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I have just recently completed my Ph.D. Throughout my Ph.D., I’ve been fascinated and motivated by incremental and focused questions that would show up in my research, either imposed by my advisors, or ones that I would figure out need addressing. I genuinely enjoyed getting into the nitty-gritty details of my research. I believe that this attitude has let me thrive in a Ph.D. program and produce good research.

But, as a result, I feel like I’m driven by curiosity only when I have a specific question to tackle (like, “I wonder what happens when I set this parameter to...”), but I have no interest in the big-picture questions of science or vision for my future research (like, “How do machines learn?”). I think I haven’t yet developed interest or skills in finding such a vision. My Ph.D. advisor has his long-term goal for his research group, but being his Ph.D. student, I never cared about or was (directly) influenced by that goal. In some sense, I couldn’t care less about what my advisor’s lab wants to develop long-term. All I genuinely cared about was another hurdle in my narrow slice and the tiny curiosities that would show up along the way.

I would like to stay in academia and apply for a TT position after my postdoc. Professor Patrick Winston mentioned in this talk, that the TT applicants have 5 minutes to convey their vision and their contributions to the hiring committee. I think that I would fail that test if I were to apply right now. I would like to develop that vision, and be able to one day say: “My lab aims to understand how machines learn.” (just an example).

I’m looking for concrete advice on actions that I can take in the coming months/years to slowly start developing this big-picture interest in my research field. Is it normal that I don’t have that interest yet? When should such interest start to emerge in me for me to be a successful professor and researcher?

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    It's worth remembering that this 'big picture vision' is largely a marketing spiel. It doesn't really matter whether it neatly aligns with all your personal motivations and interests - it just has to convince customers (i.e. a hiring or funding committee) to buy your product (i.e. you).
    – avid
    Commented May 7, 2023 at 18:25
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    @avid Thanks, I never thought about it that way. I guess I now want to ask a different question: Does having a big picture vision help run your lab? :) And I mean: in a sense that it becomes a true guidelight for the PI. Or is it only helpful when showcasing your lab?
    – student
    Commented May 8, 2023 at 10:59
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    @avid I agree with you that the "big picture" is often overrated when you're young, but you do need some vision. If you just pick problems completely at random, it's unlikely they will be of much interest to others.
    – Kimball
    Commented May 8, 2023 at 15:17
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    To your question of if it's helpful to a vision: it's necessary to have some vision to write grants and collaborate with researchers long-term. You're not limited to it, certainly, but thinking at the level of dissertations and grants (and not papers) is the responsibility of a professor. But if your focus is papers, and you're good / enjoy at writing papers (sounds like it) then I think you'd certainly be able to adapt to higher-level visions. Commented May 8, 2023 at 20:21

5 Answers 5

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As per the usual, there's every reason you should ask your advisor this question if you have a good relationship. I'm due to start a TT job at an R2 this upcoming fall, and I'm now trying to leave 15+ minutes of every meeting asking my current boss questions about how he approaches the work.

Is it normal that I don’t have that interest yet?

It's not unusual to feel like you don't have an entire program ready to sell at the end of your PhD. But you've correctly identified that if intend to try landing a job as a TT professor at a research institution you need to start developing a program and pitches.

I have no interest in the big-picture questions of science or vision for my future research

I'd urge you to think really carefully about this. If you want to be a professor at a research university, your highest priority responsibility will be articulating plans for future research and then executing them both yourself and with students. Hiring committees want to be convinced you have a program and some vision, because a primary component of that responsibility is pumping out significant numbers of project ideas for decades.

If you're in STEM, there are multiple times more remunerative career paths available to you than trying to become a professor. Those have less intellectual flexibility, but still a lot of interesting problems with potential for intellectual contribution. I'm not trying to put you off your professional plans or goals, but think this might be a useful perspective. I just ran this gauntlet and got a TT job at the last moment, and still have doubts whether it'll end up having been the best decision.

I’m looking for concrete advice on actions that I can take in the coming months/years to slowly start developing this big-picture interest in my research field.

