This is written with the goal to help students and junior researchers, and is the type of advice I give students and junior colleagues when I coach them. Of course, not everybody works the same way. This might be good advice for some, but maybe not for you. I would be happy to get feedback on this page to make it more helpful — please contact me if you have thoughts on it.
I will talk about goals, failure, forgetting, formulating questions, heroes, and communicating insights. Then a few blurbs about finding things … an advisor, your specialty, an internship, a job. And finally, a word about CVs.
1. Understand your goals. Why are you doing research?
Are you aiming for a career in academia? Do you want to work in a large company? Do you want to join or help found a small company? Is it plainly because you enjoy it? Because you want to get rich? Or because that’s what is expected of you? This is the most important questions to answer.
If you want a career in academia, you need to learn what makes a professor successful. As a professor, you need many skills. You need to be able to communicate — to teach and advise. You need to be able to apply for funding, which requires good ideas, and understanding of how to pitch them, and a lot of patience. Most universities will evaluate you on how many articles you publish (and where), how much funding you attract, and how respected you are among your peers. Life in academia has a lot of freedom, but that comes with a lot of responsibilities. Please do not choose a career in academia because you want long summer vacations — you will be very disappointed. A professor always works. That said, you will be your own boss. (At least after you have tenure…)
Do you want a job in a large company? Do internships in large companies, and learn what it is like. (Continue reading for advice on how to get good internships.) Companies are applied. Even companies focusing on research. This is because companies are driven by a need to make profit. Profit will mean job security for its employees, a chance for an annual bonus, and protection against tough times. You get profit by being relevant to your customers. That means to build and sell products, generate intellectual property, and stay ahead of the competitors. How is this relevant to you as a researcher? You need to understand the needs of the market. You need to understand a bit about the business aspect, too. A wonderful invention is useless to a company if there is nobody who wants it, or if it is impossible to detect that a company uses it — without having bought a license.
To join or start a small company, you need a lot of nerve. Most companies fail. In a small company, everybody puts in a tremendous effort. Everybody needs many skills. The CTO may have to double as a CFO, the CEO as cleaning staff, and the programmers as sales reps. Be ready to wear many hats, and do not expect immediate success. Life is much less predictable in a small company than in a larger company — for good and bad. As a researcher, that means you cannot afford just doing research, and you need very applied skills.
Are you doing research just because you like it? That is a great reason, and it will help you be successful. But you probably still need to think about what career path you want to be on.
And finally, what about if you are doing research because you want to be rich or your mom always said you are so smart? Chances are that you will struggle a lot. Is this really what you want to do?
2. Dare to fail. (Otherwise you cannot succeed.)
Research is about finding new insights. You cannot do that without taking risks. You need to dare to fail. Most senior researchers would be able to write a book about failing. Document your failures. What did you try, and why, and what went wrong? Next time, you will avoid that path.
Of course, you do not want to only fail. My trick to avoid that is to hedge my bets. I am involved in 4-5 projects at any time. Half or so fail, and I start new ones in their place. If you do not like the distraction of many concurrent projects, you may be able to do the same in a sequential manner, but I feel that having several semi-latent projects allows me to work on one when I get nowhere on another, and this makes the lack of progress feels less frustrating. It also lets me forget what I was doing on the one where I got nowhere, and when I return to it a bit later, I have a fresh approach.
Also, hedge your bets by selecting some very risky projects and some less so. How can you tell what is risky or not? That is sometimes difficult, but experience will tell you, and the general progress in the related areas, too.
It is difficult to give up on something you have spent so much time on, but sometimes you have to cut your losses and move on. Among the foremost skills of a seasoned researcher is the ability to know when that limit has been reached. If you dare to fail in the first place, you will get plenty of practice with this.
3. Dare to forget.
This is counterintuitive, because society emphasizes that knowledge is important, and knowledge means to remember. On one hand, you may avoid reinventing the wheel if you know what has already been done, but on the other hand, being too aware of what others do will restrict your thinking. You will, quite naturally, think like they do. That means that you will have the same field of vision, and will not be able to tread new territory.
Once I have established what problem I am trying to solve (more on that below), I spend a few days ignoring what others have done and sketch solution ideas. Not surprising, most are pretty worthless, others coincide with what others have already done. I round up a few candidate approaches. Then, I look a bit at the related work. What do they achieve? (I pay less attention to how they get there than what they achieve at this point.) Do any of my solutions offer opportunities that other solutions seem not to have? If yes, then that’s a good place to focus on. When I have a pretty decent solution — but still nothing solid written up, since that takes a lot of time and effort — I compare with the related work. Both what they achieve and what they do. By not doing this careful review of the related work until this far into the project, I sure waste a lot of time by reinventing the wheel, time after time, but I also manage to see things in new ways.
The same goes with your own work. If you keep thinking in the same tracks, that will stymie your efforts. Take a break from a vexing problem, forget what you really did, and return to it with a new approach. (If you are anything like me, forgetting is as natural as it is useful … but of course, it comes with the curse of always having to ask your spouse where your keys might be.) Again, you will lose time, but you will also see new angles.
