How do you decide whether a question in abstract algebra is worth studying?

Question

Dear MO-community, I am not sure how mature my view on this is and I might say some things that are controversial. I welcome contradicting views. In any case, I find it important to clarify this in my head and hope that this community can help me doing that.

So after this longish introduction, here goes: Many of us routinely use algebraic techniques in our research. Some of us study questions in abstract algebra for their own sake. However, historically, most algebraic concepts were introduced with a specific goal, which more often than not lies outside abstract algebra. Here are a few examples:

• Galois developed some basic notions in group theory in order to study polynomial equations. Ultimately, the concept of a normal subgroup and, by extension, the concept of a simple group was kicked off by Galois. It would never have occurred to anyone to define the notion of a simple group and to start classifying those beasts, had it not been for their use in solving polynomial equations.
• The theory of ideals, UFDs and PIDs was developed by Kummer and Dedekind to solve Diophantine equations. Now, people study all these concepts for their own sake.
• Cohomology was first introduced by topologists to assign discrete invariants to topological spaces. Later, geometers and number theorists started using the concept with great effect. Now, cohomology is part of what people call "commutative algebra" and it has a life of its own.

The list goes on and on. The axiom underlying my question is that you don't just invent an algebraic structure and study it for its own sake, if it hasn't appeared in front of you in some "real life situation" (whatever this means). Please feel free to dispute the axiom itself.

Now, the actual question. Suppose that you have some algebraic concept which has proved useful somewhere. You can think of a natural generalisation, which you personally consider interesting.

How do you decide whether a generalisation (that you find natural) of an established algebraic concept is worth studying? How often does it happen (e.g., how often has it happened to you or to your colleagues or to people you have heard of) that you undertake a study of an algebraic concept and when you try to publish your results, people wonder "so what on earth is this for?" and don't find your results interesting? How convincing does the heuristic "well, X naturally generalises Y and we all know how useful Y is" sound to you?

Arguably, the most important motivation for studying a question in pure mathematics is curiosity. Now, you don't have to explain to your colleagues why you want to classify knots or to solve a Diophantine equation. But might you have to explain to someone, why you would want to study ideals if he doesn't know any of their applications (and if you are not interested in the applications yourself)? How do you motivate that you want to study some strange condition on some obscure groups?

Just to clarify this, I have absolutely no difficulties motivating myself and I know what curiosity means subjectively. But I would like to understand, how a consensus on such things is established in the mathematical community, since our understanding of this consensus ultimately reflects our choice of problems to study.

I could formulate this question much more widely about motivation in pure mathematics, but I would rather keep it focused on a particular area. But one broad question behind my specific one is

How much would you subscribe to the statement that EDIT: "studying questions for the only reason that one finds them interesting is something established mathematicians do, while younger ones are better off studying questions that they know for sure the rest of the community also finds interesting"?

Sorry about this long post! I hope I have been able to more or less express myself. I am sure that this question is of relevance to lots of people here and I hope that it is phrased appropriately for MO.

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Edit: just to clarify, this question addresses the status quo and the prevalent consensus of the mathematical community on the issues concerned (if such a thing exists), rather than what you would like to be true.

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Edit 2: I received some excellent answers that helped me clarify the situation, for which I am very grateful! I have chosen to accept Minhyong's answer, as that's the one that comes closest to giving examples of the sort I had in mind and also convincingly addresses the more general question at the end. But I am still very grateful to everyone who took the time to think about the question and I realise that for other people who find the question relevant, another answer might be "the correct one".

Answer 1

Dear Alex,

It seems to me that the general question in the background of your query on algebra really is the better one to focus on, in that we can forget about irrelevant details. That is, as you've mentioned, one could be asking the question about motivation and decision in any kind of mathematics, or maybe even life in general. In that form, I can't see much useful to write other than the usual cliches: there are safer investments and riskier ones; most people stick to the former generically with occasional dabbling in the latter, and so on. This, I think, is true regardless of your status. Of course, going back to the corny financial analogy that Peter has kindly referred to, just how risky an investment is depends on how much money you have in the bank. We each just make decisions in as informed a manner as we can.

