The 7 Requirements of All Effective Scientists
By Mark Changizi on June 20th, 2012
Editor’s note: As part of an answer to a question in our recent interview, Mark Changizi shared his prescriptive guide for scientists that he used to give to all of his students as they entered the lab. We found the advice so valuable we decided to publish it on it’s own. The insights are not only timeless, but also form the basis of his upcoming book, Aloof.
1. [Turing tape] You need an idea notebook.
- It is provable that Turing machines with more tape can carry out more complex algorithms.
- Without a notebook, you forget the beginnings of all your potentially great ideas.
- And with a notebook you can systematically build on your idea, not losing where you were once you set the work down.
- From about 1998 I have about 26 notebooks.
- I split each page into two vertical strips, and write small. More information per page helps you integrate things better.
- I also now have a “meta-notebook” that keeps just the best ideas, and the hope is that it lasts while I go through a dozen or more main notebooks. Without this, many of your great ideas can even be lost within your own notes.
2. [Open-minded] Do not aim to solve some specific problem.
- In fact, do not even confine your brainstorming to any particular subdiscipline.
- The odds of getting a great idea in any given area is very low. So you need to allow your brainstorming travels to go anywhere. As true for your first discovery as for your tenth. (Perhaps more true of the tenth, because then there are fewer discoveries left!)
- Sometimes it is easier to make an important discovery in a field when you are somewhat ignorant. …because you don’t know what “everyone knows.”
- Avoid becoming psychologically invested in an idea too early, lest you waste time on it.
- However, once you think there is some potential, you can’t give up too early. Very often the true idea you end up with differed from your first idea you thought had potential, and it was only after delving into the literature with your idea in hand that you realized that your fuzzy intuition wasn’t quite coherent, but the modification was.
- The previous two bullets are so vague as to be useless, but there they are.
- Also, note that sometimes the best way to motivate yourself to learn a discipline is when you have your own idea first. You’ll read attentively now.
3. [Proliferate and select] You may need 10 to 100 ideas before you find a good one.
- Your idea has a lot of hurdles before it. It must be coherent, interesting, true, testable, publishable.
- Keep brainstorming, constantly.
- Set a very low threshold to writing an idea down.
- No idea is too embarrassing. Some of my best ideas seemed embarrassingly crazy when I first conceived of them.
4. [Aloof] Avoid feeling part of any specific academic community.
- When you become part of any community, you learn all the personalities—both your peers and the bigwigs. You naturally can’t help but want to impress them, to even become them. That’s just human.
- You learn from the community the “big problems” they respect.
- You learn about the problems in other fields that they “poo-poo.”
- All this serves to greatly constrain your ability to find a great idea, because it makes you psychologically less able to go outside your own community.
- And it can happen without you ever noticing.
- Not only are you less able to take up other kinds of problems, but it makes you less able to freshly see the problems in your own community, because you are too much of an insider. You know what “everyone knows.” That is, “Everyone knows X,” and so you wouldn’t dare put forth ideas contrary to X.
- …and you wouldn’t even realize you were being deferential in this way.
- You need to be an outsider so that you are free to stick your middle finger up at the discipline, in the form of an idea that contradicts “what everyone knows.”
- A corollary: Avoid conferences.
- Staying aloof does not locally optimize your career, because of the relative dearth of contacts.
- But it can help globally optimize your career, via your research standing out.
5. [Be the boss] Avoid working for anyone, and that includes a granting agency.
- For your graduate career, try to secure yourself some time to pursue ideas of your own, in addition to the ideas of your advisor.
- For your postdoc, apply for a fellowship where, if you get it, you are free to research as you wish. Or, find a lab where the PI is likely to let you point the way to some extent.
- For your job, avoid universities and departments where grant demands are unreasonably high. (When you have a grant, it typically means some granting agency is your boss, unless you’re so lucky that you proposed to do exactly what was the most significant research direction for you.)
- For example, if you are the lone theorist amongst experimentalists, then because everyone else needs a million dollars every two years, you’ll end up needing that much too because it becomes the social-merit-yardstick of success. …even though it makes no actual sense for you.
- And if you do get that much grant money, your ability to be creative will suffer, for your only worry will be how you can make sure that you get the next grant, so that you don’t lose your lab. And the best way to get the next grant is to get it in pretty much the same kind of thing you did in the previous grant. (And odds are you won’t get that much without becoming an experimentalist anyhow.)
6. [Data] Don’t publish without data.
- There’s no such thing as a pure theorist in the brain and cognitive sciences. Unlike in physics, you can’t publish work that will be noticed by other scientists if you don’t very seriously connect it to data. There are some physics-types who publish biologically-related stuff only in Physical Review, for example, but these are largely ignored by most scientists. …partly because of the unusual journal, but mostly because the connection to the data and existing problems is not made clear.
- May simply be a cultural phenomenon with no wisdom underlying it, due to nearly everyone in the field being experimentalist, and their standards get extended de facto to everyone. In physics this is not quite the case.
- Alternatively, it could be that brain and cognitive sciences (and the biological sciences generally) is importantly different than physics, such that a good theorist just can’t be as abstract as physics theorists can be. Perhaps in cognitive science the data are intrinsically messier, or there is a lack of shared frameworks within which problems are approached, or the gap between theory and data is inherently wider. ?
7. [Sloth] Avoid all but the simplest experiments, and avoid building complex tools.
- Being an experimentalist is difficult. It requires loads of specialized skills, great experience, and more theoretical know-how than what theorists typically need. The difference is that the experimentalist’s expertise is applied to a million problems in the lab rather than just to the scientific problem itself. Changing research directions for an experimentalist is difficult and counter-productive. For a theorist, this makes it impossible to have the freedom to find a next good idea.
- Instead, rely on easy-to-get data.
- Already-published data. There is a century-high pile of papers filled with data that is just sitting there, and if you’re lucky your question can be tailored so that you can test it from existing data, mined out from the library.
- If you must do experiments, make them easy, like very simple psychophysics experiments (although even this is very difficult to master).
- Or, you can often gather data in non-standard ways, like from natural scene images, or from the web, etc.
- Don’t build any complex tools, unless you really have to. Typically, by the time you build the fancy beast to help you do X, you’ve burned through much more time than it would have taken to just do X the slow way.
- And, worse, once you’ve built a fancy machine, you get the hammer effect: that when you’re holding a hammer, everything looks like a nail
- You also get the sunk-cost effect, that you feel you ought to use your hammer on things, now that you spent so much time building it.
- Suddenly you only want to use your tool on things, rather than picking research directions that have the most potential.
- For example: A new professor in neuroscience at UCLA took two years to get his equipment up and running from his half-million-dollar start-up, and was constantly wondering aloud what experiments he could run once it was up and running.
Mark Changizi, PhD, is the Director of Human Cognition at 2AI Labs and writes on science at Forbes, WIRED, Discover, and the Atlantic among others. Mark is also the science host of the new Discovery Channel show Head Games. Keep up with his latest thoughts on Twitter.