4. Have passion, create beauty.
Have passion. You never will create anything of lasting beauty without passion. You think “beauty” is not a word that applies to what you do? Then do something else.
5. Spend more time on the questions than on the answers.
This is a common mistake among junior researchers: To quickly pick a problem, and then spend all too much time finding answers to that very problem, not seeing how full the world is of other more pertinent problems.
I am not exaggerating when I say that more than half of the contribution is to identify exactly what the problem is, and to formulate it in a way that allows you to start finding the answers. It sounds natural that you cannot find the answer without first knowing the question, right? But if you select the wrong question, then the answer is pointless.
What is important? Why? Who cares? Or who should care? What is done today? What cannot be done? Why?
Pick a belief for a moment. “In five years, all handsets will be as fast as current desktops, but bandwidth will not grow”; “Essentially all devices will be vulnerable to malware infection in a few years, and most will become corrupted at some point”; “Governments and carriers will track their citizens and users by using cell station location information”, “People are more vulnerable to fraud when they are multi-tasking.” Whether this assumption is realistic or not, what are the consequences? What can be done to address this problem?
6. Who are your heroes? (It matters.)
We all need heroes. These are the people we wish we were more like. Pick your heroes. Spell out to yourself why they are special, and what they did to become like that. You will see that circumstances play a certain role, and dedication. Their backgrounds, the way they seem to approach problems. Listen to the way they explain things in talks. Be inspired.
(And also look at the persons behind the achievements when you get a chance to talk with your heroes. If they are nice and humble, please remember that when you are somebody else’s hero. If they act like conceited jerks, avoid being like that.)
Some of your heroes may be alive, and some of those may also be approachable and willing to give you advice. Don’t be shy. For them, talking with you may be an opportunity to enjoy helping somebody they once were like. But, when contacting your hero — by email or in person — please keep in mind that it is really annoying to get what feels like a generic message asking for an internship, and you probably will get fewer responses (if any) if that is how you reach out to your heroes.
When contacting a hero of yours, you may only get one shot. Work on your pitch. What do you have, what do you want, what are you asking for? Imagine that you are the recipient of this email. Would you have taken the time to formulate a thoughtful answer?
7. Work on your communication skills. (Or everything else is pointless.)
Most papers submitted to conferences are poorly written. It is hard to understand the claimed contributions, and the papers get rejected more often than not. Most presentations are not as amazing as they could be with a little bit more practice. The audience sometimes starts thinking of what’s for dinner, and people get less interested in coming to the speaker’s next talk.
Very few people succeed as researchers without having to communicate. That is both to listen and speak, and both about reading what others have done and do a good job explaining in writing what your results are.
It is not silly to take a public speaking class, and it is good to take a class on how to become a better writer. And it really helps seeing how others could have improved, and think of whether you make the same mistakes. So instead of tuning out during that boooring presentation, think (constructively) about how you would have done it. When reading a horrible conference submission, think about how it should be written. (If you tell the authors in a kind way, I’m sure they will appreciate it!)
Don’t kid yourself. Most of us can improve our communication skills.
Learn to adjust your pitch to your audience. You should be able to speak to technical audiences and non-technical audiences about your work, and why it matters to them. Mis-reading the audience means that you waste everyone’s time (your own included).
Learn to self-promote (responsibly). People will only reach out to you if they’ve heard of you. Make sure all your research papers are publicly accessible, in an easy to locate place, and not behind a paywall. Make sure you have a home page, which preferably shows up in the first few Google results for your name. Own your own domain name. If and when someone decides to Google you, you want to know what they are going to find, and make sure it says things that are truthful, and positive.
8. Finding stuff — an advisor, your specialty, an internship, a job.
If you are looking for a PhD advisor, what should you look for? In my view, it is not crucial that the person does exactly the kind of research you want to do. It is more important to find somebody who could become interested in what you want to do, and who has the general competence to guide that kind of work. It is important that you like — or at least can tolerate — your advisor. There will be times when the relationship is tough (especially when you think you are ready to graduate and your advisor does not), so it is best to start off with somebody whom you feel you do not mind. Should you pick the full professor who has 20 students, or the junior faculty member without a record, and with only one student? Well … my bets would be on the junior faculty member. After all, you will get much more time to talk with this person. Before you commit to working with somebody, try it out. Work on a small project. (You would not marry somebody without dating him/her first, would you? Then why commit years of your life to working for one particular advisor without first having “dated”?) And talk to other students — some who like the fellow you are considering, others who do not. You will spend a lot of time working with your advisor. This is an important choice. And it goes both ways. You will “interview” candidate advisors … they will “interview” you.