Having said this, I rather like the following example: Kac-Moody algebras could be considered 'idle' generalizations of finite-dimensional simple Lie algebras. One considers the construction of simple Lie algebras by generators and relations starting from a Cartan matrix. When a positive definiteness condition is dropped from the matrix, one arrives at general Kac-Moody algebras. I'm far from knowledgeable on these things, but I have the impression that the initial definition by Kac and Moody in 1968 really was somewhat just for the sake of it. Perhaps indeed, the main (implicit) justification was that the usual Lie algebras were such successful creatures. Other contributors here can describe with far more fluency than I just how dramatically the situation changed afterwards, accelerating especially in the 80's, as a consequence of the interaction with conformal field theory and string theory. But many of the real experts here seem to be rather young and perhaps regard vertex operator algebras and the like as being just so much bread and butter. However, when I started graduate school in the 1980's, this story of Kac-Moody algebras was still something of a marvel. There must be at least a few other cases involving a rise of comparable magnitude.

Meanwhile, I do hope some expert will comment on this. I fear somewhat that my knowledge of this story is a bit of the fairy-tale version.

Added: In case someone knowledgeable reads this, it would also be nice to get a comment about further generalizations of Kac-Moody algebras. My vague memory is that some naive generalizations have not done so well so far, although I'm not sure what they are. Even if one believes it to be the purview of masters, it's still interesting to ask if there is a pattern to the kind of generalization that ends up being fruitful. Interesting, but probably hopeless.

Maybe I will add one more personal comment, in case it sheds some darkness on the question. I switched between several supervisors while working towards my Ph.D. The longest I stayed was with Igor Frenkel, a well-known expert on many structures of the Kac-Moody type. I received several personal tutorials on vertex operator algebras, where Frenkel expressed his strong belief that these were really fundamental structures, 'certainly more so than, say, Jordan algebras.' I stubbornly refused to share his faith, foolishly, as it turns out (so far).

Added again:

In view of Andrew L.'s question I thought I'd add a few more clarifying remarks.

I explained in the comment below what I meant with the story about vertex operator algebras. Meanwhile, I can't genuinely regret the decision not to work on them because I quite like the mathematics I do now, at least in my own small way. So I think what I had in mind was just the platitude that most decisions in mathematics, like those of life in general, are mixed: you might gain some things and lose others.

To return briefly to the original question, maybe I do have some practical remarks to add. It's obvious stuff, but no one seems to have written it so far on this page. Of course, I'm not in a position to give anyone advice, and your question didn't really ask for it, so you should read this with the usual reservations. (I feel, however, that what I write is an answer to the original question, in some way.)

If you have a strong feeling about a structure or an idea, of course keep thinking about it. But it may take a long time for your ideas to mature, so keep other things going as well, enough to build up a decent publication list. The part of work that belongs to quotidian maintenance is part of the trade, and probably a helpful routine for most people. If you go about it sensibly, it's really not that hard either. As for the truly original idea, I suspect it will be of interest to many people at some point, if you keep at it long enough. Maybe the real difference between starting mathematicians and established ones is the length of time they can afford to invest in a strange idea before feeling like they're running out of money. But by keeping a suitably interesting business going on the side, even a young person can afford to dream. Again, I suppose all this is obvious to you and many other people. But it still is easy to forget in the helter-skelter of life.

By the way, I object a bit to how several people have described this question of community interest as a two-state affair. Obviously, there are many different degrees of interest, even in the work of very famous people.

Answer 2

I'm going to interpret your question in the language of Gowers's "two cultures" essay as follows:

How does one get good at theory-building?

