Management and creativity in research
What is good research management? How does current management practice measure up? Ive encountered some research managers I admired and some I did not. In order to focus on philosophy rather than personalities, I will only mention the names of people I admired.
Managers are conservative by nature, and research managers are no different. In a large company, just like in the Army, power flows only from the top down, and the bigger the company the more this is true. The most important thing for all tiers of middle management is not to be perceived as having screwed up. So if you give the green light to a project that later fails, you might be remembered forever as the guy whose bad judgment cost a bundle. After that you can forget about promotions.
On the other hand, prematurely killing a project that would have been successful had it continued is a safe thing to do because no one above you in the chain of command will ever notice what doesnt exist. Your subordinates will know, but they have no power. They can, of course, in theory go over your head to point out your misjudgment, since all top echelon people have an open door. But just let them try, and see what happens to them. So when in doubt its always safer to kill or reassign a project than to go out on a limb promoting it. I dont think there is any researcher who hasnt wept more than once over the smothering of his or her brainchild.
The prostate drug Proscar (finasteride) is the culmination of an idea generated by Glen Arth at Merck many decades ago and carried on by Gary Rasmussen after Glens death. Glen took punishment for a long time because he resisted efforts to terminate this line of research; Proscar owes its existence not to enlightened management (as Ive read in the newspaper), but rather to Glens tenacity and courage. Ive heard a similar story about the blood pressure medication Capoten (captopril), although I was not at Squibb to witness it.
In the early 1960s, a new, highly efficient process for L-Aldomet was invented to replace the then-current expensive and cumbersome one. This was important because sales were rising, and we at Merck soon would be unable to meet the demand. To my astonishment, the project planners nixed it, saying that the savings would never repay the cost of installation. Fortunately, the chief of research at that time was Max Tishler, a great leader who was not easily bamboozled. The new process was installed, and Aldomet turned out to be a tremendous moneymaker as Mercks vanguard drug as late as 1987. Had the project planners had their way, Merck would be a great deal poorer today, and no one but we chemists would have known what was lost.
Not only is there hidden prejudice against real innovation, but also against innovators. Creative people are scarce, and very unlike managers in temperament and behavior. Sometimes these differences are tolerated and even cherishedwitness Giulio Vita at Bristol-Myers, an exceptional research directorbut sometimes not. I was a friend of a very well known chemist who had several highly important and lucrative inventions to his credit. Nevertheless, he was treated by his company not as a creative genius, which he was, but rather as an oddball, which he also was. At one point his peculiar attitudes and habits prompted his company to bring in a psychiatrist to find out why he couldnt be like the rest of us.
Companies talk endlessly about how they encourage creativity and innovative research. At one outfit, we constantly heard about vision, and at another, more mystically, it was the vision. But, of course, vision actually clashes head-on with the conservative managerial mindset. Therefore, resources are usually allocated to areas that appear sure to be productive, not riskyand therefore not too novel, because novelty in itself means risk. The safest way to select areas to work in is to see what everybody else is doing. If all the other companies are doing metalloprotease Q, it must really be important, so we had better do it, too.
The outcome of this psychology is that the popular research areas are overcrowded, and the risky ones are hardly touched. Of course the flaw in playing it safe this way is that you are at great risk of not being the first to discover the blockbuster drug, and research costs are so high that anything less than a blockbuster is a failure. As a result, according to a leading accounting firms recent analysis of the drug business, many of todays companies will inevitably fall by the wayside or disappear through merger. More and more, the slack in innovation is being taken up by small startups with the courage to go off the beaten path. If their gamble pays off, they are bought up by larger firms, which thereby buy innovation instead of creating it themselves.
I might add that many of my academic friends tell me that their situation has become similar to industrial chemists; they are less and less free to choose what they do, but instead are channeled into research areas that are generally deemed hot, whether they like it or not. They depend on funds from granting agencies that favor certain popular areas, and though they might prefer to follow a different path, they had better change to a more fashionable one if they want to stay in research.
The combichem bandwagon
Over an astonishingly small span of time, every middle-size and large pharmaceutical company has set up a combichem group, which then requires a large high-throughput screening group, which in turn must have access to enormous libraries of supposedly random compounds. Everyone is afraid not to follow this trend despite the disadvantages: high cost, lack of real diversity in the libraries, and excessive numbers of hits that consume tremendous labor to investigate.
