#95 from R&D Innovator Volume 3, Number 5          May 1994

Fostering Exploratory Research
by Robert S. Root-Bernstein

Dr. Root-Bernstein is professor of physiology at the Center for Integrative Studies at Michigan State University in East Lansing.  He was a recipient of the MacArthur Prize (“genius”) Fellowship and wrote Discovering:  Inventing and Solving Problems at the Frontiers of Scientific Knowledge (Harvard University Press, Cambridge, 1989).  He is also a research management consultant.

How do you organize a laboratory to do the kind of work that will lead to significant discoveries?  How do you organize a lab to make the kind of basic--or exploratory--research that can only occur when there's freedom to explore unknown territory?

The keys to success are to enter the R&D process at the most advantageous point; to manage circumstances, not people or resources; and to organize the laboratory instead of planning its activities. 

As chemist Irving Langmuir wrote, “You can’t plan discoveries.  But you can plan work that will lead to discoveries.  You can organize a laboratory so as to increase the probabilities that useful things will happen there.  And, in so doing, keep the flexibility, keep the freedom....  We know from our own experience that in true freedom we can do things that could never be done through planning.” 

Few industrial laboratories are organized for exploratory research.  Most of them find breakthroughs at academic labs, then develop them to a marketable state.

Unfortunately, as academic budgets tighten, more and more academic labs are turning from basic research toward more fundable, applied problems.  Thus, the river of truly novel insights could dry up in every field of science and engineering, even though industrial and national competitiveness both require new insights.

Insights into basic processes can provide the next generation of key patents and intellectual property.  An old example is Selman Wachsman’s work on the ecology of soil microorganisms, which led to a general method for discovering new kinds of antibiotics (and a Nobel Prize).  A more recent example is Bernard Rosenberg’s studies of bacterial cell division, which unexpectedly led to the finding of cis-platin as an effective cancer drug.  Fostering exploratory research may thus become the most crucial element of a successful R&D program.

Of course, there's no point to fostering basic research unless you can do it right.  Otherwise, it's just a waste of your of time and money.  Here are two suggestions for planning a work environment and schedule that will lead to more discoveries.

Beating Around the Bush

You need good input to decide what exploratory research to pursue.  It should have potential to deliver value to the company, and researchers who do the actual work should believe that there’s at least a fair chance that value will be taken advantage of.

An effective way to decide on an exploratory program is to convene a group for three hours once a week.  Plan the meeting over lunch or as a late afternoon pizza-and-beer confab.  Food lubricates social interaction, creating a relaxed, congenial atmosphere, and also serves as an incentive for members to continue participating in a process that sometimes will seem aimless and unrewarding. 

Exploratory research is essentially stochastic (in the sense of having many variables).  Thus a good exploratory target will have many variables and will have ample opportunity for surprises.  In other words, it's good to know the direction to aim your musket, just so long as the field has enough game that you will be relatively sure to flush out something unexpected.

This is the point of exploring: to find something that no-one knew was there.  And then to determine its potential value.

One of the best questions for identifying targets is this:  “What are the most exciting breakthroughs in my field these days?  And where won't these breakthroughs work?”  Every technique or breakthrough has its limitations.  Most laboratories are so focused on solving the problems that a recent breakthrough can solve, that they don’t see the problems that they still cannot solve.  By looking at the limitations of cutting-edge research, you will define the problems that require the next generation of breakthroughs.

Not to put too competitive a point on it, asking these questions will put you working on tomorrow's problems, while other people are still exploring today's solutions.  Indeed, if you define these problems precisely enough, they will often suggest the criteria that must be met to create the next breakthrough, which is more than half the job.

Another strategy for initiating exploratory research is to focus on the anomalous phenomena in your field.  The things that you can’t explain, but which are easily observed and reproduced, are almost always sources of innovations.  The Geiger counter, which was developed to find the cause of spurious radiation, is an example.

The criteria for evaluating exploratory research are simple:  The more important an idea is, the simpler should be its conception; the wider its implications, the easier it should be to demonstrate, the less it should cost to do so, and the less time it should take to perform a qualitative demonstration of feasibility.   In other words:  Anything that can be done easily, simply, and right away, should have priority over everything else when doing exploratory research. 

For example, given a choice between developing a chemical synthesis (or a biological assay, if you prefer) that is time-consuming, difficult, and instrument-intensive—but likely to succeed—and a “quick-and-dirty,” low-yield synthesis (or qualitative assay) that will take an hour and a few test tubes and pipettes, and is so revolutionary it is unlikely to work (“but wouldn’t it be great if it did!”), go for simplicity.  Doing what you already know how to do opens no new vistas.  You can try dozens of simple short cuts and “fail,” and still come out ahead if even one exploration pays off.  This is particularly true of projects that would be too difficult and expensive (or too risky) to undertake unless a short cut is found.

You have to balance the risk of failure and the payoff for potential success.  In most cases, the amount of excitement generated by an idea will reflect these criteria and suffice to determine what gets done.

Who Qualifies

Who should be in your exploratory group?  I'd choose confident people with ideas; people who aren’t bound by authority or convention; who can work with people, even if they disagree; who are vocal and can give and take constructive criticism; and who have a diversity of technical backgrounds, both personally and as a group.  People unhappy with routine work, dissatisfied with their current opportunities, and who seem “difficult” to colleagues, are often the best bets.

In short, they must be people who can get things done.  As Herbert Dow, founder of Dow Chemical Company, once said, “I can find a hundred men who will tell me an idea won’t work; what I want are men who will make it work.” 

Now that you've followed all these instructions, it's your job as a manager to motivate your group.  Give the group a clear sense of its mission and why you consider this mission vital to the company's future.  This vision will give the group cohesion and drive; without it, you'll have confusion, dissent and dissatisfaction. 

Resources

Having devoted your group time to imagining a breakthrough, you must then back it.  Be sure that the group has the resources to test its ideas and develop those that work.  If you claim to value one thing and reward another, you’ll end up demoralizing and confusing your group.

Schedule time for exploratory research.  Many companies “assure” their researchers that, say, 10 percent of their time will be free to explore whatever they want, but in reality, every moment (and more) is filled by directors who demand this or request that (I hardly need point out that most of this stuff was needed yesterday--and the rest, the day before).  If you want exploratory research, you must schedule time for it--and make that time inviolate.

Realize from the outset that establishing an exploratory research group involves a huge commitment, and that you, as the leader, must be willing and able to champion whatever your group invents.  You must be prepared to take it through all the hurdles of the research and development process.  As a new idea, it will definitely attract detractors.  Be sure that invalid opinions don’t derail the project.  Test your ideas.  Don’t argue about them.  And if it isn’t easily testable, forget it, and try something that is.

Be equally ready to alter or cancel any project you begin.  The object of exploratory research is to try many things in order to find the one or two that are most promising.  If your exploratory group is functioning well, you should have several, perhaps even a dozen, possible projects under consideration at all times.  Natural selection will leave the strongest contenders.

Finally, reward participation in the exploratory process for its own sake.  The only failure is not to try new things.  Every crazy idea and every crackpot experiment, whether it works or not, is a step towards something new, and every novelty is a potential breakthrough.