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Intellectual capital

David Strayhorn (Neurology, Washington University in Saint Louis)

Published in socio.philica.com

Observation
Just as an investor must decide how to invest money, so too must a researcher decide where to invest intellectual capital. The purpose of this observation is to consider the impact of two variables — potential scientific payoff, and chance of success — on this choice. It will be argued that the practice of diversification, which is understood by any investor to play an important role in the management of economic risk, is very difficult to utilize for the individual scientist in research, the result being a suboptimal distribution of intellectual ability for science as a whole.

The essential argument is that a scientist typically is able to pick only some small number N out of the set of all conceivable projects in which to invest intellectual capital. Consider the following simple model. Any given project will result in one of two outcomes: “success,” yielding a payoff $P_{n}$ with probability $p_{n}$; or “failure,” yielding no payoff at all.

The expectation value of the yield of any given project is $E^{n} = (p_{n})(P_{n})$, the overall expected payoff being $\sum_{n} E^{n}$. For an investor, the optimal portfolio is one that maximizes the overall expectation value while simultaneously minimizing risk. This is achieved, in theory, through a large number N of investments, picked from among those with the highest expectation value.

In science, however, N simply cannot be as large as one wants it to be. To decrease risk, therefore, a scientist must forego those high-risk, high-yield projects in favor of lower risk, lower yield projects. This results, of course, in lower expectation value. From the standpoint of building a career, this is rational. But from a global perspective, the intellectual capital of society as a whole is almost certainly NOT invested optimally.

References
See Against the Gods: the Remarkable Story of Risk by Peter L. Bernstein for a very interesting discussion of the development of the very concept of probability throughout history.

Peer-review ratings (from 5 reviews, where a score of 100 represents the ‘average’ level):
Originality = 195.83, importance = 220.83, overall quality = 195.65
This Observation was published on 11th October, 2006 at 09:39:33 and has been viewed 8825 times.

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1 Peer review [reviewer #7635] added 11th October, 2006 at 11:48:04

This observation has the great merit of saying something which is obvious, but only after it has been pointed out. Stated in the terms of the author, it is clear that a professional researcher is balancing two contradicting personal requirements: the material need to make a living and the personal need to do interesting, substantial science. For those researchers lucky enough to be in universities, it is possible, to some degree, to avoid the problem, by doing science which is cheap, and using the salary from teaching and administration to pay the bills. This is a limited solution to the problem, however, because much research is inherently expensive.

One possible solution might be a change in the funding model for science. At present, in many countries, funds are awarded on the basis of a proposal’, in effect a compendium of more or less wild promises. If these promises are not kept (cancer has not been cured, the secret of the universe has not been elucidated), a researcher can simply submit a similar proposal, saying, in effect, this time I’ll get it right’ and there is no incentive to do other than write up the paperwork properly and continue publishing small incremental changes to the field.

An alternative funding model would be to pay cash up front and see what the researcher does with it. Given, say, five years funding (even a modest amount), a researcher could do the science that they believe needs to be done and produce such output as is appropriate (papers, students, patents, whatever). An audit could be performed to look at these outputs—with no penalty for honest failure—and a decision made on whether to renew the funding for the next five years. A researcher starting their career would get a free grant to start off and would be auditted thereafter to maintain funding.

Originality: 6, Importance: 7, Overall quality: 6

2 Peer review [reviewer #187] added 11th October, 2006 at 17:13:24

This is a very interesting analysis. It is true that the system we work in strongly encourages conservatism and we do not progress as fast as we probably would in a situation of greater resources.

I would say that the model might benefit from another component: A given researcher’s N (the set of projects they choose to invest effort in) is not just contrained by the factors described here but also by that researcher’s track record: one simply does not have the option of carrying out work outside one’s own field, owing to the impossiblity of obtaining funding to do this and the fact one’s knowledge is constrained. This means N is selected from a rather smaller pool than “all conceivable projects”.

