Need for support and guidance for my near future as a PhD student (or: has stable homotopy theory become an overly algebraic theory?)

Question

The question in brackets in the title is my main mathematical question, but does not reflect my initial motivation for writing this post. It is in fact above all for personal reasons that I'm affording to call on your experience and your advice.

I will be starting a PhD next year. I don't know yet with whom, or exactly what I want to get into. I have long been interested in the topology of manifolds, and seduced by the algebraic approach to problems of a topological nature. I like algebra, but questions of purely algebraic nature have always interested me less: for example I have never been concerned with arithmetics or technical commutative algebra.

It has been clear in my head for a long time that I will be doing algebraic topology as a research subject. I really enjoyed all of the introductory courses, then came an introductory course on model categories. For the first time, I completely forgot why I was there, what I was doing. Now I have a lot more perspective, I know how to appreciate the benefits of this theory and I understand its motivations. However, I am still as repelled by the "obscure formal arguments" side that this theory can have. Then came a course on infinity categories/operads, which I decided to abandon before the end, telling myself that the day I need it, I will take it up calmly, having clear ideas and motivations. The reason I am describing all this it is to emphasize my view of mathematics: having concrete motivations for studying something, if possible coming from topological situations, and use formal and technical theories if it is appropriate. I love abstract theories but only if I can see why they are useful.

I am currently working on a master's thesis, and I will have to find a PhD before the end of the year. I am currently doing stable homotopy theory, I really like it for now despite the profusion of algebra. In particular, I'm studying Thom spectra, and I was initially very seduced by their link with the classification of manifolds up to cobordism. Also, I enjoyed learning this theory (stable homotopy theory) because of its power to prove concrete results ("external to the theory") such as: which spheres have multiplicative structures, how to find a good framework to compute various cobordism groups, how to properly study loop spaces, understanding the homotopy groups of spheres. I must admit that I am a little confused by the subject on which I am offered to work: is $H \mathbb Z / p^k$ an $E_n$-Thom spectrum for $ n> 2 $. It's interesting for sure, but I have no idea of ​​the motivation to study this question, if not a motivation that I would call a "formal motivation": it is formally natural to ask this question. But I have no idea of ​​the geometric issues that may be behind it. We are gradually moving away from Mahowald's theorem which is directly linked to the cobordism of manifolds. What's the point?...

If I decided to put everything on the table on mathoverflow, it is because the people who supervise me do not seem to understand my disarray. I'm very interested in stable homotopy theory, but when I'm working on something, I want to know "why". I want to know the concrete motivation. So far, I have let myself go and have worked on the subjects that have been proposed to me, because I have not met anyone who has really been able to advise me. Today I can no longer afford that, I have to find a PhD and if I choose the wrong person or the wrong subject (in a general sense) it will have too much of an impact on my future.

Here are some mathematical questions: are some people working on stable homotopy theory from a purely geometric prospective? How much has stable homotopy theory moved from its initial geometric goals? Is it necessary to do algebraic geometry to do research in stable homotopy theory? I know that people here like really concrete questions and I am sorry to be that confused and clumsy. I just hope that, first, it is ok to write this kind of post here; that maybe some of you will identify with my experience and will be of good advice, or that experienced researchers in homotopy theory will kindly accept to help me get on the right path. I really feel lost right now.

Answer 1

I wrote an answer where I tried to address the explicit questions the OP stated, but I feel like there is more to say, so I'm writing a separate answer. Here are some things the OP wrote.

"I have to find a PhD and if I choose the wrong person or the wrong subject (in a general sense) it will have too much of an impact on my future."

I disagree with this statement. I definitely understand not wanting to make mistakes or waste time, but math (and life) is a journey. Sometimes that will involve changing course. Plenty of people choose an advisor and after a while realize they're a better fit for a different advisor. Same for field of study, research group, or even university. Plenty of people get a PhD in homotopy theory and then decide to get a job as a data scientist (spoiler alert: skills with model categories do not translate to skills in data science, and I can say that as someone who has worked in both areas). The OP seems to be feeling a lot of pressure, and I'd advise taking a deep breath, trying to take a big-picture view of mathematical studies (and life), embracing that it's a journey, and mentally preparing for the inevitable setbacks.

"It has been clear in my head for a long time that I will be doing algebraic topology as a research subject"

It's rather surprising to hear this, from someone who has not even started a PhD program yet. Part of doing research in an area is learning the main techniques that are used in that area. How can you say for sure that you'll work in this area, before you've even learned the basics (by which I mean, graduate-level basics rather than undergraduate-level)?

An analogy is useful. Imagine an undergraduate who is convinced they want to do research in linear algebra, because they love row reducing matrices. Nowadays, it turns out not to be very important to row reduce matrices by hand. When this undergraduate learns this fact, and learns about abstract vector spaces, they lament that the field has been ruined. Instead of framing it as "well, now you can't do linear algebra," it would be better to build on the strong motivation the student has already exhibited. One could tell the student to learn that it's possible to do computational research without this abstraction, or could explain what kinds of problems the abstraction helps clarify. Proper motivation, plus empathy for the student while they get comfortable with the new abstraction, is the way to go.

