MASSACHUSETTS INSTITUTE OF TECHNOLOGY
ARTIFICIAL INTELLIGENCE LABORATORY
AI Working Paper 316 October, 1988
How to do Research
At the MIT AI Lab
a whole bunch of current, former, and honorary
MIT AI Lab graduate students
David Chapman, Editor
Version 1.3, September, 1988.
This document presumptuously purports to explain how to do research . We give heuristics that may be useful in picking up the specific skills needed for research (reading, writing, programming) and for understanding and enjoying the process itself (methodology, topic and advisor selection, and emotional factors).
Copyright 1987, 1988 by the authors.
A.I. Laboratory Working Papers are produced for internal circulation, and may contain information that is, for example, too preliminary or too detailed for formal publication. It is not intended that they should be considered papers to which reference can be made in the literature.
2. Reading AI
3. Getting connected
4. Learning other fields
10. The thesis
11. Research methodology
12. Emotional factors
There's no guaranteed recipe for success at research . This document collects a lot of informal rules-of-thumb advice that may help.
This document is written for new graduate students at the MIT AI Laboratory. However, it may be useful to many others doing research in AI at other institutions. People even in other fields have found parts of it useful.
It's too long to read in one sitting. It's best to browse. Most people have found that it's useful to flip through the whole thing to see what's in it and then to refer back to sections when they are relevant to their current research problems.
The document is divided roughly in halves. The first several sections talk about the concrete skills you need: reading, writing, programming, and so on. The later sections talk about the process of research : what it's like, how to go at it, how to choose an advisor and topic, and how to handle it emotionally. Most readers have reported that these later sections are in the long run more useful and interesting than the earlier ones.
This document is still in a state of development; we welcome contributions and comments. Some sections are very incomplete. [Annotations in brackets and italics indicate some of the major incompletions.] We appreciate contributions; send your ideas and comments to Zvona@ai.ai.mit.edu.
Many researchers spend more than half their time reading. You can learn a lot more quickly from other people's work than from doing your own. This section talks about reading within AI; section 4 covers reading about other subjects.
The time to start reading is now. Once you start seriously working on your thesis you'll have less time, and your reading will have to be more focused on the topic area. During your first two years, you'll mostly be doing class work and getting up to speed on AI in general. For this it suffices to read textbooks and published journal articles. (Later, you may read mostly drafts; see section 3.)
The amount of stuff you need to have read to have a solid grounding in the field may seem intimidating, but since AI is still a small field, you can in a couple years read a substantial fraction of the significant papers that have been published. What's a little tricky is figuring out which ones those are. There are some bibliographies that are useful: for example, the syllabi of the graduate AI courses. The reading lists for the AI qualifying exams at other universities---particularly Stanford---are also useful, and give you a less parochial outlook. If you are interested in a specific subfield, go to a senior grad student in that subfield and ask him what are the ten most important papers and see if he'll lend you copies to Xerox. Recently there have been appearing a lot of good edited collections of papers from a subfield, published particularly by Morgan-Kauffman.
The AI lab has three internal publication series, the Working Papers, Memos, and Technical Reports, in increasing order of formality. They are available on racks in the eighth floor play room. Go back through the last couple years of them and snag copies of any that look remotely interesting. Besides the fact that a lot of them are significant papers, it's politically very important to be current on what people in your lab are doing.
There's a whole bunch of journals about AI, and you could spend all your time reading them. Fortunately, only a few are worth looking at. The principal journal for central-systems stuff is Artificial Intelligence, also referred to as ``the Journal of Artificial Intelligence'', or ``AIJ''. Most of the really important papers in AI eventually make it into AIJ, so it's worth scanning through back issues every year or so; but a lot of what it prints is really boring. Computational Intelligence is a new competitor that's worth checking out. Cognitive Science also prints a fair number of significant AI papers. Machine Learning is the main source on what it says. IEEE PAMI is probably the best established vision journal; two or three interesting papers per issue. The International Journal of Computer Vision (IJCV) is new and so far has been interesting. Papers in Robotics Research are mostly on dynamics; sometimes it also has a landmark AIish robotics paper. IEEE Robotics and Automation has occasional good papers.
