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 tips 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 responsibility. 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.