Light bulb moments are flashes of
creative inspiration that send your research ideas off in a new direction, and
generate new datasets or publications. Many people assume that creativity is
the exclusive domain of artists but the best science also requires the highest
levels of originality, innovation and creativity. In the Reith lectures in
2013, and in an accompanying book (“Playing to the Gallery”), the artist
Grayson Perry described his experience of becoming an artist, in a talk called
“I found myself in the art world”. I was struck during his talk about the
parallels between his experience as an artist, and mine (very probably those of
others too) as a researcher.
For the fledging researcher in science
the prospect of developing a distinctive and uniquely personal profile
can appear daunting, just as it is for artists. In Grayson Perry’s words:
“…that most difficult moment I think for a young artist is the moment
when you leave art college after all those years of education and suddenly it’s
just you and the world - unprotected, undirected.”
After years of training as a
research student, perhaps followed by periods as a post-doctoral researcher
working under the wings of a senior investigator, many early career researchers
experience the same moment Perry describes when they begin their first
established post in a university and are faced with the prospect of making
their way in the academic world as an independent researcher. Which research
direction should you choose? How can you begin to generate new and distinctive
research ideas? Here are some tips.
1. Dedication is vital
Grayson Perry says of artists:
“Most of the artists that I’ve met, most of the successful artists I’ve
met are very disciplined. You know they turn up on time, they put in the hours”.
Successful artists such as, for
example, Pablo Picasso and Lucian Freud think about and make art all the time.
They spend all day, every day in the studio. Picasso is estimated to have
produced 50,000 works. Scientists are no different in terms of the need for
dedication and hard work. This accords with my own experience of the successful
vision scientists I have been fortunate enough to know or have worked with. They
are devoted to their work; committed, focused and thorough. They put in many
hours, hone their skills, expose their ideas to the harshest scrutiny, plan
ahead, meet their deadlines, obsess about details.
2. Be persistent
But how do you create something truly
original in your research? Is there even such a thing as originality any more,
or is originality just for people with very short memories? According to the
World Health Organisation there are about 250 babies born in the world every minute.
I sometimes think, when a research paper I am reading triggers an idea for a
new hypothesis or experiment, that there must be dozens of researchers
somewhere out there in the world thinking exactly the same idea, particularly
if they are reading the same paper. But then I remind myself that this rarely
seems to be the case. Everyone thinks differently. Even if they are reading the
same paper, sitting in the same lecture, or pondering the same research
question different researchers inevitably come up with different ways of
approaching the same issues. No two researcher’s experiments are ever
identical. It then becomes a question of which approach is better; more
original, coherent, clever, skilful, incisive.
I like this story about originality
which again comes from the arts, actually from a Finnish photographer called
Arno Minkkinen. It is a story which was also told by Grayson Perry about
artists, but it applies equally well to science. It is called the Helsinki BusStation Theory. I’ll mostly paraphrase Minkkinen’s own words, changing things
here and there to make it relevant to science:
In
the bus station some two-dozen platforms are laid out in a square at the heart
of the city. At the head of each platform is a sign posting the numbers of the
buses that leave from that particular platform. The bus numbers might read as
follows: 21, 71, 58, 33, and 19. Each bus takes the same route out of the city
for a least a kilometre, stopping at bus stops at intervals along the way.
Now
let’s say that each bus stop represents one year in the life of a scientist,
meaning the third bus stop would represent three years of research.
Ok,
so you have been working in vision science for a couple of years collecting
data on the Café Wall Illusion. Call it bus #21. You present a poster on those two
years of work on the illusion at the European Conference on Visual Perception
and an eminent, seasoned visitor to your poster asks if you are familiar with
the paper by Fraser in 1908. Fraser’s bus, 71, was on the same line as yours.
Or you give a talk in London and a member of the audience suggests that you
check out Lipps (1897), bus 58, and so on.