The process of developing a good theory can seem deceptively simple. One takes some definitions, perhaps by generalizing some known definitions, and deduces simple consequences of them. In comparison with the work required to solve a hard problem, this seems easy---perhaps too easy. The catch, of course, is the one you raised: there is a significant risk of spending a lot of time studying something that ultimately has very little mathematical value. Of course there is also the risk of wasted effort when trying to solve a specific problem, but in that case, it's at least clear what you were trying to accomplish. In the case of theory-building, the signposts are less clear; maybe you succeeded in proving some things, so your efforts weren't entirely fruitless, but at the same time, how do you know that you actually got somewhere when there was no clear endpoint?

The number one principle that I keep in mind when trying to build a theory is this:

Relentlessly pursue the goal of understanding what's really going on.

I'm reminded of a wonderful sentence that Loring Tu wrote in his May 2006 Notices article on "The Life and Works of Raoul Bott." Tu wrote, "I. M. Singer remarked that in their younger days, whenever they had a mathematical discussion, the most common phrase Bott uttered was “I don't understand,” and that a few months later Bott would emerge with a beautiful paper on precisely the subject he had repeatedly not understood." Von Neumann reportedly said that in mathematics, you don't understand things; you just get used to them. This can be valuable advice to a young mathematician who hasn't yet grasped that the reason we're doing research is precisely that we don't really understand what we're doing. However, the key to theory-building is to insist on thorough understanding, especially of things that are widely regarded as being already understood. Often, such subjects are not really as well understood as others would have you believe. If you start asking probing questions---why are things defined this way and not that way? why doesn't this argument actually prove something more (or maybe it does?)?---you will find surprisingly often that what seems like a very basic question has not really been addressed before.

You asked:

How do you decide whether a generalisation (that you find natural) of an established algebraic concept is worth studying? How convincing does the heuristic "well, X naturally generalises Y and we all know how useful Y is" sound to you?

My reply is that the generalization is worth studying if it helps you understand the original concept better. Perhaps the generalization was obtained by weakening an axiom, and you can now see more clearly that certain theorems hold more generally while others don't, so you get some insight into which specific hypotheses of your original object are needed for which conclusions. The heuristic as you've stated it, on the other hand, doesn't sound too convincing to me. I see too much risk of wandering off into a fruitless direction if you're not firmly grounded in trying to understand your original object better.

Keeping firmly in mind that your goal is a thorough understanding of some particular subject is also important because your efforts will, at least initially, not be greeted with enthusiasm by others. You will appear to be a complete idiot who doesn't understand even very basic things that other people think are obvious. Even when you start getting some fresh insights, they will seem trivial to others, who will claim that they "already knew that" (which they probably did, implicitly if not explicitly). Constantly adjusting definitions also appears to others to be an unproductive use of time. Even if you get to the point where your approach leads to a new and wonderfully clear presentation of the subject, and raises important new questions that nobody thought to ask before, you may not get credit for original thinking. Thus it is important that your internal compass is pointed firmly in the right direction. To repeat: ask yourself, am I driving towards an understanding of what's really going on in this important piece of mathematics? If so, keep at it. If not, then you've lost the thread somewhere along the way.

Answer 3

"How much would you subscribe to the statement that studying questions one finds interesting is something established mathematicians do, while younger ones are better off studying questions that the rest of the community finds interesting?"

Not at all. I don't think anyone, young or old, will find success by working on questions other than those they find interesting. Mathematics is just too difficult for that.

Ideally, everyone should work on problems that are interesting to both themselves and the community. Senior mathematicians have the luxury of working on problems whose interest to the community has not been established.

Answer 4

It may be helpful to say how I got into groupoids.

In the 1960s, I was writing a topology text and wanted to do the fundamental group of a cell complex, which required the van Kampen Theorem (I have now been persuaded to call this the Seifert-van Kampen theorem, as on wikipedia, so I call it SvKT). I was kind of irritated that this did not as then formulated give the fundamental group of the circle, so one had to make a detour and do all or a piece of covering space theory.