The philosophy is not unlike trying to recreate Hamlet by setting an immense number of monkeys to typing for an immense period of time. The drawbacks are the same: high cost and the impossibilityeven if Hamlet is thereof reading all the gibberish to find it. It takes a large group of chemists and biologists several years to explore properly all the ramifications of a single hit.
Furthermore, hits from random screening have, at least initially, an unknown mechanism of action, so alterations to improve activity must be made blindly. In contrast, hits found by rational design can also be modified rationally since you already know what the molecule is doing. Finally, screens amenable to high throughput must be simplified to the point where their relationship to the desired therapeutic effect becomes more and more distant. Thus, the likelihood that a compound discovered in this way will really be effective in humans is increasingly problematic. I think that combichem does have a valuable role to play, but in lead development rather than lead discovery.
Who should initiate projects?
When I broke into chemical research in 1956, ideas arose from both the chemical and biological sides, but nowadays its very difficult to start a chemistry-driven project. Yet there are still many ways to elicit a biological response in humans, and I think that to reject out of hand all but a narrow spectrum of new proposals will result in throwing away many fruitful possibilities. An outstanding recent example of chemistry-driven research is Edward C. Taylors cancer program at Princeton, supported by Eli Lilly and Co. But I wonder whether they would have supported the same program if it had been conceived by one of their own chemists.
During my last year at Bristol-Myers Squibb, there was a great deal of agitation on the part of management to find out why productivity had been steadily declining. It was obvious to all of us doing the research that micromanagement was the problem. Despite numerous endless meetings led by an outside troubleshooting firm, they got nowhere because no one had the nervedefined as money in the bankto tell it like it was. Finally I pointed out (after first checking my own bankbook) that if we wanted more new compounds in the pipeline, we needed more new programs, and the best way to get them was to let people invent them.
I suggested that if everyone were encouraged, but not required, to create new side projects on, say, 15% of their time no questions asked and no recriminations for failures wed get 85 instead of 100 new compounds from each person who chose to participatea small sacrifice in return for which we would get a variety of ideas and compounds that could give rise to entirely new projects. The response to this proposal was that it was unacceptable because without guidancetheirseveryone would waste time following foolish tangents. I replied that we had a talented, creative staff who could think for themselves, and management had to trust them not to waste their time. This was, of course, anathema to the micromanagers.
I cannot refrain from making a few comments on the merger between Pfizer and Warner-Lambert, and all other large mergers. I consider them bad things because they create entities that are too large, giving rise to even more layers of middle management than before, and enlarging still further the gap between the decision-makers at the top and the creative scientists at the bottom.
When Bristol-Myers and Squibb merged in 1989, they recognized the problem of bigness just as I have described it, declaring that they were going to create a flat organization, that is, one with fewer layers between top and bottom in research. This didnt work because it was impossible for just a few people to digest the enormous amount of new information being generated, and spreading this burden inevitably required an increase in the complexity of the reporting structure.
I believe that there is an optimum size to a research organization. Too small is obviously inefficient, but too large is also suboptimal because it rests on the limited capabilities of human beings.
The good ones
In 1958, Karl Pfister, head of process research at Merck, sent me a Russian abstract that led us to a new synthesis of pyridoxine. We published a communication with Karl as one of the authors, but later when I included him on the full paper, he asked to have his name taken off. I was worried that he thought it was a poor paper, but he said no. His reason was that he got his kicks doing what he did, and we were entitled to our kicks doing what we enjoyed, and he had no need to horn in.
In 1967, I began to take an interest in chemical reaction mechanisms, which had nothing to do with the companys research program. My boss and his boss were hostile because, even though I did this entirely on my own time, they felt that I ought to channel my scientific energy exclusively into company matters. They threatened me with retribution if I did not desist, but I went ahead anyway and submitted my first theoretical manuscript for clearance to publish. A few days later, I came back from lunch to find Max Tishlermy bosss bosss bosssitting at my desk with a glum look and my paper clutched in his hand. He asked me if I had written it, and I said yes, while through my terrified mind flashed college loan bills, a mortgage, and an empty bank account. Then to my surprise and joy, he burst into a big smile and expressed his pleasure that someone in his organization had interests beyond just the job requirements. From that day on, he missed no opportunity to give me a smile, a wave, or a handshake.
Karl and Max showed me that you can be a research director and still be a mensch.
Raymond A. Firestone (email@example.com) is retired from Boehringer-Ingelheim Corp., where he was a highly distinguished scientific fellow. He still consults for the company part-time. This article is based on a paper he gave at a special symposium at Chem Show, New York, in November 1999.