Department of Computer Science & Engineering
University of California at San Diego
This document records some reflections and information for my current or prospective students pursuing or wanting to pursue a Ph.D in computer science at UCSD. It tries to tell you something about the research ``way of life'' as I see it, your relationship with your advisor, and the expectations and goals of the program.
The views here are entirely personal. They do not reflect those of the university, the department, or other faculty. They are not only my views but are about research in my areas, meaning about theoretical work especially in cryptography.
Interspaced with the discussions are questions. I would appreciate your answering them. Remember there are no ``right'' or ``wrong'' answers to any of the questions. Just answer as honestly as possible, and then return the completed document to me.
Why are you pursuing Ph.D in computer science? (Mark all that apply).
Maybe, but in general research is about a lot more than problem solving. It is about conceptualizing, finding issues and directions, definitions, exposition and critical insight. Problem solving is always there, but the role it plays varies.
A common situation is to be developing a new model or notion. This will involve making definitions, and then developing algorithms and analyses. When you have new models, the technical aspects of some of the first solutions may be quite simple. You might then wonder why nobody else did it. The reason is they did not ask that question, or look at it in that way. Don't look down on simplicity; good research is often simple.
Your starting research project is not likely to be to solve some known hard problem, unless you want it that way! More likely it is something like the above, where one can make progress step by step.
Don't start by thinking about a thesis or a thesis topic. Your goal is to produce papers.
You should get a sense of confidence in the power of rational thought and the range of its applicability. Everything in life is a problem of some sort of the other. How often do we think about it that way, and approach methodically the job of solving it? After a Ph.D you should have the inclination and ability to research anything, whether it be mortgages, biology, cooking or Toyota engines, and the expectation that you will understand it.
You should get the confidence and inclination to question all that is around you and seek out new ways of doing it or seeing it. You should be more likely to ask why things are done a certain why, and how it could be made better.
A Ph. D should give you the confidence that you can jump into a new area, pick it up quickly, and have something interesting to say about it, even if other people have looked at this area for a long time. More than depth in any one area it should give you the courage to jump from area to area.
You might increase your appreciation for creativity, in other people and in all areas of life. You might view art differently, or think differently about music you hear, more appreciative of what it took to do this and how it departed from the previous works. You should learn to value creativity and seek it out.
It will install a sense of taste and a critical sense. It should make you unwilling to accept the common standards and norms, and to put them to the test of your own intellect and opinions. You should naturally find yourself questioning things. You should be willing to contradict conventional widsom. That doesn't mean being a rebel just for the sake of it; you are too mature for that. It just means being constructively critical.
In the first phase I will typically try to give you a well-defined project that could lead, if successfully completed, to a reasonable quality publication. This starting project should have clear questions, goals, and deliverables, meaning a student should be clear on what is the target and what needs to be done to get there. We would typically work together on properly formulating the questions, solving them, writing up a solution, submitting it to an appropriate conference, and, if it is accepted, preparing a presentation, so that the student gets a view of the whole process.
In the second phase I could continue to suggest projects, ranging from well-defined to fuzzy, but you are more on your own with respect to solving the problems and writing up the solutions.
By then you should be well enough advanced that you can find your own questions as well as the answers. That's the third phase.
I expect to meet with you at least once a week during regular quarters and probably more often if you work here in the summer. You are also free to drop by at non-scheduled times, or send e-mail.
Working together is fun. I enjoy it and hope you will too. So if you want to discuss a problem don't feel shy to stop by. A good deal of research is spontaneous and social, arising from interactions with your peers or advisor.
You may not have something substantial to report at a meeting. That's OK, as long as it's not a habit. See the section on time allocation below.
I see my advisor
Prepare for your meetings. If you plan to present a scheme or an analysis or some solution, prepare the presentation so that you can make it clearly and well. Plan the order in which you will say things, and think about what you will write on the whiteboard, and where. There are several important reasons for this.
