Ideas: they don’t come from storks
Most graduate students have had minimal independent research experience and will depend heavily on their advisors (or on the postdoctoral fellows that they are teamed up with) to get a feel for designing experiments. Within their first year full time at the bench, however, students should be designing their own experiments. experimental design encompasses many parameters. The most important, of course, is the hypothesis the experiment is designed to test. For this you need to have an original idea. But where do ideas come from?
Although really good ideas seem to come from nowhere (at the same time, they also seem obvious after the discovery), they are seeded by information from external sources. The key concept is cross-pollination. Talk to your fellow students and more senior scientists in your department and at meetings. Discuss your (and their) research. commonly, ideas and techniques that are standard in one field are novel in another, and their application can lead to breakthroughs. read widely, but not necessarily deeply. Scan the major journals; if the title is interesting then read the abstract. Still intrigued? read the discussion. Only if the paper seems relevant should you actually look at the data and then carefully read all of the sections. While on this topic, reading the methods sections of irrelevant papers can give you good ideas about how to improve your experimental protocols or can suggest novel strategies to attack your problem. You should also attend seminars in other disciplines, but sit near the back and beat a strategic retreat if the talk turns out to be of little interest.
Growing your wings
There is nothing like enthusiastic naiveté to seed a discovery. Knowing too much about a topic can actually be a barrier to discovery. experiments that experts know won’t work sometimes do, because either the experts’ assumptions are wrong, or new reagents or technologies became available that allow nature to be queried in a new way. Imagine you have just read the latest issue of Nature Reviews Molecular Cell Biology and are struck with a stupendous idea. You excitedly barge into the office of your PI and propose your killer experiment. She spends the next 30 minutes explaining in excruciating detail, with impeccable logic, why the experiment not only can’t possibly work, but will be uninterpretable if it does. Dejected, you stumble from the office in a haze of self-recrimination and doubt. But then, while cycling home, you regain your bravura and decide that you are going to do the experiment anyway.
This is exactly the right attitude that you should have. It is crucial during your training that you develop confidence in your insight and learn to think independently of your mentor (in the wise words of my first mentor, “the outcome of the perfect training experience is that you leave the laboratory thinking that your mentor is a good person, but a bit dumb”). So you do the experiment, and 95 times out of 100 the experiment doesn’t work. Don’t freak out. Here’s a secret from the PI world: if you don’t tell us, we won’t know that you even did the experiment. When I walk through my laboratory, I have no idea what the postdoctoral fellows are doing. I know what experiments they’ve done recently, and what we discussed they should probably do next (it’s their decision), but on a day-to-day basis, I really don’t know. Just watching them pipetting something or looking into a microscope, whatever the purpose, puts a smile on my face — they might discover something today!
So when the experiment doesn’t work, put the data in your notebook (the failure will probably be useful down the road) and don’t tell your PI. On the rare occasion when the experiment gives you a glorious result, you will have the great pleasure of strolling into the PI’s office with a broad grin on your face and asking (magnanimously, of course) whether they would care to see the data from the ‘experiment that would never work’. Only a control freak PI (see figure 2 in Part I (REF. 1
)) could fail to share your joy and excitement. In fact, when you are a PI yourself be careful when discouraging your mentees from performing experiments, no matter how spectacularly flawed they might seem. There is simply no substitute for enthusiasm in science, and you douse it both at your own peril and at the peril of those whose careers are your responsibility.
Having a good idea (or even a bad idea, sometimes any idea will do, as they can all lead to serendipity) is only the start. Designing experiments is an art that you will continue to improve for as long as you work at the bench or supervise those who do. The size of the experiment is crucial (). It should be just large enough to have a sufficient number of repeat samples and positive and negative controls for you to interpret the results with confidence. Small experiments are much more likely to work than big ones, as there is less to go wrong. Furthermore, no matter how much thought you give to the experiment, the crucial controls will occur to you after doing the experiment, typically only after many repetitions, if at all. rare is the scientist who has not been confronted with an essential control when the work is presented in a seminar or for publication. By doing a series of small experiments with constant modifications based on each preceding experiment, you will progress much more rapidly than by performing larger experiments that try to anticipate all of the problems and possible outcomes. An important psychological advantage of small, rapid experiments is that failure (the typical fate of new experiments) is much less depressing than after spending huge amounts of time and energy in a much larger but equally unsuccessful effort.
Another reason for small experiments