Now, one more think about potential advisors. Their reputation matters. Look at some recent publication of your prospective advisors. Look up the conference or journal venues, and then look up how prestigious they are. If your advisor only publishes in low-to-medium quality venues, that is not so good. If he or she only publishes with the same two or three people, that is also not so good, as it suggests a small (work) social network. You want an advisor everybody knows (and admires). Then, look at whether he or she is ever first author. That is good. Look at whether he or she is listed after somebody whose name suggests that they should be listed later. That means your prospective advisor did not do a big share of the work, which is also not so good. Or, phrased positively: Does he/she publish a lot, in prestigious venues, with lots of different people, many of which are big shots? (That is good.) Now, read one or two of the papers. Were they exciting?
What is your specialty? When you graduate, you should be able to write down three or four words or short phrases that describe you and mostly nobody else. These words may change over time. When I graduated, I might have described myself as “payments, privacy, revokable”. Now, I might instead say “phishing, mobile malware, user experiments”. It is your goal to guide your research in a direction that allows you to find these words. Think of it like this: if your description is the same as hundreds of others out there, you will have a much tougher time getting what you want than if you are unique (and do good and relevant work.) Finding this specialty is not automatic or trivial, but it helps to keep in mind what would be a meaningful target.
How about finding an internship? Number one is to impress people. If your advisor and his/her colleagues think you are pretty amazing, they will tell their colleagues, and one of them will have a position. If you write a beautiful paper and do an amazing job presenting your results — whether at a poster session, a standard conference talk, or in a colloquium — somebody will think “wow”, and that somebody may be the first step towards an internship. Use your contacts, too. Who do you know that have had good internship experiences? Who do they know?
Another good thing to remember is that there is lots of competition for internships. Having proven yourself already will help you. Many people in research organizations are willing to collaborate with junior researchers by email, maybe writing a paper or two together. What better way is there to impress them? There is a large up-front cost to you — months and months of hard work — but it might take you a step closer to that internship. Or job.
And finding a job is very much like finding an internship. Yes, jobs are really like internships, but longer. And with the minor difference that they might require you to have had an internship already.
9. A few words about your CV.
Don’t pad it. If you list all your publications, and then you add three papers that are just manuscripts, that feels like a padded CV to whoever reads it. If you list memberships in irrelevant organizations, or obvious organizations, that’s the same. Don’t do it. Padding reeks of desperation and deceit, and nobody likes that.
Avoid being generic. Describe succinctly what you want, but do not simply say “an interesting job with the opportunities to work hard to solve important problems”. Everybody wants that. What are your core skills, what makes you special, how does this matter to whoever reads your CV?
Focus. Be succinct. Most people lose attention pretty quickly if they are not intrigued. You do not want that. Make your CV well structured, concise, informative, appealing. Look at CV of others, not just your peers. What makes the CVs appealing? (Hint: it is not a fancy font.)
Remember that references matter. A lot. Include a list of who your references are. If the person who reads your CV happens to know one of them, that’s a good start. But this should matter to you long before you are applying for a position. You should track down people you would want to be your references — some day — and convince them to work with you. Then, you should impress them. Then you’ll be in good shape later on.
10. What matters to be selected?
Whether you are looking for a PhD position, an advisor, a summer internship or a job, you may ask yourself: what matters?
If you are a student, you may be under the very reasonable illusion that your grades matter. After all, grades have been the main metrics of success all through your education. Most of the time, though, grades mean nothing. I mean it. In fact, if you are in a PhD program, many profs will be slightly annoyed, and say that if you keep getting straight As, then you are clearly not prioritizing your time very well: you should be focusing on your research instead!
So what matters?
For several years, I only selected trouble-makers. What do I mean? People who would get stoned, rob banks, and beat up their dates? Of course not. But students who had been found cheating in interesting ways; students who were about to be expelled for having done bizarre but harmless things; and students whom other faculty members thought were nuts — but who were still responsible and brilliant. Exactly! But why? Simply speaking, I do not want yay-sayers. I want to work with people with a personality; with beliefs (even if crooked); and with passion. That, in my view, is what is needed in research. Not people who will do what they are told. Question authority and thrive.
And of course, I would also make sure that the students either were brilliant programmers, mathematicians, social engineering geniuses, or veritable fountains of ideas (including bad ones, of course).
Another thing that matters to me is obsession. The person who thinks about research before going to bed, hoping a new insight will come to him or her in a dream; the person who will look at anything through the lens of the question he or she is trying to address. This is not to say that I want to hire workaholics. Most of the work product generated by workaholics is not really worth much. Which takes me to…
How much is too much?
Now, some final words before I let you go. Imagine a seven-hour work day. You spend three hours, say, doing administrative stuff and reading things that turn out not to be so useful. The remaining four hours: learning and thinking. Now imagine a eleven-hour work day. You still spend three hours with the administrative portion — you are left with eight hours learning and thinking. That is twice as much as for the seven-hour work day. Now, imagine a 19 hour work day. Sixteen hours of learning and thinking! You have just doubled your productive hours again.
Well, maybe not.
It may serve you well to constantly obsess about things (which gives you up towards 19 hours a day of in-the-back-of-your-mind processing), but you sure cannot be productive with a pen in your hand or a keyboard in front of you for nineteen hours a day. (At least, I cannot.) Take a break. Enjoy life. Come back rested.
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