How to do Research At the MIT AI Lab

• How to do Research At the MIT AI Lab

  • （完成）Introduction 引言
  • （完成）Reading AI 阅读

  阅读AI的知识。罗列了重要期刊和有一些如何阅读的小技巧。

  • （完成）Getting connected 建立联系

  成为AI社区的成员：建立联系一个人脉网络，可以让您随时了解最新情况，您需要阅读的内容。

  • Learrning other fields 学习其他领域

  学习与AI相关领域的知识。您将需要一个基本或深入的了解一个或两个er fields 学习其他领域]

  • Notebooks 记笔记

  记录研究笔记的

  • Writing 写作

  写论文和论文；关于撰写和使用评论草稿 以及有关发布的信息。

  • Talks 演讲

  做研究演讲的。

  • （完成）Programming 关于编程

  Al编程可能不同于你已经习惯了的编程

  • Advisors 导师

  研究生职业最重要的选择，导师。不同的导师有不同的风格。本节给出了一些寻找适合您的的导师启发式方法。导师是您的资源，本节将告诉你如何使用你的导师。

  • The thesis 论文

  您的论文或论文将占用您研究生职业大部分时间在。本节提供有关的建议选择主题并避免浪费时间。

  • （完成）Research methodology 研究方法论

  研究方法论。本节大部分尚未编写。

  • Emotional factors 情感因素

  它涉及到情感因素研究过程。它讲述了如何处理失败，如何设定目标，如何摆脱困境，如何避免不安全感，保持自尊心并拥有在这个过程中很有趣。

October, 1988

a whole bunch of current, former, and honorary MIT AI Lab graduate students David Chapman Editor

作者：一大堆现任的，前任的以及荣誉MIT人工智能实验室的研究生学生 编辑：大卫·查普曼（David Chapman）

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).

该文档的目的是为了说明如何做科研。我们抛装引玉的描述研究所需的特定技能（阅读，写作，编程）和学习和享受的过程本身（方法论，主题，导师选择和情感因素）。

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.

AI实验室工作文件供内部流通使用，可能包含的信息过于初步或过于详尽，无法提供正式信息出版物。并不打算将它们视为参考的论文可以在文献中列出。

Contents 目录

Introduction 引言

What is this? There's no guaranteed recipe for success at research. This document collects a lot of informal rules-of-thumb advice that may help.

这是什么？没有保证成功的秘诀。这个文件收集了很多非正式的经验规则建议，可能会有所帮助。

Who's it for? 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.

给谁用 本文件是为麻省理工学院AI实验室为研究生新生而写的。但是，这可能对许多其他机构从事AI研究的人有用。甚至其他领域的人们也有用。

How do I use it? 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.

如何使用？一次坐着看完太久。最好浏览一下。人们发现翻阅整个内容以了解什么是有用的，然后在遇的它们时再来详细翻看

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.

该文件大致分为两半。前几节讲有关您需要的具体技能的知识：阅读，写作，编程等等。后面的部分讨论研究过程：它是什么样的，如何进行，如何选择导师和主题，以及如何处理情感问题。最早的读者报告说，从长远来看，第二部分将更有用，并且比第一部分更有趣

2 is about getting grounded in AI by reading. It points at the most important journals and has some tips on how to read.

第2节是关于通过阅读AI的知识。罗列了重要期刊和有一些如何阅读的小技巧。

• Reading AI 阅读

3 is about becoming a member of the AI community: getting connected to a network of people who will keep you up to date on what's happening and what you need to read.

3 是关于成为AI社区的成员：建立联系一个人脉网络，可以让您随时了解最新情况，您需要阅读的内容。

• Getting connected 建立联系

4 is about learning about fields related to AI. You'll want to have a basic understanding of several of these and probably in-depth understanding of one or two.

4 是关于学习与AI相关领域的知识。您将需要一个基本或深入的了解一个或两个er fields 学习其他领域](#learrning-other-fields-学习其他领域) 。

• [Learrning oth 5 is about keeping a research notebook.

5 是关于记录研究笔记的。

• Notebooks 记笔记

6 is about writing papers and theses; about writing and using comments on drafts; and about getting published.

6 是关于写论文和论文；关于撰写和使用评论草稿 以及有关发布的信息。

• Writing 写作

7 is about giving research talks.

7 是关于做研究演讲的。

• Talks 演讲

8 is about programming. Al programming may be different from the sorts you're used to.

8 是关于编程的。Al编程可能不同于你已经习惯了的编程

• Programming 关于编程

9 is about the most important choice of your graduate career, that of your advisor. Different advisors have different styles; this section gives some heuristics for finding one who will suit you. An advisor is a resource you need to know how to use; this section tells you how.

9 是您的研究生职业最重要的选择，导师。不同的导师有不同的风格。本节给出了一些寻找适合您的的导师启发式方法。导师是您的资源，本节将告诉你如何使用你的导师。

• Advisors 导师

10 is about theses. Your thesis, or theses, will occupy most of your time during most of your graduate student career. The section gives advice on choosing a topic and avoiding wasting time.

10是关于论文的。您的论文或论文将占用您研究生职业大部分时间在。本节提供有关的建议选择主题并避免浪费时间。

• The thesis 论文

11 is on research methodology. This section mostly hasn't been written yet.

11 是研究方法论。本节大部分尚未编写。

• Research methodology 研究方法论

12 is perhaps the most important section: it's about emotional factors in the process of research. It tells how to deal with failure, how to set goals, how to get unstuck, how to avoid insecurity, maintain self-esteem, and have fun in the process.

12 也许是最重要的部分：它涉及到情感因素研究过程。它讲述了如何处理失败，如何设定目标，如何摆脱困境，如何避免不安全感，保持自尊心并拥有在这个过程中很有趣。

• Emotional factors 情感因素

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 ZvonaQai.ai. mit. edu.

