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Your thesis, or theses, will occupy most of your time during most of your career as a graduate student. The bulk of that time will be devoted to research, or even to choosing a topic, rather than to the actual writing.
The Master's thesis is designed as practice for the PhD thesis. PhD-level research is too hard to embark on without preparation. The essential requirement of a Master's thesis is that it literally demonstrate mastery: that you have fully understood the state of the art in your subfield and that you are capable of operating at that level. It is not a requirement that you extend the state of the art, nor that the Master's thesis be publishable. There is a substantial machismo about theses in our lab, however, so that many Master's theses do in fact contribute significantly to the field, and perhaps half are published. This is not necessarily a good thing. Many of us burn out on our Master's work, so that it is notorious that MIT Master's theses are often better than the PhD theses. This defeats the preparatory intent of the Master's. The other factor is that doing research that contributes to the field takes at least two years, and that makes the graduate student career take too damn long. You may not feel in a hurry now, but after you've been around the Lab for seven years you'll want out badly. The mean time from entrance to finishing the Master's is two and a half years. However, the CS department is strongly encouraging students to reduce this period. If a Master's topic turns out to be a blockbuster, it can be split into parts, one for the Master's and one for a PhD.
To get some idea of what constitutes a Master's thesis-sized piece of research, read several recent ones. Keep in mind that the ones that are easy to get at are the ones that were published or made into tech reports because someone thought they extended the state of the art-in other words, because they did more than a Master's thesis needs to. Try also reading some theses that were accepted but not published. All accepted theses can be found in one of the MIT libraries. PhD theses are required to extend the state of the art. PhD thesis research should be of publishable quality. MIT machismo operates again, so that many PhD theses form the definitive work on a subarea for several years. It is not uncommon for a thesis to define a new subarea, or to state a new problem and solve it. None of this is necessary, however.
In general, it takes about two to three years to do a PhD thesis. Many people take a year or two to recover from the Master's and to find a PhD topic. It's good to use this period to do something different, like being a TA or getting a thorough grounding in a non-AI field or starting a rock and roll band. The actual writing of the PhD thesis generally takes about a year, and an oft-confirmed rule of thumb is that it will drag on for a year after you are utterly sick of it.
Choosing a topic is one of the most difficult and important parts of thesis work.
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.
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.
Some people find that working on several potential thesis projects at once allows them to finish the one that works out and abandon the ones that fail. This decreases the risk. Others find that the substantial thrashing overhead this engenders is too high, and choose a single topic before starting any work in earnest.
You may only be interested in a particular subfield, in which case your thesis topic search is narrowed. You may find, though, that there's no faculty member who can supervise a topic in that field whom you are comfortable working with. You may also find that there doesn't seem to be a natural topic to work on in that field, whereas you have good ideas about something else.
Choosing a Master's topic can be harder than choosing the PhD topic, because it has to be done before you know very much and before you've built much self-confidence.
One parameter of PhD topic choice is whether to continue working in the same subfield as your Master's, perhaps extending or building on that work, or to switch to another subfield. Staying in the same field simplifies things and probably will take one to two years off the total time to graduation, especially if a PhD-sized topic becomes obvious during the course of the Master's work. But it may leave you ``typecast'' as someone who does shape-from-shading or circuit analysis; changing fields gives you breadth.
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.
Not all MIT AI Lab theses are about AI; some are hardware or programming language theses. This is OK.
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.
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, overoptimizing 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.)
A whole lot of people at MIT