Shocked,
you realize that what you have been doing for two years others have already
done. So you hop off the bus, grab a cab (because life is short) and head
straight back to the bus station looking for another platform. This time you
are going to study a new illusion you discovered, called the Moving Wall
Illusion.
You
spend a year at it, with some funding from BA/Leverhulme, and produce a series
of experiments that elicit the same comment when you present it: haven’t you
seen the work of Gregory and Heard (1983)?
So
once again, you get off the bus, grab the cab, race back and find a new
platform. This goes on all your scientific life, always presenting new research,
always being compared to others.
What
to do?
It’s
simple. Stay on the bus. Stay on the f****** bus.
Why,
because if you do, in time you will begin to see a difference. The buses that
move out of Helsinki stay on the same line but only for a while, maybe a
kilometre or two. Then they begin to separate, each number heading off to its
own unique destination. Bus 33 suddenly goes north, bus 19 southwest.
For
a time maybe 21 and 71 dovetail one another but soon they split off as well, the
other researchers never used your experimental techniques anyway.
It’s
the separation that makes all the difference, and once you start to see that
difference in your work from the work you so admire (that’s why you chose that
platform after all), it’s time to look for your breakthrough.
Suddenly
your work starts to get noticed. Now you are working more in your own way,
making more of the difference between your work and what influenced it. Your
vision takes off.
The moral of the story is that you
need to be persistent and not easily
put off; stay with your initial inspiration. You have to work a lot, as the previous
tip about hard work indicated. You have to immerse yourself in research
thinking. This can be done in many different ways and many places.
3. Go to conferences
You can avoid some of the problems
described in the Helsinki Bus Station Theory by making sure that you know your
field inside out, and this is one of the reasons why you need to be dedicated.
By going to conferences and reading the literature you learn about the history
of your research field, and will develop an awareness of important current
trends and the issues which are attracting attention and debate. These issues
point the way towards research ideas that have the potential to make more
impact on the field.
Think of a few people in your
research field who you regard as thought leaders. Their published papers,
especially review papers, may identify issues which will set the research
agenda (and attract funding) over the next few years. Journal papers can age
quite quickly, so it is really important to go to conferences that the leading
researchers attend, and be sure to attend their talks. Seek them out in poster
or social sessions to ask them questions (almost all researchers love talking
about their work). Leading researchers are the most reliable guides to future
directions, and often sit on funding panels.
4. Go to research seminars and research group talks
Don’t pass on other opportunities
to attend talks, whether internal to your institution, elsewhere in the UK, or anywhere
you can find them. I am not talking about disseminating your work – that is a
whole different issue – but about listening to others talking about their work.
If the talk is close to your own
area of research, then it can often directly prompt new ideas for you to follow
up, of course. Talks outside your area give you a chance to hone your critical
thinking skills. What are the weak spots in the rationale or experimental
design of the speaker’s research? Are their claims justified? Early in her
career the eminent astrophysicist Jocelyn Bell-Burnell had a good strategy for listening
to talks and making an impression in a male-dominated discipline. She would listen
intently to the first 5-10 minutes of the talk, when speakers generally lay out
the background and general assumptions behind their work. These are almost
always fundamental to the research and conclusions and can be very revealing
about the clarity of the speaker’s thinking, the rigour of their reasoning.
Sometimes their assumptions limit the scope of the work in ways that only
become clear later on, though the speaker may prefer not to draw your attention
to these limitations. Jocelyn Bell-Burnell would focus her questions on the
validity of those assumptions, and how they relate to the conclusions. E.g ‘If
your assumption about blahblah was incorrect, would your conclusion still be
valid?’ ‘How solid is the assumption?’
The questions other people ask at
talks are also instructive. Did the presentation leave loose ends for an
attentive listener to pick up? Did you think of them? Do they indicate a
weakness in the ideas on the one hand, or lack of clarity in the presentation
on the other? How did the speaker respond to them? Did they evade a question, or
come clean about a problem, or deal with it convincingly?