The OP listed many awesome results from the 1940s-1970s, that serve as a great motivation for getting into stable homotopy theory, but those results have already been proven. There is no reason to expect them to be representative of the state of the art today. Most researchers in this area could, if pressed, draw a line from their current research to those old motivational results. But clearly that doesn't mean the OP would enjoy each potential area that has grown out of that old work. This is why my other answer focused on finding subfields of algebraic topology that the OP might like, based on their expressed preferences so far.

I am still as repelled by the "obscure formal arguments"

While I do understand this feeling, I think it's worth interrogating. I believe that building comfort with "obscure formal arguments" is an important part of certain areas of math. You've actually done this before, many times, because it's the essential nature of abstraction. Children start off by working with very concrete things. Three blocks plus two blocks equals five blocks. Then comes the abstraction of negative numbers, a general algorithm for how to add two numbers, etc. Soon enough comes variables and expressions like $3 x = 6$. The abstraction machine keeps going at university, and grad school is even more abstract. Many people get fed up with abstraction, and exit math at various points. Most readers will have met people who say "I hate math" or "I'm terrible at math" because they exited rather young. At my university, students who don't like the abstraction they see in calculus often become physics majors instead. Those who don’t like the abstraction in linear algebra generally become applied math majors instead of math majors. In grad school in the US, exposure to the first-year qualifying exam courses helps students figure out which branch of math they want to work in, and comfort with abstraction (vs preferring concrete combinatorial arguments, etc.) is part of that decision. This doesn't mean the field you rejected is "bad" or "has become overly algebraic." It just represents that maybe it's not your cup of tea, and that's perfectly ok, both for you and for that field. We need mathematicians of all types. Also, it's entirely possible to be uncomfortable with a particular abstraction right now, but become comfortable with it later on.

Let's consider another analogy. The question "has stable homotopy become too algbraic" is analogous to the following questions:

1. Has number theory gotten too schemey? Why do I need to know anything about schemes or categories to prove results like Fermat’s last theorem, since it can be stated without that language?
2. Has graph theory gotten too probabilistic? Or too algebraic? The answer is that probabilistic techniques like random graphs provided an important way to answer questions of broad interest, including bounds on Ramsey numbers. And, techniques of Robertson-Seymour, involving algebraic concepts like pre-orders, have proven statements in graph theory that a priori have no connection to those techniques but are nevertheless extremely important to working graph theorists.
3. Has analysis gotten too logic-ish? Sometimes amazing results have been proven by bringing in techniques from logic (e.g., the continuum hypothesis, or almost any proof by Shelah). I’m sure that made some folks uncomfortable, but others learned those tools and now can use them to prove similarly amazing results.

I hope these analogies help make my point. Certainly it’s possible to be successful in the three fields above without the tools I mentioned, but refusing to engage with those tools does tend to limit one’s impact. The same is true of stable homotopy theory. While it's possible to work in that area without the tools of $\infty$-categories, model categories, or operads (as my other answer explained), having facility with these tools might help you solve problems you're interested in. There is no need to develop this facility all at once, right at the start of your journey, and the OP already knew this, writing:

"telling myself that the day I need it, I will take it up calmly, having clear ideas and motivations"

That's spot-on, definitely the right way to go. My expertise is in model categories and Bousfield localization, but my motivation for getting into algebraic topology was the same as the OP's, going back to questions regarding stable homotopy groups, multiplicative structures on spheres, cobordism, etc. I was lucky to have an advisor with broad interests, great explanatory/motivational skills, and a lot of patience. When we started working together, I read his book about model categories and didn't understand why this was important at all. I actually hated model categories. So, I asked for a problem not involving model categories. And he gave me such a problem. I worked on it for about a year, and didn't manage to solve it. But, as I kept coming up with ideas to hit this problem, again and again I came up with approaches rooted in localization. That led me to want to learn about localization in a deeper way, and eventually I picked up facility with model categories. Having the right motivation (and a bit more mathematical maturity) really mattered! That first thesis problem is still unsolved. The second problem my advisor suggested built on my interest in localization and probably could have been answered without model categories or operads. But, the more I learned about localization, the more I liked the abstract way of thinking about it. In the end, I wrote a thesis that solved that second problem as a special case of a much more general theorem involving model categories, Bousfield localization, and operads. And that gave me a research program that I've quite enjoyed in the ten years since then. I'm by no means the only person who was reticent to adopt abstract techniques. Peter May has written a lot about how, early on, he resisted model categories, but eventually came to embrace them. You can read many of his answers on mathoverflow.

One last comment the OP made:

"my view of mathematics...having concrete motivations for studying something, if possible coming from topological situations, and use formal and technical theories if it is appropriate."