Then I found a paper by Olum on nonabelian cohomology and van Kampen's theorem which I extended to a Mayer-Vietoris type sequence which did give the fundamental group of the circle. Unfortunately, when written out in full, it was rather boring! I then came across a paper of Philip Higgins which included the notion of free product with amalgamation of groupoids. So I decided to put in an exercise using this notion for the fundamental groupoid of a space. Then I wrote out a solution for this, and it was so much nicer than the nonabelian cohomology stuff that I decided to make the account in terms of groupoids. It still needed the key notion of the fundamental groupoid on a set $C$ of base points, written $\pi_1(X,C)$. For the circle, this needed $C$ to have 2 elements. This result appeared in the first 1968 edition, and in subsequent ones, of the book on topology, but in no other topology text in English since then.

In 1967 I met George Mackey who told me of his work on ergodic groupoids. This persuaded me that the idea of groupoid was, or might be, more important than met the eye.

On writing out the proof of the SvKT for groupoids maybe 5 times, it occurred to me in 1965 that the proof should generalise to higher dimensions if one had the `right' gadget generalising $\pi_1(X,C)$. This was finally found with Philip Higgins in 1974 as the fundamental double groupoid $\rho_2(X,A,C)$ of a space $X$ with subspace $A$ and set $C$ of base points. So we got a SvKT in dimension 2, published in 1978, and had extended this to all dimensions by 1979. Work with Chris Spencer in 1971-2 on double groupoids and crossed modules was essential as a basis for all this.

The point I am making is that the initial aim of an improved proof of the fundamental group of the circle was very modest, but based on an aesthetic feeling, and the aim would not have got many marks for a research proposal! But in the end it opened out a new area.

One main driving force for the higher dimensional work was the intuitions of subdividing a square into little squares, and getting the inverse to that, i.e. composing the little squares into a big one. Another problem was that of expressing the idea of commutative cubes.

Philip Higgins told me of a remark of Philip Hall that one should try to make the algebra model the geometry, and not force it into an already known mold. I think that is what people were doing in avoiding the groupoid concept, despite its obvious nature. Indeed the idea of `change of base point' for the fundamental group is a bit like giving a railway timetable in terms of return journeys and change of start-- i.e. is bizarre.

Perhaps the moral is that is good to look for ways of expressing intuitions in a rigorous mathematical form. And if that means building up some maths from scratch, previous to definitions, examples, theorems, proofs, as was needed in the higher dimensional work, then that is a lot of fun! (More fun than doing someone else's problem!) But it may take a long time, need lots of attempts, and searching for related ideas, and as it gets going, hard work, and in our case fruitful collaborations.

Research students liked the idea of a big plan (what is or might be `higher dimensional group theory'?) and the attempts to pick from this something that might be doable.

I'd better not go on about the opposition!

Does that help?

Answer 5

Dan Schechtman, winner of the 2011 Nobel Prize in Chemistry for the discovery of quasi crystals, said: “The main lesson that I have learned over time is that a good scientist is a humble and listening scientist and not one that is sure 100 percent in what [they read] in the textbooks.”

My research on groupoids and higher groupoids was started in the 1960s by a dissatisfaction with a van Kampen theorem that did not compute the fundamental group of the circle, a basic example: but groupoids were at the time regarded as "rubbish" by many senior mathematicians, and the idea of higher van Kampen theorems using higher groupoids was described by one such for 10 years as "ridiculous". (He gave in eventually!)

My worry is that people may be encouraged to follow high ups, rather than to analyse a programme on mathematical grounds, and so to develop their own feeling for mathematical structures.

January, 2015: One needs a variety of strategies, one of which is to look at what a theory does not do but somehow in principle should. This is the notion of anomaly. I have listed 5 anomalies in standard algebraic topology in this presentation Dec, 2014, Galway.

See also the advice given to me 1964 by S. Ulam, quoted in my web page discussing the issue of famous problems in category theory.

Alexander Grothendieck wrote to me that: "Throughout my whole life as a mathematician, the possibility of making explicit, elegant computations has always come out by itself, as a byproduct of a thorough conceptual understanding of what was going on. Thus I never bothered about whether what would come out would be suitable for this or that, but just tried to understand -- and it always turned out that understanding was all that mattered."

