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.


Leah Jamieson: You know people who have been working the same problems for 15 - 20 years? Do you know people like that? You know people who every, seems like, year jump on the new bandwagon, whatever it is? Neither of those is probably a great formula for success, either professional or personal.

If you jump on every bandwagon, your credibility in any given field is probably not really high. If you stay doing the same thing forever, it works for a while and after a while, the rest of the world looks at you and says, "Aren't they ever going to move on and do something else?" So, there really is a balancing act here to say, "Okay, I'm going to change. I'm going to do something different." What's it going to be? How are you going to decide it?

The other thing, I would just comment on the *why*, is that the factors that go into this are really diverse. They can be strategic or tactical. They can be very well planned in terms of saying, "Okay, here's my career. Here's where it ought to be. I can make this major shift or if I do this other thing, it can push me in the right direction." So, they can be very carefully planned things.

But I think there can also be, obviously, technical motivators and personal/emotional things. Just saying, "I really want to do something else." And those are absolutely valid reasons to be doing this. There has to be an idea. You can't just go out there and say you're going to change or reinvent your research career without some idea. Obviously, there's a piece of saying, "What ideas? What directions?"

I really would never advocate the bandwagon approach, but it does make sense to have some awareness of current trends, like what's going on. If you're going to start over or at least take off in a major new direction, it makes a lot of sense not to do it in a direction that is of no interest to anyone. So, it's valuable to know something about what the current trends are.

There are some resources that are always available for that. There are some senior people who are very good at this. I tend to call them "forest people." They're people who actually do, every once in a while, stand back and try to look at the forest instead of the trees of their own research. You have to sort of identify who those people are, but it's usually not that hard. They're the ones who actually seem to know about research other than their own. They're a good sounding board. Go to lunch with them. Where do you think things are going? Where do you see the opportunities being?

The other thing at the moment, which just makes it really to see possible trends, is that there's a tremendous amount of activity going on in terms of the presidential budget and the legislative review of the presidential budget, to say, "Where should research be going in information technology over the next five to ten years?" So, there are actually reports out there where they've had incredibly esteemed panels of people get together and say, "Look, here are the areas where we need things."

And the *P-tack* report is one of these. I can never remember exactly what it is, but if you go to the *CRA* home page, there are links to all of the *P-tack* and the *Trends* things. You go to government affairs and from there it tells you what is currently going on. What is going on in the policy thinking about where the research needs are. Even though this is coming out of sort of a government direction, the emphasis - and this is actually on basic research - and so there is a tremendous amount of material there.

There are some factors that have to do with modes of research. If you're thinking about changing, do you like working by yourself? Do you like supervising a few students very personally? Do you like managing a very large group of students? Do you want to be working with people, either people locally or elsewhere? And those are all things that bear on changing research directions and what kind of direction you might want to go into. If you like collaborative work, are there potential collaborators? The key here is really just knowing what, if you're going to do this, know what you want. Know what your strengths are, what your interests are, and thinking about the timing.

I'm going to put this back just to say a little bit about, you know, I've actually done this sort of twice. Once, I think, a fairly modest change and the other, much more dramatic. The first one actually came about somewhere in here. It was while I was an assistant professor but towards the end and I was working in speech processing, which is very experimental and which is a **** field that I dearly love and actually still work in.

This wasn't reinventing 100 percent, it was simply looking at what I was doing and saying, "You know, this field is very experimental. I am publishing, at best, one paper a year. I'm not going to get tenure at this rate." I had a real need to do something that was more analytical and so I fell back on some things that I had been interested in algorithms and parallel processing. Over a course of about two years, carved out an area, looking at signal processing algorithms from a parallel processing point of view. Doing, initially, analytical things but then moving into more experimental and software-oriented things.

For the next 10 to 15 years, I actually spent much more time on that than I did on the speech processing because it was an interesting area. There was funding available, and it involved taking some time off, in the sense of just freeing up time, to make sure that I knew what I was talking about, and putting together some collaborations. I sort of view that as, maybe, a 45-degree shift.

The other one, which has been much more dramatic, happened - I don't know, somewhere in here - was a shift, actually, into something... There's a research piece of it, but it really is activities and education. There's research in it because it's an education program that is very different from anything that existed. It has been all consuming. It's definitely one of the ones that just grew out of some talks with some people. A couple of us looking at something and saying, "There was an idea." It was just so compelling we had to do it. Dropping a large part of other stuff we were doing to say, "We need to spend to spend all our time on this."