文档仍处于开发阶段；我们欢迎您的贡献和评论。有些部分非常不完整。[括号内的注释和斜体表明一些主要的未完成的。我们赞赏的贡献;将您的想法和评论发送到ZvonaQai.ai.mit.edu

Reading AI 阅读

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.

许多研究人员将一半以上的时间花在阅读上。你可以学得更快，通过阅读别人的工作。本节谈论AI阅读；第4节涵盖了有关其他主题的阅读。

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.)

现在开始阅读的时间到了。一旦开始写论文，您将有更少的时间，并且您的阅读将必须更加专注于主题区域。在您的前两年中，您大部分时间会在上课，全面了解AI。为此，充分阅读教科书和发表期刊文章。（后期，您可能主要阅读草稿；请参阅第3节。）

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.

为了拥有具有坚实的基础，您需要阅读的材料数量似乎令人生畏，但由于AI仍然是一个小领域，因此您可以几年里，阅读过的重要论文中有很大一部分。有点棘手的是找出那些是。

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.

一些有用的参考书目：例如，研究生AI课程的教学大纲。其他大学的AI资格考试的阅读清单-特别是斯坦福大学（Stanford）也很有用，可以开阔你的眼界。

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.

有如果您在-对特定子领域感兴趣，然后去那个子领域的高级研究生那里，问他十大最重要的论文是什么，看看他是否会借给你复印。最近，出现了许多关于子领域的论文，特别是由 Morgan-Kauffman发表的。

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.

在AI实验室有三种内部出版物系列，工作文件，备忘录，和技术报告，形式上依次递增。它们在八楼游戏室机架。回顾过去的几年它们并获取任何看起来很有趣的副本。除了事实其中很多是重要论文，政治上非常重要保持知道实验室里的人在做的最新状态。

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

有很多关于AI的期刊，您可以花光所有时间阅读它们。幸运的是，只有少数值得一看。最重要的资料杂志是《人工智能》，也称为“人工智能杂志”或“ AIJ”。大多数真正重要的论文都在上面。

in Al 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. ComputationalIntelligence 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 PAMIis probably the best established vision journal; two or three interesting papers per issue. The InternationalJournalof 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 Alish robotics paper. IEEE Robotics and Automation has occasional good papers.

AIJ之所以成为AIJ，所以它的价值就是每一年左右扫描一次；但是它的很多东西确实很无聊。《计算智能》是值得一试的新竞争对手。《认知科学》还印有大量重要的AI论文。《机器学习》名副其实。《IEEE PAMI》可能是最佳的视觉期刊。每期有2、3篇有趣的论文。《国际计算机视觉杂志（IJCV）是新手，到目前为止很有趣。《机器人研究论文》是主要在动力学方面；有时它也具有里程碑意义的Alish机器人技术论文。《IEEE机器人技术和自动化》偶有好论文。

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 Al technical reports from other universities and reading the ones that look interesting.

值得去您的计算机科学图书馆（麻省理工学院的在技术广场一楼）大约每年一次，然后浏览去年的其他大学的AI技术报告，并阅读那些看起来很有趣的报告。

Reading papers is a skill that takes practice. You can't afford to read in full all the papers that come to you.

阅读论文是一种需要练习的技能。你负担不起阅读所有提交给您的文件的全文。

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.

阅读其中的内容分为三个阶段。首先是看看是否有任何感兴趣的东西。人工智能论文有摘要，应该告诉你里面有什么，但经常不告诉你；所以你有了跳来跳去，在这里或那里阅读一些内容，以了解作者的实际意图。目录，结论部分和简介是不错的地方。如果所有其他方法都失败了，那么您可能必须彻底阅读。

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.

一旦弄清楚了一般性内容以及所声称的内容贡献在于，您可以决定是否继续第二阶段，就是要找到文件中包含好东西的部分。大多数情况下，十五页论文可以重写为一页纸；您需要查找页面有令人兴奋的东西。通常这隐藏在不太可能的地方。什么作者发现对他的作品感兴趣可能对您而言并不有趣，反之亦然。最后，如果值得，您可以回头阅读全文。

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.

阅读时请牢记一个问题。“ 我该怎么用？” “这确实是作者声称什么？”“如果...？”读到的内容与理解论文并不相同。大部分的了解是在找出动机，作者做出的选择（其中许多隐含的），假设和形式化是否切合实际，论文建议的方向，眼前的问题，作者的研究计划中不断出现的困难的模式，论文指出的方向等，依此类推。

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.

将您的阅读和编程结合在一起是一个好主意。如果你是对某个领域感兴趣并阅读了一些相关论文，请尝试实现玩具版本。这使您更具体地理解。

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.

可悲的是，大多数AI实验室都是近亲繁殖的。人们经常阅读和引用工作仅在自己的学校完成。其他机构有不同的方式考虑问题，值得阅读，认真对待和参考他们的工作，即使您认为自己知道他们的问题。

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.

经常有人会给你一本书或纸，然后大叫你应该阅读它，是因为它是（a）有史以来最辉煌的事物（或之一）（b）精确地适用于您自己的研究。通常，当您真正阅读它时，您会发现它不是特别出色，仅适用于模糊的情况。这可能令人困惑。“我有什么问题吗？我错过了什么吗？” 真相是，最常见的情况是通过激发您的朋友对您的研究主题他们脑子里已经形成了一条思路。偶然的阅读相关书籍或论文认为或多或少是对你有帮助。

Getting connected 建立联系

After the first year or two, you'll have some idea of what subfield you are goifig to be working in. At this point-or even earlier-it's important to get plifged into the Secret Paper Passing Network.

第一个一年或两年后，你将有一些想法，关于你将来要在哪个方面研究。在这时候-甚至更早-重要的是要加入秘密论文传递网络。

This informal organization is wheie 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.

这个非正式的组织是AI的真正的情形。酷人们知道了这一切之后至少一年，引领潮流的工作才最终变成了出版论文。这意味着很酷的人有一年的时间开始使用新的想法。

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.