In short, start practicing. Just off the top of my head:

  1. Start reading your senior colleagues' research statements. In mathematics I usually find a short version on their websites. A minority of professors also post their job search materials, so you can get your hands on what they actually sent to a committee that way.
  2. Draft a research statement yourself. The act of trying to do so is, at least in my experience, initially frustrating. That's because it forces you to think and articulate a program that's distinctive from your advisor's. I'm shocked you didn't have to do this for postdoctoral positions, but maybe that's just a difference in subject culture. This takes time away from your research, but it's worthwhile to have drafts of these things well in advance. You can send drafts to your mentors for feedback months before due dates that way.
  3. Develop spoken "elevator pitches" for your research at lengths of 1 minute, 3-4 minutes, and if you like 5 minutes. You can also do this for individual projects, but your entire program is also useful. These are useful at conferences anyway, and explicitly doing the exercise should sharpen your ability to contextualize your research. Get feedback from your friends.
  4. Talk to your advisors and mentors about this question. Also about writing grants, which is highly related. Coming up with a pitch for your program that is unique and interesting is not easy, but that is your goal. Your colleagues have distinct perspectives on developments in your general area of research, and probably even hiring more generally. They're not going to be able to tell you what to do, but can be very useful at helping you identify your strengths (to emphasize) and weaknesses (to distract from).
  5. Start thinking about and integrating motivation about your broader program, or at least pieces of your broader program, into all of your research talks. This will also improve your talks. One thing I notice about greener PhD students' talks (my own included for a few years) is that they often include too little vision at the beginning. If you're aiming to become a permanent researcher, part of your goal is to get as many of your colleagues as possible to remember you, what research you do, and why they should care about it. You don't need to be saving the universe, but view and present yourself and your research as consistently shedding light on distinct and interesting aspects of the fields it interacts with.
  6. Start paying particular attention to the programmatic elements of the talks colleagues in your area give at conferences and colloquiums. That both gives you context about how other people are thinking about things, but also gives you the chance to think about how to stand out against your colleagues who are going to be on the market around the same time as you.
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So, full disclosure, I'm a PhD student still and I'm still learning and growing myself. But, I think I kind of might have an answer here. Your research is driven by (in part) personal curiosity. You thrive in those details of whatever your interests are, and you have little to no interest in the so called `big picture' questions that scientists ostensibly are kept up late at night over.

Okay. That's great!! Why deviate from that path? I myself am the same way. Last semester (or two semesters ago now, I guess), I took PHD logic of policy inquiry at the Georgia Institute of Technology. In it, we read Thomas Kuhn, whose book consisted of discussing the process of revolutionary development in science. To be simplistic, we essentially have two kinds of scientists: those who take a Bird's Eye view of their discipline (how do machines learn, how does facial recognition software influence popular opinion, how do Black Holes prove some physics theorem), and people with very very focused views of their discipline (How to do donor selection for synthetic controls in econometrics, how can we use LASSO or other ML ideas to better predict counterfactuals, how do we asymptotically justify using this penalty for this estimator...)

My point is, there is no right way to play. Both paths will lead you to your intended experience. `Big picture' work always builds on the "small picture" work. It is partly by that process, argues Kuhn, that we make advances in science on those big picture questions, yes, by having people who dedicate their lives to big picture questions, but ALSO by having researchers like you who are very narrowly interested in developing part of your field.

I'm a public policy PHD student. Most of my cohort have very specific substantive interests (labor market policy, housing, etc.). But I don't! I'm an econometrician, a statistician who's interested in methods used for causal analysis of policy. I'm not married at all to any field or set of topics, I have papers in the works in policy, criminology, marketing science, and other areas. What I'm married to, is econometrics and advancing certain causal models in my field and to anyone who would find them useful. Even if I'm not working on some big picture question, my work and skillset is still valuable,

So, my advice to you is to explore your curiosities. Make them your own, and publish great work in great journals with it. It's perfectly okay not to be really into big picture questions as a matter of profession. You like what you like, and that's okay. Academia is about finding your own path. Find your own path, and make no apologies for your work not sounding as earth-shattering as other people's. I guarantee you, even if your work isn't "how do machines learn", the quality work you do will be used by the people who are answering that question, to eventually have those pathbreaking discoveries.

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    Thank you for sharing your perspective, it's a comforting one for sure. Thanks for a book recommendation too! "I'm not married at all to any field or set of topics" -- I think it's very similar to my situation. I can imagine developing those little curiosities in so many disciplines.
    – student
    Commented May 7, 2023 at 14:57
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    I would still like to hear someone's perspective though on how your recommended strategy will work out in applying for TT positions. I could probably convey to a hiring committee my interest in answering a very specific research question, but would this be enough to hire me? I imagine them saying: okay, that's work for one journal publication, what do you plan to do after you have that published?
    – student
    Commented May 7, 2023 at 14:57
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So like other answers, I definitely recommend talking to your advisor if you have a good relationship with them. I'll also echo @avid's comment that this is largely a "marketing spiel" in the sense that you don't in any way have to limit yourself to the "vision" that you label yourself with. Nevertheless, a large portion of the work of a TT position is some form of "marketing" (I recommend calling it "getting other people excited about what you're excited about" instead). The benefit of having a good, pithy explanation helps communicate what you're excited about and what you want to work on.

