Readers, please note: In the interest of providing information on this subject, we are posting the raw transcripts from the FCRC CRA-W workshop. This is an unedited transcript, but still should provide you with background information of use. The edited transcripts will be completed by spring 2000.


Anne Condon: Unfortunately, Joanne Martin won't be with us today. In the remaining time that I have I'd like to make two points. The first one is that research, as a career, is really rewarding. I'm sure that many of you are just getting started on research and maybe not sure yet whether you're committed to a career of research but I hope that by the end of this workshop you'll realize that a research career is a really great thing and something to strive for. The other point that I want to make is that knowing how to go about research is really critical in ensuring a productive, rewarding research career and I've learned a lot about the hows over the years from my colleagues, both at the University of Washington and at the University of Wisconsin and I'd like to share some of those with you today. I particularly like to acknowledge my advisor, Richard Ladner*, who's been a supporter and a mentor and an advocate for my research since I started. I'd also like to acknowledge some of my colleagues at the University of Wisconsin, Eric Bach*, who also does theoretical computer science and somebody who's taught me a lot about independence of mind and good judgment. Mark Hill and Lloyd Smith. Mark is a professor in Computer Science and Lloyd is a professor in Chemistry at the University of Wisconsin. I've had the good fortune to work on research with both of them and it's helped me broaden into new areas and also I think it's helped me appreciate what a great thing enthusiasm is and being able to inspire other people to do research. Both of them are really good at that. And finally, I'd like to acknowledge Mary Vernon, who's been a mentor and supporter also for all the years I've been at Wisconsin, someone who's judgment I really value.

O.K. So, why research? Why should you do research in Computer Science and Engineering, Computer Engineering? Well, Computer Science is really a very exciting field. They are relatively young fields and growing fields right now and they're really good fields to do research in. There are opportunities ranging from the theoretical to applied work. Opportunities for innovation, for creating new technology and products. And also, in my opinion, opportunities for interdisciplinary work, work at the interface of Computer Science and other fields, more than ever before. So for all of those reasons, Computer Science is a great field in which to do research.

But what I want to talk about right now are sort of more personal reasons that research is really a rewarding career and a rewarding endeavor. When I told my daughter that I was preparing this talk a week or two ago, she said "Well, Mom, I think that research as a career is a good thing because I'm curious." And I thought, well, I hope she stays curious. And for sure, research is one of the ways that keeps your mind curious and keeps your mind stimulated and this seems to me to be one of the most basic human needs, one of the things that's really satisfying is to be able to be stimulated mentally, to be able to discover new things. It doesn't happen very often but when it does it's really a wonderful thing.

The second reason that I think research as a career is really rewarding is the collaborations that I've been able to participate in. I've worked with people in different areas and people in theoretical Computer Science and being able to share ideas with people, being able to hear other people's ideas, being able to sift through ideas, synthesize ideas is really a wonderful thing and I really value that.

A third reason is membership in a community of scholars or innovators. When you get started out in research, I think, it's not clear where you're contributing to or who's listening to what you're doing or who's reading what you're doing but over time, there really is a sense of belonging to a community of people. I think that the computing research community contributes much that is valuable to society and does really great work. It's nice to feel like I'm really a member of that community. And membership in a community like this happens because of effort on my part and contributions on my part, and also because I get the recognition back that my contributions are valued. But it also means that when really remarkable or exciting or unexpected results are proved by somebody else in the community I can personally feel really excited and in that sense, the results of the community are mine, as well as mine being part of the community. And for me this is, again, one of the real rewards of being in a research community.

Gaining perspective on ideas is another thing. It's nice to have been around long enough, I've been doing research now for about 15 years and it's nice to see ideas that seemed wild and unrealistic 15 or 20 years ago become valuable and mainstream ideas today. This kind of perspective on ideas is something that comes only if you stick with it and you continue to do it for many years. I feel like I can, I have a good, better judgment on original ideas and valuable ideas than I did when I started out.

And finally I think that doing research has dividends in other activities that I do. It certainly changes the way I teach and it also probably changes the way I interact with my kids, for example, the kinds of things I encourage them to do.

So now let me talk about some of the hows. So I think these points may seem very obvious but if you think about them, there's a lot of strategies that you can develop that can make a big difference in your ability to do research successfully. In a nutshell, what I want to say is first of all, you've got to work on important problems. You've got to work productively. It's really nice if you can work with good people. And of course you need a supportive environment if you want to be able to do good work. And finally but not least, it's important to seek out and enjoy recognition for your work.

Let me expand on these points in the next few slides. * said if you want to make important discoveries, work on important problems. Well, as I said, that seems kind of obvious when you think about it but it's really something to keep in mind because you have many choices over time on choosing what things you're going to work on and it's important to have good judgment and develop independence of mind and pick the important things to work on. How do you do that? Well, reading critically, listening critically to what other people are doing, having role models, people whose work you really admire and aspire to and expecting the same from yourself and ways that you can make sure you work on important problems. It's good to have a coherent research plan. If you're going to work on important problems, you probably can't solve them all in a year. You're going to have to break it down, work on little pieces, understand how the little pieces are going to get you to closer at least to solving the really important problems that you're interested in. And so expect to spend time and to work over time towards the important goals that you're trying to achieve. And third of all, get on with it. What I mean by this is that you probably can solve the hard problems quickly or fast but it's important to be involved in the research process, to feel like you're making progress, even on really small things. For example, you may re-derive a result in a paper independently yourself that you know somebody else has derived. You may rerun an experiment and see how different algorithms compare with each other. This gives you something to talk about when you meet people at conferences. It gives you something to talk about at * sessions at conferences even if you haven't gotten to the point that you're not ready to talk about your major result yet. So being involved in the process and making sure you have short-term reasonable goals is also a good thing.

