What is an important mathematical question? $\DeclareMathOperator\GL{GL}$Many times I have heard people say sentences like X is an important question/ X is a natural question. I find this very surprising because to me it's all a matter of taste. I am having people ask me why study certain things and my mental response is it's fun or just out of curiosity; but often what I found is when I present my question with enough jargon then they agree my questions are worth studying.
An example is Schur positivity: for me it's an extremely rare phenomenon and every time a family of symmetric functions is Schur positive I feel it's worthy of study in its own right. But when I need to explain to people I need to talk in terms of Frobenius map, representations of $\GL_n$ and so on. But I never understood myself why representations of symmetric group or $\GL_n$ is more important than symmetric functions.
So I really want to know how to decide whether a question is worth studying? How do I decide what question is important to ask in mathematics?
I am sorry if this is not the right place to ask this. I will remove it if it violates MO policy somehow.
 A: It is indeed somewhat subjective. A discussion of this, with examples, is contained in Hardy's book Mathematician's Apology. But mathematicians frequently disagree on many questions whether they are important or not. For example, Vladimir Arnold disagrees with Hardy in many cases. And Jacobi disagreed with Fourier, in their famous exchange.
A: As Gil Kalai mentions in his answer that he "will not try to define depth", here's a possible complement to his answer. John Stillwell has an excellent lecture on this question and its history, available here: "What Does 'Depth' Mean in Mathematics?".
One particularly nice example I enjoy from there is early on, where there are four commonly-accepted-as-deep theorems presented: Dirichlet's theorem on primes in arithmetic progressions, the Poincaré conjecture, Fermat's last theorem, and the Classification of Finite Simple Groups. One overarching reason he mentions that, even though they are all theorems about discrete objects, one of the things that makes them deep is that somehow continuity enters into the proofs. Furthermore, he goes on to use history as a gauge of depth, and mentions (as a high-level, summary, idea) that:

[the theorems are deep because] it took a long time to prove them, they involves several stages, and
generally it was very good mathematicians who worked on them.

He then gives the excellent definition of depth as "the number of shoulders of giants that one must stand on to reach the result"!
I recommend anyone interested in this topic to watch the full lecture.
A: The question what makes a mathematical problem worth studying and even important is itself an important meta question about mathematics. Here are a few points (at time subjective) one can consider

*

*Difficult - For a problem to worth your effort it need to be difficult. If it is easy or the solution is routine, it is a weakness.

*Not hopeless - Both for individual mathematicians and for mathematics as a whole, problems that are utterly hopeless, are less worthy.

*Deep - I will not try to define depth.

*Fundamental - There are problems which are obviously fundamental to a mathematical area like what are the finite simple groups (or infinite simple groups) and what is the structure of p-groups. Sometimes the solution leads to fundamental insights.

*Requires new tools

*Natural - I tend to see problems that come up naturally as important. (But this is controversial.)

*Beautiful - Mathematicians may have different tastes for beauty but individual tastes are not orthogonal.

*Connected to other problems; (added by Dirk) helpful to resolve other problems or understand them better.

*Applied; connected to other areas of science and technology

A: I'd rather ask "how is" a math question important as opposed to "what is" an important mathematical problem. Some examples

*

*(Solves a bottleneck) If the question you address is the first in line of a bunch of related but unaccessible problems, and by giving answer to the first you imply the truth/falsehood of all problems thereafter, this problem is important.


*(Develops a tool) If the method you introduce to address the question can be vastly reused, then the question was an important one.


*(Captures the essence in a 'common phenomena') If the question you ask leads to a useful definition or useful conceptual framework for capturing the underlying phenomena you are trying to reason about, then you've asked an important mathematical question.


*(Fashion / Timing) The importance of a mathematical question can rise and fall like fashion. If you are a Pythagorean, figuring out the diagonal of a square was an important question. If you are a mathematician today, maybe the Langlands program is more important.
I think sometimes an important question is one a lot of people cares about and don't know how to answer, but other times, it might be just a handful of people asking the question, yet from having answered this question you are led to a whole bunch of discoveries.
The key word seems to be impact, and where the question leads in the network of mathematical ideas.
(Edit)
A bit more down to earth, no one is going to wake up each day and ask a question that is going to go down history as one of the top 1% questions ever asked. But if you ask a question that by thinking through you refreshed your understanding or just think time was not wasted then it's an important question for you to ask. If you develop this habit of asking a question that advances your understanding, and one day you happen to be working at the frontier of mathematics where nobody understands things quite so well, the questions you ask may well turn out to be important mathematical questions.
A: Beauty. Beauty is important factor. A question may appear irrelevant at first, but if it admits a beautiful proof, that may make the result important. And it does not need to be complex, a proof may be dazzling even in its simplicity.
A: I think most people would agree that the criteria Gil Kalai highlighted are what we, as a community, would say to the layman, or to politicians, or other scientists (say biologists or chemists). But since we are on a math website, I am naïve enough to think we can be more honest.
In most cases, what makes a question important is that the big shots in your field decided that the question is important. This is perfectly illustrated by your feeling about Schur positivity. The big shots in representation theory decided that some questions are important and you feel that people are much more inclined to listen to you if you relate your interesting problem to the questions of the big shots.
But then you may ask "How to define a big shot". The answer is very simple : this is someone who solves important questions. And you get a perfectly virtuous circle of "important people" asking important questions and their students (or post-docs) solving them, becoming in the process the new big shots.
A long (long) time ago, I asked my master thesis adviser why is it that the students of such or such big shot would get permanent position so early in their career, while some other young researchers, who looked more productive, more original and more dedicated to Science in general, would have so much trouble to find a job. And he told me "The answer is very simple : the big shots get the best students to do a Phd with them, they give them the important and interesting questions for their theses and then the students get the best Phd theses, so they get the best positions early on in their career."
Crystal clear!
Edit added later : After afew more thoughts, I would like to argue that the word important should be avoided to describe a mathematical question. "Well-motivated, surprising, fun, well-connected,..." seem to me much more adequate to describe the mental reactions you may have when facing a (new) question.
"Important" is in my opinion a word of power that people with sociopathic behaviours in academia (see for instance this paper) may use to break the career of someone not working in their area ("this paper is not worth being published, it deals with unimportant questions") or to favour the careers of those closely working with them (" this Phd thesis is awsome, it deals with a very important question").
A: I want to point out that you raised two questions, and in my opinion they are very different questions.