So I always advocate writing and rewriting to make things clear to yourself, testing that by explaining to other people. At Bangor we explained to research students that a thesis must have a "thesis". So having decided on the latter, the first thing for the student to do is write up the background to that "thesis", which can always be expected to be a useful part of the final thesis. All sorts of things may turn up in that process.

Answer 6

I have just now looked again at this interesting blog and thought to add a few points.

1) Methodology: You could read the comments of Grothendieck on "speculation" http://groupoids.org.uk/Grothendieck-speculation.html. I also think that in private one should test an idea `beyond the bounds of human thought': that is, just for fun, take it as far as you you think it can possibly go, and if all went as well as possible. This I call the "ideal scenario". If, under the ideal scenario, the result does not look all that exciting, then you might put is aside. On the other hand, if, under the ideal scenario, the result would be wonderful, then you might say to yourself: "Life is not like that, there must be some obstructions to this working." So you look for obstructions, small things that you think you might be able to do. If these obstructions turn to be real, then that would be interesting, and you should modify your scenario. On the other hand, if these obstructions disappear one by one, that would be even more interesting! Either way, this is a win-win research strategy. If some negative person (these abound in mathematics!) says "your idea cannot work because...." then that gives another obstruction to work on.

I also like the idea of writing a (draft!) paper on your new idea, in which a key part is the Introduction, which should be as free ranging as possible, following flights of fancy, catching ideas as they occur. These can always be later relegated to another document (the great advantage of mathematical wordprocessing). The process of writing can make these ideas more real. So can talking about them, though you do sometimes get funny looks from superior people!

You may write a draft 4 times, ending in failure, then the fifth time the paper writes itself! (It took me 9 years, and many drafts which ran into sand, trying to write a paper on a new homotopy double groupoid, before realising with Philip Higgins in 1974 that it was useful to try a definition for a pair of spaces, rather than a plain space!)

2) The composer Ravel said you should copy. If you have some originality, then this might come out as you copy. If not, then never mind! I feel copying is a way of getting the rusty wheels of the brain slowly turning! The originality may come out later. So I advise trying to write up a known piece of mathematics in as "nice" a way as you can. Nothing can be lost by this.

3) A question for Scott: Is there a (hopefully useful) groupoid version of quandles related to the fundamental groupoid and a `peripheral subgroupoid'?

4) A dictum of the algebraist Philip Hall was that one should try to make the algebra model the geometry rather than force the geometry into an already existing algebraic mold. For me, an example of this "forcing" is to try and get a group, and then bring in the idea of change of base point, when the naturally occurring structure is a groupoid. There are many other examples!

Answer 7

Jordan algebras were introduced first by P. Jordan and J. von Neumann in order to give a mathematical context for observables in quantum mechanics (say, a structure that generalizes the space of Hermitian matrices). At the end, the classification was disappointing, and Jordan algebras do not play a role any more in QM, but the topic survived in Mathematics until now.

Answer 8

Not sure I agree with the whole post in detail. Distinguish "pure algebra" from "applied algebra"; and within "pure algebra" distinguish "structural" issues from "combinatorial" ones such as the Burnside problem. Remembering that "abstract algebra" is the modern term for what used to be called "modern algebra", we should probably drop the "abstract" to get a more reasonable view (the scope of "old" or 19th century algebra being that of Chrystal's Algebra say, some would now count as other branches of mathematics, such as numerical methods).

So which questions are worth studying? Not just one kind, surely. Algebraic geometry, algebraic topology, algebraic number theory all do ask serious and interesting algebraic questions. See for example the Golod–Shafarevich theorem which is pure algebra to start with. Parts of algebra come across as "general" compared to mathematics as a whole, but this is somewhat subjective criterion these days. There are both general-structural and general-combinatorial parts of algebra. There do need to be some criteria operating in, say, infinite group theory and infinite-dimensional Lie algebra theory. Generality in the sense of category theory is rather 1960s in feel; derived categories are "abstract" but I wonder who these days would argue that they are too "general"? I suppose the general module over the general ring still looks troublesome as a setting for research.