Work productively. For me it's important when I'm working on a new problem to set aside time when I can get totally absorbed and think about it. If I just set a few hours a week aside, I'm never really going to get on top of it and so it's important to make sure you find time. That's probably the most difficult thing to get some times.

Think creatively. When you read literature, when you listen to what other people are saying, challenge the assumptions they're making. Think about connections between other people's work and your work and when you do that, ideas will come.

Cultivate a research mentality in related activities. So when you're teaching, for example, it's possible to teach in a way, an inquiry-based way where you try to get students to come up with ideas, you try to expand your own thinking about a problem rather than just presenting the material without those extra perspectives and this can make a difference in research too.

Using resources effectively is very important. I think, it's my personal opinion, that people in Computer Science don't use the library as well as they should and I think that it's very important to be a scholar and to look back, see what was done 20, 30 years ago that may be relevant to what you're doing now.

And finally value your time and that of others. When you come to meetings be prepared. Make sure that you're not wasting other people's time, that you've got something to contribute and good questions to ask.

Work with good people. It's really a nice thing to be able to discuss your research with your colleagues and with the best people in your area. Try to get to conferences where you can meet these people and tell them what you're doing. If you're a student, sometimes your fellow students are the best people that have time and energy and interest to give you feedback on your work.

Seek out good collaborators. As I said before, collaborations are really, really rewarding, and it's not that hard to find good collaborators. If you go to conferences and you have some half-baked ideas and you're willing to share them with other good people, they're bound to be excited and want to work with you on the same thing.

And finally, provide, if you're a professor like I am, provide peer guidance and feedback to your advisees. I think it's really important when people are making an effort to praise their efforts, to make sure that they understand that it's valuable. You don't come up with great results in a short time but effort and sticking with the process is really a good thing and something that should be rewarded.

Work in a supportive environment. Well, in my opinion support means a lot of things. It means time, money, constructive feedback, role models, mentors and advocates, for example, and it's hard to get all of those things but it's important to get them. And it's important to be able to reason effectively for the resources you need. One way you can figure out what resources you should have is to look around and see what other people like you have and to make sure that you have similar resources. If you have comparison points, you can always make effective case for what you need as well. It may be that you need to make that with the head of your group or the chair of your department or maybe with your spouse or your partner, but in any case, make sure that you get the resources that you need to do the job. In addition to getting support for yourself, I believe that it's really important to support others. As I said before, supporting your students is really important but more generally, things that are good for your colleagues, things that are good for your institution, things that are good for your field are probably good for you. And if you can support other people it is a rewarding thing to do and it pays off.

Finally, enjoy recognition for your work. This is something that's easy to forget. One way to get recognition for your work, of course, is to publish in the best journals and conferences in your field. Find out what those are and make sure that you're able to present your work at these places. Give talks regularly at good institutions. When I was an assistant professor, if I happened to be somewhere, I would contact people that I knew at a neighboring institution and ask if I could come give a talk. And that's perfectly acceptable and a good way that you get out there and your work gets recognized.

I just want to say a word about interdisciplinary work. I think it's important as being valuable by people in the relevant disciplines that that work is involved in and it's important to make sure that that happens.

And finally, celebrate your accomplishments. Again, this is something that I've learned particularly from Mark Hill. Every time his students submit a paper that's the time they go out and celebrate. They don't wait to see if its accepted or rejected. The fact that they've done the work and that it's out there is what's important and that's the time to celebrate. And that's really an important thing. Make sure you realize how valuable your efforts are and celebrate that, because getting recognition and celebrating your accomplishments are a way to feel good about what you're doing, and it increases your commitment and your interest and your motivation to do the best you can in research, so I really can't overstate this point.

At this time, I'd like to ask the other panelists to talk.

Jeanne Ferrante: So I think Anne's given us a very nice introduction into the how of research. I'd like to say a little bit about the where. Particularly this is based on my experience. As Anne mentioned, working at IBM, TJ Watson Research Center, I was there from '78 to '94, so quite a long time and have been at UC San Diego for the last five years. So, I'd like to organize a talk by talking first about what's difference for industrial versus academic research. Again, this is based on my own experience, so certainly need to keep that in mind.

So one thing that was different about my experience at the two places is at IBM I was able to resist for the entire time I was there being a research manager. And so in that kind of a setting you needn't be a manager, although there is pressure to do it. On the other hand, being at the university, you were very much research manager. You cannot avoid it. That's been a big difference in terms of the responsibility I have to think about in terms of my own research. It's not just me, it's my group. In terms of industry, I think it's very important to develop company contacts, support within the company. Whereas as a university researcher you really have to develop the contacts for grant support and industrial contacts are important also, but it's a much broader and larger sense. At IBM I would up working with people from IBM like Barbara Simons. We actually did some work together. But now it's a much broader playing field and there's really much more, there's many more opportunities, I think, because you're not just working with one company. You can work with many companies and do much more varied kinds of things. One thing that was surprising to me in coming to academia was that really have a fundamentally different research relationship with the people you work with, because primarily you're working with your students. You do work with colleagues but working with your students is really quite different. I was very much used to a equal colleague kind of relationship at IBM and everyone was basically on the same footing. That's really not true in terms of your student relationship. I really have to think much more about the students development, what's good for them, how they, what kinds of experiences they need and where they need to go. And so that's been a big difference. Initially when you join a place like IBM research, at least in the years that I was there, you sign on to a project. You're expected to be a good team member of that project. Usually that project's in the area that you've been working in, but it might not be exactly what you've been doing. My experience there is that you're expected to initially pay y our dues and be a good team member of this project and then you can go on and be more independent and propose your own research and so forth. Whereas as soon as you land at the university you're an independent person. You're setting your own agenda and setting your own directions and goals and from that point on, you take the responsibility.