Our communication goes better and quicker if you prepare well, and this makes better use of our limited time. If I have to spend more time understanding you, you get lower quality feedback and it is harder to work together towards a solution. Don't underestimate the importance of the quality of your presentation to the fruitfulness of our interaction. If I find it difficult to understand you, I pay less attention and tune out, and if it continues over time, have less and less inclination to know what you are up to, and that is probably not to your advantage.
Students often launch into the middle of their current technical problem. It is at the forefront of your mind because you have been working on it. It is not necessarily at the forefront of mine: I have many projects, and my memory is flakey in my advancing old age. Please bear with me here. Start from the beginning, checking up where I am and what I remember. Present things in logical sequence, slowly.
Think of your presentations to me as practice for ones to other people and larger audiences.
Preparation for presentation is different from the actual technical work. No matter how deep you are into your problem, you have to think separately about how to present it concisely and clearly.
Not all meetings call for presentation, so don't go overboard either. You may not be presenting anything.
With regard to my preparation and presentation for meetings with my advisor: (Mark all that apply)
Some of you remember what we discuss, others don't and I have to repeat it next time. I suggest you bring a notebook with you to our meetings and take notes. Don't hesitate to spend time doing that or to ask me to stop while you do. Ask for clarifications or repetitions if necessary. Make sure we are clear with each other about the technical issues and what to do next. If we have to go over the same thing again at the next meeting, time is wasted for both of us.
Try to be clear about where you think you are headed in the period up to the next meeting. What are the tasks, questions, deliverables, if any? Have this written down if you are unsure you will remember it.
With regard to what I get out of meetings: (Mark all that apply)
Learning by thinking
The first rule of research is to think, think and think again. Never hesitate to throw your mind at anything. That should be the first thing you try. Before looking up a book or paper, before asking anyone, think. For example, suppose you are reading a paper and there is a lemma, with the proof referred to another paper. Should you go get the other paper to look it up? No. First, try to prove the lemma yourself. If you don't succeed after a reasonable time, go look it up. But if you solve it yourself, you will have understood it better. What you solve by thinking is your baby from then on; what you look up you will forget and have to look up again and again.
Never be lazy about thinking. That's how you build up understanding and develop a bag of techniques that you can use.
Thinking is fun. If you don't find it so, it's an indication you are in the wrong business.
Learning by example
You pick up how research is done by seeing examples and extrapolating. Papers, and discussions with your advisor or peer, are a source of materiel. You learn how to write a paper by looking at other papers. Make anologies. When you see a new primitive or problem, ask yourself what kinds of questions were asked about previous ones and use that to ask questions about the new one.
As you go on, you should be able to extrapolate more and more, and farther and farther.
Perhaps the best indicator I have seen of a student's research proclivity is the extent to which they find the ``right'' things ``natural''. There are some students who, when shown some technical item, react, somehow naturally having good reactions and viewpoints, about the import of the item and what to do next. These are simply people who learn extremely well by example.
Understanding versus knowledge
It is more important to understand well what you know than to know a lot. Successful research comes from having a good understanding, especially of the basics.
When you read a paper, ask yourself questions. What if I changed the scheme in the following way: would it be secure or not? How does this compare to the following other scheme? Why is this novel? Can I come up with a different proof? Understanding means the ability to go beyond the immediate. It means knowing not just what is the item in question, but how it fits into a larger context, what are its variants, and what happens if you ``perturbe'' it one way or another.
When do you think about research problems? (Mark all that apply)
How comfortable are you with your advisor? (Mark all that apply)
What does my advisor think of me? (Mark all that apply)
What's the student's job?
Nothing, really. Students sometimes view a project suggested by an advisor as a ``job'' they need to get done. That may be appropriate for systems work; it is not in theoretical work. There is really no ``job'' I need you to do. You are working for yourself, not for me. When I suggest projects they are only suggestions for things we can do together or that you might do yourself.
