How do we acquire the practice necessary to become perfect? This is a very general question, and I’m considering the question with regard to mathematical skill. Suppose my aim is to become a mathematics researcher. How do I acquire the practice necessary to do mathematical research?

In this blog post, I consider a specific trade-off: is it better to develop practice and intuition by considering a large number of simple problems, or simple things, or is it better to go after some of the big fish?

I’m personally in the “small fry” camp, and I’ll explain my reasons here.

**Building a balanced repository of experience**

As I mentioned in a previous post, the main advantage of experience is the presence of a large repository of knowledge that allows for more efficient pattern identification. I’ve been studying group theory for many years now, and thus, when confronted with a question in group theory, I am likely to either have seen the question before or at least have some meaningful closely related past experiences. Within a few years, by which time I should hopefully have explored more of the subject, I should be even better at tackling new questions in the subject.

A large repository of experience depends on knowing a lot of small facts here and there. These facts are connected in different ways. By tackling the small fry, either randomly or systematically, I am likely to cover many of these small facts. If I concentrate on the big fish, I may get to know very well all the small stuff that leads to that big fish, but many other things may have poor foundations.

Here’s an analogy. Suppose I want to explore the city of Chennai (Chennai is an Indian city, formerly known as Madras). One approach (the big fish approach) may be to identify a particularly difficult-to-locate spot in the city, and decide to reach that spot, with no help whatsoever. So I start walking around the streets of Chennai, going into some blind alleys and getting stuck at times, but I soon find my way and reach my destination. I go through a lot of parts of the city but my eyes are always seeking the destination point. Another approach would be to explore a new street each day. I might do this with an explicit ordering of the streets to explore, or I might do it in a pseudo-random way: each time I pick a new street that is slightly beyond the area I am currently familiar with. In the big fish approach, I might get to know the streets that lead to my destination very well, and I may also get to know very well the streets that misled me for a long time. In the small fry approach, I have a little knowledge of a much larger number of streets, but there is no overarching organizing framework to my knowledge, and no single goal.

The thrust of my argument is that the big fish approach leads to a less balanced and comprehensive repository of experience, as opposed to the small fry approach, leading to less preparedness for later research life. This is particularly important keeping in mind that most of us aren’t great at predicting what research problems we will work on a few years from now — so having a broader base makes more sense.

**An argument for big fish: a more authentic research experience**

There are at least a few ways in which the big fish approach seems more appealing. Because there are bigger fruits and bigger fish at the end, it can be more motivating and inspiring than simply doing a random collection of things on different days. I don’t disagree that big fish can be more exiciting to fish for, and juicier and larger fruits can be more exciting to reach for. In some cases, the greater excitement of something bigger can make up for the lack of breadth that may result from chasing it too hard.

But it is a mistake to look down upon, or sneer at, the tackling of small problems that aren’t aligned towards a specific big goal. In a sense, tackling a host of small problems without an overarching agenda is *harder* and *more challenging* than going out after a clearly defined problem. This is analogous to the fact that it may be a greater indication of inner strength to wander aimlessly rather than stride briskly and purposefully. At the same time, tackling small problems can be *more rewarding*, because it reduces the extent of commitment to a particular big problem and increases the amount of serendipity.

My final argument is that it is *more efficient* and *less risky* to consider and tackle a large number of small problems, or even settle wrinkles in many little definitions, than to try to prove big things. Just as we’re taught to diversify monetary investments in order to get a better average rate of return and be less prone to extreme risks, diversifying the problems being worked on is a good strategy against ruin. Some might view this as a “thinking small” attitude, citing people such as Andrew Wiles and John Nash who tackled and successfully solved hard problems. But there are a lot of people who tackled hard problems and did *not* solve them — and when you start out, you don’t really have an idea which camp you’re in (if you’re really really sure you can get the big fish, reading this blog post isn’t going to change your mind).

**How do small fry and big fish compare with the theory versus practice divide?**

There is a dichotomy between the theory builders and problem solvers in mathematics (something I alluded to earlier). Theory-building, *a la* Grothendieck, involves building general theories, while problem solving tackles specific problems.

The dichotomy between small and big is, as far as I understand, largely independent of the dichotomy between theory-building and problem-solving. Both theory-building and problem-solving can be done in minor incremental steps as well as in major, directed steps. Andrew Wiles, for instance, wanted to solve a problem (the so-called Fermat’s last theorem) and spent years doing that — his intention wasn’t to solve a theory. On the other hand, most problem-solvers are tackling separate isolated problems without the aim of making it to the national newspapers. Similarly, some theory-builders like Grothendieck seek to alter the foundations of geometry and mathematics. Others add in a few definitions here and there, introduce new symbol calculi or formalisms, and adapt past ideas to increase the strength of existing theories.

The difference between theory-building and problem-solving possibly lies with the inherent risks associated. With reasonable levels of rigor having entered mathematics, few published mathematical results have errors. Theory-builders, who are working incrementally based on what is known, are less likely to develop *wrong* theories, but run greater risks of being *irrelevant*. Problem-solvers, who are working on problems that others have identified as important, are more likely to do *relevant* work, but they are also more likely to not get anywhere or not succeed at all.

**Can small fry lead to big fish, and vice versa?**

Can a person chasing small fry end up netting the big fish? Can people chasing the big fish end up getting good at all the small stuff?

Paradoxically, it seems that the less efficient one is at chasing the big fish, the *more* one may learn about the small stuff. This follows from the *I learn more when I do it wrong* phenomenon, and is conditional to having a continued (and misplaced) sense of optimism on getting it right the next time. Chasing big fish, specially those totally out of reach, may therefore be an appealing strategy to learning more small stuff through self-deception.

Can a person chasing small stuff land a big fish? This is unlikely, and at any rate, a person chasing small stuff is unlikely to have the *multiple* insights needed to land the big fish. Nonetheless, the person may, without aiming to do so, develop some incremental insights that make the big fish look a little smaller for other people. Thus, even while a single individual who decides not to try for the big stuff foregoes the opportunity to hit it big, the mathematical community as a *whole* may not be adversely impacted in terms of the number of big problems it gets solved.

**Big fish — later or earlier in life?**

It would be folly for me to argue that people who spend many years tackling big problems are doing a disservice to mathematics by spending their time inefficiently. Tackling the big fish has positive externalities beyond the mathematical value it creates. First, it generates buzz about mathematics outside the mathematics community, and provides meat to popular math writers who can help entice more people to the subject. It is hard to entice kids into math by telling them that they can do a little more stuff every day and become cogs in the mathematical wheel. Big conjectures carry the romance of jackpots of lottery tickets.

Second, it makes the mathematical community bolder and braver and more confident of its abilities when a long-standing conjecture is resolved. Apart from the specific techniques developed to solve the conjecture, the idea that conjectures that have withstood assault for so long have yielded to perseverance and hardwork speaks to that ideal we so often want to believe in and yet keep doubting: “There is nothing that fails to yield to intelligence, hardwork, and sheer perseverance.”

Third, and perhaps most importantly, it saves other less talented people the agony of trying to prove the conjecture. With Wiles having settled Fermat’s last theorem, there are fewer people spending hours trying to settle it in the hope of winning fame.

Nonetheless, the question remains: when trying to *build* one’s research skills and abilities, is it a good idea to tackle relatively bigger fish? Here, I think the answer is *no*. Bigger fish may be incorporated as further inputs for random exploration, but a systematic attempt to go after a big fish is likely to lead nowhere.

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