One thing that I found at IBM is that it was easier to change fields being at a company. I actually went, as Anne mentioned, my Ph.D. was in math and I actually worked in theoretical computer science, though I didn't bother to switch departments because you had to have a master's to switch, so I decided not to. So when I went to work for IBM, I basically switched fields. I went into the area of compiler optimization, where I've been working for the rest of my career. I really felt very grateful to IBM because in some sense they let me do that. It's certainly a start-up time involved in that. I basically had to learn the area, I was working in the area. This is also a part of working on the project and paying my dues so I really learned a lot. But that's not uncommon in a company like IBM. I think it's very ordinary for people to move from one area to another and if you think about it in a group like that you've got a very large computer science department, more on the order of hundreds rather than tens. And so you've got lots of different areas represented and different people that you can consult. It's possible, I think, to change areas in academia but I certainly wouldn't advise it pre-tenure. You can do it by kind of overlapping what you're doing but it's more difficult.

One difference I found also is that I work a lot harder in academia than I did in industry. It's a very marked difference. Yes, and one of my students actually asked me, well, didn't you know that this was going to happen to you and how come you did this, very wisely said? And I said "well, I thought I'd be different." But of course that wasn't true and not only did I get embroiled in most of the other activities that a professor does but I've also become department chair after two years, so that's perhaps, I did find that I could strike a better balance in my life when I was in industry. Which is not to say that I regret at all the decision. I think it's a wonderful change for me and I really like all the things I'm doing, it's just that there are a lot more of them.

Anne mentioned interdisciplinary work. I think for the same reason that changing fields is easier in industry, I think interdisciplinary work, by that I mean working with people in other departments, can also be easier. I think it's certainly doable in academia and again, it's harder to do pre-tenure just because then you might get several departments judging you in terms of voting on your tenure case, so it's easier to do that later.

Again, because I think you have a little more time in industry it's easier to do outside service, so be on committees and organize things. It's harder to find the time to do that.

So I'm happy to answer questions about this now or later, but I also wanted to talk about some of the issues that are the same in industry and academia. I think many of the things that Anne talked about are the same. The activities are the same, we're writing papers, serving on program committees, going to conferences and workshops, making contacts, reviewing papers, mentoring, etc. And the aims are very much the same. I think we all want to do excellent work. We all know that we need to establish a presence and there may be differences in the way you do that, whether you're in industry or academia. The other thing that I think is important and was underlined with what Anne was saying is it's important to have fun. We really should be enjoying what we're doing. Research is an activity which has a lot of uncertainty to it, in the sense that we don't know what we're doing most of the time. We might as well say it. Really that's it's most positive and it's most negative aspect. The best thing about is we don't know where we're going. We're setting the direction. We're finding out new things and so it's a very fluid environment.

The other thing, another thing that's the same is that it's extremely important to get advice and feedback. Anne mentioned mentoring. I think mentoring is extremely important. Finding a mentor and talking to them, using them, what conferences and journals should you be publishing in, whether you should be on this program committee or get involved in this conference, it's really good to get advice. It's also important to have role models. Find people or think about people that you would like to be like and would like to emulate. That's been a very important direction setter for me in terms of my own life.

Something else that's the same is how we feel about research in either activity and the part that has to do with the uncertainty of research. There's a large probability that we might fail. Maybe not large, maybe small, but there's always this expectation that maybe this won't work out. And we can't let that stop us from going ahead. One of the things that's really important is to take risks. I think the other extreme is to have overly high expectations of what you might get. So it's really important to listen to others, think about what you're doing and have an overall plan. One of the things that I've really noticed is that the most important factor in success is just the will and determination to keep going and if in fact you give up you're not going to get there.

There is this sort of contrasting thing where my gosh, I'll never succeed versus I'm going to win the * award and one can vacillate before you even get going on the problem between those two extremes and so it's important to let that happen but keep going.

Sabbaticals are something that's common to both, that may be surprising but I had several sabbaticals when I was at IBM, so industry does have them too. It's very important to have them and to use them to take a long-term view of what you're doing, to reevaluate. Maybe that's a time to switch areas a little bit. But it's an important time. I found all of the sabbaticals that I've taken have been very transforming.

Anne mentioned also a supportive environment. I think that that's extremely important, both working to set it up and making sure it happens. It's extremely important with students but it's also important with industry and I think we as researchers have to be proactive in making sure that that happens.

Another thing that's in common is the need for networking. Some people are born networkers, others are not. If you are not, you really have to do it and so even if you have to set goals for yourself, like I will talk to the following five important people at the next conference I go to, it's important to do that.

O.K. I think that's basically all I wanted to say. Oh, I have one more thing. The other thing that's both industry and academia have in common is there's still a two body problem and it may be a little bit easier in industry but it's possible to work things out in academia as well. My husband and I both work at, we met at IBM and we both work at UC San Diego, in fact in the same department. In fact, we share some of the same students and work in the same research area. And we're not the only such couple now. We just hired last year Ron * and *, who are both at UCSD so it's becoming a more common occurrence. So basically that's all I wanted to say and now can turn it over to Barbara.

