(gentle music)
- There are several different ways that people
can ask scientific questions, some of which are more
qualitative, where you want to know does this phenomenon
occur or not, but there are also quantitative
type of questions which get at how often does
something occur or by what extent
does this phenomenon occur?
- If you think about, pretty much every scientific paper
that you read, it fits in one of these categories.
What is there?
How does it work
And why is it like that?
And they are all important aspects of science.
What is there can be technique papers, right,
that let you see something that you couldn't see before,
or screens, right, these sorts
of hypothesis generating
large scale systematic efforts.
A lot of functional genomic efforts can look like that.
How does it work, right?
This is a question that draws
on mechanism, right, which is, I think,
a really interesting word
because it means something different
to every different subfield of biology.
Some people think that a mechanism is how particular
amino acids wiggle around in a protein.
Some people think mechanism is how two proteins
interact together.
Some people think mechanism is a circuit diagram.
So it happens at different scales,
but they are all related to this explanation of the parts
and how the parts work together.
Then the last one is this question of why is it like that?
This is where biology can get philosophical
but often, evolution can fall into this category too.
How did the system end up the way that it is
or what are the costs and benefits
of the system design?
What are the trade offs in that?
I think if you try hard to break down
every paper that you read into these categories,
you can start seeing
how they really do fit into these categories.
- One of the important aspects of coming up
with a scientific question is actually refining it down
into something that is answerable.
For example, you might be interested in studying evolution.
One student that joined the lab who was interested
in this area was particularly interested in studying
the adaptive immune system as a complex evolving population
that literally evolves in real time.
As we're exposed to different pathogens,
as we get vaccines, how does our antibody repertoire
evolve or develop to combat that antigen
that it's attacking.
To go from this broad question of studying evolution
in real time to studying something that is a very focused
question such as how does the immune system respond
to a vaccine is one way of thinking about how you can take
a broad question of interest, hone it down to something
that is answerable.
- An example might be something like I want to study
the 3D architecture of the nucleus.
Well, that's great, 3D architecture of the nucleus
is very interesting, but it's an area, its not a question.
Even something like what does the 3D architecture
of the nucleus look like isn't a good scientific question
because it's too broad.
The art of taking a general area that you're interested in
and then pushing on it until it's a very specific idea
about how the field thinks about it currently
and whether that can account for some prediction
you might have or some type of experiment you might do
is the key.
Often that question is narrower
than students realize.
- Pretty much any question needs to be thought about.
You have to focus on whether or not the question itself
is indeed answerable and if it's not a question
that you can really come up with a technique for answering,
then you need to refine the question.
That doesn't necessarily mean that it was a good question
or a bad question.
It just means that the question itself may need
some refinement.
- I think the biggest question and the most important
question you can ask yourself, is how will the field
be different after I answer this question.
That means that you need to consider what the current
thinking is in the field
and what the current methodology is in the field.
Will you confirm
an existing idea
that people are already pretty confident in?
That might not be a great scientific question.
- The people who join my lab are very interested
in taking technologies or things that we do in our lab
and making a difference in the medical world.
One of the ways that we try to motivate
our scientific question is by figuring out
where are the unmet needs that are out there.
They could be basic science unmet needs.
They could be clinical unmet needs,
but before we pursue a question, asking the question
so what.
If we, best case scenario, everything worked,
what would this actually do?
If we can't answer that, we generally step back
and say well, maybe that's not the right question
or the right approach to take.
It's not always so easy, right?
Sometimes you don't know what will be the end goal
but at least it's a a place to start.
- There are like a set of litmus test questions
that you can ask yourself to evaluate your
own scientific question.
One is, is there some
hypothesis that's already
out in the field but isn't tested?
People might think differently in the sense that
if you confirm it, they might finally feel confident
that this is a real phenomenon.
Is there a hypothesis that you think needs
to be overturned?
That's a big one.
People think very differently about things if that is true.
Are there ways that people have been doing experiments
that are technically limiting,
such that you do things
in a technically new way that allows them to think
about the question and do their work in a new way.
That can be another really good kind of question.
Not all questions have to be revolutionary, right?
I think that there can also be really good scientific
questions that are
taking existing ideas
and moving them into a new system where you might be able
to do different kinds of experiments.
That also can be incredibly valuable, where you're not
changing conceptually how people are thinking
about a problem but you're enabling a whole different
sort of sphere to work on that problem.
- This year's Nobel Prize in medicine and physiology
went to Yoshinori Ohsumi
who discovered autophagy in yeast.
He described the pathway that was already known
in mammalian cells but in a situation much like I had
done for secretion that allowed the molecular details
to be elucidated in a way that was not going to
be possible in mammalian cells.
He published two papers
on which his Noble Prize was based.
One, in the Journal of Cell Biology
and the next in FEBS Letters.
Neither of those papers would have been accepted
by Cell Nature and Science because they weren't flashy
because yeast
autophogy, what does that mean.
It was only clear to those who could see
what advantage he provided
that this was going to solve the problem.
Finding a problem like that is the challenge.
That's what, I think the most creative people do.
They find a challenge like that and a potential solution.
That's the kind of thing that to me is the most exciting.
- It's not that everything that you do has to pass
this test of novelty.
If you're sequencing a human chromosome,
there's not much innovation
because someone next door sequenced another
human chromosome.
You sort of do the same thing.
It's not innovative but is it important, is it impactful,
will it be significant.
I think innovation and novelty are things that
you want to have at the kind of big picture level,
but don't have to be drilled down to every experiment.
- I think the broadest, again, just to reiterate,
the sort of broadest advice is to think about how will
the world change?
How will your field change?
How will your lab's thinking
or doing change after this gets answered?
You want something to change, right, you don't want
it to just sort of, everybody's sort of just happily
going along.
You want to be able to define yourself some aspect
of how your work will impact what's going on.