Originality: 6, Importance: 6, Overall quality: 6

3 Author comment added 14th October, 2006 at 08:30:58

Each of the two reviewers has raised the very important issue of how to measure cost C_n (a variable that was not included in my simple model, but certainly could have been) or payoff P_n. How should we model (in the words of the first reviewer) “the personal need to do interesting, substantial science?” Or the cost of coming up to speed on a project that is (in the words of the second reviewer) “outside one’s own field?” In some cases, the majority of C_n is time. And the greatest payoff P_n of a successful project in the scientific community is prestige in the eyes of peers — “publish or perish,” as the saying goes — or in extreme cases, in the eyes of the public. The next Einstein will be guaranteed fame, but (probably) not fortune; certainly not in proportion to the economic value of the contributed knowledge.

So the inherent difficulty is that some aspects of C_n, but I think especially P_n, cannot be converted into something that meets the qualifications of a genuine currency: something of value that can be easily transferred from one person to another. Can a researcher who has gained a lot of prestige reward his “investors” by distributing his prestige among them? Nope.

Imagine what would happen to our economy if we had to stop using currency; if all we had, say, was the barter system. Or maybe not even that. What effect would this have on the GNP? It would be absolutely destroyed, of course. I would be surprised if it were to keep one-tenth of its value. Or even one-one hundredth! Turn that around: if we could establish a “currency” for research (in those areas where it does not currently exist), how much increase would there be of the “scientific GNP”?

Is there any way to improve the current system of currency in science — the publish or perish system?

4 Peer review [reviewer #296] added 15th October, 2006 at 07:59:53

I agree with the previous reviewers. The author is expressing views held my many of us, in a way that I’ve not seen before. Much of the problem is clearly that time spent at work is very regimented, a lack of ‘thinking time’ for want of a better phrase, means that moving research on and widening it is almost discouraged. The article expresses the ideas of limited possibilities, almost a straight jacket, very well.

Much research is, clearly, very costly, but much is not it has to be said. It is a time constraint and the requirement to publish in particular journals that focusses the mind of the scientist much of the time. Perhaps a playng field that encourages risk of some kind should be encourged. Maybe Open access facilities like this one can help with expression of ideas, sharing and development of research ideas and progression. Lets hope so. A fascinating set of ideas that has us talking here. Thanks.

Originality: 6, Importance: 6, Overall quality: 6

5 Peer review [reviewer #2144] added 19th October, 2006 at 13:48:21

Perhaps we could increase the number of scientists, effectively increasing N? Another suggestion could be to reduce the teaching load of scientists, leaving them more time to focus on the high-yield projects, Philica is on the right track, as it encourages more “investments” by providing an avenue for article publishing.

However, I would note that many eminent scientists have spent many years doing low-risk, low-yield research, that maybe have trained and prepared them for the ground-breaking, high yield research.

For instance, Charles Darwin spent many years studying barnacles, while Newton spent much of his time investigating alchemy.

Originality: 4, Importance: 4, Overall quality: 4

6 Peer review [reviewer #71237] added 11th November, 2006 at 06:15:19

The topic is a very important one. Case studies of previous discoveries can provide some clues about factors that can increase the probability that an important discovery will be made. Several case studies in the biosciences are available via the Breakthroughs in Bioscience webpage of the Federation of American Societies for Experimental Biology (FASEB). For example, in the case study Helicobacter pylori and Ulcers: A Paradigm Revised, it’s clear that the creative insights of an independent investigator, chance, and persistence all played very important roles. According to the blurb for a forthcoming book by Morton Meters, Happy Accidents: Serendipity in Modern Medical Breakthroughs, “it takes intelligence, insight, and creativity to recognize a ‘Eureka! I found what I wasn’t look for!’ moment and know what to do next”. Perhaps one needs to focus attention on how to maximize the probability that a (very rare) “eureka moment” will be recognized?

Originality: 4, Importance: 7, Overall quality: 5

7 Additional peer comment [reviewer #71237] added 11th November, 2006 at 13:24:18

There’s a typo in my review. The author of “Happy Accidents: Serendipity in Modern Medical Breakthroughs” is Morton Meyers. Also, the set of case studies entitled “Breakthroughs in Bioscience” can be found at: http://opa.faseb.org/pages/Publications/breakthroughs.htm

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