It's worth going to your computer science library ( MIT 's is on the first floor of Tech Square) every year or so and flipping through the last year's worth of AI technical reports from other universities and reading the ones that look interesting.
Reading papers is a skill that takes practice. You can't afford to read in full all the papers that come to you. There are three phases to reading one. The first is to see if there's anything of interest in it at all. AI papers have abstracts, which are supposed to tell you what's in them, but frequently don't; so you have to jump about, reading a bit here or there, to find out what the authors actually did. The table of contents, conclusion section, and introduction are good places to look. If all else fails, you may have to actually flip through the whole thing. Once you've figured out what in general the paper is about and what the claimed contribution is, you can decide whether or not to go on to the second phase, which is to find the part of the paper that has the good stuff. Most fifteen page papers could profitably be rewritten as one-page papers; you need to look for the page that has the exciting stuff. Often this is hidden somewhere unlikely. What the author finds interesting about his work may not be interesting to you, and vice versa. Finally, you may go back and read the whole paper through if it seems worthwhile.
Read with a question in mind. ``How can I use this?'' ``Does this really do what the author claims?'' ``What if...?'' Understanding what result has been presented is not the same as understanding the paper. Most of the understanding is in figuring out the motivations, the choices the authors made (many of them implicit), whether the assumptions and formalizations are realistic, what directions the work suggests, the problems lying just over the horizon, the patterns of difficulty that keep coming up in the author's research program, the political points the paper may be aimed at, and so forth.
It's a good idea to tie your reading and programming together. If you are interested in an area and read a few papers about it, try implementing toy versions of the programs being described. This gives you a more concrete understanding.
Most AI labs are sadly inbred and insular; people often mostly read and cite work done only at their own school. Other institutions have different ways of thinking about problems, and it is worth reading, taking seriously, and referencing their work, even if you think you know what's wrong with them.
Often someone will hand you a book or paper and exclaim that you should read it because it's (a) the most brilliant thing ever written and/or (b) precisely applicable to your own research . Usually when you actually read it, you will find it not particularly brilliant and only vaguely applicable. This can be perplexing. ``Is there something wrong with me? Am I missing something?'' The truth, most often, is that reading the book or paper in question has, more or less by chance, made your friend think something useful about your research topic by catalyzing a line of thought that was already forming in their head.
After the first year or two, you'll have some idea of what subfield you are going to be working in. At this point---or even earlier---it's important to get plugged into the Secret Paper Passing Network. This informal organization is where all the action in AI really is. Trend-setting work eventually turns into published papers---but not until at least a year after the cool people know all about it. Which means that the cool people have a year's head start on working with new ideas.
How do the cool people find out about a new idea? Maybe they hear about it at a conference; but much more likely, they got it through the Secret Paper Passing Network. Here's how it works. Jo Cool gets a good idea. She throws together a half-assed implementation and it sort of works, so she writes a draft paper about it. She wants to know whether the idea is any good, so she sends copies to ten friends and asks them for comments on it. They think it's cool, so as well as telling Jo what's wrong with it, they lend copies to their friends to Xerox. Their friends lend copies to their friends, and so on. Jo revises it a bunch a few months later and sends it to AAAI. Six months later, it first appears in print in a cut-down five-page version (all that the AAAI proceedings allow). Jo eventually gets around to cleaning up the program and writes a longer revised version (based on the feedback on the AAAI version) and sends it to the AI Journal. AIJ has almost two years turn-around time, what with reviews and revisions and publication delay, so Jo's idea finally appears in a journal form three years after she had it---and almost that long after the cool people first found out about it. So cool people hardly ever learn about their subfield from published journal articles; those come out too late.
