The most important thing you do in graduate school is your research. It may seem obvious, but it's easy to lose track of the importance of your research amid all the other competing things you’ll be asked to do as a student researcher: take classes, TA a class, submit and review papers, respond to paper reviews, organize/support various activities, etc. Some of these will be fun; many will feel more important at the time than making progress on your research. However, I would like you to prioritize your research and triage everything else after this.
I advise students to aspire for impact in their work. Not by accident, this is also what I hope for in my work (which intersects and overlaps with your work). It's important to have impact in mind when approaching problems (before you select and commit your time to them). Some guidelines on impact might include:
What difference will this work make if you succeed?
- Whose lives will be made better by this research?
- How will this non-trivially improve upon current state-of-the-art?
- Why is this one of the most important questions in the field?
- Will it inspire a new class of methods, systems, tools, or computers?
Who will care about it when you’re done?
- Will government agencies care?
- Will industry/companies care?
- Will other academics care enough to cite it?
- Will other academics care enough to teach it to their students?
- Will anyone care about it 10, 20, 50 years in the future?
How will this change what other people (defined broadly) are doing?
- Will other researchers change what they're working on after seeing your work?
- Will practitioners do something different?
- Will users adopt what you made/found/created?
This is a note about what you should strive to achieve in terms of output during your Ph.D. This differs from what I expect as your output, but what you should expect to try to produce. These expectations are also averaged over multiple years. You should expect to produce less in your first and second years (for example, it's okay to have only one project to begin with, possibly through a collaboration with a senior student) and more as you get closer to graduation.
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Try to produce one very high-quality paper per year. This should yield 3-4 published versions of these throughout your Ph.D. Some of these papers won't be accepted somewhere exceptionally competitive or may not work out well in the research process (e.g., the approach didn’t work, the context of the problem changed, etc.). That's the nature of research. This is the most important output you might produce as a student researcher.
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At the same time, I'd like you to have a straightforward project underway. This is the lower-risk, lower-reward paper. 1.5 of these every 2 years is about the right fit (i.e., slightly less than one of these projects ongoing per year). More of these should be published, and fewer will fall apart. That's the nature of this work. This might be in collaboration with a larger group, but you should play a significant role. This is important for your sense of progress, as the more challenging work might stall and frustrate you. This is also important to get exposure for you and your ideas in wider venues.
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Concurrently, try to be a supporting author on at least one other project. This isn’t your core work; it’s someone else-led. It should take less than 1/2-1/3 of a day of your time per week. But you have something to offer and will be listed in a supporting author position. Also, of the lower-risk, lower-reward variety. This contribution is important for you to become known (even locally) for your expertise, improve collaboration skills, and contribute to your immediate academic community.
Note that if all of these are going on, and with other tasks and roles you will be taking, you are likely to have your plate feel very full. You'll need to balance your time and remember to take time off as needed.
I dislike dictating how anyone works, so I minimize 'rules' and keep them flexible when possible. But, in general, it's very useful for me to keep track of my research work intentionally. I use cloud services and GitHub for documents, code, data, etc., and you should use the GitHub group organization here for your work. Outside of this, pick what works best for you, but I suggest you do something intentional from the outset of a project. Don't just go from meeting to meeting, waiting and receiving the next advice.
Rule: Backup your work daily. Your research work should never live solely on one hard drive. I provide every student with a high-capacity backup hard drive. If you don't have one, please ask for one.
Have ideas!
I don't like advising students without their own ideas, nor do I think it's good for your development as a scholar. As noted above, the major thing that we’re doing here is turning you into a world-class scholar. One key way you do that is by coming up with new ideas. Moreover, it's important to be competitive in academic job applications; those evaluations are impacted by your future work ideas, not only your work to date.
Good ideas are rare and take work to come by. Most of my ideas, which you can expect to hear plenty of, are bad. I love to hear ideas, good or bad; some might be the opposite after a short (or long) discussion. Ideas are everywhere; if you let yourself, you'll always have new ones. It can be easy to constantly find yourself submerged in the details of ongoing projects without popping up to think about and consider new projects, ideas, and directions. Both are important: a good scholar can move between levels of detail (i.e., "What's the right statistical technique for these data in this paper?" to "Which of these 5 new ideas would have the most impact?").
Some concrete ways in which one might find good ideas:
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More commonly, remember that we stand on the shoulders of giants. When you read a good paper (really, any paper), think about how components of that paper could apply to your research. For example, the authors' methods, the way they asked their research questions, the type of analysis they performed, or even how they presented their results can all provide key insights.
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When you read a good paper in your research area, ask yourself what should come next. What assumptions do they make? What would make this even better? What are the authors missing that is not an immediate "future work" for that scholar's arc? Identifying papers like that can impact your research directions over time.
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Many phenomena we see online and around technology are not, strictly speaking, new. Many of them have been thought about and studied in earlier forms. Try to read broadly (e.g., from computational mathematics to physics to mechanical and aerospace engineering), and consider how these texts and concepts are related to your work.
I recommend keeping track of ideas.
You can use a file called ideas.txt to keep track of new ideas as they come to mind, or whatever other mechanism you like, but do something.
Importantly, while there is no such thing as "too many ideas," you shouldn't pursue more than a few at a time and carefully balance new ideas with ongoing work. This brings us to...
What ideas and research direction should you pursue? Can a student choose any topic and research direction? Do I dictate research agendas and projects to the student? The reality is that we decide which ideas and directions to work on together. It's an iterative, long-term process that results in alignment.
This process starts when students pick to work with me and me with them because we have a shared interest. I am likely to steer new students towards directions and questions that are interesting (sometimes new, sometimes existing), especially projects that I have funding to work on. But I try to entirely avoid "assigning" projects. If the student is not excited and motivated about a research direction, the outcome will not likely be good (if you think I put you in this situation, please let me know so we can align). Similarly, students can pursue a project that I am less interested in, making me less engaged and less helpful as an advisor. The process of coming up with ideas, research questions, and project decisions thus naturally gravitates towards mutually interesting directions that overlap with existing or potential funding.
At the same time, "interest splits" happen, and students often pursue questions and directions. If there's no overlap, one option is to switch advisors. I have had students leave me to work with other advisors as it became clear that their pursuit and intellectual passion do not overlap with mine. This is normal and healthy. What is unhealthy is staying in an advising relationship even though passions do not overlap meaningfully.