Barbara Simons: Picking up on one thing that Jeanne said, I just thought I'd mention there's never been a woman * award winner and I really hope as president I get the chance to give the * award to the first woman who gets it so I'm keeping my fingers crossed on that. I also should mention that it's 6:20 on my watch and I just flew in from California last night so anything I say I'm not fully responsible for. Already this morning I started off by going down to the Crystal Ballroom. No one was there so I went up to my room with my breakfast, tried to get into the wrong person's room, came back downstairs, went back to the Crystal Ballroom; there was still nobody there. And since it was after 8:30 I was getting nervous so I finally found my way up here. So that's how my day has begun. Couple of points. I actually am no longer chair of the U.S. * Policy Committee of * although I did start it. That's called USACM. And I also wanted to mention that although it is true that I have a master's degree but I had to get it at the same time as my Ph.D. and I don't count it because they wouldn't have given me the Ph.D. if they hadn't also given me a master's degree which I didn't earn. Because my career's been very non-standard and I should also say that I was 40 when I got my Ph.D., so you might say wow, that's really neat, she's got only a Ph.D. or you might say it took her a damn long time. And my parents just couldn't believe it. How many graduate students are here? A lot, oh good. O.K. I want to talk to you. I thought I'd talk about my experience as a graduate student and how I finally did get this Ph.D. and I was not a graduate student for 20 years, it wasn't that bad. I did take time off and I dropped out of school, basically, and had a family and then went back. But going, well, when I went back, I went back, actually after my marriage broke up, with no degrees and the feeling that I should learn how to do something so that I could support myself so I took a programming course and since I'd been a math major I wasn't too afraid of taking a programming course and I kind of liked it. Once I'd done that I was already ahead of the game because this was back in the early 70s, it was really a long time ago. Back in those days, you didn't actually need a Computer Science degree in order to get a job as a programmer. If you knew how to program you could get a job doing that. So I was already ahead of the game from where I was before I took the programming course and so I just figured I would, I kept on, I didn't start off to get a Ph.D.. If I started off to get a Ph.D., there's no way I would have done anything. It was far too intimidating. I mean, how could I possibly hope to solve a problem which all these really brilliant people who already had their Ph.Ds couldn't solve? I mean that just didn't make any sense but I could set little goals for myself. So like the first little goal was to learn how to program and then the next little goal was to keep on and to take more courses and after a while, it didn't take too long back in those days because there was less to our field then there is now, I found myself doing graduate work. This is back at Stonybrook and somebody observed, I mean I was still going to school part time, not a matriculating student. I should add that I had been chairman's wife in the math department before this all happened so one of the things that I learned was that you can always get around the system. And in particular, you should never accept no for an answer. These were very valuable, because I see, you know, when you're a student and you look at the structure there, it all looks so foreboding but when you're on the other side and you see what these guys are doing and you know that the rules, that they break rules, any rule they want to break, well, I shouldn't say that but if there's a rule that is in the way of something that the more senior people want to do, they usually find a way around it. And the fact you can too. But you sometimes have to be more persistent because, you know, you're a graduate student.

So I was doing graduate work and someone observed that well, you know, you're doing the work of a master's student, you might as well become an official master's student, otherwise you might do all the work and have nothing to show for it. So I applied for admission and because I was older when I went back and much more serious than I was the first time around, they admitted me. I later found out they actually knew I'd been married to the, in fact I was still literally married to the chairman of the math department but fortunately no one told me that at the time. `Cause it was very intimidating going back to school and having professors who you knew socially and when you felt incredibly incompetent, which I did when I went back to school. So anyway, I ended up transferring to Berkeley and sure I would never get a Ph.D. from Berkeley `cause Berkeley was just far too intimidating a place to be to possibly hope to get a Ph.D. but I knew I liked Berkeley and what the hell, I'd get something, at least a master's degree. And then the way I did my thesis, which was pretty amazing for me, I was taking a graduate course in scheduling theory and my professor had this really nice trick of giving us some open problems and he said if you solve an open problem, you won't have to take the final and I hate taking final exams. So a colleague of mine said why don't you work on a problem? And I said, oh, I can't do that, and he said, well, just try. Take a very simple, I actually, in this case, my real advisor was another student, I have to say and you get a lot, I'm sure you must, hopefully you already have learned this that your fellow graduate students are wonderful resources. Because I could talk to my fellow graduate students in a way that I felt intimidated, I was intimidated by the faculty, even though I was older than a number of them. I didn't feel the same comfort in talking to them that I felt in talking to the other graduate students. So he said well, why don't you take a very simple version of it and see if you can solve that and I did and I played around with it and my God, I solved it. And they said, well, O.K. So then I started, this was all part of what my whole history of just going step by step by step and each step being a little bit above where I was and if I failed, I still had gotten as far as I had gotten and so it wouldn't have been a disaster. So try to generalize it a little bit and I did and I finally got an answer. I basically came up with an algorithm for the general problem, which no one had known prior to then. If it was ** or * complete. In fact, I saw Dave Johnson was floating around the back of this room for a while. It would have, it was supposed to be one of the open problems in * and Johnson before it came out so this was, if I had known that I would have kept my mouth shut until they published their book, but anyway, I got the solution and I wrote this paper and it was a horrible proof. I mean, it was really, it was a recursive algorithm and proving correctness for a recursive algorithm is really grungy. Believe it or not, I actually ended up struggling with that problem for another two years even though I'd already solved it, because my thesis advisor wasn't going to give me a thesis just on that. He wanted me to do something more and I knew that there was something more I could do. I knew that there was a way I could generalize it. In this case, I had a problem for a single machine. It was a single machine-scheduling problem and I knew that that damn thing generalized to multiple machines but I couldn't get it to work. And I just wrestled with that baby for a couple years and until I finally figured it out. When I finally figured it out, I ended up with a four-page paper. And I've actually been able to explain the algorithm and that correctness proof to people who aren't computer scientists in not very much time. It's that simple. Now, obviously I'm very proud of this result but I mention this also because I think there are different levels of understanding. I had one level of understanding when I got the original proof but I didn't have the real deep level of understanding that I subsequently got by the time I got it down to a four-page paper. This is a luxury that you have as a graduate student that you frequently don't have when you're trying to get tenure. You can't afford to spend two years working on really getting that problem down to a four-page paper. Some problems you can never hope to get down to a four-page paper but I do believe that some times, I mean, when I've read technical papers and I've found them very confusing and I had a sense that the people who wrote them didn't have a deep understanding of what they were talking about and that's why they were so hard to read. And so one point I would make is that if you have trouble understanding a talk, a technical talk, and something where you think you should be able to understand it or reading a paper and something which you think you should be able to understand, think about the fact that it's quite possible the person who's giving the talk or who wrote the paper didn't spend the time to acquire this deep level of understanding that would make it possible to write the paper so you could understand it or give the talk so that you could understand it. More likely than not, the problem is not with you but with the speaker. So that's one thing to think about.