You, too, can be a cool people. Here are some heuristics for getting connected:
It used to be the case that you could do AI without knowing anything except AI, and some people still seem to do that. But increasingly, good research requires that you know a lot about several related fields. Computational feasibility by itself doesn't provide enough constraint on what intelligence is about. Other related fields give other forms of constraint, for example experimental data, which you can get from psychology. More importantly, other fields give you new tools for thinking and new ways of looking at what intelligence is about. Another reason for learning other fields is that AI does not have its own standards of research excellence, but has borrowed from other fields. Mathematics takes theorems as progress; engineering asks whether an object works reliably; psychology demands repeatable experiments; philosophy rigorous arguments; and so forth. All these criteria are sometimes applied to work in AI, and adeptness with them is valuable in evaluating other people's work and in deepening and defending your own.
Over the course of the six or so years it takes to get a PhD at MIT , you can get a really solid grounding in one or two non-AI fields, read widely in several more, and have at least some understanding of the lot of them. Here are some ways to learn about a field you don't know much about:
Now for the subjects related to AI you should know about.
Computer science is grounded in discrete mathematics: algebra, graph theory, and the like. Logic is very important if you are going to work on reasoning. It's not used that much at MIT , but at Stanford and elsewhere it is the dominant way of thinking about the mind, so you should learn enough of it that you can make and defend an opinion for yourself. One or two graduate courses in the MIT math department is probably enough. For work in perception and robotics, you need continuous as well as discrete math. A solid background in analysis, differential geometry and topology will provide often-needed skills. Some statistics and probability is just generally useful.
This all seems like a lot to know about, and it is. There's a trap here: thinking ``if only I knew more X, this problem would be easy,'' for all X. There's always more to know that could be relevant. Eventually you have to sit down and solve the problem.
Most scientists keep a research notebook. You should too. You've probably been told this in every science class since fifth grade, but it's true. Different systems work for different people; experiment. You might keep it online or in a spiral notebook or on legal pads. You might want one for the lab and one for home.
Record in your notebook ideas as they come up. Nobody except you is going to read it, so you can be random. Put in speculations, current problems in your work, possible solutions. Work through possible solutions there. Summarize for future reference interesting things you read.
Read back over your notebook periodically. Some people make a monthly summary for easy reference.
What you put in your notebook can often serve as the backbone of a paper. This makes life a lot easier. Conversely, you may find that writing skeletal papers---title, abstract, section headings, fragments of text---is a useful way of documenting what you are up to, even when you have no intention of ever making it into a real paper. (And you may change your mind later.)
You may find useful Vera Johnson-Steiner's book Notebooks of the Mind, which, though mostly not literally about notebooks, describes the ways in which creative thought emerges from the accumulation of fragments of ideas.
There's a lot of reasons to write.
Anything worth doing is worth doing well.
Another mistake is to imagine that the whole thing can be written out in order. Usually you should start with the meat of the paper and write the introduction last, after you know what the paper really says. Another cause of writer's block is unrealistic expectations about how easy writing is. Writing is hard work and takes a long time; don't get frustrated and give up if you find you write only a page a day.
If you put off writing until you've done all the work, you'll lose most of the benefit. Once you start working on a research project, it's a good idea to get into the habit of writing an informal paper explaining what you are up to and what you've learned every few months. Start with the contents of your research notebook. Take two days to write it---if it takes longer, you are being perfectionistic. This isn't something you are judged on; it's to share with your friends. Write DRAFT---NOT FOR CITATION on the cover. Make a dozen copies and give them to people who are likely to be interested (including your advisor!). This practice has most of the benefits of writing a formal paper (comments, clarity of thought, writing practice, and so forth), but on a smaller scale, and with much less work invested. Often, if your work goes well, these informal papers can be used later as the backbone of a more formal paper, from an AI Lab Working Paper to a journal article.
Once you become part of the Secret Paper Passing Network, you'll find that people give you copies of draft papers that they want comments on. Getting comments on your papers is extremely valuable. You get people to take the time to write comments on yours by writing comments on theirs. So the more people's papers you write comments on, the more favors are owed you when you get around to writing one... good politics. Moreover, learning to critique other people's papers will help your own writing.
