Book by Donald W. Braben on scientific progress.
In the 1970s, the nature and pace of scientific discovery began to stagnate due to a combination of peer review, mandated justification of spending, and the push for short-term miracles. In Scientific Freedom, first published in 2008, Donald W. Braben presents a framework to find and support transformative scientific innovation.
Transformative research: research that sets out to radically change the way we think about an important subject
Critiques on current institutions for science
- Research proposals are not treated as if they were completed works, and the so-called best, as selected by peer review, determine the search that gets done. This inhibits the scope of scientific progress
- The limit is what you imagine it to do — this presumes the person doing the selecting has the best overall grasp as to what is worthwhile to presume. Often this is wrong — these researchers are the top of their field. Trust them to pick for themselves what is worthwhile to work on.
- Nature does not respect consensus. We cannot expect to actually make progress simply because we have agreed among ourselves that progress lies in a particular direction. Unless, of course, that direction is a simple extrapolation from what has gone before, but such objectives usually serve only to consolidate — unless researchers are free to follow interesting observations wherever they might lead.
- Committees can rarely, if ever, be creative. The fact that the best scientists might be involved is irrelevant. It can, of course, provide a defense against criticism as a committee’s membership can cloak its conclusions with respectability, but the collective responses of any group, however distinguished they may be as individuals, are usually uninspiring and based on compromise
- On March 3, 2007 The Economist published a well-documented briefing on the shift from research to development, particularly in the big companies. Industrialists presiding over R&D’s loss of the ampersand, as The Economist succinctly puts it, might therefore have a rude awakening when, as they have long been accustomed to doing, they turn to academia for new scientific insights. It may simply not be available in the quality or breadth they look for.
- Scientists back then could afford the investments of time and energy to make their work more accessible because they had much more security in those days. Those taking on these duties today would be penalized as they would have less time to spend on their endless searches for new funding. See also: research debt
Case study of the rise and fall of the UGC in the UK
In the early 20th century the UK government “acknowledge and assured the existence of a large area of free action in which the universities did as they thought right, according to the lights that were interior to them” (Daalder and Shils 1982, 439).
In 1919, it created the University Grants Committee, a body that at least until 1963 rigorously and jealously protected that autonomy. Importantly, it was an instrument of the Treasury. The Treasury, not being a spending department, would probably be content if the UGC kept to its spending limits and generally did not rock the boat. The UGC then could resist all attempts by most politicians and run-of-the-mill officialdom to interfere, or to closely examine academic expenditures or impose such strictures as “earmarked grants”. Thus, universities were free to deal with such labeled offerings as they thought fit. Furthermore, in those heady days funds came to them through rolling five-year grants — the quinquenniun — and each university was more or less free to spend their allocation “according to their own rights”
In 1963, however, the tanks of a harsher regime began to roll when responsibility for the UGC was transferred to the Department of Education and Science, the same body that had responsibility for the research councils. Zealous civil servants long denied access to university affairs now became increasingly free. The quinquennium was one of the first casualties, and in the early 1970s the university had to limit their planning horizons to a single year. In 1989, the government replaced the Olympian UGC with the University Funding Council, and in 1993 with the regional Funding Councils, one for each member of the UK. The bombardment continued with Research Assessment Exercises, Foresight, and Quality Assessment., and other bureaucratic impositions that thankfully for scientific enterprise have largely been confined to the UK.
Thus, university autonomy became severely compromised, and the climate of fear these bombardments induced was such that the universities offered barely a whimper of protest. Subsequently, the average number of Nobel Prizes per year in the sciences dropped from ~1.1/yr to ~0.38/yr (1 every 2.6 years). The primary agent of that autonomy — the UGC — was eliminated solely on misplaced idealogical grounds.
- “The state of mind which furnishes the driving power here resembles that of the devotee or the lover. The long-sustained effort is not inspired by any set plan or purpose. Its inspiration arises from a hunger of the soul.” (Albert Einstein, in his Preface to Max Planck’s book, Where is Science Going?)
- Scientific progress on a broad front results from the free play of free intellects, working on subjects of their own choice, in the manner dictated by their curiosity for exploration of the unknown (Vannevar Bush, 1945)
- Creativity is the essence of the human spirit, and flowers best when it’s unconstrained. If you try to control it for your own ends you must learn that you can get only what you ask for. The unexpected will not arise. Unfortunately your world leaders have now decided that wonder is inefficient because it cannot be controlled, quantified, or targeted.
- Researchers today are rarely free to be full-fledged scientists — that is, to survey Nature’s vast unexplored domains and to plan their forays accordingly to their personal inclinations. Instead, they are subject to financial and intellectual pressures to deliver the results that consensus deems would be the best value for money. Thus a generation of researchers has been encouraged to think parochially rather than globally, and not surprisingly, this has led to a death of major new discoveries
- In the consultancy field, the old adage was that successful consultant merely delivered the advice their customers wanted to hear. Do we really want that of our researchers? If we oblige them to provide precisely what our various proxies think that we need, according to timetable and balance sheet, they may have little energy left to do the other things.
