- So, prioritizing experiments is something that's a difficult skill
and something that's absolutely critical to making progress in
science. So, it's absolutely the case that it takes a little bit of
time to have a giant list of experiments that you're trying to weigh,
but also, this is a protection that students have against their own
mentors. So, mentors have lots of ideas and they might throw them all
at you and they say, "Oh, it would be great idea to do experiment X
"and it would be a great idea to do an experiment Y." And then you
talk to them a day and a half later and they say, "Oh my God, you know
what's a wonderful idea "is if we do this other experiment." So, you
might have a list of ten experiments that your advisor is excited
about. So, having some sort of idea of what you should spend your time
doing is really, really important. I think the one guiding principle,
no matter what experiment you're thinking about, is going back to the
big picture question. It's really easy to get off on a tangent and go
follow something that really piques your curiosity and sometimes that
will and sometimes that will not get you back towards your picture
question. So, having that North Star is really, really important. So,
that would be step one. But, I think the other factors that go into
deciding how to prioritize an experiment are feasibility and then also
having availability.. of reagents and availability of technologies.

- When, I'm thinking about feasibility and risk for when a student is
designing an experiment, my first question is always: do we have the
reagents to do that experiment? Do you need to generate those
reagents? How long is that gonna take? And will that actually answer
the question that you're hoping to answer? Is there a way that you can
answer this question, this complicated model that you've come up with?
Are there predictions that this model makes with reagents we have and
that we can easily engineer into your strain of interest to be able to
know whether or not it's worth doing that? Now, the caveat to that is
that there are plenty of examples where somebody went whole hog, made
the reagents, and it turned out to be right. I guess my issue will
always be: how feasible is it in the organism you work in, how
effective you are at generating those reagents on your own, and is the
time you spend generating those reagents worth your model being
potentially wrong and instead, should we evaluate if we can address
your model with reagents we currently have or through another
experiment that might not answer the question directly, but may answer
the question obliquely so you know you're on the right path.

- So, one thing that I tell students and postdocs always is to have a
small line of working experiments that they know is gonna work, that
they know is gonna make progress, and that all of these other
experiments, some of them are really, really worth doing. Some of them
are high risk, high reward experiments. Some of them are experiments
that really take a longer time to develop, but ultimately will really
get to your big picture question. And so, you don't wanna really just
focus on incremental progress or really just focus on the big picture.
But, you want to have both of those things going at the same time. So,
a lot of that will depend on the tools you have available and the
feasibility of the experiment. And so, this is something that's
really, really important in trying to decide which way you should go
with an experiment, knowing that you have a feasible set of
experiments always going.