酷人如何发现新想法？也许他们在会议；但更有可能的是，他们通过秘密论文传递网络。

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.

方式如下。Jo Cool有个好主意。她把一个半途而废的实现及其工作，所以她写了一篇有关它的草稿。她想知道这个主意是否有正确，所以她将副本发送给十个朋友，并要求他们对此发表评论。

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 fivepage version (all that the AAAI proceedings allow).

他们认为这很酷，并且告诉Jo哪里有问题，他们将副本借给朋友复印。他们的朋友们将副本借给他们的朋友复印，依此类推。几个月后，乔对它进行了修改并将其发送给AAAI。六个月后，它首先以缩小版的五个字出现在印刷版中（AAAI程序允许的所有版本）。

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.

乔最终到处在清理程序并编写更长的修订版本（基于反馈（在AAAI版本上）阶段，并将其发送到AI Journal。AIJ已经将要花两年，评论和修订以及发布延迟的原因，所以Jo's想法发表三年后，她的想法终于出现在期刊中了-几乎很酷的人们第一次发现它后三年。酷人几乎不会从已发表的期刊文章中了解其子领域；那些也出来晚了。

You, too, can be a cool people. Here are some heuristics for getting connected:

你也可以成为一个很酷的人。以下是一些建立联系的启发式方法

• There's a bunch of electronic mailing lists that discuss Al subfields like connectionism or vision. Get yourself on the ones that seem interesting.

一堆电子邮件列表讨论了Al子领域，例如连接主义或计算机视觉。让自己加入到一些列表。

• Whenever you talk about an idea you've had with someone who knows the field, they are likely not to give an evaluation of your idea, but to say, "Have you read X?" Not a test question, but a suggestion about something to read that will probably be relevant. If you haven't read X, get the full reference from your interlocutor, or better yet, ask to borrow and Xerox his copy.

当您谈论与某个认识领域，他们可能不会对您的想法进行评估，而是说：“您读过X吗？”。这不是反问句，而是关于阅读内容的建议。如果您还没有阅读X，请获取完整的参考从您的对话者那里，或者更好的情况下，要求得到副本。

• When you read a paper that excites you, make five copies and give them to people you think will be interested in it. They'll probably return the favor.

阅读使您兴奋的论文时，请复印五份并交给您认为会对此感兴趣的人。他们可能会回馈你。

• The lab has a number of on-going informal paper discussion groups on various subfields. These meet every week or two to discuss a paper that everyone has read.

实验室有许多正在进行的非正式论文讨论小组。这些会议每周或每两周开会，讨论每个人已阅读的论文。

*Some people don't mind if you read their desks. That is, read the papers that they intend to read soon are heaped there and turn over pretty regularly. You can look over them and see if there's anything that looks interesting. Be sure to ask before doing this; some people do mind. Try people who seem friendly and connected.

些人不介意您看他们的书桌。也就是说，阅读论文他们打算阅读，很快就会堆在那里，并定期翻阅。您可以查看它们，看看是否有任何有趣的东西。在执行此操作之前，请务必先询问。有些人还是很在意。试试看似友好的人联系。

a Similarly, some people don't mind your browsing their filing cabinets. There are people in the lab who are into scholarship and whose cabinets are quite comprehensive. This is often a faster and more reliable way to find papers than using the school library.

同样，有些人不介意您浏览文件柜。那里是实验室里有奖学金的人，他们的橱柜相当全面。这通常是一种更快，更可靠的论文查找方式而不是使用学校图书馆。

• Whenever you write something yourself, distribute copies of a draft of it to people who are likely to be interested. (This has a potential problem: plagiarism is rare in AI, but it does happen. You can put something like "Please do not photocopy or quote" on the front page as a partial prophylactic.) Most people don't read most of the papers they're given, so don't take it personally when only a few of the copies you distribute come back with comments on them. If you go through several drafts-which for a journal article you should-few readers will read more than one of them. Your advisor is expected to be an exception.

当您自己写东西时，分发它的草稿副本给可能感兴趣的人。（这有潜在的问题：AI盗窃在AI中很少见，但确实会发生。你可以放“请不要复印或引用”一些东西在首页上）大多数人不会阅读他们收到的大多数论文，所以不要当您分发的副本中只有几本回来时带有他们的评论，不要在意。想象一下，如果您要看几份草稿（这很花时间），只有很少的读者会读一篇以上。您的导师将是一个例外。

• When you finish a paper, send copies to everyone you think might be interested. Don't assume they'll read it in the journal or proceedings spontaneously. Internal publication series (memos and technical reports) are even less likely to be read.

完成论文后，将副本发送给您认为可能会感兴趣的每个人。不要以为他们会在期刊中阅读它，内部出版物（备忘和技术报告）甚至不太可能被阅读。

• The more different people you can get connected with, the better. Try to swap papers with people from different research groups, different Al labs, different academic fields. Make yourself the bridge between two groups of interesting people working on related problems who aren't talking to each other and suddenly reams of interesting papers will flow across your desk.

与您建立联系的人越多越好。尝试与来自不同研究小组，不同AI实验室的人交换论文，不同的学术领域。让自己成为两个正在与相关问题打交道但是并不沟通小组之间的桥梁的人，然后成堆的其他有趣论文会在您的办公桌上流淌。

• When a paper cites something that looks interesting, make a note of it. Keep a log of interesting references. Go to the library every once in a while and look the lot of them up. You can intensively work backward through a "reference graph" of citations when you are hot on the trail of an interesting topic.