Even of you can salvage realtively little
from a talk, just going to it gives you mental space, and puts you in the
mindset for thinking critically about research. As academics, none of us can
spend all day everyday thinking about and doing research so we have to take
advantage of every opportunity that we can to keep in the mindset.
5. Learn new techniques
Dynamic research fields are
continually evolving. Creative researchers develop new techniques, or co-opt
techniques from other disciplines, which open up new avenues of research and
theorising. Keep an eye out for technical developments and think about how you
can exploit them, preferably before other researchers latch on to them. Invest
in the time needed to learn and apply the techniques, but beware of a potential
pitfall. Some researchers fall back on technical tinkering as a safe harbour
from the stormy waters of critical debate if you set sail with a new idea or
experimental result. Techniques are useful only as instruments rather than ends
in themselves.
As an example, a technical
innovation worked well for me in the early part of my research career. There
had been a couple of research papers in visual motion perception in the early
1970’s based on a technique in which human actors were filmed in dark conditions
while wearing lights (or reflective material) positioned at their joints. All
that was visible in the film was a collect of a dozen bright points flitting
across a dark background. The paper reported that viewers spontaneously perceived
the complex movements of the disconnected dots as meaningful human forms (examples can be viewed on my website). The work
raised lots of interesting questions, and some possible explanations, but not
much was done to follow it up because the creation of these videos was quite
laborious before personal computers came along. I came across a technical paper
from the late-1970’s which listed a computer program to simulate the displays. At
the time very few researchers seemed to be using this technique but I could see
that it had a lot of potential so I spent quite a bit of time translating the
program code into the language I was using, got it going on my computer
graphics system, and carried out some pilot work. On the back of this initial
work I applied for and won a research council grant in the late 80’s and early
90’s, with post-doc, to do the research. The proposal focused on the new
possibilities the technique opened up, motivated by the theoretical importance
of the results. The publications based on this work are among my most cited papers.
6. What kind of ideas?
What kind of research ideas should
you focus on, particularly in the context of generating ideas that lead to
fundable research proposals. It’s always best to start with research that you
would like to carry out, of course and try to shape the ideas into a fundable
project, rather than think of a funder and try to come up with a project which
fits its remit.
Funders are not going to be
impressed by a proposal that just allows you to carry on what you are already
doing, such as what you did in your PhD. Incremental research which follows-on from
previous work, tying up loose ends (like a lot of follow-on PhD projects) is
not an exciting prospect for a funder. You have to begin thinking differently. You
need your work to take a quantum leap in a novel direction, in which you are
clearly making an independent and valuable contribution to the field. For
example:
- Collect a new data set which has a major
impact on current theories.
- Develop a theoretical innovation which
alters the interpretation of current data sets.
- Introduce or apply new technique which opens up
many new possibilities for future experiments which challenge current theories.
Don’t be too ambitious, and try to
solve everything at once. If the funding scheme allows it, you need to shape
the idea into a project that requires someone else – a pre- or post-doctoral
research assistant. This is really important for building your research
capacity, your ability to scale up the amount of research you will be able to
conduct, and it is usually by far the biggest cost element in the project. But
the justification has to be clear.
Wherever possible, and this partly depends
on your research field, start from a clear theoretical position and spell out
the implications of your work for this theory. That was an important element of
my case for the motion work in the previous tip. There is a temptation in research
to fall back on data collection - when a researcher is not sure what to do next,
apart from learning a new technique they may conduct another experiment just to
see what happens, hoping that the new data will prompt some new ideas. This is
a risky and inefficient strategy which funders do not like– if the experiment
is not soundly based, it could be a waste of time and money. Reviewers are
practiced at spotting poorly motivated research (they go to lots of talks, and read
lots of proposals!). Of course there are situations when you need some basic
empirical data as a starting point for thinking about research questions, but
the motivation has to be very clear and focused.
