Thesis

• Choosing a topic is one of the most difficult and important parts of thesis work.
  • General rules
    • Pick something you find interesting - if you work on something solely because your advisor wants you to, it will be difficult to stay motivated.
    • Pick something your advisor finds interesting - if your advisor doesn't find it interesting he/she is unlikely to devote much time to your research. He/she will be even more motivated to help you if your project is on their critical path (although this has down sides too!).
    • Pick something the research community will find interesting -if you want to make yourself marketable.
    • Make sure it addresses a real problem
    • Remember that your topic will evolve as work on it
    • Pick something that is narrow enough that it can be done in a reasonable time frame
    • Have realistic expectations (i.e. Don't expect the Nobel Prize)
    • Don't worry that you will be stuck in this area for the rest of your career. It is very likely that you will be doing very different research after you graduate.
       
  • A good thesis topic will simultaneously express a personal vision and participate in a conversation with the literature.

    Your topic must be one you are passionate about. Nothing less will keep you going. Your personal vision is your reason for being a scientist, an image or principle or idea or goal you care deeply about. It can take many forms. Maybe you want to build a computer you can talk to. Maybe you want to save the world from stupid uses of computers. Maybe you want to demonstrate the unity of all things. Maybe you want to found colonies in space. A vision is always something big. Your thesis can't achieve your vision, but it can point the way.

    At the same time, science is a conversation. An awful lot of good people have done their best and they're written about it. They've accomplished a great deal and they've completely screwed up. They've had deep insights and they've been unbelievably blind. They've been heros and cowards. And all of this at the same time. Your work will be manageable and comprehensible if it is framed as a conversation with these others. It has to speak to their problems and their questions, even if it's to explain what's wrong with them. A thesis topic that doesn't participate in a conversation with the literature will be too big or too vague, or nobody will be able to understand it.
     

  • The hardest part is figuring out how to cut your problem down to a solvable size while keeping it big enough to be interesting. ``Solving AI breadth-first'' is a common disease; you'll find you need to continually narrow your topic. Choosing a topic is a gradual process, not a discrete event, and will continue up to the moment you declare the thesis finished. Actually solving the problem is often easy in comparison to figuring out what exactly it is. If your vision is a fifty-year project, what's the logical ten-year subproject, and what's the logical one-year subproject of that? If your vision is a vast structure, what's the component that gets most tellingly to its heart, and what demonstration would get most tellingly to the heart of that component?

    An important parameter is how much risk you can tolerate. Often there is a trade-off between the splashiness of the final product and the risk involved in producing it. This isn't always true, though, because AI has a high ratio of unexplored ideas to researchers.

    In any case, a good topic will address important issues. You should be trying to solve a real problem, not a toy problem (or worse yet, no problem at all); you should have solid theoretical work, good empirical results or, preferably, both; and the topic will be connected to -- but not be a simple variation on or extension of -- existing research. It will also be significant yet manageable. Finding the right size problem can be difficult. One good way of identifying the right size is to read other dissertations.

    An ideal thesis topic has a sort of telescoping organization. It has a central portion you are pretty sure you can finish and that you and your advisor agree will meet the degree requirements. It should have various extensions that are successively riskier and that will make the thesis more exciting if they pan out. Not every topic will fit this criterion, but it's worth trying for.

    Topics can be placed in a spectrum from flakey to cut-and-dried. Flakier theses open up new territory, explore previously unresearched phenomena, or suggest heuristic solutions to problems that are known to be very hard or are hard to characterize. Cut-and-dried theses rigorously solve well-characterized problems. Both are valuable; where you situate yourself in this spectrum is a matter of personal style.
     

  • The ``further work'' sections of papers are good sources of thesis topics.
     
  • Whatever you do, it has to have not been done before. Also, it's not a good idea to work on something that someone else is doing simultaneously. There's enough turf out there that there's no need for competition. On the other hand, it's common to read someone else's paper and panic because it seems to solve your thesis problem. This happens most when you're halfway through the process of making your topic specific and concrete. Typically the resemblance is actually only superficial, so show the paper to some wise person who knows your work and ask them what they think.
     
• Once you've got a thesis topic, even when it's a bit vague, you should be able to answer the question ``what's the thesis of your thesis?'' What are you trying to show?
  • You should have one-sentence, one-paragraph, and five-minute answers. If you don't know where you are going, people won't take you seriously, and, worse, you'll end up wandering around in circles.
  • When doing the work, be able to explain simply how each part of your theory and implementation is in service of the goal.
  • Make sure once you've selected a topic that you get a clear understanding with your advisor as to what will constitute completion. If you and he have different expectations and don't realize it, you can lose badly. You may want to formulate an explicit end-test, like a set of examples that your theory or program will be able to handle. Do this for yourself anyway, even if your advisor doesn't care. Be willing to change this test if circumstances radically change.
  • Try a simplified version of the thesis problem first. Work examples. Thoroughly explore some concrete instances before making an abstract theory.
     
• The divide-and-conquer approach works as well for writing as it does for research. A problem that many graduate students face is that their only goal seems to be ``finish the thesis.'' It is essential that you break this down into manageable stages, both in terms of doing the research and when writing the thesis. Tasks that you can finish in a week, a day, or even as little as half an hour are much more realistic goals. Try to come up with a range of tasks, both in terms of duration and difficulty. That way, on days when you feel energetic and enthusiastic, you can sink your teeth into a solid problem, but on days when you're run-down and unmotivated, you can at least accomplish and few small tasks and get them off your queue.

  It also helps to start writing at a coarse granularity and successively refine your thesis. Don't sit down and try to start writing the entire thesis from beginning to end. First jot down notes on what you want to cover; then organize these into an outline (which will probably change as you progress in your research and writing). Start drafting sections, beginning with those you're most confident about. Don't feel obligated to write it perfectly the first time: if you can't get a paragraph or phrase right, just write *something* (a rough cut, a note to yourself, a list of bulleted points) and move on. You can always come back to the hard parts later; the important thing is to make steady progress.
   

• There are a number ways you can waste a lot of time during the thesis. Some activities to avoid (unless they are central to the thesis): language design, user-interface or graphics hacking, inventing new formalisms, over-optimizing code, tool building, bureaucracy. Any work that is not central to your thesis should be minimized.

  There is a well-understood phenomenon known as ``thesis avoidance,'' whereby you suddenly find fixing obscure bugs in an obsolete operating system to be utterly fascinating and of paramount importance. This is invariably a semiconscious way of getting out of working on one's thesis. Be aware that's what you are doing. (This document is itself an example of thesis avoidance on the part of its authors.)