当一篇论文引用了一些有趣的内容时，请记录下来。保留有趣的参考记录。偶尔去图书馆并查看其中的很多内容。当你对一个有趣的话题非常感兴趣时，你可以通过引用的“参考图”来深入研究。

A reference graph is a web of citations: paper A cites papers B and C, B cites C and D, C cites D, and so on. Papers that you notice cited frequently are always worth reading. Reference graphs have weird properties. One is that often there are two groups of people working on the same topic who don't know about each other. You may find yourself close to closure on searching a graph and suddenly find your way into another whole section. This happens when there are different schools or approaches. It's very valuable to understand as many approaches as possible-often more so than understanding one approach in greater depth.

参考图形是引用的网页：论文A引用论文B和C，B引用C和D，C引用D，等等。您注意到的论文经常被引用总是值得一读。参考图有很奇怪属性。一是通常有两组在彼此不认识的人在处理同一个话题。您可能会发现自己接近搜索图时突然发现自己进入另一大块东西。特别是不同的学校或方法是，就会发生这种情况。了解尽可能多的方法往往比更深入地了解一种方法更有价值。

• Hang out. Talk to people. Tell them what you're up to and ask what they're doing. (If you're shy about talking to other students about your ideas, say because you feel you haven't got any, then try talking to them about the really good-or unbelievably foolish-stuff you've been reading. This leads naturally into the topic of what one might do next.) There's an informal lunch group that meets in the seventh floor playroom around noon every day. People tend to work nights in our lab, and so go for dinner in loose groups. Invite yourself along.

出去玩。与人交谈。告诉他们你在做什么，问他们在做什么。（如果您不愿意与其他学生谈论您的想法，请说因为您觉得自己一无所有，然后尝试与他们讨论有关你读到的非常好或令人难以置信的愚蠢的东西。这导致自然而然地成为下一步的话题。）

每天中午在七楼游戏室举行的非正式午餐会。人们倾向于在我们的实验室里上夜班，所以零散地去吃晚餐。邀请自己加入进去。

• If you interact with outsiders much-giving demos or going to conferencesget a business card. Make it easy to remember your name.

如果您大量与外部人进行互动，进行演示或参加会议，准备一张名片。让人轻松记住您的名字

• At some point you'll start going to scientific conferences. When you do, you will discover fact that almost all the papers presented at any conference are boring or silly. (There are interesting reasons for this that aren't relevant here.) Why go to them then? To meet people in the world outside your lab. Outside people can spread the news about your work, invite you to give talks, tell you about the atmosphere and personalities at a site, introduce you to people, help you find a summer job, and so forth. How to meet people? Walk up to someone whose paper you've liked, say "I really liked your paper", and ask a question.

在某个时候，您将开始参加科学会议。当你这么做的时候，你将发现以下事实：在任何会议上发表的几乎所有论文都是无聊或愚蠢的。（有一些有趣的原因但与此无关。）那为什么要去参加呢？在实验室之外认识世界上的其他人。外界人士可以传播有关您工作的新闻，邀请您演讲，告诉您现场气氛和个性，介绍您给其他人，帮助您找到暑假的工作，等等。如何遇见人？走到你喜欢的论文的人那里，说“我真的很喜欢您的论文”，并提出一个问题。

• Get summer jobs away at other labs. This gives you a whole new pool of people to get connected with who probably have a different way of looking at things. One good way to get summer jobs at other labs is to ask senior grad students how. They're likely to have been places that you'd want to go and can probably help you make the right connections.

在其他实验室获得暑假工作。这为您提供了全新的与可能与众不同的建立联系。在其他实验室获得暑期工作的一个好方法是请高年级研究生如何。他们可能曾经是您想要的地方工作过，可以帮助您建立正确的联系。

Learrning other fields 学习其他领域

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 Al, 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-Al 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:

• Take a graduate course. This is solidest, but is often not an efficient way to go about it.

• Read a textbook. Not a bad approach, but textbooks are usually out of date, and generally have a high ratio of words to content.

• Find out what the best journal in the field is, maybe by talking to someone who knows about it. Then skim the last few years worth and follow the reference trees. This is usually the fastest way to get a feel of what is happening, but can give you a somewhat warped view.

• Find out who's most famous in the field and read their books.

• Hang out with grad students in the field.

• Go to talks. You can find announcements for them on departmental boards.

bulletin

• Check out departments other than MIT's. MIT will give you a very skewed view of, for example, linguistics or psychology. Compare the Harvard course catalog. Drop by the graduate pick up any free literature.

office over there, read the bulletin boards,

Now for the subjects related to AI you

should know about.

• Computer science is the technology we work with. The introductory graduate courses you are required to take will almost certainly not give you an adequate understanding of it, so you'll have to learn a fair amount by reading beyond them. All the areas of computer science-theory, architectures, systems, languages, etc.-are relevant.

• Mathematics is probably the next most important thing to know. It's critical to work in vision and robotics; for central-systems work it usually isn't directly relevant, but it teaches you useful ways of thinking. You need to be able to read theorems, and an ability to prove them will impress most people in the field. Very few people can learn math on their.own; you need a gun at your head in the form of a course, and you need to do the problem sets, so being a listener is not enough. Take as much math as you can early, while you still can; other fields are more easily picked up later.

Computer science is grounded in discrete mathematics: algebra, graph the-

ory, 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 grad-

uate 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.

• Cognitive psychology mostly shares a worldview with AI, but practitioners have rather different goals and do experiments instead of writing programs. Everyone needs to know something about this stuff. Molly Potter teaches a good graduate intro course at MIT.

• Developmental psychology is vital if you are going to do learning work. It's also more generally useful, in that it gives you some idea about which things should be hard and easy for a human-level intelligence to do. It also suggests models for cognitive architecture. For example, work on child language acquisition puts substantial constraints on linguistic processing theories. Susan Carey teaches a good graduate intro course at MIT.

• "Softer" sorts of psychology like psychoanalysis and social psychology have affected AI less, but have significant potential. They give you very different ways of thinking about what people are. Social "sciences" like sociology and anthropology can serve a similar role; it's useful to have a lot of perspectives. You're on your own for learning this stuff. Unfortunately, it's hard to sort out what's good from bad in these fields without a connection to a competent insider. Check out Harvard: it's easy for MIT students to cross-register for Harvard classes.

