TRANSCRIPT
“When I started off at graduate school I thought a good scientist was somebody who just collected masses and masses of data, and I remember turning up to my supervisor after my first few months and he said, "How are you getting on." I said, "Oh I'm doing really well," and I showed him these books full of numbers, and he said, "Oh wow, well done, that's great. And what hypothesis are you testing?" And that really stopped me in my tracks. I didn't really have a hypothesis; I was just watching and trying to collect data and I was sure that by looking through the data something would emerge. And of course it didn't. And that's, I think, the best lesson I ever learned early on: that a good scientist has got to have interesting hypotheses to test, not just collecting lots and lots of data.”
-Nick Davies, Ph.D.
Professor of Behavior Ecology, University of Cambridge
“The basic trick of science is to ask the right question, and to ask a question in a way which can be answered. Not, “How does the brain work?” That's a question, but that's not an answerable question. Something like, “Is a particular sodium channel involved in pain?” for example. That would be a terrific question… and the reason I think this is X, Y, and Z, so now I'm going to test it. I'm going to block the sodium channel, or whatever, and see if pain is still experienced.”
-Joe Herbet, Ph.D., M.D.
Professor of Clinical Neuroscience, University of Cambridge
“People often come into graduate school thinking they are going to answer lots of big, grand questions, and that's great; that sounds really great when you're at the interview and you've got lots of big picture questions in your mind. But then, it can be a bit demoralizing when you realize how you've got to focus on one particular question. So that process of focusing down can be a challenge for people to deal with.”
-Chris Jiggins, Ph.D.
Professor of Evolutionary Biology, University of Cambridge
“Sometimes the questions are very obvious. The big question is obvious and the skill comes in breaking it down into smaller steps that are tractable. So if you know that you want a technique, like being able to visualize gene expression in tissues, then you have to know how to break that down into a series of questions... and designing good assays that will tell you whether or not you achieved what you want at a given step.”
-Michael Acam, Ph.D.
Head of Department and Professor of Zoology, University of Cambridge
“The good questions come basically just like that. The thing goes round in your head, round, round, round, and then suddenly you think, “Yeah that's not a bad idea.” Then you’ll think about that again tomorrow and it turns out to be a lousy idea. Then one day you get one that is quite a good idea, you do an experiment, you get a result, and think, “Yeah, that was a good idea.” It's kind of a process. It's like an artist getting an idea for a picture, or a novelist getting an idea for a novel, or a composer for a symphony. It slowly generates in your head and you refine it and refine it and refine it until suddenly you realize, “Okay, I think I'm just about where I should be now, so I'll go for it.”
-Joe Herbet, Ph.D., M.D.
Professor of Clinical Neuroscience, University of Cambridge
“My lab tends to do hard experiments, difficult things that maybe other people don't want to do. But the research always has to be driven by, "Is this an interesting question, is this worth knowing?" It's got to be driven by, "So what?" There are always experiments you can do and you can generate vast amounts of data but at the end of the day one should ask oneself, “So what, who cares, does this matter, have we learned anything?” This has been imparted to me by my Ph.D. advisor and by my post-doc advisor who are both very good at asking good questions (one in the States, one in the UK). And so they just sort of taught me that asking the key question is the right thing. So it has to be an interesting question. It doesn't have to be a big question, it has to be interesting, and then when you get the answer it has to move you forward.”
-Brian Hendrich, Ph.D.
Principle Investigator, Department of Biochemistry, University of Cambridge
“You can think of scientific problems as being surrounded by a huge ball of fluff, and the bigger the ball of fluff, the more important the problem. Now at the core of this fluff is the actual problem. But most people working in the field are attracted to it because it looks like an important field, so many people are working on it, but they don't actually understand what the basic problem is. As I said, his opinion was that most scientists were fluff wipers. They look at it from the outside and there are lots of little problems all around this core and they wipe away a bit of fluff, they get a JBC paper and their career progresses, but they are never going to make a major discovery. But then there are others who can see through the fluff and really understand what the problem is that people are trying to solve, and then they try and attack that as directly as possible.”
-Sir Michael Berridge, Ph.D.
Emeritus Fellow of Cell Signaling, Babraham Institute
“When you're trying to find things to do lots of alternatives come up, and you need a guiding light to tell you which ones to choose, because they are going somewhere, in a particular direction (or might be going somewhere), so I find that very helpful. So it's useful to have a big problem. For me the big problem was how you build animals in terms of design. How genes are used to build space and pattern and shape. That was my kind of guiding light. I had that out there. Whenever I seemed to be drifting off in some other direction I would try and think, “Is there something better I could do?”
-Peter Lawrence, Ph.D.
Professor of Zoology, University of Cambridge
“You ask people, "What's your working hypothesis," and you'd be surprised what kind of answers you get. Many people don't have a strong working hypothesis. They can tell you little bits of why they are doing it, but the big field, the big problem they are trying to approach, and their attempt to solve this is lacking, really. It's the working hypothesis that drives your research. If you've got a good problem and you spend a lot of time reading about it, you develop a working hypothesis of how you think it works, and then that drives your research. And that's something you want to develop very early. Don't leave it to your supervisor or somebody else; you must be in on the act very early, so you're a master of your own research and what you're going to do.”
-Sir Michael Berridge, Ph.D.
Emeritus Fellow of Cell Signaling, Babraham Institute
“Try and pick on a puzzle, I would think, that's doable within the period of a PhD. You don't want a problem that's so big that you're not going to even start to tackle it. But you don't want something too trivial, so the art of choosing something that's answerable, I think, in a time frame, is really important for a student starting off.”
-Nick Davies, Ph.D.
Professor of Behavior Ecology, University of Cambridge