I would also say that this carries over to all kinds of writing. I do a lot of writing now on policy issues, for example, and I find it very hard. I also found technical writing very hard. In both cases, I think, well, I know, the reason I find it hard is that it forces me to make my ideas precise. It's a wonderful exercise when you can make yourself do it, to really write something clearly, because that does force, you can't have the fuzziness if you really look at what you've written, when you put it down on pencil, well, if you put it on the monitor. It really gets out the bugs and frequently, like if you're doing theory, trying to write up a proof, you find out that the proof isn't exactly there yet. Which brings me to a comment that Anne made about celebrating when you submit a paper. I think that's a wonderful idea but I just have a word of caution. Also when I was in graduate school, one of my fellow colleagues, fellow graduate students got this really wonderful result. It was just a great result and everybody was so excited and that summer he went around and gave talks as he said on four different continents on this `cause he was traveling around and he gave these talks. He hadn't written it up yet. And there was this one little piece that just needed but you know, it was, it was very simple to state, he knew he could prove it. Well, when he came back and started working on it he was having some problems and he eventually discovered this little piece that he hadn't bothered to write the details about was equivalent to an open problem, a major open problem, and in fact, his result had been true for the summer but then it disappeared in the fall and I love to relish proofs while they're true as well but it's a little bit dangerous. You don't want to make too many public appearances about, talking about these proofs until you've really tackled them. It's just something to be careful about.

I guess that's enough for now and if you want to find out about the no electronic theft act, ask me a question.

Thanks Jeanne and Barbara. Let's have some questions. Feel free to direct them to any one of us.

Q: I was just gonna ask Barbara to tell us about the no electronic theft act?

A: O.K. I guess I should give a little background because this is being taped, right? The no electronic theft act was passed in '97 in response actually to a student named * who was at MIT and who posted several software programs on a relatively obscure web site, which were downloaded by a number of his colleagues and when the software companies found out about this they were unhappy. The copyright laws that stood then allowed them to go after, I mean it was illegal, what he did was illegal. And they could go after him for civil penalties but because he did, because he didn't sell them, they couldn't go after him for things, the law assumed that when people were stealing copyrighted materials, usually for profit but in this case he wasn't making any money. So they could sue him in civil court for damages but that was all they could do. And he didn't have any money. So instead of going after him for civil, for copyright violation, they went after him for wire fraud. And it went to the Supreme Court and the Supreme Court said this ain't wire fraud. So then there became what was known as the * loophole. I don't know how serious a loophole it was but anyway, you had very well financed lobbyists from companies that have a lot * intellectual properties lobbying congress extensively on this and they eventually passed the no electronic theft act and what that does if you post material on your web site and $1,000 worth of this material, well, you don't have the copyright, is downloaded over a period of half a year, it becomes a federal misdemeanor. The punishment is up to six months in jail and up to $50,000 fine. If the amount downloaded, this is retail value both cases, is $2,500 the penalty I think is $250,000, these are maximum penalties and up to 3 years in jail and second offense is double for the felony. Now, so for example, if you post material that you've written for which you don't have the copyright you could in theory be, I mean, you would be, violating this law. Doesn't mean you'd necessarily be prosecuted. Now, some of the issues and this is an interesting example because it shows the problems. How do you determine the value of what's being downloaded? If you post Windows 3.1, does that have the retail value it had when it was sold? I don't think so. But how are the courts going to decide this? How do you know if something has actually been used? Someone clicks on your web site, you know, on the particular item, and doesn't do anything with it? Does that count? How do you measure these things? Just the whole issue of measuring and evaluating is very complex and how do you determine worth of something? So, that's one of the issues. That's a big issue and then of course the penalties are quite severe. We're talking about relatively small thresholds here, for some pretty severe penalties to start kicking in.