• Neuroscience tells us about human computational hardware. With the recent rise of computational neuroscience and connectionism, it's had a lot of influence on AI. MIT's Brain and Behavioral Sciences department offers good courses on vision (Hildreth, Poggio, Richards, Ullman) motor control (Hollerbach, Bizzi) and general neuroscience (9.015, taught by a team of experts).

• Linguistics is vital if you are going to do natural language work. Besides that, it exposes a lot of constraint on cognition in general. Linguistics at MIT is dominated by the Chomsky school. You may or may not find this to your liking. Check out George Lakoff's recent book Women, Fire, and Dangerous Things as an example of an alternative research program.

• Engineering, especially electrical engineering, has been taken as a domain by a lot of AI research, especially at MIT. No accident; our lab puts a lot of stock in building programs that clearly do something, like analyzing a circuit. Knowing EE is also useful when it comes time to build a custom chip or debug the power supply on your Lisp machine.

• Physics can be a powerful influence for people robotics.

interested in perception and

• Philosophy is the hidden framework in which all AI is done. Most work in AI takes implicit philosophical positions without knowing it. It's better to know what your positions are. Learning philosophy also teaches you to make

and follow certain sorts of arguments that are used in a lot of AI papers. Philosophy can be divided up along at least two orthogonal axes. Philosophy is usually philosophy of something; philosophy of mind and language are most relevant to AI. Then there are schools. Very broadly, there are two very different superschools: analytic and Continental philosophy. Analytic philosophy of mind for the most part shares a world view with most people in AI. Continental philosophy has a very different way of seeing which takes some getting used to. It has been used by Dreyfus to argue that AI is impossible. More recently, a few researchers have seen it as compatible with AI and as providing an alternative approach to the problem. Philosophy at

MIT is of the analytical sort, and of a school that has been heavily influenced by Chomsky's work in linguistics.

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.

Notebooks 记笔记

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. 6

Writing 写作

There's a lot of reasons to write.

• You are required to write one or two theses during your graduate student career: a PhD and maybe an MS, depending on your department.

• Writing a lot more than that gives you practice.

• Academia runs on publish-or-perish. In most fields and schools, this starts in earnest when you become a professor, but most graduate students in our lab publish before they graduate. Publishing and distributing papers is good politics and good publicity.

• Writing down your ideas is the best way to debug them. Usually you will find that what seemed perfectly clear in your head is in fact an incoherent mess on paper.

• If your work is to benefit anyone other than yourself, you must communicate it. This is a basic responsibility of research. If you write well more people will read your work!

• AI is too hard to do by yourself. You need constant feedback from other people. Comments on your papers are one of the most important forms of that.

Anything worth doing is worth doing well.

• Read books about how to write. Strunk and White's Elements of Style gives the basic dos and don'ts. Claire Cook's The MLA's Line By Line (Houghton Mifflin) is about editing at the sentence level. Jacques Barsun's

Simple and Direct: A Rhetoricfor Writers (Harper and Row, 1985) is about

composition.

• When writing a paper, read books that are well-written, thinking in background mode about the syntactic mechanics. You'll find yourself absorbing the author's style.

• Learning to write well requires doing a lot of it, over a period of years, and getting and taking seriously criticism of what you've written. There's no way to get dramatically better at it quickly. * Writing is sometimes painful, and it can seem a distraction from doing the "real" work. But as you get better at it, it goes faster, and if you approach it as a craft, you can get a lot of enjoyment out of the process for its own sake.

• You will certainly suffer from writer's block at some point. Writer's block has many sources and no sure cure. Perfectionism can lead to writer's block: whatever you start to write seems not good enough. Realize that writing is a debugging process. Write something sloppy first and go back and fix it up. Starting sloppy gets the ideas out and gets you into the flow. If you "can't" write text, write an outline. Make it more and more detailed until it's easy to write the subsubsubsections. If you find it really hard to be sloppy, try turning the contrast knob on your terminal all the way down so you can't see what you are writing. Type whatever comes into your head, even if it seems like garbage. After you've got a lot of text out, turn the knob back up and edit what you've written into something sensible.

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.

• Perfectionism can also lead to endless repolishing of a perfectly adequate paper. This is a waste of time. (It can also be a way of semideliberately avoiding doing research.) Think of the paper you are writing as one statement in a conversation you are having with other people in the field. In a conversation not everything goes perfectly; few expect that what they say in a single utterance will be the whole story or last word in the interchange.

• Writing letters is good practice. Most technical papers would be improved if the style was more like a letter to a friend. Keeping a diary is also a way to practice writing (and lets you be more stylistically experimental than technical papers). Both practices have other substantial benefits.

• It's a common trap to spend more time hacking the formatter macrology than the content. Avoid this. LaTeX is imperfect, but it has most of the macrology you want. If that's not enough, you can probably borrow code from someone else who has wanted to do the same thing. Most sites (including MIT) maintain a library of locally-written extensions.

• Know what you want to say. This is the hardest and most important factor in writing clearly. If you write something clumsy and can't seem to fix it, probably you aren't sure what you really want to say. Once you know what to say, just say it.

• Make it easy for the reader to find out what you've done. Put the sexy stuff up front, at all levels of organization from paragraph up to the whole paper. Carefully craft the abstract. Be sure it tells what your good idea is. Be sure you yourself know what it is! Then figure out how to say it in a few sentences. Too many abstracts tell what the paper is generally about and promise an idea without saying what it is.

• Don't "sell" what you've done with big words or claims. Your readers are good people; honesty and self-respect suffice. Contrariwise, don't apologize for or cut down your own work.

• Often you'll write a clause or sentence or paragraph that you know is bad, but you won't be able to find a way to fix it. This happens because you've worked yourself into a corner and no local choice can get you out. You have to back out and rewrite the whole passage. This happens less with practice.