Well, I think "follow the masters" is probably the best advice,

Answer 9

There are surely no hard and fast rules as to assessing the importance of a generalization of a concept. I once took a look (chap. 9) at debates surrounding the move from groups to groupoids. One important step up for a concept is being deemed essential rather than merely useful. To achieve this it must find its place in an array of good storylines.

Answer 10

Alex, don't feel as if the weight of the burden of proof (of concept generalization) has to rest completely on your shoulders. I realize you already agree that curiousity and your own interest can be enough reason to pursue a topic or generalization, but...

Isn't it the same as asking a question on mathoverflow about a topic which is interesting to you on its own merits, and finding out about the existence of either a longer history of it based on a parallel set of definitions or other possible applications of it in other branches of mathematics or physics? I had been working on a particular topic, but having approached it from one direction I could only perceive the question from my point of view.

Even my attempts to research it found nothing initially because I was using the wrong key-words to look for similar work on my topic. It turned out that there was a long history of work on the topic using different terminology which I had not been aware of.

Perhaps giving a short summary on mathoverflow (as a different question) of the generalization which you are working on would provide you some different points of view from other mathematicians.

As to the utility of a generalization or of a particular approach, it is not possible to predict or find all of, many of, or even more than a few of, the possible applications of a mathematical technique on your own because you cannot survey the entirety of it yourself. It's often the intersection of multiple disparate interests that creates the application of a technique onto a problem, and every individual (and every individual mathematician) has a different set of disparate interests. (As long as the number of categories of possible interests is greater than the logarithm in base two of the size of the population under consideration; otherwise the pigeonhole principle requires that there must be at least two individuals with exactly the same interests. :) )

Answer 11

Hi Alex!

About the second question: I think senior mathematicians don't necessarily escape the criterion of general interest, but it can become a self-fulfilling prophecy: The mere fact that a senior mathematician is studying something can raise interest in the object of study among the mathematical community - I guess they easier grant him that he will see connections or analogies to other areas accepted as interesting. See Minhyong Kim's nice "money in the bank" comparison.

About the first: Of course you want to study this concept you are interested in. So to make it interesting for others you could go for some introspection - what is it that you find intriguing about it? Can you pass it on to others (this is surely easier in talks than in papers)?

It does not always have to be a big range examples that apply to it. Maybe you feel it behaves unexpectedly well in spite of weak axioms. Maybe it clarifies that many of the facts about Y depend only on the fact that it is an X and thus improves the understanding of the well-accepted theory of Y. Maybe you have a single application where it showed up and feel that there it greatly helped to separate the algebraic content of the situation (which is strictly more than the structure of a Y) from the rest. These seem all like potential good reasons to work on the theory of X.

But maybe your fascination comes from the feeling that your X shows unusual behaviour for an algebraic structure, then spelling that out you could find that this just reflects your prejudices about algebraic structures, which others don't have - this could be a criterion record this as learning experience and do something else for publishing...

Answer 12

I think something is worth studying if it helps one of:

• solving a problem I know about,

• giving a new perspective on something I know, or

• raising interesting questions, some of which are easy to solve and some of which aren't.

Especially, I study it if it gives me some degree of gratification. Here are a couple of examples of things that I hope to pursue after my current interests wane:

Recursive clone theory: A class of functions on a set which is closed under composition and having projections is called a clone; the notion is a part of basic general algebra. Something that should be mentioned in basic recursion theory classes but is not is that various definitions are specializations of clones: primitive recursive functions, partial recursive functions, total recursive functions. I think it would be useful to blend the ongoing research in clone theory with a computational component that can answer how complex a class can be.