It was a much more dramatic thing and it definitely has this feeling of taking over your life. The positive side is that it goes well and so, in the course of - I guess I was trying to do some counts to give you an estimate on this. So this is a program in education. It started four years ago and we're, at this point, we've raised about $1.5 million in external funding for it and about $2.5 million in matching funds to go with that. For education, which is not typically a terribly well- funded field. So, the effort was high, but it is was actually feasible to go in there and take an idea and have something promising enough to say, "Okay, this is just a new direction."

I want to say something about resources because you don't do this casually. There is an investment that - some thing has got to go if you're going to do something brand new. There are some things that are potentially a help. Summers can actually be a big help. When I was doing the shift into more of the parallel/algorithms work, I just really worked at not committing my summers and spent the entire summers reading and thinking things through and trying to develop ideas, making no other commitments.

Sabbaticals were wonderful because, when that evolved more into something, looking at software and methodologies, all of the background work for that, I was able to do by being on sabbatical. I could just actually just spend weeks and do nothing but read and look at what other people were doing. I didn't try to jump into a field with zero knowledge of what anybody else had done in the field, because that is probably not a real good recipe for success.

You can think about leaves and visiting appointments, especially if you're talking about something where there is some strength some place else and you've done some background and you want to go somewhere. It's a reasonable approach to this.

NSF is always looking for really good program directors. So this is a way to step back and look at a lot of what other people are doing; to think about a broader research picture. So, if one of your senses is that you've been very focused in one area and you would really like to say, "What's a bigger area of research?", doing something at NSF or *Dorfer* or something, and see if there is interest in your being a program director is a viable possibility.

There can be - and this one that is going to be real uneven - there may be department or university resources. So I would certainly recommend that you talk to department heads, deans, to say, "I'm changing research directions. I want to make a major change in what I'm doing. Can you provide me with some release time? Support or whatever? Or are there internal programs that I can apply for that will give me some summer support or student support to get going in something new." Some of these things do exist, but you have to ask about them. They're probably not going to walk up and offer themselves to you, so it's at least worth asking. In most cases, department chairs are going to think that something that is revitalizing or taking off in new directions, typically, is a good thing. There is possibly support for it.

NSF, the power program, and whatever it evolves to, because these things seem to change every few years. It's an area where they're conscious of - that there are needs to sort of get past what you did early on and move to something else and to try to provide some capabilities for that.

Things you can try to do. Again, talking to your department. Leverage your teaching assignments so instead of teaching whatever it is you've been teaching, see if you can teach either a background course that's really relevant to whatever you want to move into or a seminar course, ideally, where you can start using that. So that you can use the time you're spending in teaching to try to leverage that. To make sure that your thinking is moving more and more into a new area.

One of the things that it took me many, many years to figure out is that you actually can go to conferences, even if you don't have a paper. This is permitted. So, if there's a conference in a new area, it's okay to go, even if you're not presenting something. You can go and find out what other people are doing and meet people.

Reading really helps. Talking to colleagues, looking at collaborations. Writing a proposal. You don't want to do this when things are too half-baked. On the other hand, as a vehicle for pulling ideas together, it is actually a really good way to make to focus on some piece of something and see where the holes are. The payoff - there is this sort of time stretch. Sometimes the ideas or the compelling thing - the chance to do something good.

My bottom line in doing this is that it's not easy being a faculty member. I've never heard anybody claim it's an easy job. There has to be some reason why we're doing it and, I guess my reason is that you've got to love it. If you're not passionate about what you're working on, there's a real value in trying to find something that you can be passionate about and really get involved in and make that something that makes this worth doing.

That's my sort of general overview. I'm going to turn it over to Maria and see what we can do with questions.

Maria Klawe: Leah and I did not discuss what we were going to say - at all - before this and what I find really interesting is... First of all, I agree with absolutely everything she said. Secondly, there is a lot of overlap in what we were intending to say, which makes sense since we agree. I'm probably going to take a slightly different slant.

First thing I am going to say is that probably every single one of you, you either have changed research directions already, or you're going to change research directions probably more than once in your life. The question is the degree to which you are going to change and whether you're going to sort of make changes slowly, in little pieces over time, or whether you're going to do - as Leah and I have done - is every once in a while, make a sort of right turn direction, or even a 180 degree turn and change things.

