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The ivory tower from
The Neverending Story |
Science has a problem. The present organization of academia discourages research that has tangible outcomes, and this wastes a lot of money. Of course scientific research is not exclusively pursued in academia, but much of basic research is. And if basic research doesn’t move forward, science by large risks getting stuck.
At the root of the problem is academia’s flawed reward structure. The essence of the scientific method is to test hypotheses by experiment and then keep, revise, or discard the hypotheses. However, using the scientific method is suboptimal for a scientist’s career if they are rewarded for research papers that are cited by as many of their peers as possible.
To the end of producing popular papers, the best tactic is to work on what already is popular, and to write papers that allow others to quickly produce further papers on the same topic. This means it is much preferable to work on hypotheses that are vague or difficult to falsify, and stick to topics that stay inside academia. The ideal situation is an eternal debate with no outcome other than piles of papers.
You see this problem in many areas of science. It’s origin of the reproducibility crisis in psychology and the life sciences. It’s the reason why bad scientific practices – like p-value hacking – prevail even though they are known to be bad: Because they are the tactics that keep researchers in the job.
It’s also why in the foundations of physics so many useless papers are written, thousands of guesses about what goes on in the early universe or at energies we can’t test, pointless speculations about an infinitude of fictional universes. It’s why theories that are mathematically “fruitful,” like string theory, thrive while approaches that dare introduce unfamiliar math starve to death (adding vectors to spinors, anyone?). And it is why physicists love “solving” the black hole information loss problem: because there’s no risk any of these “solutions” will ever get tested.
If you believe this is good scientific practice, you would have to find evidence that the possibility to write many papers about an idea is correlated with this idea’s potential to describe observation. Needless to say, there isn’t any such evidence.
What we witness here is a failure of science to self-correct.
It’s a serious problem.
I know it’s obvious. I am by no means the first to point out that academia is infected with perverse incentives.
Books have been written about it.
Nature and
Times Higher Education seem to publish a comment about this nonsense every other week. Sometimes this makes me hopeful that we’ll eventually be able to fix the problem. Because it’s in everybody’s face. And it’s eroding trust in science.
At this point I can’t even blame the public for mistrusting scientists. Because I mistrust them too.
Since it’s so obvious, you would think that funding bodies take measures to limit the waste of money. Yes, sometimes I hope that capitalism will come and rescue us! But then I go and read things like that Chinese scientists are paid bonuses for publishing in high impact journals. Seriously. And what are the consequences?
As the MIT technology review relays:
“That has begun to have an impact on the behavior of some scientists. Wei and co report that plagiarism, academic dishonesty, ghost-written papers, and fake peer-review scandals are on the increase in China, as is the number of mistakes. “The number of paper corrections authored by Chinese scholars increased from 2 in 1996 to 1,234 in 2016, a historic high,” they say.”
If you think that’s some nonsense the Chinese are up to, look at what goes on in Hungary. They now have exclusive grants for top-cited scientists. According to
a recent report in Nature:
“The programme is modelled on European Research Council grants, but with a twist: only those who have published a paper in the past five years that counted among the top 10% most-cited papers in their discipline are eligible to apply.”
What would you do to get such a grant?
To begin with, you would sure as hell not work on any topic that is not already pursued by a large number of your colleagues, because you need a large body of people able to cite your work to begin with.
You would also not bother criticize anything that happens in your chosen research area, because criticism would only serve to decrease the topic’s popularity, hence working against your own interests.
Instead, you would strive to produce a template for research work that can easily and quickly be reproduced with small modifications by everyone in the field.
What you get with such grants, then, is more of the same. Incremental research, generated with a minimum of effort, with results that meander around the just barely scientifically viable.
Clearly, Hungary and China introduce such measures to excel in national comparisons. They don’t only hope for international recognition, they also want to recruit top researchers hoping that, eventually, industry will follow. Because in the end what matters is the Gross Domestic Product.
Surely in some areas of research – those which are closely tied to technological applications – this works. Doing more of what successful people are doing isn’t generally a bad idea. But it’s not an efficient method to discover useful new knowledge.
That this is not a problem exclusive to basic research became clear to me when I read
an article by Daniel Sarewitz in The New Atlantis. Sarewitz tells the story of Fran Visco, lawyer, breast cancer survivor, and founder of the National Breast Cancer Coalition:
“Ultimately, “all the money that was thrown at breast cancer created more problems than success,” Visco says. What seemed to drive many of the scientists was the desire to “get above the fold on the front page of the New York Times,” not to figure out how to end breast cancer. It seemed to her that creativity was being stifled as researchers displayed “a lemming effect,” chasing abundant research dollars as they rushed from one hot but ultimately fruitless topic to another. “We got tired of seeing so many people build their careers around one gene or one protein,” she says.”
So, no, lemmings chasing after fruitless topics are not a problem only in basic research. Also, the above mentioned overproduction of useless models is by no means specific to high energy physics:
“Scientists cite one another’s papers because any given research finding needs to be justified and interpreted in terms of other research being done in related areas — one of those “underlying protective mechanisms of science.” But what if much of the science getting cited is, itself, of poor quality?
Consider, for example, a 2012 report in Science showing that an Alzheimer’s drug called bexarotene would reduce beta-amyloid plaque in mouse brains. Efforts to reproduce that finding have since failed, as Science reported in February 2016. But in the meantime, the paper has been cited in about 500 other papers, many of which may have been cited multiple times in turn. In this way, poor-quality research metastasizes through the published scientific literature, and distinguishing knowledge that is reliable from knowledge that is unreliable or false or simply meaningless becomes impossible.”
Sarewitz concludes that academic science has become “an onanistic enterprise.” His solution? Don’t let scientists decide for themselves what research is interesting, but force them to solve problems defined by others:
“In the future, the most valuable science institutions […] will link research agendas to the quest for improved solutions — often technological ones — rather than to understanding for its own sake. The science they produce will be of higher quality, because it will have to be.”
As one of the academics who believe that understanding how nature works is valuable for its own sake, I think the cure that Sarewitz proposes is worse than the disease. But if Sarewitz makes one thing clear in his article, it’s that if we in academia don’t fix our problems soon, someone else will. And I don’t think we’ll like it.