My context is that I just accepted a TT position at an R2 starting next year in computer science in the US. I had the benefit of a failed search last year, so I didn't have to start this year's job search with a lot of work already behind me. It's OK for the development of this vision to feel exceedingly slow and difficult. Taking the time to actually think about this vision was really hard (my research statement was a high priority for weeks, and there were several times it was substantially re-written with advisor and mentor feedback). But the benefit is that it's a line of thinking I've got developed for the next 5-ish years.

First, I think it's important to understand what you're developing, exactly. From the tone you have (and the example of "how machines learn") I think you might be looking for too grand of a vision and intimidated by that prospect. I found this article by Yitong Yue very helpful when working on my research statement, and I'd like to highlight two paragraphs in particular.

An Interesting “Medium-Level” Agenda. It’s relatively easy to craft a good high-level agenda (e.g., AI for Science, AI for Social Good, Protein Modeling, Real-World Robotics, etc.). It’s also pretty easy to get into the details of your research (e.g., summarizing the key findings in individual papers). However, it is the medium-level story that often ties your research agenda together in a coherent and intellectually interesting way. The alternative is to jump straight from a relatively vague/abstract high-level story into what might feel like a laundry list of projects and results. What are the key insights that propel you forward when you seek out new projects? Why are your previous results realizations or instantiations of these insights? Based on my experience advising and evaluating faculty applicants, this is the most important thing to work on. (emphasis added)

And here's another, specifically about what that vision is valuable for, which can help you evaluate whether a vision is good or not:

Frame Future Work in Terms of PhD Thesis Topics. A heuristic I like to follow is to list future directions that can be compelling thesis topics. The supporting sentences in the paragraph on each future direction might then point to specific results (e.g., specific papers you might write). Don’t present future directions that are scoped at the scale of individual papers, as those don’t really support your medium-level agenda.

In other words, if you have a vision that can inspire 3-4 dissertations, which is certainly an order of magnitude work larger than a paper (at least in my domain, yours may be different), you have a good vision. "How machines learn" is too broad - I'd categorize it as one of those "high-level agendas".

I was able to develop my vision (medium-level research agenda) over several conversations with other researchers, my advisor and mentor, and even conversations with friends and family (they often have good ways to phrase insights that are a lot less academic).

I'd also say that my advisor's mid-level vision(s) were ones I agreed with and saw the value of but certainly wouldn't have made them my own, so being lukewarm about your current advisor's vision doesn't count you out either. I certainly borrowed big ideas from my advisor and his work, but I had a chance to re-prioritize those values and set them in a different light.

You mentioned you enjoy those "tiny curiosities" - I think those are the starting grounds of a mid-level vision. Why do those curiosities strike your curiosity? Why do you find them interesting and others might not? What about your background or your interests makes you well-suited to tackle those? That unifying theme isn't necessarily some type of application or theory - it could be a method, if you focus on why that method (not just the algorithm) is 'interesting'. Also, I think I used about half of my work in my PhD in support of my vision - it doesn't have to encompass all of your (previous or future) work. If you can write a statement that feels like a good way to sum up a sizable portion of the work you've done so far and leaves room for future work, then that would seem like a good vision.

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I’m looking for concrete advice on actions that I can take in the coming months/years to slowly start developing this big-picture interest in my research field. Is it normal that I don’t have that interest yet? When should such interest start to emerge in me for me to be a successful professor and researcher?

We have research on this! From Huang et al, 2022, we know that successful researchers are able to exploit academic hotspots, while exploring emerging topics and combinatorial innovation more during their early career and exploring diverse interests during their later career, putting less emphasis on exploiting mature topics.

So if you want to hone your research acumen, you should learn how to explore emerging topics and combinatorial innovation -- that is, what are new and interesting trends in your field, and what are some unexpected ways in which your field combines with other fields?

Note that knowing what is new in your field requires you to know what is old in your field, and also requires deep curiosity about what everyone else in your field is doing. For example, you should eventually know who the few most interesting researchers in your area of interest are, and roughly what they are doing, and why they are pursuing their particular area of interest and not another. The granular, social understanding of your field is what your subconscious processes so that you can eventually carve out your own niche. And when you say:

My Ph.D. advisor has his long-term goal for his research group, but being his Ph.D. student, I never cared about or was (directly) influenced by that goal. In some sense, I couldn’t care less about what my advisor’s lab wants to develop long-term.

that is a significant red flag (unless you've developed your own peculiar vision -- but you haven't!). Every other researcher you meet has a research strategy, and the more you learn about others' research strategies, the more you are able to craft and articulate your own (even if as examples of what not to do).