Writing useful comments on a paper is an art.
There are a variety of sorts of comments. There are comments on presentation and comments on content. Comments on presentation vary in scope. Copy-edits correct typos, punctuation, misspellings, missing words, and so forth. Learn the standard copy-editing symbols. You can also correct grammar, diction, verbosity, and muddied or unclear passages. Usually people who make grammatical mistakes do so consistently, using comma splices for example; take the time to explain the problem explicitly. Next there are organizational comments: ideas out of order at various scales from clauses through sentences and paragraphs to sections and chapters; redundancy; irrelevant content; missing arguments.
Comments on content are harder to characterize. You may suggest extensions to the author's ideas, things to think about, errors, potential problems, expressions of admiration. ``You ought to read X because Y'' is always a useful comment.
In requesting comments on a paper, you may wish to specify which sorts are most useful. For an early draft, you want mostly comments on content and organization; for a final draft, you want mostly comments on details of presentation. Be sure as a matter of courtesy to to run the paper through a spelling corrector before asking for comments.
You don't have to take all the suggestions you get, but you should take them seriously. Cutting out parts of a paper is particularly painful, but usually improves it. Often if you find yourself resisting a suggestion it is because while it points out a genuine problem with your paper the solution suggested is unattractive. Look for a third alternative.
Getting your papers published counts. This can be easier than it seems. Basically what reviewers for AI publications look for is a paper that (a) has something new to say and (b) is not broken in some way. If you look through an IJCAI proceedings, for example, you'll see that standards are surprisingly low. This is exacerbated by the inherent randomness of the reviewing process. So one heuristic for getting published is to keep trying. Here are some more:
Like all else in research , paper writing always takes a lot longer than you expect. Papers for publication have a particularly insidious form of this disease, however. After you finally finish a paper, you send it in for publication. Many months later it comes back with comments, and you have to revise it. Then months after that the proofs come back for correction. If you publish several forms of the paper, like a short conference version and a long journal version, this may go through several rounds. The result is that you are still working on a paper years after you thought you were through with it and after the whole topic has become utterly boring. This suggests a heuristic: don't do some piece of research you don't care for passionately on the grounds that it won't be hard to get a publication out of it: the pain will be worse than you expect.
Talks are another form of communication with your colleagues, and most of what we said about writing is true of talking also. An ability to stand in front of an audience and give a talk that doesn't make the audience fall asleep is crucial for success in terms of recognition, respect and eventually a job. Speaking ability is not innate---you can start out graduate life as a terrible public speaker and end up as a sparkling wit so long as you practice, practice, practice, by actually giving talks to groups of people.
Some ways to learn and practice speaking:
Some key things to remember in planning and delivering a talk:
Not every AI thesis involves code, and there are important people in AI who have never written a significant program, but to a first approximation you have to be able to program to do AI. Not only does most AI work involve writing programs, but learning to program gives you crucial intuitions into what is and isn't computationally feasible, which is the major source of constraint AI contributes to cognitive science.
At MIT , essentially all AI programming is done in Common Lisp. If you don't know it, learn it. Learning a language is not learning to program, however; and AI programming involves some techniques quite different from those used for systems programming or for other applications. You can start by reading Abelson and Sussman's Structure and Interpretation of Computer Programs and doing some of the exercises. That book isn't about AI programming per se, but it teaches some of the same techniques. Then read the third edition of Winston and Horn's Lisp book; it's got a lot of neat AI programs in it. Ultimately, though, programming, not reading, is the best way to learn to program.
There is a lot of Lisp programming culture that is mostly learned by apprenticeship. Some people work well writing code together; it depends strongly on the personalities involved. Jump at opportunities to work directly with more experienced programmers. Or see if you can get one of them to critique your code. It's also extremely useful to read other people's code. Ask half a dozen senior grad students if you can get the source code for their programs. They'll probably complain a bit, and make noises about how their coding style is just awful, and the program doesn't really work, and then give you the code anyway. Then read it through carefully. This is time consuming; it can take as long to read and fully understand someone else's code as it would take you to write it yourself, so figure on spending a couple of weeks spread over your first term or two doing this. You'll learn a whole lot of nifty tricks you wouldn't have thought of and that are not in any textbook. You'll also learn how not to write code when you read pages of incomprehensible uncommented gibberish.