Phase by phase
Referring to the research path above, my minimal expectation at the end of Phase 1 is that you have a deep understanding of the subject of your first project. You should know it inside out. You should know what happens if something in your construction is twiddled, and how it compares to other constructs. This phase should typically take at most a year from when you begin research. By the time you are in Phase 2, you should be ``swimming'' fairly comfortably in the materiel. You should be able to pick up new concepts rapidly and do simple proofs in your head. You should be able to make connections across different sub-areas, have some sense of what is known and not known, and be at ease with basic techniques. By the time you are in Phase 3 you should have a sense of taste, critical sense and maturity in addition.
Publications versus thesis
The quantity and quality of publications you should look for varies with your Ph.D goal. If you want to head into research, whether at a research lab or in academia, they will look at your publication record, not your thesis. You want more than a minimal Ph.D. You want to have had recognized publications and exposure. Students headed this way shouldn't really even be thinking about a ``thesis'': this is only a formality for the university and less than you need. Try to do good research and get recognition in the research community.
What is enough?
The minimal Ph.D is probably about four papers, but there is no hard and fast rule. Sometimes you may have stronger papers, or a larger contribution to co-authored papers than in other cases, in which case fewer papers may be enough. In other cases you may have more minor results or a lower contribution to co-authered papers, in which case you may need more.
Remember if you want to head into research, whether at a research lab or in academia, they will look at your publication record, not your thesis, and you want recognized publications and exposure in the research community.
In addition to papers I expect you to develop communication skills, both written and verbal. You should be able to plan and give clear talks and to write clear and correct technical papers. There is no under-estimating the importance of communication.
When is enough?
Accomplishment is measured by output, not time. For time, one can only talk about the typical. The typical time-frame is five years, assuming the first year is spent in coursework and you start research the second year. Finishing in less time than that is neither unusual nor unusually difficult. If it looks like you may take more than five years, it is not a good sign. At that point, funding and lab space start getting denied, so beware.
With regard to my rate of progress towards my Ph.D goal
As an advisor, what I look for is long-term productivity. A successful Ph.D student should typically display some degree of productivity and progress over the course of a reasonably long period, like a summer, a quarter, or more typically, a year. This would include signs of increased understanding, confidence and maturity, and some visible output or ``deliverable'', like a complete paper.
It is not unusual if on a particular day, or even week, you don't find yourself inclined to do much research. Take time off now and then; if you find you can't concentrate, a vacation might do more good than trying to sit in the lab and push yourself to work. You come back refreshed and productivity increases. I don't want to ``micro-manage'': how you allocate time on a short-term basis is up to you. But if a long period passes without significant progress, you should worry, and talk to me about it.
If you don't know whether you are making ``enough'' progress, ask. Don't be shy about that.
Above I discussed how time allocation varies across people and their moods, and how the long-term and short-term views differ. With those discussions in mind, it is still useful, both for me and for you, to get a sense of how you allocate time or other resources to research. I am not trying to ``check up'' on you! Rather this information will give both of us some sense of your productivity. It will help me to ``extrapolate'', meaning guage your progress towards completing the Ph.D by a certain date. Remember that the time in the question below is to be taken on the average, across a long period, like a summer or a quarter or even a year.
Approximately how many hours a week do you spend on research, in an ``average'' week? Include time spent thinking about research problems, writing technical papers, or discussing research topics with other people including your advisor.
How often do you have technical discussions with other students?
Don't kid yourself
Liking research it is liking DOING it, not liking thinking about where it puts you, or liking to view yourself as someone who does it. Separate the process from any perceived goal. You will only be happy in research if you enjoy the process, the day-to-day nuts and bolts of it. If to you it is only a means to some end, you are unlikely to enjoy yourself.
I had a friend once who from childhood had a dream of being a mathematician. She loved the idea of being a person of the intellect. That way of life appealed to her. However, at the time she had this dream, she had no idea what mathematics really involved. She followed mathematics and theoretical computer science in college and grad school. However, she had a really hard time setting herself to the task. Working on math problems was tiresome for her. It was very hard to have the discipline to sit down and do this boring thing. She was not at all dumb; far from it, being extremely intelligent. The problem was that although she wanted to be a mathematician, she actually hated doing the stuff. But you can't be it without doing it. What is exhibited here is the gap between a picture of how you want to see yourself and what is involved in actually being that. Be wary of falling in love with a high-level goal when you find the nuts and bolts tiresome.
