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thank you for taking the time to read this post.

Some Context on My Background: I am an undergraduate student in mathematics, and I recently coauthored my first paper with my summer mentor. While working on the project, I had the chance to attend a few conferences in the area, and sat in on research seminars and colloquia regularly -- I continued attending seminars, when my schedule allowed, this past fall. For coursework, I've completed "core" subjects of linear algebra, abstract algebra, real analysis, (elementary) number theory, combinatorics + graph theory, and an advanced linear algebra course. My current interests are in algebraic combinatorics, but I'm not 100% sure where I'd want to specialize (and still have a lot to learn), should I get the privilege of joining a PhD program down the road.

I mainly include this section to acknowledge inevitable gaps in my understanding of niche topics, and remain well aware of the "reinventing the wheel" phenomenon in early projects -- Professor Tao's advice on "healthy skepticism" has been helpful.

The Topic -- Brief Overview: Since this post is centered around the research process generally, I'll try to keep my explanation concise, and remain open to any questions/constructive critiques. I'm curious about a class of graphs that resemble a collection of windmill graphs (I've seen various forms of notation for these graphs -- namely $K_n^{(k)}$ and $W_d(n,k)$), all joined at a common "central vertex." Specifically, each of our $n$ windmill graphs, $W_d(m,k)$, are constructed for a fixed integer $k\ge1$ and integers $m=1,2,...,n$, respectively, where $k$ represents the total number of copies of the complete graph $K_m$ in each individual windmill graph.

My motivation for this idea comes from a naive question in linguistics I was thinking about in October, which somewhat "evolved" into something with mathematical structure that I feel more comfortable handling. Initially, I aimed to describe this class of graphs using a recursive style of construction, where edges are weighted based off "distances" from specific vertices, but this method still requires a lot of refinement (I have an algorithm that successfully depicts the weighted graphs with python, but would prefer a formal explanation for study).

I've shared this idea with a few friends and mentors at my university/local universities, and many of them believe the class of graphs could be novel. If this is true, there are some things I'm wondering about:

How does one define and communicate a class of graphs in a meaningful way? What would the structure of the associated paper look like? What graph properties would people be most concerned with at first?

Windmill graphs are well studied -- should I start my literature review by familiarizing myself with results involving windmill graphs? There are so many interesting directions I could see this project going in -- how to choose?

Conducting a Review of the Literature: As noted in one of the questions above, I've begun collecting a few papers involving windmill graphs that could be interesting, but my search has been otherwise haphazard at best. I'm curious how mathematicians narrow their search, especially if the topic of interest is initially quite broad. I also began reviewing Diestel's Graph Theory, to ensure I'm approaching the project with decent and refreshed (general) graph theory knowledge-base; Do others have additional book/resource recommendations in graph theory and related areas?

Mentorship/Talking About My Idea: I know undergraduate students typically have mentors for projects like these... because we often have no idea what we're doing! My summer mentor was great, but I'm not sure this exactly falls into his area of specialty. I also worry that my excited tendency to share the idea, with various mathematicians I meet, will make me seem immature/annoying -- if I don't do it correctly. Thus, I'm wondering:

What's the best way to open up these conversations? Do I need a mentor at this point? If my ideas aren't developed enough for mentorship, what else should I focus on? Who/which specialties might be interested?

Overall Process + Misc.: If I'm able to refine this idea as I hope, how do I organize ideas for -- as mentioned in the literature review portion -- a general class of graphs that one could say possibly many things about; how many of these "directions" should I realistically focus on? (my previous project involved proving a specific conjecture, so less of these specific skills were touched upon -- although I learned a good deal about organizing the smaller pieces of that idea + reading academic papers).

Finally, how do I go about judging the "significance" of this work -- is it even valuable/possible to do at my career stage, or should I be more focused on learning/enjoying the process. Since I'm still building my foundations in math, I probably ought to refrain from dedicating myself to lossy "rabbit-holes," over working on my problem sets, once the spring semester starts up...

