I’m ripping off a blog post by Peter Coles–which was itself taken from a comment to a post on Sean Carroll’s blog–by pointing out some interesting articles by Avi Loeb that discuss cosmological conformism, cosmological conservatism, and rating the potential success of various research areas. I’ll briefly discuss Loeb’s articles in chronological order.
In this article, Loeb argues that young researchers ought to allocate time to innovative, high-risk, high-reward research areas, as well as to the more conservative mainstream research agendas. Loeb discusses the cultural barriers to this type of research. One of the obvious troubles is that:
Clearly, failure and waste of time are a common outcome of risky projects, just as the majority of venture capital investments lose money (but have the attractive feature of being more profitable than anything else if successful). The fear of losses is sure to keep most researchers away from risky projects, which will attract only those few who are willing to face the strong headwind. Risky projects are accompanied by loneliness. Even after an unrecognized truth is discovered, there is often persistent silence and lack of attention from the rest of the community for a while. This situation contrasts with the nurturing feedback that accompanies a project on a variation of an existing theme already accepted by a large community of colleagues who work on the same topic.
He then gives some examples of low-, medium, and high-risk research, and suggests that astrophysics postdocs should adopt a 50-30-20 distribution of research time to low-, medium-, and high-risk topics, respectively, as opposed to the usual 80-15-5 distribution. Although this article concerns theoretical astrophysics research, I suspect that most of this carries over directly to the rest of theoretical physics.
In the next article, Loeb proposes and discusses the idea of a website run by graduate students that uses publicly available data to assess “the future dividends of various research frontiers”. I quite like this idea in principle. One concern would be that such an assessment would not be any more objective than, say, university rankings, which are frequently criticised for giving seemingly arbitrary weightings to the various factors used in their evaluation metrics. In Loeb’s scheme, this problem is dealt with by using historical data to calculate the weightings that would correctly predict a research areas likelihood of success. Of course, in practice there are enough ill-defined concepts involved that this couldn’t be implemented without bias. As to whether or not this is nevertheless a useful enough idea to implement, I’m undecided.
This article, titled “How to Nurture Scientific Discoveries Despite Their Unpredictable Nature”, suggests that funding agencies should give more support to open research that has no programmatic agenda because the potential benefits from unexpected breakthroughs are so vast that they outweigh the high risk of failure. It’s persuasively written and I completely agree with the main idea: that it’s important to financially support risky innovation, as well as established physics. I’m too ignorant to know whether current practice underfunds research “without programmatic reins tied to specific goals”, but based on what I’ve read in books and on blogs, it’s probably the case. Here’s the final paragraph, mainly because he managed to incorporate a biblical reference:
Progress is not linear in time and sometimes it is even inversely proportional to the contemporaneous level of invested effort. This is because progress rests on lengthy preparatory work which lays the foundation for a potential discovery. Therefore, it is inappropriate to measure success based on the contemporaneous level of allocated resources. Lost resources (time and money) should never be a concern in a culture that is not tied to a specific programmatic agenda, because the long-term benefits from finding something different from what you were seeking could be at an elevated level, far more valuable than these lost resources. This echoes a quote from 1 Samuel (Chapter 9, 20), concerning the biblical story of Saul seeking his lost donkeys. The advice Saul received from Samuel, the person who crowned him as a king after their chance meeting, was simple: “As for the donkeys you lost three days ago, do not worry about them…”.
The most recent article, from May this year, encourages senior scientists to mentor young astrophysics researchers to be bold, creative “architects”, rather than conservative “engineers”. (This reminds me of Lee Smollin’s discussion of “seers” and “craftspeople”.) The opening paragraph sums this up nicely:
Too few theoretical astrophysicists are engaged in tasks that go beyond the refinement of details in a commonly accepted paradigm. It is far more straightforward today to work on these details than to review whether the paradigm itself is valid. While there is much work to be done in the analysis and interpretation of experimental data, the unfortunate by-product of the current state of affairs is that popular, mainstream paradigms within which data is interpreted are rarely challenged. Most cosmologists, for example, lay one brick of phenomenology at a time in support of the standard (inflation+Λ+Cold-Dark-Matter) cosmological model, resembling engineers that follow the blueprint of a global construction project, without pausing to question whether the architecture of the project makes sense when discrepancies between expectations and data are revealed.
The roots of this conformism are obvious:
The unfortunate reality of young astrophysicists having to spend their most productive years in lengthy postdoctoral positions without job security promotes conformism, as postdocs aim to improve their chance of getting a faculty job by supporting the prevailing paradigm of senior colleagues who serve on selection committees.
He goes on to argue why modern cosmology needs architects:
Some argue that architects were only needed in the early days of a field like cosmology when the fundamental building blocks of the standard model, e.g., the inflaton, dark matter and dark energy, were being discovered. As fields mature to a state where quantitative predictions can be refined by detailed numerical simulations, the architectural skills are no longer required for selecting a winning world model based on comparison to precise data. Ironically, the example of cosmology demonstrates just the opposite. On the one hand, we measured various constituents of our Universe to two significant digits and simulated them with accurate numerical codes. But at the same time, we do not have a fundamental understanding of the nature of the dark matter or dark energy nor of the inflaton. In searching for this missing knowledge, we need architects who could suggest to us what these constituents might be in light of existing data and which observational clues should be searched for. Without such clues, we will never be sure that inflation really took place or that dark matter and dark energy are real and not ghosts of our imagination due to a modified form of gravity.
In the original post by Sean Carroll that I mentioned at the start of this post, which is worth reading, Sean plays devil’s advocate to this idea. He ends with this sobering perspective:
Then again, you gotta eat. People need jobs and all that. I can’t possibly blame anyone who loves science and chooses to research ideas that are established and have a high probability of yielding productive results. The real responsibility shouldn’t be on young people to be bomb-throwers; it should be on the older generation, who need to be willing to occasionally take a bomb to the face, and even thank the bomb-thrower for making the effort. Who knows when an explosion might unearth some unexpected treasure?
Phew, it must be time for coffee.