All of the things that Leah told you are good things to know about, whether you're going to make a tiny change, just like a 5 degree change, or whether you're going to make a 90 degree change or a 180 degree change.

What I am going to do is say a little bit about my story; the changes I've made in my career. Then I'm going to give you some of my reasons why I think reinventing your research career is a good idea, why you might want to do it. Some of them are similar to Leah's and some of them are a little bit different. Then I'm going to talk about, at least from my experience, what useful strategies **** be. And then I'm going to spend some time talking about something that Leah didn't spent a whole bunch of time on, and that is things to watch out for. Where are the pitfalls when you try and do this?

Let me start off with my story. The first thing is that I reinvented my career one year after I finished my PhD. I finished my PhD in pure mathematics in 1977, went to teach in a university in Michigan, called Oakland University, and decided I hated living in this particular area of Michigan. It's about 25 miles north of Detroit. I had lived the year before that in Vancouver. Now you may have noticed that I am back in Vancouver and this can tell you something about how I feel about Vancouver. It is the best place in the world to live.

There is a place called Rochester, which is four miles on one side of Oakland University, and a place called Pontiac, four miles the other side. You can figure out what happens in Pontiac, Michigan, pretty easily. They make cars. Culture in this area consisted of K-Marts and McDonalds and things like that. Vancouver is a wonderful city, much like Atlanta, San Diego, or San Francisco, or a few other great places. Somehow, moving to Michigan didn't really suit me and I really wanted to come back to Canada and I really wanted to live in a place and be at a university I really liked.

I had done my PhD in functional analysis, which is an area of pure mathematics, and I knew nothing about computer science. But, I found out, just by chance, that there were people who did mathematics in computer science departments and decided to go into a second PhD in computer science. So, one year after I finished my PhD in mathematics, I was back at the University of Toronto as a graduate student in computer science. Five months after that, I was getting phone calls from departments all across Canada saying, "Wouldn't you like to apply for a tenure-track position in the computer science department?"

I mean, this is the bandwagon idea - sometimes there are opportunities to do things in the world that are very close to what you already know how to do; and yet, there are many, many more opportunities just by making a small change in direction. So, a year after I had left my job at Oakland University in Michigan, I was tenure-tracked assistant professor at the University of Toronto and started working in theoretical computer science.

Now, theoretical computer science really was very different from functional analysis. The kinds of problems and a lot of the techniques you use are really different, but it was still mathematics and it was close enough that I really loved it. A year after that, I went to IBM research in California, did that for eight years, and came back as head of the Computer Science Department at the University of British Columbia in Vancouver. I managed to make it back to Vancouver eventually, about four or five years, after I came to UBC.

So I would have said that that change, from functional analysis to theoretical computer science, was something like a 60-degree change. It's a pretty big change. There were not a lot of the things I had learned in doing my research in functional analysis that translated directly.

So now about six years ago, about six and one-half years ago, I made what I would call a 180-degree change. I started a research project on looking at the design of - I was going to say, interactive multimedia for mathematics education, but the way that you'll understand this is to say, using computer games for mathematics education in grades 4 to 7. This was really a huge change. Within computer science, you'd say it is human-computer interaction. That's the closest area of computer science that you could say was involved. It's a long way from theoretical computer science.

I knew nothing about human-computer interaction, about mathematics education in a formal way, and about designing computer games. We're now six and one-half years into this and it's been a tremendous adventure. It's been extremely interesting. It's definitely something I've been very passionate about and it is something that I think has probably had more impact, in terms of impact on the world, than anything thing I ever did in theoretical computer science. Although, theoretical computer science is still an area I love dearly and I'm delighted to be here for *STALK* for a change.

Two years ago or one and one-half years ago, I made another minor change. I took on a position as the *NCIRC* -IBM chair for Women in Science and Engineering to focus on how we get more women into computer science and computer engineering and general careers in information technology. Now I hadn't really intended that to be a change in research; I just intended that to be something I would do that involved a lot of activities similar to things I had done in the past with the *CRA* and *CRAW*.

It has turned out that it involves research as well, because if you want to figure out what actually works, you do have to end up doing research. I can't tell you what kind of a change that is, in terms of how many degrees it is, but it certainly is, yet, another change.