Another example of legislation that you should be aware of is the digital millennium copyright act which passed last year and what this does is again, it's a lot of concern about how digital and the net make it really easy to copy information. And so owners of intellectual property are really terrified of this technology that we've developed. So instead of going after people for violating the law, what they've done is they've gone after the technology and the legislation makes it illegal to develop technologies or technological devices that can be used for circumventing intellectual property laws. As opposed to doing actions, the intent of which is to circumvent. So you see the difference in action, which is an intent to circumvent versus a technology and there was an alert sounded by * who's a well-known computer security professor at Perdue University saying my God, if this law passes, this could make a lot of what I teach illegal because he teaches his students how to circumvent, how to penetrate systems, how to get around, because that's how you test if a system is secure or not. Now this part of the law hasn't gone into effect yet. There was a two-year waiting period during which the details were supposed to be worked out but the law was passed and this is an issue. There was what was called a carveout for encryption research.

(TAPE TURNED OVER)

Everybody is afraid. We're afraid at every step of the way. I mean we're afraid as graduate students. I was certainly afraid and felt insecure but I've given enough of these talks to find out that lots of people who I thought oh my God, that person is really sure of herself or himself have the same fears, so if the fact that it's intimidating shouldn't stop you because of course it's intimidating. It's intimidating to everybody.

?: I just wanted to add one thing to what Barbara said. There's the external reward of a Ph.D. but there's also the internal difference that it can make and I know it made an incredible difference for myself in how I thought about myself. It was just, it was a grueling experience to finally get through and it really did mean something at the end and you know, six months later I could say wow, I did a really good piece of work. It took me a while to get to that point. From that point of view, it may just be a valuable experience as well as for the external recognition.

Barbara: It will make your parents very happy.

Karin Peterson: I just want to add something to that and then ask a question. At PARC the difference between the people who have a Ph.D. and who don't actually vanishes pretty quickly, because people work together on the projects and it depends on your contributions on the project so you can have a Ph.D. and not make contributions and then you become the underdog and the person who doesn't have a Ph.D. really makes good progress on the project and they become the star. It really, really averages out pretty quickly, at least in my lab in CSL. My question is to a lot of people who train for a research career, in the process of doing so they may discover that research is not for them. Can you say something about how you've advised either your students or people even later in their careers, how to go about getting out of research as the career? I know people who have graduated with their Ph.D. and really want to go into consulting and feel this incredible stigma hanging over their head because oh my God you're gonna get out of the academic route, why are you gonna do that to your professors and things like that and I find that to be very unfair to them.

?: I'll just say one thing about that. I don't have any experience in the area of industry and consulting, moving from research in industry into consulting but for sure a lot of graduate students that I know are really aspiring to be educators primarily, rather than researchers primarily and they say the process of doing a Ph.D. and doing research is valuable but once they're done, the plan is to go to an institution where teaching and educating is the primary mission and I think that's a wonderful thing. I still think that getting the Ph.D. and research and having that experience is a very valuable thing for people who want to be educators and so while sometimes in research institutions, the people who get the most kudos are the people whose research is most widely noted, I think alternative options are certainly supported by professors. Another example is people who want to start their own companies or create something new as opposed to doing scholarly research. That happens all the time as well, so it does happen but sticking with the research is difficult at times and sometimes there's almost not enough support for people who want to do that so I want to emphasize that to, that it's not necessary to have a burning desire to be a researcher all the time in order to be good at it. Just the commitment and the sticking with it is valuable and ultimately leads to a rewarding career, too.

Q: I'll make a comment and then the question. Just to give another perspective from a research lab, I think what Karin said is probably true of my lab too, that once you're in the lab and working on a project, that the difference between the people with Ph.D.s and those without probably drops off pretty quickly. I think the difference is really in getting the job in the first place. We have a process that's geared towards recruiting fresh Ph.D.s for research positions and if you don't have that prior research experience, that credential, I think it's much harder to get a job in the lab. It's much more based on, you know, somebody knowing that you're good, having previous contact with you, so to get into the labs it really helps to have a Ph.D.. My question is to Jeanne. I wanted to know if you could comment on that process from switching from industrial research to academia. That's typically considered to be difficult to do. If you're in an industrial lab for a long time, it's hard to get a job as a professor.

Jeanne: What's necessary if you want to think about that is that you, assuming you go to industry first and think about switching, is that you really have to keep an academic profile. You've gotta get the papers out, be on program committees, make sure your work gets known, do all the things that you need to do to have a presence and make sure people know your work. Now, when I was at IBM Research that was a fine thing to do and it was rewarded. I think things have switched a little bit. It's still the case that you can do that but there's more of a pull towards making a contribution to the company and at the time that I was there, you could be rewarded for either. I think that now there's more of a pull towards what are you gonna do for the company? So, it may not be as easy as it was at that point but the absolutely critical thing is to have a sufficient research presence and make sure that your work is known, because you've gotta get the right letters from people. Now, I'll also say I moved with tenure, so that's actually, was a very nice way to get tenure. Instead of moving up through the academic ranks, you're in industry, you don't have to move but you apply for a job with tenure and then you get tenure. So you don't have the excruciating pain that you have of going through the tenure process. I think it's still possible to do but again, you have to think and plan ahead.

Q: Hello, my name's *, I'm a grad. student at the University of Pittsburgh. I just defended my thesis and I'm in the job market now. You talked about resisting being in a managerial position for some time. My question is when you assume such a position, how much of your research do you have to give up, or do you become such efficient that you can have both of them? If you wanted to have such a position, what would be the steps you would take at the beginning of your career so that you can become a manager later on?

