If you do not work on an important problem, it’s unlikely you’ll do important work.
—Richard Hamming, You and Your Research
How can you distinguish important problems from those which aren’t? A problem’s importance is determined by the amount of good that work on it produces.
On all plausible theories, everyone’s well-being consists at least in part in being happy, and avoiding suffering.
—Derek Parfit, On What Matters
The essence of “what is good” is the extent to which something reduces suffering and increases happiness. This is not to claim that these are the sole factors that determine goodness, but rather that any theory of the good would be incomplete without them.
More Good is Gooder
That is wise. Were I to invoke logic, however, logic clearly dictates that the needs of the many outweigh the needs of the few.
—Spock, Star Trek II: The Wrath of Khan (1982)
It’s better to save two lives than one. The more people that work on a problem helps, the more good that work does and the more important that work is.
Work on impossible problems is not important. It will not lead anywhere. The human condition will not be improved. The more likely it is that work on a problem will do a lot of good, the more important that problem is. It is better to work on something where you have a 95% chance of saving a million lives than it is to work on something where you have a 5% chance of saving a million lives.
Working on something hard is not in and of itself virtuous. People working on research in pure mathematics are working on hard problems, but given how disconnected pure mathematics is from reality, just donating money to a charity is probably more important than working on the millennium problems.
You might think, “Yeah, but sometimes pure mathematics does have important real world consequences.” I agree. This is not a real objection, though. We are again talking about the likelihood of doing a lot of good.
One could argue, for example, that you might have some kind of powerful insight into many of the world’s greatest ills by setting the record for most olives eaten in a single sitting. The chance is negligible. You would have a higher likelihood of success by working directly on solving world hunger, etc.
If Not Me, Then Who?
It has always appalled me that really bright scientists almost all work in the most competitive fields, the ones in which they are making the least difference. In other words, if they were hit by a truck, the same discovery would be made by somebody else about 10 minutes later.
—Aubrey de Grey
It is important to consider context when deciding whether or not to work on a problem. Consider two scenarios:
- Curing a rare disease that will save 20 lives per year. Discovering the cure is an active area of inquiry within your discipline and there is a 90% chance that someone will discover a cure within the next year regardless of your contribution.
Curing a rare disease that will save 5 lives per year. The disease is absent from the academic literature and most researchers have no idea that it exists. Those that do know of its existence are not interested in finding a cure. There is less than a 1% chance that someone will discover a cure within the next year without your contribution.
You should work on the second problem.
This has an odd implication. Most people believe that Isaac Newton’s discovery of calculus and Alexander Graham Bell’s invention of the telephone were important. However, all of these were discovered by other people: Leibniz (among others) discovered calculus at the same time as Newton. Elisha Gray filed a patent for the invention of the telephone on the same day as Alexander Graham Bell. The infamous formula \( E=mc^2 \) was chanced upon by Henri Poincaré, Olinto De Pretto, Paul Langevin and, of course, Albert Einstein.
It’s useful here to make a distinction. I’m not claiming that the discovery of calculus or the invention of the telephone were not important. Rather, my point is that the individual work of Alexander Graham Bell and Isaac Newton was less important than it first appears. The world may have been better off if they had invested energy in some other pursuit.
Our aim should be an efficient distribution of intellectual resources among problems so that we maximize the amount of good accomplished. One aspect of reducing waste is to prevent duplicated work, such as two people inventing the telephone. By taking into account the amount of work that other people are doing on a problem before you begin working on it, you can maximize the amount of difference you can make as an individual.
Recognition and Reproduction
Doing important work doesn’t always feel important and is often not recognized as such. Important work is distinct from recognition for doing important work. When we think of doing groundbreaking research, we think of Albert Einstein and how great it would be to be like him.
This is a focusing illusion. We only hear about important work when it has been recognized. Important work without recognition is invisible. We have no memory of it because we’ve never heard of it. Who knows how many important discoveries have been ignored?
A significant amount of the appeal of doing important work is connected to the social status that we expect to gain as a result of doing that work. In this sense, then, aspirations of being a great researcher are not much different from dreams of being rich and famous. Our monkey brains want desperately to maximize their reproductive fitness.
The model I have presented here is not about maximizing reproductive fitness. If that is your goal, you would be better served by donating to a sperm bank or studying seduction than by setting out to do important work. This model is concerned with doing important work regardless of whether or not one achieves recognition for it.
Would you be content with improving the world even if someone else received credit for it? If the answer is yes, then you are interested in defining important work as I’ve presented here. If not, you are interested in something else and ought to be focusing on that goal instead.
- Robin Hanson explores some similar themes in this post.
- For more multiple discoveries, like the invention of the telephone, Wikipedia has a list.
- The idea that one should choose whatever will do the most good is standard consequentialism, which you can read more about here.
- The dependence of a problem’s importance on the probability of solving it is an expected value calculation, which Wikipedia covers here, and is related to the concept of comparative advantage in economics.
- The failure to take into consideration a decision’s context is termed “system neglect.” You can read more about it in this paper.
- The observation that unrecognized things are invisible is what Donald Rumsfeld called “unknown unknowns” in a 2002 speech.
- Daniel Kahneman has a great paper on a relevant focusing illusion, the relationship between income and happiness.
- The intimate relationship between goals and reproductive fitness is described in this paper.