And at the same time, there have been other parts of my career that have been changing at the same time. I've been in administration for a long time, but I've been doing different kinds of administration. I was head of the Computer Science Department at UBC for six and one-half years. I'd been a manager at IBM for four years before that. Four years ago, or a little bit more than that, I took on a job as a Senior Vice-President at UBC for, I call it, everything but the kitchen sink; but it was information technology, library, student services, athletics, and the **** Center for the Performing Arts. It was a very strange job. Did that for a bit more than three and one-half years and I started as Dean of Science at UCB six months ago. So, I've also been doing a lot of changes in terms of what I actually do, in terms of administration.

I would be one of these people who doesn't change what they do every six months, but it would be fair to say that I change what I do, probably, every three to five years. So, I'll just tell you that much and then go into what I wanted to say about why I do it. There are lots of different reasons why you might change what you're doing, what you're focusing on.

The first one is that might be something that you've always been interested in, but you've never quite had an opportunity to do it and the opportunity comes along. I would say that, probably of all the reasons, that is certainly one of the best. That was the one that is like Leah's, something you're going to be passionate about. For me, I've always been interested in education and I'd always been interested in how to make children excited about mathematics. So, doing these computer games was an opportunity to really do something creative that let me focus on something I'd been thinking about since I was probably 16 or 17 years old, and gave me the chance to really do it.

It was also the case that my children, at that point, were about 7 and 10 when I started that project. Particularly my 10-year-old son was really into computer games. So, for me, it was a way to do something that was really close to my children's interests and be engage them in my research and bring two things together that I really wanted to bring together.

The second reason, - and this is probably actually an even bigger reason why I took on the computer game research project - is that when you see something that needs to be done and you wish that somebody would do something about it, you look around, you try and convince people to do something about it, and somehow it just doesn't happen. I suspect that might *Leah* and the education project. It was certainly for me and the computer games project and it is certainly me and the women in computer science chair, right now.

Sometimes you just want something to happen and it ends up being easier trying to get it to happen yourself organizing a group of people to do it, than trying to persuade somebody else to do it. For the computer games project, which is known as *EGEMS*, Electronic Games for Education, Math, and Science, I spent six months going around and talking to people in math education and people in computer game development companies, trying to persuade them that they should do it. Ninety percent of the people said, "Oh, that's a great idea, but.... not me." And ten percent said, "Oh, that's the stupidest idea I've ever heard." So, eventually, after six months, I just - well, the truth of the story is that I heard somebody else, a woman that I know quite well, giving a talk about her research on the use of *porfrens*, which are light sensitive chemicals for treating cancer. I heard her give this talk and I was saying to her afterwards, "You know it must be really wonderful getting up every day and knowing that you're doing something that is so important to society." She said, "Yeah, it is." Then next morning, we were in a taxi going to the airport - it was October 15, 1992 - and I said, "You know, Julia, I'm going to make computer games for mathematics education. I want to do something that I can get up in the morning and say that I am changing the world in a really positive way." I'm glad I did it. I can't say that I change the world quite the way I would like to have changed the world, but it's the same with this Women in Computer Science thing.

You might as well, during your life, do some crazy things and just decide that you're going to reach out and take on something that you think is important and that needs to be done.

The third reason is that sometimes you just get an opportunity. Sometimes, something just comes along and somebody offers you an opportunity to do something and it's worth doing it and you do it. So that was this bit about, sort of, the opportunity for collaboration or you meet somebody who is doing something exciting; something just triggers it.

The fourth one is that sometimes you really have to do it because you don't have other options. Or at least, you don't have other options that you consider really acceptable. For me, I think, when I made the move to theoretical computer science, a lot of it was for that. Certainly, I could have stayed in my position at Oakland University. If I would have stuck it out long enough, I probably would have been able to come back to Canada in a Mathematics Department, but I really hated being in Michigan. For me, it was really worth while to look for something that was close enough to what I loved to do that I could genuinely still love to do it; but the effort to learn something else, so that I could open up opportunities.

Many of us are married and have spouses or significant others and we have to figure out a way to combine two careers. Sometimes you end up being in different places and you commute, but often, what you end up doing is somebody - in fact, often both of the people - makes some minor or major changes in what they're working on in order to have an opportunity so they can live in the same place.