Laura Haas: I'm a manager at IBM Almaden research center. There are a lot of answers to that question. My first management job I did essentially no research. Well, I used to say two weeks a year for three years and it was not a very good experience. I'm currently a manager and I've never done more research in my life. I grew a lot between taking those two jobs but also the nature of the jobs was quite different. So it's really a matter of the opportunity that you're offered and who you have working for you, how well defined the tasks are, how much scope there is for research. You just have to look at your opportunities very carefully and understand what's going to be required. My first position I had a lot of people to manage and a lot of morale issues and this later position was very much, it came much more from my heart, it was something I wanted to do much more and I think my enthusiasm caught people up a lot more, so it was a lot easier to sell it and to make progress doing research.

?: I'll just add a few words. I think one of the things you want to do in moving towards such a position is to take technical lead on a project. We've heard from a couple of people who are in industry that the people who put effort in and get some results on a project are gonna get recognized and I think more quickly than you would expect you will find that someone will be talking to you about well, you've shown a lot of technical leadership here. Would you like to consider a possibility of being a manager and it's important also to have someone in the company who's maybe not in your management chain that you can talk to about such things. I would certainly ask their advice, because different companies operate differently. My experience at IBM, the first level managers still all did research and to varying degrees worked on administrative things. But the most fun part of the managerial job really is being the technical leader I think.

Q: Colleen McCarthy at the University of Pittsburgh. I'd like to each when I'm done but when I finish my Ph.D. I have to work for a government institution where I won't be allowed to publish and I'll have to work for them for two years. What do you do?

A: I would say make sure that you've published your thesis results. I assume you can still be publishing your thesis results as you go along. I would certainly make sure that you take the time to do that and make sure that all gets out and it's a two-year period I think you said? Then I think you also have to be pretty clear with when you're applying for jobs about what you were allowed to do and so forth. I think that hopefully that will be understood but I'm not sure that there's anything else you can do short of making sure that you get all your results out there in a timely way.

A: If you have an idea of the kind of position you're looking for and you know where the people that might have those positions may be, whether it's conferences or educational forums, I think attending those is a way to keep up contact. Let them know you'll be in the market in two years and how enthusiastic you are about the prospect of getting a job.

A: Occurs to me you might even apply for a job early, so with a one-year lead or one and a half year lead, even, that's been known to happen. In that case you'll just have been relatively fresh, and so they may be willing to wait for you.

Q: Hi, I'm Marcia * at US West Advanced Technologies. Could any of you talk about university and industry collaborations, successes, pitfalls, that sort of thing?

A: Well, we could go on for hours about that. I think you really have to make good technical contacts at the level where the research is being done, in terms of the most successful. But sometimes that's now where the money comes from and so I think in a lot of ways you have to treat it the same as applying for a grant but you really have to listen to the people who are there at that particular company, in terms of what their problems are and what their needs are. I found it to be incredibly stimulating to hear a set of problems that maybe I wouldn't have heard about and to go from there. It can give you a direction to your research that you might not have otherwise, so it's definitely valuable. But it does have its pitfalls. You want to make sure you don't get involved in issues of whether you can publish or not and that the work that you're doing is work that you really want to be doing. I think that's an important issue.

?: Patents. Patents can be a real headache. I think it also depends on, you also want to be really careful about who you, who it is from industry with whom you have this arrangement. I mean, I've heard both good stories and really kind of horror stories about how these things have worked out and I think some of it's personality, some of it's as Jeanne said, expectations. I think you have to, I think if you're looking for an industry-collaborative, university/industry collaboration you have to be more careful about the details then say with a government grant because the government's a known quantity, whereas industry could vary considerably.

?: The best way to get money is as a gift, that supports your research.

Q: Hi, my name is Leslie Schwartzman*, I'm a doctoral candidate at U of I, University of Illinois in Chicago and I have done my work without an advisor in the field. I found doing the work pretty manageable but I'm finding writing it up quite difficult as you can imagine. But it raised some questions for me that I wonder if you still wrestle with as women very much into your professional lives at this point. As I'm writing I have a lot of questions about the audience for which I'm writing and the kinds of background which I can presume and the way to phrase things and frame them and also I have a lot of experience trying to read things which I couldn't get through very easily and I thought about that when Barbara Simons, when you made your comment. I'm wondering as you write now, do you think about a particular audience, do you still wrestle with questions about the audience for whom you write? How do you make presumptions about the background? Do you typically write just to people with a background in your field? Do you want to expand that? I wonder how you address those questions.

?: I think the writing I do is addressed to people at all levels. Sometimes what I write is addressed to undergraduates, sometimes at a very broad cross-section of people who might be interested in a subject, maybe people in graduate school who may not do research in it. For example, when I write survey papers that's the way it usually is. And then sometimes if I prove a result that's a little piece as part of a very well-defined research area, I might just write it for the people who are already in that research area, because it's not something that I think is going to be broadly disseminated outside of my area. So I think we have to write it all those levels and keep in mind the audience that we're writing to. Personally, I work very hard on writing to make sure that things are clear and I think it's good to write things as clearly as possible and to reach as broad a community as possible within the constraints of what you're writing because people appreciate it when they can understand what you're trying to say. It's really worth the effort.

