CRA-W Grad Cohort: Finding a Research Topic

What makes a topic appropriate for a PhD dissertation? What is and isn't computer science research? What should you do when you're stuck? All these questions and more were answered by Prof. Lori Pollock from University of Delaware in the CRA-W Grad Cohort talk on choosing a research topic.

What is computer science research?

• Research is the systemic investigation to establish facts and reach new conclusions.
• We don't know the answer or how to get it.
  
• Experimental research involves:
• observing a problem
• generating a hypothesis
• developing a strategy to solve the problem
• performing experiments, demonstrating evidence
• interpreting results
• Theoretical research involves:
• identifying an open problem
• proofs, analysis of hypothesis
• a possible combination with experimental research

What isn't PhD research?

These ideas were generated from audience discussion. I suspect some of these are probably worthy of a Masters dissertation, but be sure to ask the experts before assuming as much!

• Figuring out how existing software applications work (though this might be part of the observation stage of research).
• Implementing an existing algorithm or solution (again, might be a step toward completing the overall research).
• Comparing various solutions against a benchmark.
• Developing new metrics for comparison, unless you can show why the new benchmarks are useful or give new information.
• Putting together software components in a new way, unless you can show that you are solving the problem in a better way by doing so.

How do I choose a topic area to research?

• Make sure the area grabs the interest of you, your supervisor, and your research community.
• Gain breadth (say, in your courses) to broaden your options.
• Love your topic! You will be spending 2-3 years on it, and it may be defining your post-grad options.
  
• Think about your strengths and weaknesses. Are you good or bad at programming, design, data analysis, or proofs?
• What drives you? What bores you? Technology, puzzles, applications, interdisciplinary work?
• Check how much funding there is in your area.
• Did you find an advisor before your area? This is fine, but know that it may limit your choice of area.
• Make sure you find an advisor that in knowledgeable in the area you will work in, and that is compatible with you in terms of working/mentoring style.

Moving from an area to a specific topic

• An 'area' is too broad for a thesis - must narrow down to a specific topic.
• A topic is a set of open questions, or a well-defined problem.
• Characteristics of a PhD topic (from audience discussion):
  • novel, open problem
  • high impact
  • non-incremental solution
    
  • community is interested
    
  • can measure success

Seven ways to identify a good research problem

1. Flash of brilliance: You wake up one morning with a brilliant idea. This is rare, and you will have a hard time selling the idea to your supervisor.
   
   
2. The apprentice: Pick something from a list of topics your advisor has. Be careful that you are not picking something boring, fruitless, or that other students might also choose.
   
   
3. Extended course project: Take a project course that leads to a new perspective. You may get lucky and be able to extend it to a thesis topic, but if not, you may get distracted from your topic search.
   
   
4. Redo, reinvent: Identify improvement to an algorithm or proof, discover a new topic. This may lead you to be without a topic for a long period of time, and you run the risk of it not being dissertation worthy.
   
   
5. Analyze data: Help a senior student with their project, potentially leading to new open challenges and a new topic. Be sure to agree which of you will actually get to work on the open problem.
   
   
6. The stapler: Weave together a number of small topics (such as those from various conference papers). Finding the tie might be challenging.
   
   
7. Synthesis model: Read papers, make connections, get insights. The downside is you may spend lots of time reading papers without a topic.

These seven ideas were credited to someone else, but I can't remember who. It's also worth considering how they might be combined together.

General tips (and what to do when stuck)

• Both your topic and your advisor are important to your success.
• Keep a research ideas journal and wiki (I use private Google Docs to make notes to share only with my supervisor rather than the whole world, as would likely happen with a research blog).
• Keep an annotated bibliography. (See these posts for advice on organizing your research papers.)
• Follow your interests and passions.
• If you just aren't really getting into the topic, adapt!
• Read and present papers regularly to find open research problems (pay special attention to the future work section, often in the paper's conclusion).
• Work with a senior PhD student on their research.
• Actively participate in research meetings.
• Get feedback and ideas from others. Attend conferences, listen for open problems, talk to attendees, do internships.
• Read a PhD thesis in your area.
• Read advisor's grant proposals.
• Attend thesis and proposal defences.
• Assess your progress with your supervisor.
• Divide your project into milestones.
• Remember that change can be invigorating, but it can also slow you down.
• Also remember that you run the risk of being scooped if you are choosing a topic in a hot area.

Conclusion

Prof. Pollock recommended the ACM articles on How to Success in Graduate School (Part I and Part II), which I haven't read yet but am about to. If you are further along in your PhD, I'd love to hear which of these tips worked (and didn't) for you, and any other advice you have.