- Managed creativity can, at best, produce only what its managers specify.
- Why do people doing independently guided research tend to attempt riskier ventures?
- Take skydivers for example. They, while acknowledging and even enjoying risks, do not expect that their next jump will be other than successful. They would not jump otherwise. As their own necks are on the line, they take every reasonable step to reduce, eliminate, or control every identifiable source of risk. As a result, they are confident that their jump will be exhilarating and enjoyable, and that they will land in one piece more or less where they thought they would.
- On the other hand, if it were decreed that the risks of skydiving had to be managed by those paying to enjoy the spectacle — that is, the spectators had to take full responsibility for anything that might happen — it is most unlikely that any jumps would take place. Responsibility shared is responsibility declined. In these circumstances, consensus opinion would opt for safety first as it usually does, and yet another expression of joie de vivre would vanish
- In any event, when funding agencies foster high-risk research, they promote the idea that science is intrinsically risky. It is not. It is difficult, but scientists are fully aware of that fact when they begin careers in research
On advancing knowledge
- Planck once said that science advances one funeral at a time: “A new scientific truth does not triumph by convincing its opponents and making them see the light, but rather because its opponents eventually die, and a new generation grows up that is familiar with it.” The role of young researchers — their exuberance, confidence, and tendency to ignore tradition — is as vitally important today as it always has been.
- Edward Denison’s study of American growth between 1929 and 1982 concluded that education per worker accounts for 30% of the increase in output per worker and the advance of knowledge accounts for 64%. Technology remains the dominant engine of growth with human capital investment in second.
- There are few defining names or living legends that might resonate in the imaginations of future commentators or inspire the young. we seem to have turned research into a faceless industry. Is it any wonder that young people are turning away from science?
On starting venture research initiatives
- In 1960s, IBM’s chairman, Thomas Watson Sr., began the Fellows program, in which he appointed Fellows for five years to be “dreamers, heretics, mavericks, gadflies, and geniuses”
- Their remit was simply to “shake up the system”. Of course, this Fellows program was extremely successful by any metric, even without explicitly trying to. Only some 165 scientists were appointed, but 5 of these won Nobel Prizes. General Electric and Bell Labs ran similarly distinguished programs
Case study of the BP Venture Research Program
This program was run by the author.
Written applications could be made on one page or preferably less, and if researchers needed a quicker reply, they could apply by telephone.
Any researchers who did not agree with our apparent rejection could return at any time with a rebuttal. Thus, however long (or short) our dialog might be, we tried to arrange that we always returned the ball to the applicant’s court. The onus would always be on them to respond the line we had taken
In effect, therefore, we were creating an environment in which researchers could select themselves.
The second part of the application sat them down near a whiteboard and talked about whatever science interested them. Almost invariably, the first thing we had to do was to discourage them from describing the possible benefits that might flow from their proposed work (applications, technology, etc.). In this, they merely seemed to be following normal practice by telling us what they thought we as a funding agency wanted to hear. The level of possible funding was another of their priorities. Our response was to ask them to assume that we had an infinite amount of money and could offer freedom to match! with these and other extraneous issues so beloved of conventional funding agencies out of the way, we could finally ask them to tell us what they would like to do that they were not doing now.
The final step was to satisfy ourselves that the researchers were capable of doing what they set out to do. This is not the same as peer review, we had effectively made up our minds, but wanted to be reasonably sure that we had not missed anything.
One of us would then visit their home environment “to kick the tires”. They would show us what they were doing and something of what was going on elsewhere in their department. Almost invariably, the fields would be new to us, but we found that it is remarkably easy to judge levels of competence from the fluency with which presentations are made, or questions answered (or avoided). As we would often tour their labs, it was interesting to note other scientists’ response to what had been proposed and the degrees of respect (or otherwise!) in which the applicants were held.
We also arranged annual two-day meetings at our headquarters in London to which all Venture Researchers were invited. It took a few years to work out a viable format for these meetings, covering the entire spectrum of research as we did. we knew that we had got it about right when the attendance, which was not compulsory, of the more than 100 participating scientists reached close to 100%. indeed, many researchers told us that despite the plethora of conferences nowadays, ours was a “must go”
One of their attractions was that they were a festival of science — specific disciplines were rarely mentioned, and we hope that Pasteur would have been at home
Out of the 26 groups that were running at the initiative’s close in 1990, perhaps 14 made transformative discoveries: that is, they did radically change the way we think, and several succeeded in achieving important scientific objectives that their peers had thought were impossible or irrelevant.