Is there any published research on the value of finding new proofs for old theorems?

There have been many conjectures in history of mathematics that some of them after passing long journey have resulted in lengthy and high-level-math proofs. Perelman's proof on the Poincare's Conjecture and Wiles' proof on Fermat's Conjecture are some examples. I believe that to come up with simpler and shorter proofs for any of the two mentioned (now-)theorems would be invaluable ...

But, there are also many theorems that have many proofs and some of the those proofs of that single theorem use same level of math (and same sub-fields in math!) and usually takes almost same length on paper to write.

Theorem of compactness of $[a,b]$ in standard topology (I already know two proofs of same level/field-of-study/length) and Pythagoras Theorem are just a few examples.

My question is about the latter case: Is there any research that looks at cases of theorems being re-proven and assesses the value of that kind of activity?

Thank you very much.

• Depends how you define "worthy". From an applied perspective (as someone from an engineering background), once you know something is true, who cares if you can show it in a different way? But finding different ways to show something is true can result in new techniques that can be useful in other problems (among many other things). Sometimes new techniques (from a new or different field) can make it much simpler to prove something as well. – Phill Jun 18 '15 at 3:47
• @Phill: What if we define "worthy" as how are opinions of majority of mathematicians on? – MKR Jun 18 '15 at 3:58
• I think you have to clarify what you mean. At the end, are you excluding stuff like Gowers' proof of Szemerédi's theorem? That's a proof of an already known result that more or less won somebody Fields Medal. Someone thought that was important. – Hoot Jun 18 '15 at 4:04

This question (or a close variation of it) was discussed in detail in:

Dawson, J. (2006). Why do mathematicians re-prove theorems? Philosophia Mathematica (III) 14 (3), 269-286.

Dawson's article is itself a kind of sequel to an earlier (and well-known) paper of Yehuda Rav:

Rav, Y. (1999). Why do we prove theorems? Philosophia Mathematica (3) 7, 5-41.

In that earlier paper, Rav argued (p. 6) that

the essence of mathematics resides in inventing methods, tools, strategies and concepts for solving problems.... Proofs, I maintain, are the heart of mathematics, the royal road to creating analytic tools and catalysing growth

and that in many cases (Rav, I think, would say all cases) the techniques and insights generated by a proof are more important than the result itself. In fact Rav refers to proofs (not theorems, but proofs) as "the site and source of mathematical knowledge" (p. 12).

In the subsequent paper by Dawson, this thesis is picked up and further developed. Dawson spends a fair amount of time examining the question "What makes two proofs different?" This turns out to be a fairly non-trivial question; for example, there may be structural differences, different strategies or techniques (e.g. one proof might use induction, another might not), and so forth. Dawson provides 8 different reasons why mathematicians might re-prove theorems:

1. To remedy perceived gaps or deficiencies in earlier arguments;
2. To employ reasoning that is simpler, or more perspicuous, than earlier proofs;
3. To demonstrate the power of different methodologies;
4. To provide a rational reconstruction (or justification) of historical practices;
5. To extend a result, or to generalize it to other contexts;
6. To discover a new route;
7. Concern for methodological purity;
8. To provide something analogous to the role of confirmation in the experimental sciences.

Dawson elaborates on each of those eight reasons in some detail, providing historical examples of how certain re-proofs play those roles.

With respect to your question "Is it worthy to spend time on doing research in finding other proof(s) for already proven theorems... rather than focus on unsolved problems or at least extending the edges of mathematics?", Dawson writes (p. 269):

Today, new proofs of old theorems continue to appear regularly and to enrich mathematics. Indeed, in 1950 a Fields Medal was awarded to Atle Selberg, in part for his elementary proof of the prime-number theorem.

So, yes, there is value in finding a new proof of an old theorem. Indeed, a Google Scholar search for papers with the phrase "a new proof of" in the title finds many examples of the genre.

• Thank you very much both for editing of and brilliant answer to my question. – MKR Jun 20 '15 at 3:40

Since mathematical research is a human enterprise it is always worthwhile to have multiple angles to understand a given theorem. If nothing else, there are many different types of audiences and what constitutes a useful theorem for one crowd need not be of any use to another. For example, you might find a careful epsilonic proof of the inverse function theorem in a classic text on advanced calculus. Very rigorous, but, gives little intuition on how to realize the theorem pragmatically. On the flip-side, you might prefer the sketch of the theorem I usually offer in my advanced calculus course. My proof (based on Edward's Advanced Calculus ) is not quite rigorous, but, it gives you a sense on how to approximately implement the inverse function theorem through iterative approximates.

Besides these sort of disparities in presentation, there is also active research in what is known as reverse mathematics. More specifically, these folks ask the minimalist questions of how much can be stripped away from a theorem and still have it be true. This sort of choose your own adventure mathematics can be very challenging. Not exactly my thing, but, certainly those who engage in it successfully bring a new angle to established mathematics.

• +1 Thank you very much esp. for introducing Reverse Mathematics. – MKR Jun 18 '15 at 12:36

There are lots of reasons that different proofs help.

One is that a new proof shows new insight - for example, there are proofs in algebra involving lengthy calculation, and entirely elementary, which are hugely simplified once the Noetherian condition is analysed.

Sometimes it is useful to know which assumptions are vital to a proof. For example, the Sylvester-Gallai theorem in geometry can be proved in various ways - but it is useful to know in which geometries it is true, and that means stripping it down to the very basics.

Then there are existence proofs which tell us little about the thing which exists. A proof which constructs the object, or which gives new information about it, is a definite advance, even if it takes more work.

And then, as maths moves on, we encounter more general situations - from one dimension to many, from fields and vector spaces to rings and modules etc - and the properties dear to us in the first context need to be tested in the new one.

From the perspective of the individual, I would dare to say that it is always personally worthy, because the researcher will gain experience in the field.

From the perspective of the general benefit, sometimes it is very worthy, for instance some theorems can not be applied to real life problems in their initial expression, so when other ways of defining the same problem are found (even using the same fields of research), the results can be applied into real life problems.

E.g. any primality test: we can now in multiple ways if a number is a prime number, but for instance a main point is how many time do we need to know it, so any new research in that same matter, even finding alternative proofs, is worthy, each one of them can lead to a better solution.