Here are some specific questions you can ask yourself to hone your research vision:

  • Are there specific papers or journals I cite disproportionately often in my work? (That's a sign of an emerging focus of your interest, and is easy and objective to determine.)
  • What are the key terms in my field, and how would I define them and why they're important? (For example, when I read your question, I immediately googled for "explore / exploit scientist" -- which tells you a great deal about how I understand scientific innovation.)
  • Who are the most interesting people in the field, and what are they doing, and why?
  • Why do I care about [parameter I'm optimizing]? What's the range of possible improvements I expect to get? If it's a large range, why is that parameter so crucial? If it's small, should I really be bothering with it?
  • If I wanted to brainwash attract a PhD student to help me on a project, what would I ask them to work on? How would I pitch it to them?
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Answering this as a new assistant professor: I agree this is a real challenge! It may help to note that this is a very good problem to have: it's much easier to start from specific technical expertise and "zoom out" to a broad research agenda than the other way around. This happens all the time among more established researchers -- it's fundamental to managing a research project and getting funding.

To do the process of zooming out, I think there are two components: First, establish your expertise; and second, establish your agenda.

Establish your expertise

To find your expertise, you can start with your individual paper abstracts. What does each abstract say to sell the paper? Additionally, what are several key results -- such as an experiment or buzz phrase (e.g., you are 10x faster than some other technique, first to do XYZ, etc.) that you can lift from that paper? Do this for all of your papers, and you may find a pattern. Are there several distinct lines of work? Are there common themes? "cluster" these into groups and identify what do your contributions mean in aggregate for someone who has never heard of your research before.

Then, try to condense this to a simple sentence like I work on X or I'm an expert in applying Y to Z. Typically, it is as simple as the jump from "I studied how to use nanofunks to create foobars with applications to thingamajigs" to "I am an expert on nanofunks and foobars". Once you have a pattern of important results in an area, experts will trust you to know some things about that area, what are the typical techniques, and what things are often difficult and lead to unsolved problems.

This process can even be surprising -- sometimes as researchers, when stuck in the details, we don't fully recognize our own strengths and expertise in an area. For example, maybe you have published 3 papers in a general topic X. That fact alone often makes you stand out quite a bit compared to other researchers, and you are now (surprise!) an expert in topic X.

Establish your agenda

Second, you need to establish your agenda. This is a similar process to before, but this time, focus on the future work and unsolved problems for each of your research papers or projects. What are some things that would be nice to have? Often you will have a dozen ideas for each project, and you can list these out. Then, how do these fit into a common theme that might take 5-10 years of work to play out?

Try to be interdisciplinary about writing down your future work. Compared to establishing your expertise, future work should be ambitious, collaborative, and exciting. You can, for instance, introduce future work in an area you have never worked on before (e.g. applying thingamajigs to health science), if you think it ties in to the general agenda you lay out and sounds fun to do. You can also list some future work that is specific to your area, but I find researchers are much more likely to get excited about general collaborations.

When thinking about your broader agenda, it's also helpful to identify any common themes in your research process (rather than just research content) that distinguish you. What is your "secret sauce" that you can apply to any area and generate interesting ideas? For example, do you think more theoretically about problems -- looking for the foundational principle behind a particular phenomenon? Or do you prefer to start from a concrete application? Do you like to do data-driven research? Do you like to work incrementally building on past results, or do you like to pursue broad crazy ideas?

Other suggestions

This sort of process is extremely iterative; you won't get it right the first time. It will take successive refinements and lots of conversations. So it's critical to do lots of things to broaden your exposure to other researchers. For example:

  • Take every opportunity to interact with others in your department;
  • Get feedback on a draft of your research statement;
  • Attend conferences in your field;
  • Attend talks, especially those not in your area; and
  • Talk to experts and mentors to hear how they think about broad agenda and the future of your field.

Don't be afraid to ask the big questions, like: What are the important problems of your field? Think about other researchers in your area or related areas. What are they doing that is most impactful and most relevant to the broader community?

At the end of the day, there is no substitute for practice: practice speaking, practice giving your 5-minute elevator pitch, and practice writing -- ideally write a bit every day. Research problems can be very specific, but broader ideas can only take shape by being refined and simplified over time.

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