?: I think it's good if possible to find a colleague or a friend who can read it for you. Obviously if you're writing a dissertation you expect the readers to be technical, to be presumably computer scientists. I don't know whether or not you're expecting to be in your, how close to the area that you're doing the research in you expect them to be. But if you can find somebody who is relatively reasonably well fits the profile of who you think should be reading it and can, I mean, when I write, almost writing I do, if it's anything I care about, I try to get someone else to read it and give me feedback. By the way, I think a problem you might have when you said you had no advisor, I was thinking oh my God, how is she gonna get a job, because advisors play a big role in or they can play a big role in getting the word out and in writing, you must have some faculty member you're working with, don't you?

?: Inaudible.

Q: Hello, I'm Anna * from University of Maryland *, I'm a graduate student there. Before joining as a graduate student, I've been a lecturer in university in India and I just love teaching so even after finishing my graduate studies and Ph.D. I want to go back to academia. At the same time, I want to do research, so how do you balance the teaching and research? That's my question. How do you balance it? Because I think the teaching also takes a lot of time if you want to be a good teacher.

?: I think that's absolutely true and you know, I'm glad to hear you say that you really love teaching. I think that's a really strong reason for going to academia. I think that the teaching initially takes an enormous amount of time. One can try and balance that by, you develop a course that you teach multiple times and you may even teach it twice the same year and so forth, to try and minimize the amount of time. Hopefully when you first go into you'll get a reduced teaching mode. You should certainly ask for that and that's because you really need more time at the beginning because you'll be expending an enormous amount of time. As to how to strike a balance, I'm still working on it so I can't give you any secret formula but I think that basically you have to be able to set aside time and it has to be uninterrupted time, O.K. I've certainly learned this as department chair. You can't just simply set aside time where people can come in and interrupt you every fifteen minutes. Working at home might be a good idea. Just say on Tuesdays and Thursdays I'm not coming in and really try and resist everyone trying to set up meetings when you're there. I think you just have to, as Barbara said, just say no, you have to be ruthless about setting aside that time.

?: One other point is that sometimes you can weave the teaching and the researching in together. It's very common to be given the opportunity to teach a graduate course in your research area. Maybe it'll just be a seminar during the start and that's a way to get graduate students involved in your research. And even at the undergraduate level it's sometimes possible to talk a little bit about your interests and to find undergraduate students who want to do summer research.

Q: Hi, my name is Michelle *, I'm at UC San Diego. Actually I work for Jeanne. I was wondering if you guys could comment on how much your thesis topic affects your future research. How much and in what ways?

?: My thesis topic was on a subject that at the time I worked on it it seemed very theoretical. It concerned models of computation that involved randomness and nondeterminism and comparing the power of say time-bounded or space-bounded models with standard models that people understand better, like deterministic **, NP or whatever. And I just found the problems to be really fun and this was back in the mid 80s when no matter what you worked on as long as somebody thought it was good, you'd probably get a job, even in pure theory. So I had a lot of fun on my research and I continued it when I started out in Wisconsin. I think for a long time it seemed like it was an area that was fun theoretically but sort of a sandbox for theoreticians. It wasn't clear what these results were ever going to lead to and over time, however, it became clear that these problems were technically interesting and many people were able to prove very exciting results about these complexity classes and as a result of those proofs they were able to make connections with hard open problems that again will probably over 20 years ago be able to show that certain hard problems are hard to approximate. I wasn't at the center of much of that activity but at the same time I was able to benefit a lot from the fact that these results were so exciting and the fact that I had the background and the knowledge also to contribute in my own way to that whole area. So for me it's been really interesting because midway through my tenure years it looked like I was working on something that was going nowhere and by the time that I came up for tenure it was clear that this was the hottest area in theoretical computer science at that time and it worked out really well for me. And it's still the case that the work I started on in my thesis is finding applications in places that I might not necessarily have expected back then. I have a paper with two a * student and * professor at the University of Washington that will be in the AAA icon, for instance, this summer and it's based on finite ** with non-deterministic and random states and so I think again if you work on problems that are really interesting to you and important in your thesis, the payoffs can come over a decade later and it's really fun to see that. At the same time, I've also worked on problems in totally different areas. I work in DNA computing right now and I also work with the computer architects at University of Wisconsin and those are things that I started on many years later after I did my thesis work. But it's still really nice. There's a sense that I understand the work that I did in my thesis better than anything else I've taken on ever since, just because it's been sort of in my mind on and off over 15 years and that's really a good thing.

Jeanne: I think it's really important if you're going to be going into a tenure check job in academia to pick a thesis topic that you can continue into the five, at least a five-year time frame in terms of that you really like that area and want to keep working on that area `cause that's the easiest way to proceed in the academic position. I also think it's important to find an area that you really, really like working on and I think that's the best way of getting success, because if you really like what you're doing and you're really involved in it, it doesn't necessarily have to be the hot topic area but it should be something that can make a splash, O.K.? And I think you can really do that in any area but you should really like what you're doing for a thesis topic, because you're gonna be working on it for a long time.

?: Just one other comment, `cause Jeanne was talking about making a splash and I was thinking how does one, how do you make a splash, I mean, how do you know you're gonna make a splash? One thing I would say is when you talk about what you do, when you talk about your work, be sure you don't downplay it. It's so easy to do. I mean, if I understand it it has to be simple. If I can do it it's not that hard a problem. Don't take that attitude publicly. What you're doing is damn good, whatever it is. I mean, if you project that I think people are more likely to respond that way and I think women have a tendency to underrate the work we do.

I think we'll wrap this session up. It's been really great to have you all here and I look forward to seeing you through many more sessions today and tomorrow.