All the standard boring things they tell you in software engineering class are true of AI programming too. Comment your code. Use proper data abstraction unless there is a compelling reason not to. Segregate graphics from the rest of your code, so most of what you build is Common Lisp, hence portable. And so on.
Over your first couple years, you should write your own versions of a bunch of standard AI building blocks, such as
whatever turns you on. You can write stripped-down but functional versions of these in a few days. Extending an existing real version is an equally powerful alternative. It's only when you've written such things that you really understand them, with insight into when they are and aren't useful, what the efficiency issues are, and so forth.
Unlike most other programmers, AI programmers rarely can borrow code from each other. (Vision code is an exception.) This is partly because AI programs rarely really work. (A lot of famous AI programs only worked on the three examples in the author's thesis, though the field is less tolerant of this sloppiness than it once was.) The other reason is that AI programs are usually thrown together in a hurry without concern for maximum generality. Using Foobar's ``standard'' rule interpreter may be very useful at first, and it will give you insight into what's wrong if it doesn't have quite the functionality you need, or that it's got too much and so is too inefficient. You may be able to modify it, but remember that understanding someone else's code is very time consuming. It's sometimes better to write your own. This is where having done the half-dozen programming projects in the last paragraph becomes real handy. Eventually you get so you can design and implement a custom TMS algorithm (say) in an afternoon. (Then you'll be debugging it on and off for the next six weeks, but that's how it is.) Sometimes making a standard package work can turn into a thesis in itself.
Like papers, programs can be over-polished. Rewriting code till it's perfect, making everything maximally abstract, writing macros and libraries, and playing with operating system internals has sucked many people out their theses and out of the field. (On the other hand, maybe that's what you really wanted to be doing for a living anyway.)
At MIT there are two kinds of advisors, academic advisors and thesis advisors.
Academic advisors are simple so we'll dispose of them first. Every graduate student is assigned a faculty member as academic advisor, generally in his or her area, though it depends on current advisor loads. The function of the academic advisor is to represent the department to you: to tell you what the official requirements are, to get on your case if you are late satisfying them, and to OK your class schedule. If all goes well, you only have to see your academic advisor in that capacity twice a year on registration day. On the other hand, if you are having difficulties, your academic advisor may be able to act as advocate for you, either in representing you to the department or in providing pointers to sources of assistance.
The thesis advisor is the person who supervises your research . Your choice of thesis advisor is the most important decision you'll make as a graduate student, more important than that of thesis topic area. To a significant extent, AI is learned by apprenticeship. There is a lot of informal knowledge both of technical aspects of the field and of the research process that is not published anywhere.
Many AI faculty members are quite eccentric people. The grad students likewise. The advisor-advisee relationship is necessarily personal, and your personality quirks and your advisor's must fit well enough that you can get work done together.
Different advisors have very different styles. Here are some parameters to consider.
The range of these parameters varies from school to school. MIT in general gives its students a lot more freedom than most schools can afford to.
Finding a thesis advisor is one of the most important priorities of your first year as a graduate student. You should have one by the end of the first year, or early in the second year at the latest. Here are some heuristics on how to proceed:
AI is unusual as a discipline in that much of the useful work is done by graduate students, not people with doctorates, who are often too busy being managers. This has a couple of consequences. One is that the fame of a faculty member, and consequently his tenure case, depends to a significant extent on the success of his students. This means that professors are highly motivated to get good students to work for them, and to provide useful direction and support to them. Another consequence is that, since to a large degree students' thesis directions are shaped by their advisors, the direction and growth of the field as a whole depends a great deal on what advisors graduate students pick.