Personally, I believe that you should do things that you can be passionate about, but I also think that we tend to often live our lives with blinders on and to think that I can only be impassioned about this little piece that I got excited about first, which probably I'm only excited about because of some weird set of coincidences about a course a took with a professor I liked, and then an advisor that I really liked to work with or a talk that I heard at a conference, or somebody I met. You end up in this tunnel-vision thing about what you think makes you passionate. In fact, the kinds of things that you can be passionate about are humongous. So, sometimes, and often we feel quite bitter about being forced to make changes in our career, because - for what ever reason - there aren't opportunities in the particular, narrow area we had chosen that we thought we were destined to do. Sometimes you have to, in order to have the things you want in your career and your family or personal life, you have to make some changes.

I think it's a very legitimate reason and if you can go into it knowing yourself, as Leah says, and knowing what you might like, you can often be very grateful in the long run about the fact that you were forced to look at other things.

So, the fifth on my list of "why do it," is to learn. Through doing my computer games project, my **** project, I met somebody who is now the Dean of Education at Queens University. Her name is *Rena Upitus* and she an amazingly talented, wonderful, inspiring person. I think she was 36-years-old or 37-years-old when she started being Dean of Education at Queens. Queens is a pretty traditional, conservative University. So, that was definitely an unusual thing to do.

One of the things that *Rena* told me, I met her because I needed somebody who knew about education to work on the *EGEMS* project and at that point she was doing sabbatical at UBC just after she'd gotten tenure and had been promoted to Associate Professor. One of the things she told me about a master's course that she taught for education students was that what she makes those students do in this course is they have to pick something they've always wanted to learn in their life but have never taken the time to learn. So it could be playing the guitar, or painting watercolors, or rollerblading, or bungee jumping, or speaking Russian or Japanese or whatever. Anything. Could be number theory. But they have to pick one of these things and then they have to go and learn it during this year and keep a journal and observe themselves as they learn. Because the best way to learn about teaching others is to learn about how you learn, or at least one of the very important ways, and to learn about how others learn.

What *Rena* told me was that she makes an effort to learn one new thing that she has always wanted to be go at or to know about, every year. Since I met *Rena*, I can't say that I've picked one new sort of formal subject to learn every year, but it certainly has empowered me to learn things I've always wanted to do. The year after I met *Rena*, I started taking guitar lessons. I even traveled with my guitar to this conference. That's how addicted I am to my guitar.

Learning is a wonderful thing and so often, we think tat once we're 20 or 30 or 40 or, I'm coming on to 50 - Fran, are you 50 yet? Are we going to be 50 the same year? You're 48. Okay, I'm going to be 48 this summer. Yeah, we're going to be 50 the same year. We're going to celebrate being 50 the same year.

You think you're too old to do these crazy things. Learning is the best. It is just absolutely wonderful. So, that's a great reason to empower yourself and make changes in what you're working on, because it's an opportunity to learn.

Okay. That was "why do it." There are lots of other reasons to do it too, but those are my list. Some useful strategies.

The top one on my list is, get help. You'd be amazed at how much people like to help. Now, there are jerks in this world. We've all met at least one in our life. People that you'll go up to and ask for help and not only will they not help you, but they'll make you feel like an idiot for asking. They are the exception. Most people, they might not help you, but they'll at least be nice about it. You'll be surprised at how many people do help.

First of all, when I started the switch to computer science, I started by asking somebody, "Where are good departments to go to do a second PhD?" and "Whom should I contact in those departments?" I got names of people. When I decided to start the computer games project, I spent months - literally months - asking people, "Who are the right people to talk to in education? What are the right companies? Who are the right people to talk to in those companies about developing computer games? Who are the right people to talk to in human-computer interaction? Who are the right people to talk to in psychology?" I just got used to making lists and I probably contacted 75 percent of all the names I got. The standard thing is , "Hi, my name is Maria Klawe. I have this crazy idea that I want to do and you name was given to me by such-and-such and I thought you might be able to help with...." Right?

For the most part, people say, "That's a wonderful idea! Maybe you should do such-and-such." or "That's one of the dumbest ideas I've heard." But, that's a small fraction of people. So, get names of people who might be able to help you. Get advice on how to go about it. Find out the names of books and papers and conferences. It took me a long time, like Leah, to understand that I could go a conference without having a paper there. I don't know why we're raised this way, but conferences are wonderful ways to meet people in new areas and to learn about things.