I think most algebraic topologists share the same view. Almost every piece of research has some motivation. Usually, the authors also have a deeper motivation, which you might be able to read about in the introductions to their papers, but you can definitely read about in their research statements and grant proposals. Believe it or not, most people are not developing theory purely for its own sake. Of course, some papers do develop theory, but usually the author has some idea about what it will be good for. As I wrote in my other answer, one should never be afraid to ask for motivation. This can be done with your advisor (or a potential advisor) but can also be done at/after seminars and conferences. In math, we have a culture of writing the cleanest proofs and definitions, and not always showing the steps that got us there. This can sometimes hide the motivation, or make it harder for a student to follow. Pushing back against this style of writing was part of the motivation of a group of homotopy theorists in writing User's Guides to their papers. I mention this in case the OP (or any other reader) is curious about some of the motivation that doesn't always make it into the final, journal version of a paper.

Answer 2

I’m surprised that this question never received an answer (though it did receive many helpful comments) despite being so highly upvoted. I will try to answer.

First of all, I think it’s great that the OP has "long been interested in the topology of manifolds, and seduced by the algebraic approach to problems of a topological nature." Motivation is one of the most important aspects to being a good mathematician because the nature of our work is to constantly pit ourselves against very hard problems, and spend most of our time not actually understanding things. Likewise, I am dismayed to read that "the people who supervise me do not seem to understand my disarray" and "I really feel lost right now."

It seems clear to me that the OP needed guidance from a mentor who could take the time to explain the importance of the research questions being proposed. My view is that research students should never be afraid to ask their advisors for motivation. It is extremely hard to do research under the best conditions, and doing it when you don't even know why you should care is even harder. The student will eventually need to understand the motivation, or else they will not be able to write a reasonable introduction to their resulting paper, won't be able to craft a research program, won't be able to explain their research in interviews, etc. So it's in the best interest of both the student and the advisor for this motivation to be provided up front. If a student is telling their advisor that they want to understand why the research is important, and the advisor is unwilling to explain it, then this student probably would be better served with a different advisor.

The OP asked four questions. I get the sense that the OP defines "overly algebraic" as anything to do with model categories, infinity categories, or operads.

1. Are some people working on stable homotopy theory from a purely geometric prospective?

It depends on what you mean by "purely geometric" but certainly plenty of people are working in stable homotopy theory without anything to do with model categories, $\infty$-categories, or operads. It was suggested in the comments to look into the work of Kupers, Randall-Williams, and Galatius. You can also look at Dev Sinha, Michael Weiss, John Klein, and Pascal Lambrechts. You should also look at the students of these people, like Sam Nariman, and look at who they are citing in their papers. It also might be worthwhile to look into low-dimensional topology, e.g., work of Benson Farb, Andy Putman, Shelly Harvey, Adam Levine, Akram Alishahi, etc. Google is your friend, and it sounds like "ability to motivate their research" (which is related to writing good introductions) is part of your selection criteria.

(2) How much has stable homotopy theory moved from its initial geometric goals?

Again, stable homotopy theory is a very broad area. Like the OP, and probably most homotopy theorists, I came to this subject after enjoying topology and algebra, and getting interested in cobordisms, stable homotopy groups, and algebraic structure in homotopy (e.g., wanting better invariants). From that starting motivation, there are different ways to go. Some people get at the problem via chromatic homotopy theory and generalized cohomology theories (which are, generally, easier to compute than stable homotopy, but still shed light on the latter), like the $E_n$ question in the OP. Some use equivariant homotopy theory, e.g., the great work of Hill, Hopkins, and Ravenel, resolving the Kervaire Invariant One problem, which no one had been able to solve from 1969 till 2009. This work also relied on model categories and operads, because that language provided great tools for organizing information (e.g., all the multiplicative norms) and for computations. Others have recently been doing computations in the stable homotopy groups of spheres using motivic homotopy theory, e.g., Dan Isaksen. So, these "overly algebraic" tools are actually very useful, if properly motivated. That said, it's still possible to do good work in stable homotopy theory without these tools, e.g., people do work on diffeomorphism groups, loop groups, and string topology (just to name a few examples) without these tools, though note that even in the wikipedia page for "string topology" the word "operad" does appear because it's a useful way to keep track of algebraic information.

(3) Is it necessary to do algebraic geometry to do research in stable homotopy theory?

Certainly not. I gave plenty of examples just above that do not use algebraic geometry. The only ones that do use it are chromatic homotopy theory and motivic homotopy theory (and for Isaksen's computations you actually don't need anything from algebraic geometry).

(4) Has stable homotopy theory become an overly algebraic theory?

I think most people who identify as (stable) homotopy theorists would say "no", because the evolution of the field has provided powerful tools that have yielded real results, to questions whose formulation had nothing to do with $\infty$-categories, model categories, or operads, like the examples I gave after (2) above. Of course, because stable homotopy theory is a broad area, some whose work does not use these tools might be annoyed that these tools are getting so much attention, but it doesn't really stop them from doing their work. I used to be afraid that referees would want me to rewrite my papers using the language of $\infty$-categories, but it never happened. I think most mathematicians take the point of view that there's plenty of math to go around, and different people have different interests, tastes regarding solutions, and comfort with the wide variety of tools available. My point is that it's a big tent, and you're welcome to join the community, even if you want to use a more geometric approach and never write a paper with the words "model category" or "$\infty$-category."