After you've picked and advisor and decided what you want from him or her, make sure he or she knows. You advisor may hear ``I'd like to work with you'' as ``Please give me a narrowly specified project to do,'' or ``I've got stuff I'd like to do and I want you to sign it when I'm done,'' or something else. Don't let bad communication get you into a position of wasting a year either spinning your wheels when you wanted close direction or laboring under a topic that isn't the thing you had your heart set on.
Don't be fully dependent on your advisor for advice, wisdom, comments, and connections. Build your own network. You can probably find several people with different things to offer you, whether they're your official advisor or not. It's important to get a variety of people who will regularly review your work, because it's very easy to mislead yourself (and often your advisor as well) into thinking you are making progress when you are not, and so zoom off into outer space. The network can include graduate students and faculty at your own lab at others.
It is possible that you will encounter racist, sexist, heterosexist, or other harrassment in your relationships with other students, faculty members, or, most problematically, your advisor. If you do, get help. MIT 's ODSA publishes a brochure called ``STOP Harrassment'' with advice and resources. The Computer Science Women's Report, available from the LCS document room, is also relevant.
Some students in the lab are only nominally supervised by a thesis advisor. This can work out well for people who are independent self-starters. It has the advantage that you have only your own neuroses to deal with, not your advisor's as well. But it's probably not a good idea to go this route until you've completed at least one supervised piece of work, and unless you are sure you can do without an advisor and have a solid support network.
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.
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.)
[This section is weak. Please contribute!]
A research methodology defines what the activity of research is, how to proceed, how to measure progress, and what constitutes success. AI methodology is a jumbled mess. Different methodologies define distinct schools which wage religious wars against each other.
Methods are tools. Use them; don't let them use you. Don't fall for slogans that raise one above the others: ``AI research needs to be put on firm foundations;'' ``Philosophers just talk. AI is about hacking;'' ``You have to know what's computed before you ask how.'' To succeed at AI, you have to be good at technical methods and you have to be suspicious of them. For instance, you should be able to prove theorems and you should harbor doubts about whether theorems prove anything.
Most good pieces of AI delicately balance several methodologies. For example, you must walk a fine line between too much theory, possibly irrelevant to any real problem, and voluminous implementation, which can represent an incoherent munging of ad-hoc solutions. You are constantly faced with research decisions that divide along a boundary between ``neat'' and ``scruffy.'' Should you take the time to formalize this problem to some extent (so that, for example, you can prove its intractability), or should you deal with it in its raw form, which ill-defined but closer to reality? Taking the former approach leads (when successful) to a clear, certain result that will usually be either boring or at least will not Address the Issues; the latter approach runs the risk of turning into a bunch of hacks. Any one piece of work, and any one person, should aim for a judicious balance, formalizing subproblems that seem to cry for it while keeping honest to the Big Picture.
Some work is like science. You look at how people learn arithmetic, how the brain works, how kangaroos hop, and try to figure it out and make a testable theory. Some work is like engineering: you try to build a better problem solver or shape-from algorithm. Some work is like mathematics: you play with formalisms, try to understand their properties, hone them, prove things about them. Some work is example-driven, trying to explain specific phenomena. The best work combines all these and more.
Methodologies are social. Read how other people attacked similar problems, and talk to people about how they proceeded in specific cases.
Research is hard. It is easy to burn out on it. An embarrassingly small fraction of students who start PhD programs in AI finish. AT MIT , almost all those who do not finish drop out voluntarily. Some leave because they can make more money in industry, or for personal reasons; the majority leave out of frustration with their theses. This section tries to explain how that can happen and to give some heuristics that may help. Forewarned is forearmed: mostly it's useful to know that the particular sorts of tragedies, aggravations, depressions and triumphs you go through in research are necessary parts of the process, and are shared with everyone else who does it.
All research involves risk. If your project can't fail, it's development, not research . What's hard is dealing with project failures. It's easy to interpret your project failing as your failing; in fact, it proves that you had the courage to do something difficult.