*

*So I really want to know how to decide whether a question is worth studying?





*How do I decide what question is important to ask in mathematics?


The answer to Question 1 lies in your personal values, whereas the answer to Question 2 lies in community values.
Importance, as others have explained well, is inherently a question about what the mathematical community values.  The way you learn what is important is by studying the words and actions of the mathematical community.
Deciding whether a question is worth studying, however, is a personal choice. It can, of course, be informed by knowledge of what the mathematical community values. But in the end, it's your time, your mind, and your life that you are making a decision about.  Only you can make the final determination of what is worth investing yourself in.  Part of becoming a mature scholar is setting your own internal compass.
Of course, there are practical realities to consider.  If the community is offering you something that you want, and will give it to you only if you work on things that it considers to be important and that you do not consider to be important, then you may choose to compromise.  Nevertheless, even in such situations, I think you will make wiser decisions if you clearly distinguish between what you value and what others value.
A: Gil gave you an excellent answer already. I'll just add a small piece of advice: when you hear that somebody says that a certain open problem/question is worth studying, add 1 point to the problem score on your scoreboard and when you hear that somebody says that a certain open problem/question is not worth studying, subtract one point from the score of the person who said that.
A: Words like "important" and "natural" are obviously subjective, and that's OK! It shouldn't surprise you to learn that other people have opinions about the value of certain mathematical ideas, just as you probably hope that they aren't surprised that you have opinions, too.
That said, your question suggests a comparison between two types of value judgements: "important" or "natural" vs. "fun" or "curious". The first type suggests that people should work on the problem out of some sense of obligation, whereas the latter suggests that it would be pleasurable to do so. It sounds like you're asking: where does this sense of obligation come from?
The answer is once again obvious: it's determined informally by how the mathematical community allocates resources - journal space, grant money, academic jobs, and so forth. The community has certain informal standards, expressed very beautifully by Gil Kalai's list, for instance.
But presumably those standards exist to ensure that the mathematical community is achieving some sort of larger objective, which makes it worthy of investing resources in the first place. I think that objective is something like "organize and preserve mathematical knowledge". As more and more mathematical knowledge is generated, it becomes harder for even a modestly sized group of experts to keep track of it all. So in order for all of that knowledge to survive in a form that can be easily consumed and appropriated by future generations, there has to be a constant process of simplifying and clarifying the most fundamental ideas.
So that's what I think "important" means. A student today can graduate college knowing how to solve a dozen problems each of which past mathematicians spent their entire lives working on, and it's because the intervening generations isolated a small number of crucial ideas that tie it all together - things like the definition of a limit, or Fourier series, or Galois theory. I think many mathematicians today feel an obligation to provide a similar service for students of the future.
A: Today the iso 2023-02-24, according to mathoverflow, here are the important questions
in mathematics (vote > 200, the word important appearing somewhere).
What to do? is the most important question.
Why is a topology made up of open sets ?
Examples of common false beliefs are also important.
Mistakes are important.
The axiom of choice.
Knowing what is the best algebraic textbook. For some reason, Hartshorne is disqualified.
Again why is a topology made up of open sets ?
The surprising connections in mathematics are important.
What makes dependent type theory more suitable than set theory for proof assistants?
What are the fundamental examples is important.
Philosophy behind Mochizuki's work on the ABC conjecture.
Widely accepted mathematical results that were later shown to be wrong  are important
Finally, rigour is important.
Other questions have not received much votes or failed to name themselves
as important, so they can be decently ignored.
A: In my experience, often "importance" flows from big, challenging problems down to esoteric, slightly-less-challenging problems, in a long convoluted stream that may become totally obscure.
In computer science, we care about P vs NP. Well, we can't solve that. What would be a step toward solving that? Maybe showing that 3SAT requires superlinear time or space. Well, we can't show that. Maybe we can show that restricted classes of circuits can't solve 3SAT (or an even simpler problem). Okay, if that's hard, maybe we can formulate an algebraic version of the question. Okay, solving that involves understanding how intricate a low-degree polynomial can be. Etc.
Oh, but maybe we can't solve that problem either, but we can formulate an analogous problem for polynomials of certain degree over a different finite field, and hope that techniques and ideas developed could lead to breakthroughs in $\mathbf{F}_2$, or whatever (I am not an expert in the area, so I'm making things up at this point).
In the end, you have a continuous stream of "important" papers with results such as improving bounds on properties of the Fourier spectrum of certain polynomials, and newcomers (perhaps even oldcomers) can't trace the motivation any more.
