(soft music)
- When you get ready to ask a scientific question,
it's important to think about your skills,
your interests, and your temperament.
In my mind, it's a lot like trying to find balance
on a number of different axes.
So, one of the most common ones that people think about
is their preexisting skillset,
so, like, things that they already know how to do.
Now, you don't want to take on a project
that just leverages the things you know how to do,
because then you're not learning anything,
and the point of being in graduate school
is to learn some stuff.
But you also don't want to be on the end
where you're just completely lost at sea
and don't feel like you can bring anything
of what you knew before to a problem,
because that can be really frustrating,
and the ramp-up time to feeling productive
can be really long.
So, ideally you want some mix right in there
of stuff you know how to do,
and so you're going to be able to do right away
and start feeling really productive,
and some things that are technically challenging
or conceptually challenging,
so that you'll have to stretch yourself.
- So, when we choose a project,
we can consider our skillset.
That's one of the basic determinants
of how feasible the project will be.
It depends a little bit on how open you are
to explore and learn new skills,
versus how much you want to play it safe
with the skills that you have.
I would say it's personality the situation depends on.
My first project from my first student
was to take this commercial 96 well fluorometer
and rewire it to oscillate with the temperature,
so we could determine the affect of
the frequency of temperature changes
on bacterial growth rate,
and this student had never even grown bacteria.
So, after two weeks, I saw his motivation go down.
It was just too hard.
And so, I said, "Okay, okay, okay,
"let's just streak bacteria on a Petri plate
"and count colonies."
Great, it worked.
Now let's do a growth curve.
Great, it worked!
Now let's do another growth curve to see the error bars.
Oh, great, 10% error, that's great!
So, every time I could both give feedback
and keep the project at the right scale of competence.
So, it's a communication, and students
can communicate to the mentors,
it's actually your role, to see where you are
between the scales between easy and impossible
so as to keep the project always in a good place
that takes you close to your edge, but not quite,
so that you feel challenged enough, and yet capable.
- The other axis is the kinds of problems that you like.
And this is not just what kinds of biology do you like,
because most biologists I know are pretty
interested in a lot of different kinds of things.
I feel like this has more to do with
the kinds of experiments that you like to do,
or the sorts of ways that you like thinking about a problem.
- Self-assessment and evaluation of
what you like to do personally is a major driving force
to deciding what project you're going to do.
So just knowing myself, I knew, okay,
cancer runs in my family.
You know, I really want to know why
my family's susceptible to breast cancer,
so I kind of knew that I wanted to be
in the field of cancer.
- One other thing that I would say about
choosing a research topic is that
it's not very helpful if you choose to work on something
that nobody in the lab has experience on,
and your advisor's not interested in.
As a graduate student, you do rely on
the people around you to help mentor you,
and you're likely to get the most out of that environment
if you are working on things
for which there's knowledge within the lab.
- So, we have interest and feasibility.
Now, these of course, there's no units,
so we can't just rank projects by
most to least feasible and most to least interesting.
Just don't get stuck on a project that's down there,
you know, not interesting and not feasible.
Some people make a mistake and think that
hard equals interesting.
So, if what's interesting for you
is to overcome a technical challenge,
to measure things that have never been measured before,
then it's also interesting.
- And then the other piece about
finding the right question for individual people
is about their temperament.
So, everybody is more or less comfortable with,
like, degrees of risk in their project.
There are also different degrees of organizational aptitude.
Right, so there are some people
who are incredibly good at organizing
complicated projects with a lot of moving parts,
and collaborators, and things like that,
and other people who are much better off
working sort of more on their own, maybe,
on something that they can kind of control themselves
in their own sphere,
and some people who need sort of short term rewards,
so, like, experiments that happen on a shorter timescale,
and other people who are more tolerant
of very long term efforts.
And you need all the types.
None of these are better than another,
it just means that they should populate
different parts of the project sphere.
- So, if we take the effort to
write down several projects for ourselves,
and then we notice that we can have in our toolbox
a list of projects, a range of projects.
Some of them are low hanging fruit.
Others are grand challenges.
They're very interesting, but they're not so feasible.
Maybe, to break them up in the future
into smaller projects, or to think about them as a goal
for a long term PhD, or a long term faculty position.
So, for a beginning PhD student, I would say
a low hanging fruit could be a way to train.
Or maybe if you are the end of your PhD
and you have just a limited amount of time,
a good low hanging fruit might work.
So, just to develop this idea that
you can have a range of projects,
and according to the situation,
you might choose different ones.