible, and the desires of the external world.

Unfortunately, it’s rarely obvious where the intersection is. All the cards are stacked against its existence:

  • You can't choose what you're interested in or what you're talented in.
  • You can't choose what the rest of the world cares about.
  • If you're interested/talented in some area to the point that you want to solve problems in it, then your reasons for being interested in it are probably not shared by the rest of the world.

So how do you find (or create) the intersection?

What’s worked for me is to live two parallel lives – one in which you do solve problems that interest you, and another in which you solve problems that interest the rest of the world. You continually try to push the parallel lives closer and closer together, and eventually, you figure out how to unify them.