• Make sure your paper has an idea in it. If your program solves problem X in 10 ms, tell the reader why it's so fast. Don't just explain how your system is built and what it does, also explain why it works and why it's interesting.

• Write for people, not machines. It's not enough that your argument be correct, it has to be easy to follow. Don't rely on the reader to make any but the most obvious deductions. That you explained how the frobnitz worked in a footnote on page seven is not a justification when the reader gets confused by your introducing it without further explanation on page twenty-three. Formal papers are particularly hard to write clearly. Do not imitate math texts; their standard of elegance is to say as little as possible, and so to make the reader's job as hard as possible. This is not appropriate for AI.

• After you have written a paper, delete the first paragraph or the first few sentences. You'll probably find that they were content-free generalities, and that a much better introductory sentence can be found at the end of the first paragraph of the beginning of the second.

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.

• To write really useful comments, you need to read the paper twice, once to get the ideas, and the second time to mark up the presentation.

• If someone is making the same mistake over and over, don't just mark it over and over. Try to figure out what the pattern is, why the person is doing it, and what they can do about it. Then explain this explicitly at length on the front page and/or in person.

• The author, when incorporating your comments, will follow the line of least resistance, fixing only one word if possible, or if not then one phrase, or if not then one sentence. If some clumsiness in their text means that they have to back up to the paragraph level, or that they have to rethink the central theme of a whole section, or that the overall organization of the paper is wrong, say this in big letters so they can't ignore it. * Don't write destructive criticism like "garbage" on a paper. This contributes.. nothing to the author. Take the time to provide constructive suggestions.

It's useful to think about how you would react to criticism of your own paper when providing it for others.

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:

• Make sure it is readable. Papers are rejected because they are incomprehensible or ill-organized as often as because they don't have anything to say. * Circulate drafts for a while before sending it in to the journal. Get and incorporate comments. Resist the temptation to hurry a result into publication; there isn't much competition in AI, and publication delays will outweigh draft-commenting delays anyway.

• Read some back issues of the journal or conference you are submitting to to make sure that the style and content of your paper are appropriate to it.

• Most publications have an "information for authors," a one page summary of what they want. Read it.

• The major conferences choose prize papers on the basis of excellence both of content and presentation from among those accepted. Read them.

• It's often appropriate to send a short, early report on a piece of work to a

conference and then a longer, final version to a journal.

• Papers get rejected-don't

get dejected.

• The reviewing process differs greatly between journals and conferences. To get quick turn-around time, conferences must review quickly. There is no time for contemplation or for interaction. If you get bounced, you lose. But with a journal, you can often argue with the editor, and with the referee through the editor.

• Referees should be helpful. If you get an obnoxious referee report, you should complain to the program chair or editor. Don't expect much feedback from conference referee reports. But from journals, you can often get excellent suggestions. You don't have to do all of them, but if you don't you should explain why, and realize that it may take further negotiation. In any case, no matter which side of the reviewing process you are on, be polite. You

are going to be working with the people whose papers you review as part of a community for the rest of your professional life.

• MIT AI Lab Memos are generally of publishable or near-publishable quality. De facto, Technical Reports are almost always revised versions of theses. Working Papers can be and often are very informal. They are a good way to get a lot of copies made of a paper you'd want to send to a bunch of colleagues anyway. You publish one of these internal documents by getting

a form from the Publications Office (just off the eighth floor playroom) and getting two faculty members to sign it. 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 maygo 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 演讲

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:

• Patrick Winston has a great short paper on how to give talks. He also gives a lecture based on it every January which simultaneously illustrates and describes his heuristics.

• If you feel you are a bad speaker, or if you want to be a good one, take a course on public speaking. An intro acting class is also useful.

• If your advisor's students have regular research meetings, volunteer to talk about your stuff.

• The MIT AI lab has a series of semiformal talks known as the Revolving Seminar. Volunteer to give one if you have something worth turning into an AI memo or a conference paper.

Learn enough about the Lab's various robotics projects so when your relatives or friends from out of town come you can give them a tour and a little 60 second talk in front of each robot about it. (Your relatives and non-AI friends will usually love this; they won't be so impressed by the intricacies of your TMS.)

• Since revising a talk is generally much easier than revising a paper, some people find that this is a good way to find the right way to express their ideas. (Mike Brady once remarked that all of his best papers started out as talks.)

• Practice the talk in an empty room, preferably the one in which you will deliver it. Studies of context effects in memory suggest that you will remember what you are going to say better if you have practiced in the room you deliver in. Practice runs let you debug the mechanics of a talk: what to say during each slide, moving overlays around smoothly, keeping notes and slides synchronized, estimating the length of the entire talk. The less time you spend fumbling around with your equipment, the more time you have left to communicate.

• Practicing with a mirror or tape or video recorder is another alternative. The lab has all three. They might help debug your voice and body language, too.

• For a relatively formal talk-especially your Oral Exam-do a practice run for half a dozen friends and have them critique it.

• Watch the way other people give talks. There are a lot of talks given by people visiting MIT. Attending such talks is a good way to get a taste of areas you aren't so familiar with, and if the talk turns out to be boring, you can amuse yourself by analyzing what the speaker is doing wrong. (Going to a seminar is also a way to cure the mid-afternoon munchies...)

• Cornering one of your friends and trying to explain your most recent brainstorm to him is a good way both to improve your communication skills, and to debug your ideas.

Some key things to remember in planning and delivering a talk:

• You can only present one "idea" or "theme" in a talk. In a 20 minute or shorter talk the idea must be crystal clear and cannot have complicated associated baggage. In a 30 or 45 minute talk the idea can require some buildup or background. In an hour talk the idea can be presented in context, and some of the uglies can be revealed. Talks should almost never go on for more than an hour (though they often do).