When you sit down daily to do your work in the lab, working on your research problem, writing the paper, are you bored? Is it hard to motivate yourself to be there? Is it really not fun? Are you saying, ``I have to do this''? Those are bad signs. It is not fun everyday, and all of it is not fun, but those of us that are in this business enjoy a large fraction of the process. For me, for example, thinking about a research problem is not work. It is probably about the most fun thing I can think of doing. You don't have to be that fond of it, but if to you it is just work, to be done and gotten rid off as soon as possible, you are in the wrong business. You might with a great deal of discipline finish your Ph.D, but experience has shown that even then you will not have a real sense of accomplishment or happiness. You will also make my life difficult.
Again, liking research it is liking DOING it, not liking thinking about where it puts you. Be wary of childhood dreams; they are often formed without any idea of what is actually involved in the process of attaining them.
Am I smart enough?
That's the wrong question. There is no such thing as ``smart enough''.
If you love playing the piano, play it. You don't expect to be Alfred Brendel or Vladimir Ashkenazy. But you are doing something productive for yourself and those around you. Research is the same. If you enjoy doing it, pursue it. You will usually find that you can contribute something. As you go on, you will discover your strengths and find you have something unique to offer. Maybe there are others who are smarter in some way; they can compute complex probabilities in their head faster than you can, or whatever. But your contributions may be valuable in other ways.
As discussed above, research has many components. Problem solving, identifying issues, presentation, modeling, and criticism are amongst them. See what aspects best suit your abilities and personality. There is probably a niche for you somewhere.
What is written above about kidding yourself does NOT refer to ability or perception of ability; it refers to motivation and honesty about motivation. I want to be sure you are pursuing research for the ``right'' reasons.
Self-confidence affects our performance and success in all walks of life, from sports to socializing to dating. It plays a role in research too. Sometimes I meet students who don't have confidence. This can lead to a disinclination to work. Fear of failure leads to inactivity. People ``freeze'' up because they are so worried they aren't ``good enough''. If this sounds familiar, at least you know you are not alone.
Increasing your self-confidence is very much a personal issue, but here are some reflections from my experience.
You can find confidence only within yourself. Don't expect to get it from others, even your advisor. Someone telling you that you did well is useful to boost morale, but in the end you must believe in yourself.
If you are afraid of failure you will have a hard time succeeding. You have to fall a few times to learn to skate or ride a bicycle. Research is worse. Once you learn to ride a bicycle you don't fall again, but in research you never stop failing. You will fail far more often than you succeed. But it is from your failures that you learn. They increase your understanding and maturity. If you find the process of research fun, failure to solve a problem is not daunting. In fact, it leads to all kinds of discoveries. So you need to learn to not care about failing, but use it to get new ideas.
One nice thing about research is that nobody need know when you failed. You write papers only about your successes. But that is also deceptive, because you don't see the failures of others. But they are there. Even the top people don't always succeed. Gauss failed sometimes, as did Einstein.
Try to ask yourself exactly why you lack confidence. Be entirely honest with yourself. Go back to the discusions above about your motivations.
How much self-confidence do I have with regard to research? (Mark all that apply)
Choosing an area and an advisor
It is never too late to change areas. If you don't like where you are now, switching to a different area or advisor can make a marked difference. Try to explore before settling down.
You should feel you have some understanding of the importance of the area you choose, that it is worth your investment of time in it. Your advisor should be able to inspire you about the work and give you a sense that it is worth it and worth your time.
When you pick an advisor, ask yourself why you chose that person. Good reasons include that you like that advisor's area, that he or she can inspire you, that you understand each other and get along. A poor reason is that you are afraid you won't get through and maybe this person is your best bet to make it.