Money. It's amazing. People will give you money. I mean they really will. So, when I started this computer games project, the first few thousand, I mean, often you can do a lot with $10,000 or $20,000 or $30,000 or $40,000. Especially if you're in Canada and your universities don't charge overhead. But, it really helps to have a little bit of money to do travel, to hire some students to work on things, to get a little bit of equipment. Often, your department head, your dean, your vice-president of research, a company, a government agency, will give you seed funding to start things before you get the big funds.

We survived on little bits of money for the first, I'd say, about 12 months and then - well, more than 12 months, maybe 18 months - before we got major grants of several hundred thousand dollars a year. It really helps to get going.

You can also get people to lend you equipment, software, to lend you students. If you have an idea that you're passionate about and if you talk to lots of people, you can usually gather lots of things to help you in getting started.

Next useful strategy. Plan long term. If you're going to make one of these transitions, it takes a long time to really see progress and it's really easy to give up in the first year to two years. So, realize that you're in at least a five-year project, if it's a major change. If it's a small change, that may not be so true, but you need to have a long-term strategy. The second thing about your long-term strategy is that you need to realize that it's just a plan. You're going to make changes to it. In order to make it work, you're going to have to be flexible, you're going to have to be opportunistic. For this computer games project, we had this plan. We had this company that had signed up to provide support, we were going to get matching dollars from the Canadian government, etc., and then the president of the company left and this particular project was his baby. All of a sudden, even though we had commitments in writing and this sort of stuff, it was gone. It would have been really easy; I mean, we had invested probably nine months of work with that company in getting them to agree to support us. It was just totally gone. Six months later, we got the company to sign on again. The reason we got the company to sign on is that we didn't go away. We just paid attention to what might get them interested again. Eventually, we found a computer game that they were working on and had problems with, and we ended up doing - for free - the educational design for that computer game that pulled them out of a big problem. When they saw that we could actually do something for them, then they came back and they gave us the funding that they had originally promised to do.

So, sometimes you just have to be flexible and be willing to respond when things change.

The last thing I would say is, don't give up. I don't know how many times I've been in the situation, or see other people be in a situation, where things look absolutely, totally hopeless. For months. Just disastrous. And over and over again, the people who succeed in doing wonderful, crazy, innovative things are the people who persevere through those times. Sometimes, you do actually have to give up. Sometimes, after several years of disaster, you really have to be willing to say, "Okay. I tried. It didn't work." So, it should really be, don't give up to soon.

The second thing I would say is, failure is not bad; failure is good. You learn much more from failure than you ever learn from success. Much more. And if you're not failing, you're probably not aiming high enough or trying enough kinds of things.

Okay. Last was, things to watch out for. First one is, when you learn a new area or make a significant change, your productivity goes down. It is highly likely to be a period of time when you're not publishing as many papers as you were before. So, make sure that if you're in a situation coming up for tenure or promotion or whatever else, that you take that into account. As *Leah* says, the right thing to do is talk to your department head about it. Get their advice. Pick your timing carefully.

The second thing is, and this is probably an even bigger one, is that, particularly if you move into an interdisciplinary field, but even if you move between areas in computer science, the cultures are different. That can really cause problems for you if you're not aware of it ahead of time. So, what's different about the culture? The language they use can be different. You can say exactly the same thing and people understand quite different. So, be careful. I'm seeing some nods around the room.

The second thing is that the value system can be different. For example, little trivial things, you have a group of people working together on a project and you're writing up a paper, who deserves the most credit after the paper has been written? Is it the person that thought of the idea? The person that brought in the grant funding for it? The person who did most of the work? The person who wrote up the paper? Quite often on a large project, those will be four different people. In different disciplines, the person is thought of as playing the most important role, is totally different. It can be any of those four. For instance, in computer science, it's not often the person who actually did the first draft of the paper if they hadn't done the other three things, who would be though of as the most important person. Not often.

In education, that's usually the person who is the most important person. It turns out in education, that it's harder to write the papers. Because the results are fuzzier and it's harder to draw the interpretations, a lot of the intellectual work goes into writing the paper. But you can imagine, if you had a team with both education people and computer science people, where the computer science people had done most of the work and had thought up the ideas and came up with the money, and then the education person wrote the paper, that you can have two unhappy groups of people. Each feeling that the other side was not appreciating their huge contribution. That 's just one example. There are lots of them.

Second thing to be aware of, particularly if you're going to do something crazy and innovative.....