• The people in the audience want to be there; they want to learn what you have to say. They aren't just waiting for an excuse to attack you, and will feel more comfortable if you are relaxed.

• Take at least one minute per overhead. Some people vary in their rate, but a common bug is to think that you can do it faster than that and still be clear. You can't.

• Don't try to cram everything you know into a talk. You need to touch. on just the high points of your ideas, leaving out the details.

• AI talks are usually accompanied by overhead transparencies, otherwise known as "slides". They should be kept simple. Use few words and big type. If you can't easily read your slides when you are standing and they are on the floor, they're too small. Draw pictures whenever possible. Don't stand in front of the screen. Don't point at the overhead if it is possible to point directly at the screen. If you must point at the overhead, don't actually touch the transparency since you will make it jerk around.

Programming 关于编程

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.

并非每个AI论文都涉及代码，并且AI中有重要人物从来没有写过重要的程序，但是你需要能够编程做AI。大多数AI工作不仅涉及编写程序，但是学习编程将使您了解哪些可行和哪些不可行的直觉。是AI对认知科学的贡献的造成约束的主要来源。

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.

麻省理工学院，基本上所有的AI编程都是在Common Lisp中完成的。如果你不会，就去学。但是，学习编程语言并不是学习编程。AI编程所涉及的某些技术与系统所用的技术完全不同编程或用于其他应用程序。你可以开始通过阅读阿伯尔森和Sussman的《计算机程序结构和解释》，并做一些练习。这本书不是关于人工智能编程每本身，而是它教导一些相同的技术。然后阅读第三版的温斯顿和霍恩的《Lisp》书; 它里面有很多简洁的AI程序。最终，多编程，而不是阅读，是学习编程的最好方法。

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.

Lisp程序的文化是主要由学徒方式。有些人可以很好地一起编写代码。这在很大程度上取决于所涉及人的性格。抓住机会直接和有能力的程序员开展更多工作。或者查看是否可以让其中之一来批判您的代码。

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.

读其他人的代码也非常有用。您可以找高年级要他们程序的源代码。他们可能会抱怨一下，并抱怨他们的编码风格多么糟糕，该程序并没有真正起作用，然后无论如何都要给您代码。然后仔细阅读。这很耗时。它可以采取只要阅读和充分了解别人的代码，但是可以让您自己学会编写代码，因此在您的第一个学期或第二个学期中花费了几个星期的时间。你会学习很多您不会想到的绝妙技巧，而这些绝非在任何教科书中。

You'll also learn how not to write code when you read pages of incomprehensible uncommented gibberish.

您还将学习如何不写出烂代码，当您阅读到难以理解的页面未注释的胡言乱语。

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.

他们在软件工程课程中告诉您的所有标准无聊的事情都是真正的人工智能编程。注释您的代码。使用适当的数据抽象除非有编译的理由不这样做。将图形与您的代码分开，因此您构建的大部分内容都是Common Lisp，因此可移植，类似。

Over your first couple years, you should write your own versions of a bunch of standard Al building blocks, such as

在最初的几年中，您应该编写一堆自己的版本标准Al构建块，例如

a truth maintenance system,

a means-ends planner,

a unification rule system,

a few interpreters of various flavors,

an optimizing compiler with flow analysis,

a frame system with inheritance,

• several search methods,

• an explanation-based learner,

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

随便你。您可以在几天之内编写精简但实用的版本。也可以扩展现有的真实版本。

alternative. It's only when you've written such things that you really understand

只有当你写出来，你才真正理解

them, with insight into when they are and aren't useful, what the efficiency issues are, and so forth.

何时有用时，效率问题是什么是，依此类推。

Unlike most other programmers, Al 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 Al 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.)

与大多数其他程序员不同，Al程序员很少可以借用彼此代码。（视觉代码是个例外。）部分原因是AI程序很少真正起作用。（许多著名的AI程序仅在论文三个例子中起作用，尽管该领域现在已经不在有这种这种草率的曾经容忍度）

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.

另一个原因是AI程序通常被着急的组合在一起，并不考虑最大通用性。使用Foobar的“标准”规则解释器一开始可能非常有用，您会深入了解它，如果它没有您需要的功能或者功能太多或者效率太低。您也许可以对其进行修改，但是请记住，理解他人的代码非常耗时。有时候更好自己写。在这里完成了六个编程项目在最后一段变得非常方便。最终，您可以进行设计并在下午实施自定义的TMS算法（例如）。（那么你会在接下来的六周内对其进行调试，这就是如何运转的。）有时使标准包可以工作本身都可以变成论文。

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.)

像论文一样，编程可能会被过度抛光。重写代码直到完美，使所有内容最大化抽象，编写宏和库，然后和操作系统内部组件的交互会吸引了很多人偏离自己的方向甚至领域的。（另一方面，也许这就是您真正想做的谋生。）

Advisors 导师

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, Al 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 Al 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.

• How much direction do you want? Some advisors will hand you a welldefined thesis-sized problem, explain an approach, and tell you to get to work on it. If you get stuck, they'll tell you how to proceed. Other advisors are hands-off; they may give you no help in choosing a topic at all, but can be extremely useful to bounce ideas off of once you find one. You need to

think about whether you work better independently or with structure.

• How much contact do you want? Some advisors will meet with you weekly for a report on your progress. They may suggest papers to read and give you exercises and practice projects to work. Others you may not talk to more than twice a term.

• How much pressure do you want? Some advisors will exert more than others.

• How much emotional support do you want? Some can give more than others.

• How seriously do you want to take your advisor? Most advisors will suggest thesis topics fairly regularly. Some can be depended on to produce suggestions that, if carried out diligently, will almost certainly produce an acceptable, if perhaps not very exciting thesis. Others throw out dozens of off-the-wall ideas, most of which will go nowhere, but one in ten of which, if pursued with vision, can result in ground-breaking work. If you choose such an advisor, you have to act as the filter.