I'd appreciate any thoughts you may have. Thank you again! (below are a few figures depicting some variations of the graph, should you be curious)

Images of Graphs: for $n=4$ and $k=1,2,...,6$ respectively

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I want to preface this by saying that I'm only slightly ahead of you on my career; I'm a masters student, expected for next July, who's just getting into research on graph theory (mainly extremal and random graph theory); so you might want to take my opinion with a grain of salt. First of all, congratulations on your paper! It's really uncommon for undergrads to write actual papers of actual siginificance. I'll try to answer as many of your questions as I can with the little experience I have.

First of all, just because something is novel, that doesn't make it interesting, and just because something is interesting, that doesn't make it relevant. I could come up with a hundred different families of graphs; and ask a million questions about them; but that doesn't make them worth your time. A good rule of thumb, as my advisor told me once, is "[at the point you're at right now] Most anything that you can come up with, that wasn't asked by someone else, is not very relevant or interesting. Focus on solving problems others posed, and then, when you have a stablished career, and results to back it, you can start asking novel questions. If Noga Alon comes and says 'here's a problem I thought about, and solved' that can be interesting, but that's because that's Noga Alon; once you get to that point you can start doing stuff like that".

Right now you don't have a problem, just a definition; you haven't even asked questions about them, nor is it clear how they're related to stuff people have been thinking about. It's not a natural definition and there aren't any natural questions to ask about them that don't apply to literally any other family of graphs I could define.

So, after all of that; how do you figure out which problems are worth your time? That's where your advisor comes in; they're someone who's been working on the area for decades, has a lot of experience and can guide you to which problems are worth thinking about. For instance, there's no much point in thinking about the union closed sets conjecture at this point; because it's too hard; so maybe focus on some recent papers and see what follow-up questions they asked, what couldn't they do and how might you approach that. Again, your advisor is a really great tool to figure out what techniques you might try, or whether it seems like something doable.

In that same line; choosing a problem that someone else asked gives you credibility whenever you want to actually publish something (research is not just about posting on arXiv, you aslo have to actually publish on peer-reviewed journals). You solving a problem by some already stablished mathematician gives the journal much more reason to puiblish than just "some random thought about a problem no-one's ever cared about and solved it" (I know it sounds harsh but that's the way it works)

Graph theory, (or at least the stuff I work on) is a super accessible area, where you actually don't need mountains and mountains of theory to get into research (as it is the case with most other areas of math), for instance, just with these lectures you're like 70% of the way there to be able to understand and do stuff in extremal and probabilistic combinatorics. I don't know if that translates to algebraic combinatorics, but I wanted to mention it either way.

Choosing problems that come form someone else asking them also eases the process of looking up references, since whoever wrote the paper already did that for you! Having an advisor I think it's probably the most important part of getting into research, they have experience both with research and with the area, so they can guide you with references, academically, with ideas and if you have a good avisor even spiritually. Start by looking who at your college does the stuff you're interested in. Since you took it out from your profile since I started writing the answer, I won't directly reference any professors that you might want to contact.

Another important thing, is thinking about specific problems (which you weren't doing), a good piece of advice that my advisor gave me (they have the name for a reason) passed to him by B. Bollobás, who was his advisor; is to be actively thinking about one or two problems at most; while having some 7 or 8 in the back of your mind at all times.

That is most of what I can recommend when it comes to research. Asides from that, you have no rush to get married. Mathematics has so many areas that you are probably still to get to know. How much ergodic theory do you know? How about algebraic geometry? Probabilities? Or even just probabilistic graph theory? There's no rush to choose algebraic graph theory; you still have plenty of time to decide; and it's probably for the best

I think the main take aways are that advisors are super important; so talk with professors of whichever area you're interested in, at this point it's better to think about problems that others posed, and that there's no rush. Enjoy the trip; think about problems, read papers; but don't pigeon-hole yourself too hard; you'll have plenty of time to get stressed when you start your graduate studies hahahaha.

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  • $\begingroup$ Thank you for the advice, and I apologize for my late response! All your points make sense, and I definitely won't rush things regarding research and specializing too early. Right now this is still just a fun idea (for when my mind wanders), and I've been able to speak with a few experts who had interesting ideas. If it connects to something significant, that would be cool, otherwise I'm enjoying the chance to explore math outside of problem sets! $\endgroup$ Commented Feb 1 at 19:46

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