The few people in the field who seem to consistently succeed, turning out papers year after year, in fact fail as often as anyone else. You'll find that they often have several projects going at once, only a few of which pan out. The projects that do succeed have usually failed repeatedly, and many wrong approaches went into the final success.
As you work through your career, you'll accumulate a lot of failures. But each represents a lot of work you did on various subtasks of the overall project. You'll find that a lot of the ideas you had, ways of thinking, even often bits of code you wrote, turn out to be just what's needed to solve a completely different problem several years later. This effect only becomes obvious after you've piled up quite a stack of failures, so take it on faith as you collect your first few that they will be useful later.
Research always takes much, much longer than it seems it ought to. The rule of thumb is that any given subtask will take three times as long as you expect. (Some add, ``...even after taking this rule into account.'')
Crucial to success is making your research part of your everyday life. Most breakthroughs occur while you are in the shower or riding the subway or windowshopping in Harvard Square. If you are thinking about your research in background mode all the time, ideas will just pop out. Successful AI people generally are less brilliant than they are persistent. Also very important is ``taste,'' the ability to differentiate between superficially appealing ideas and genuinely important ones.
You'll find that your rate of progress seems to vary wildly. Sometimes you go on a roll and get as much done in a week as you had in the previous three months. That's exhilarating; it's what keeps people in the field. At other times you get stuck and feel like you can't do anything for a long time. This can be hard to cope with. You may feel like you'll never do anything worthwhile again; or, near the beginning, that you don't have what it takes to be a researcher. These feelings are almost certainly wrong; if you were ad mit ted as a student at MIT , you've got what it takes. You need to hang in there, maintaining high tolerance for low results.
You can get a lot more work done by regularly setting short and medium term goals, weekly and monthly for instance. Two ways you can increase the likelihood of meeting them are to record them in your notebook and to tell someone else. You can make a pact with a friend to trade weekly goals and make a game of trying to meet them. Or tell your advisor.
You'll get completely stuck sometimes. Like writer's block, there's a lot of causes of this and no one solution.
Most people find that their personal life and their ability to do research interact. For some, work is a refuge when everything else is going to hell. Others find themselves paralyzed at work when life is in turmoil for other reasons. If you find yourself really badly stuck, it can be helpful to see a psychotherapist. An informal survey suggests that roughly half of the students in our lab see one at some point during their graduate careers.
One factor that makes AI harder than most other types of work is that there are no generally accepted standards of progress or of how to evaluate work. In mathematics, if you prove a theorem, you've done something; and if it was one that others have failed to prove, you've done something exciting. AI has borrowed standards from related disciplines and has some of its own; and different practitioners, subfields, and schools put different emphases on different criteria. MIT puts more emphasis on the quality of implementations than most schools do, but there is much variation even within this lab. One consequence of this is that you can't please all the people all the time. Another is that you may often be unsure yourself whether you've made progress, which can make you insecure. It's common to find your estimation of your own work oscillating from ``greatest story ever told'' to ``vacuous, redundant, and incoherent.'' This is normal. Keep correcting it with feedback from other people.
Several things can help with insecurity about progress. Recognition can help: acceptance of a thesis, papers you publish, and the like. More important, probably, is talking to as many people as you can about your ideas and getting their feedback. For one thing, they'll probably contribute useful ideas, and for another, some of them are bound to like it, which will make you feel good. Since standards of progress are so tricky, it's easy to go down blind alleys if you aren't in constant communication with other researchers. This is especially true when things aren't going well, which is generally the time when you least feel like talking about your work. It's important to get feedback and support at those times.
It's easy not to see the progress you have made. ``If I can do it, it's trivial. My ideas are all obvious.'' They may be obvious to you in retrospect, but probably they are not obvious to anyone else. Explaining your work to lots of strangers will help you keep in mind just how hard it is to understand what now seems trivial to you. Write it up.