Transforming Shelah's classification theory: In determining how many inequivalent models of cardinality kappa exist for a first order theory, Saharon Shelah came up with conditions on the theory which (loosely and inaccurately speaking) sometimes dealt with whether a theory could encode a particular order or a certain simpler theory. I think the ideas can be moved into the domain of computation over finite structures. In particular, languages that are members of some complexity class (oh, say, NP) could be shown to satisify properties analogous to what Shelah developed for first order theories. I think that this would be a promising route to find a language in NP - P .

Granted, these are not generalizations so much as taking tools, trying them on a new kind of widget, and then retooling the tool to work on the widget. The justifications for working on them should be the same and (I think) apply to your questions.

Gerhard "Ask Me About System Design" Paseman, 2010.09.24

Answer 13

I am thinking of specific examples. In much the same way, David Corfield mentioned groupoids.

I am personally not a big fan of the general theory of loops. In part, my own disinterest is because I have not found an application. On the other hand, I have seen enough to believe that Moufang loops are interesting even if I personally don't know a lot about them. Still I like the idea of algebraists thinking about the structures of loops because they find them interesting.

Closer to my own interest is the idea of quandles. These were introduced essentially in the 1940s, then again in the late 1970s and early 1980s, rediscovered, and have only found some greater applicability because quandle cohomology gives interesting topological invariants. The idea, apparently was natural: it was discovered, forgotten, rediscovered, forgotten, and found to be applicable. Nevertheless, some of you might find it to be be a fringe notion. Even knot theorist might believe that there is not much in the quandle concept because the information in the quandle is present in the fundamental group and a peripheral subgroup.

I think Tim's articulation of Ronnie's list should include that the algebraic concept yields a more concise language in which ideas can be expressed.

Answer 14

This is really an add-on to David Corfield's answer.

Since David mentions groups and groupoids, I will mention that Ronnie Brown (https://groupoids.org.uk/hdaweb2.html) considers some of the possible criteria as follows:

Tests for a theory which is successful in a mathematical and scientific rather than sociological sense could be the following. A successful theory would be expected to yield. He wanted to evaluate some new concepts and proposed the following advantages.

• a range of new algebraic structures, with new applications and new results in traditional areas;

• new viewpoints on classical material;

• better understanding, from a higher dimensional viewpoint, of some phenomena in group theory;

• new computations with these objects, and hence also in the areas in which they apply;

• new algebraic understanding of the structure of certain geometric situations;

• a stimulus to new ideas in related areas;

• a range of unexplored ideas and potential applications;

• the solution of some classical famous problems.

I would suggest that this list (albeit incomplete as Ronnie suggests) applies to algebraic situations as well as his higher dimensional group theory context and that, suitably interpreted for other contexts, they can provide some very partial answer to the question.

The second question is perhaps best answered by saying that 'established' mathematicians are expected to have some sort of 'gut' feeling about the importance of a question or area. Sometimes they just have blind prejudice however. One task of a research supervisor 'should' be to train a PG student towards getting that intuition, but not to hand on the prejudices.

At a pragmatic level a debutant mathematician needs to get work published and noticed and that is easier in established areas (or near established areas).

Answer 15

In some sense, mathematical structure is simply analogy at a very high level. One tries to fill in details in a way that is likely to pay off. (E.g. looking for a natural way to make a semigroup you are looking at into a group may just pay off, simply because groups are ubiquitous and useful.) This may be the reason why an eye toward mathematical structure is a good thing to cultivate. This is usually a decent way to meet algebraic problems that need attention, when a "picture" needs to be filled in. Ultimately, this "picture" should provide some unification or better understanding of diverse phenomena, or the solution of a reticent problem. Looking for or working on mathematical (or simply algebraic) structure is just another strategy for building a better conceptual picture of the mathematical landscape.

Answer 16

If it interests you.

Answer 17

This paper has a very nice introduction (it is on "pointless topology"). So apparently, one may come up with very random definitions for their own sake and hope someone "applies" them to more "concrete" problems. Link

Answer 18

Right now? "If you can use it in Quantum mechanics, it is worth studying" seems to be the general idea behind a lot of math these days (I have 2 ongoing articles with this explanation)..