• What kind of research group does the advisor provide? Some professors create an environment in which all their students work together a lot, even if they are not all working on the same project. Many professors get together with their all their students for weekly or biweekly meetings. Will that be useful to you? Are the advisor's students people you get along with? Some students find that they construct important working relationships with students from other research groups instead.

• Do you want to be working on a part of a larger project? Some professors divide up a big system to be built into pieces and assign pieces to individual students. That gives you a group of people that you can talk to about the problem as a whole.

• Do you want cosupervision? Some thesis projects integrate several areas of AI, and you may want to form strong working relationships with two or more professors. Officially, you'll have just one thesis supervisor, but that doesn't have to reflect reality.

• Is the advisor willing to supervise a thesis on a topic outside his main area of research? Whether or not you can work with him or her may be more important to both of you than what you are working on. Robotics faculty at MIT have supervised theses on qualitative physics and cognitive modeling; faculty in reasoning have supervised vision theses. But some faculty members are only willing to supervise theses on their own area of interest. This is often true of junior faculty members who are trying to build tenure cases; your work counts toward that.

• Will the advisor fight the system for you? Some advisors can keep the department and other hostile entities off your back. The system works against certain sorts of students (notably women and eccentrics), so this can be very important.

• Is the advisor willing and able to promote your work at conferences and the like? This is part of his or her job, and can make a big difference for your career.

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: * Read the Lab's research summary. It gives a page or so description of what each of the faculty and many of the graduate students are up to.

• Read recent papers of any faculty member whose work seems at all interesting.

• Talk to as many faculty members as you can during your first semester. Try to get a feel for what they are like, what they are interested in, and what their research and supervision styles are like.

• Talk to grad students of prospective advisors and ask what working for him or her is like. Make sure you talk to more than one student who works with a particular advisor as each advisor has a large spectrum of working styles and levels of success in interaction with his or her students. You could be misled either way by a single data point. Talk to his or her first year advisees and his seventh year advisees too.

• Most or all faculty member's research group meetings are open to new grad students, and they are a very good way of getting an idea of what working with them is like.

Al 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.

The thesis 论文

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-Al 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 ticipate in a conversation with the literature.

vision and par-

• 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. al

of this at the same time. Your work will be manageable and comprehensibleif 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.

*eThe 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 shapefrom-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.)

Research methodology 研究方法论

[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. Al methodology is a jumbled mess. Different methodologies define distinct schools which wage religious wars against each other.

(本节内容薄弱，请贡献)研究方法论定义研究的活动是什么，怎么进行，如何衡量进度以及成功。Al方法一团糟。不同的方法论定义了不同的学校，彼此甚至到了进行宗教战争的地步。

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."

方法就是工具。使用它们; 而不要让他们使用你。不要迷上口号，认为一个高于其他的观点：“人工智能研究需要在坚实的基础上进行；”“哲学家只是说。AI是关于做的；“，“您必须知道在计算什么你问如何计算前。”

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.

为了在AI成功，你必须要善于技术方法，同时您必须对这些感到怀疑。例如，您应该能够证明定理，同时你应该怀疑定理是否证明任何东西。

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."

AI的大多数优秀作品都巧妙地平衡了几种方法。例如，您必须在过多的理论之间走出一条细线，可能与任何理论都无关真正的问题和大量的实现，这可能表示不连贯临时解决方案。您不断面临研究决策沿着“整洁”和“臃肿”之间的边界划分。

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.

你应该拿该问题在某种程度上正式化的时间（例如，您可以证明它的难处理性），还是应该以其原始形式处理它（定义不明确但更接近现实？采用前一种方法会（成功时）导致明确，某些结果通常会很无聊或至少不会解决问题；后一种方法会冒着变成一大堆魔改的风险。任何人工作，任何人都应以合理的平衡为目标，子问题似乎为此而哭，同时又对大局保持诚实。

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.

有些工作就像科学。你看人们如何学习算术，大脑如何运作，袋鼠如何跳动，并试图弄清楚并做出可测试的结果理论。有些工作就像工程：您尝试构建更好的问题解决程序或成形算法。有些工作就像数学：您跟 公式打交道，尝试了解它们的特性，对其进行磨练，证明有关它们的东西。一些工作以实例为导向，试图解释具体现象。最好的作品结合了所有这些以及更多。

Methodologies are social. Read how other people attacked similar problems, and talk to people about how they proceeded in specific cases.

方法学是社会的。阅读其他人如何解决类似的问题，并与人们讨论在特定情况下如何进行。

Emotional factors 情感因素

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. Youll 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 window-shopping in Harvard Square. If you are thinking about your research in background mode all the time, ideas will just pop out. Successful Al 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 admitted 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.

• Setting your sights too high leads to paralysis. Work on a subproblem to get back into the flow.

• You can get into a positive feedback loop in which doubts about your ability to do the work eat away at your enthusiasm so that in fact you can't get anything done. Realize that research ability is a learned skill, not innate genius.

• If you find yourself seriously stuck, with nothing at all happening for a week or more, promise to work one hour a day. After a few days of that, you'll probably find yourself back in the flow.

• It's hard to get started working in the morning, easy to keep going once you've started. Leave something easy or fun unfinished in the evening that you can start with in the morning. Start the morning with real workif you start by reading your mail, you may never get to something more productive.

• Fear of failure can make work hard. If you find yourself inexplicably "unable" to get work done, ask whether you are avoiding putting your ideas to the test. The prospect of discovering that your last several months of work have been for naught may be what's stopping you. There's no way to avoid this; just realize that failure and wasted work are part of the process.

• Read Alan Lakien's book How to Get Control of Your Time and Your Life, which is recommended even by people who hate self-help books. It has invaluable techniques for getting yourself into productive action.

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 Heliz.

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!"

Endnote

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 Al," by Alan Bundy, Ben du Boulay, Jim Howe, and Gordon Plotkin.