A recent survey of a group of Noble Laureates in science asked about the issue of self-doubt: had it been clear all along to these scientists that their work was earth-shattering? The unanimous response (out of something like 50 people) was that these people were constantly doubting the value, or correctness, of their work, and they went through periods of feeling that what they were doing was irrelevant, obvious, or wrong. A common and important part of any scientific progress is constant critical evaluation, and is some amount of uncertainty over the value of the work is an inevitable part of the process.
Some researchers find that they work best not on their own but collaborating with others. Although AI is often a pretty individualistic affair, a good fraction of people work together, building systems and coauthoring papers. In at least one case, the Lab has accepted a coauthored thesis. The pitfalls here are credit assignment and competition with your collaborator. Collaborating with someone from outside the lab, on a summer job for example, lessens these problems.
Many people come to the MIT AI Lab having been the brightest person in their university, only to find people here who seem an order of magnitude smarter. This can be a serious blow to self-esteem in your first year or so. But there's an advantage to being surrounded by smart people: you can have someone friendly shoot down all your non-so-brilliant ideas before you could make a fool of yourself publicly. To get a more realistic view of yourself, it is important to get out into the real world where not everyone is brilliant. An outside consulting job is perfect for maintaining balance. First, someone is paying you for your expertise, which tells you that you have some. Second, you discover they really need your help badly, which brings satisfaction of a job well done.
Contrariwise, every student who comes into the Lab has been selected over about 400 other applicants. That makes a lot of us pretty cocky. It's easy to think that I'm the one who is going to solve this AI problem for once and for all. There's nothing wrong with this; it takes vision to make any progress in a field this tangled. The potential pitfall is discovering that the problems are all harder than you expected, that research takes longer than you expected, and that you can't do it all by yourself. This leads some of us into a severe crisis of confidence. You have to face the fact that all you can do is contribute your bit to a corner of a subfield, that your thesis is not going to solve the big problems. That may require radical self-reevaluation; often painful, and sometimes requiring a year or so to complete. Doing that is very worthwhile, though; taking yourself less seriously allows you to approach research in a spirit of play.
There's at least two emotional reasons people tolerate the pain of research . One is a drive, a passion for the problems. You do the work because you could not live any other way. Much of the best research is done that way. It has severe burn-out potential, though. The other reason is that good research is fun. It's a pain a lot of the time, but if a problem is right for you, you can approach it as play, enjoying the process. These two ways of being are not incompatible, but a balance must be reached in how seriously to take the work.
In getting a feeling for what research is like, and as inspiration and consolation in times of doubt, it's useful to read some of the livelier scientific autobiographies. Good ones are Gregory Bateson's Advice to a Young Scientist, Freeman Dyson's Disturbing the Universe, Richard Feynmann's Surely You Are Joking, Mr. Feynmann!, George Hardy's A Mathematician's Apology, and Jim Watson's The Double Helix.
A month or two after you've completed a project such as a thesis, you will probably find that it looks utterly worthless. This backlash effect is the result of being bored and burned-out on the problem, and of being able to see in retrospect that it could have been done better---which is always the case. Don't take this feeling seriously. You'll find that when you look back at it a year or two later, after it is less familiar, you'll think ``Hey! That's pretty clever! Nice piece of work!''
This document incorporates ideas, text, and comments from Phil Agre, Jonathan Amsterdam, Jeff Anton, Alan Bawden, Danny Bobrow, Kaaren Bock, Jennifer Brooks, Rod Brooks, David Chapman, Jim Davis, Bruce Donald, Ken Forbus, Eric Grimson, Ken Haase, Dan Huttenlocher, Leslie Kaelbling, Mike Lowry, Patrick Sobalvarro, Jeff Shrager, Daniel Weise, and Ramin Zabih. We'd like to thank all the people who gave us the wisdom that we pass on in this document (and which, incidentally, got us through our theses), especially our advisors.
Some of the ideas herein were lifted from ``On Being a Researcher'' by John Backus and ``How to Get a PhD in AI,'' by Alan Bundy, Ben du Boulay, Jim Howe, and Gordon Plotkin.
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