Looking up

Scientific research fields evolve in time depending on their own progress, and contemporary historical, political and technological contexts. In this post, I would like to build on the inception post of this blog and try to put in words my increasingly uneasy personal feelings about the evolution of astrophysics over the last decades, which are among the reasons (although by far not the only ones) underlying my intention to transition to a different field.

Before we start, let me make it clear that the criticism I make below is first and foremost systemic. Most colleagues, myself included, are at their individual level just trying to make the best lemonade out of the bitter lemons that perverse short-termist systemic incentives, vertical management and the inertia of “big science” policies provide us with.

Let me start with a bit of (approximative) history. Astrophysics in the twentieth-century started as a very theory- and physics-oriented field buoyed by the contemporary revolutions of general relativity and quantum mechanics: relativistic gravitation, spectroscopy, compact objects and black holes, nucleosynthesis in stars, the big bang theory and theory of the cosmic microwave background, radiation transfer, plasma & fluid dynamics in stellar, galactic and high-energy astrophysics, just to name a few, all of these were born and developed between the 1920s and the 1970s, largely in the creative minds of theoreticians…. After the second world war, there was a particular golden age in the 50s-70s during which theoretical astrophysics and observational astrophysics went hand in hand and made incredible progress, largely fueled – let’s face it – by the cold war competition between the US and the soviets, and the unhealthy but highly scientifically fertile interactions between military and astro research. If you want to read in detail about the history of astrophysics and cosmology in the twentieth century, I highly recommend Malcolm Longhair’s “The cosmic century”.

I was fortunate to meet a few of the great theoreticians of this period (Eugene Parker, Russell Kulsrud, Donald Lynden-Bell to name just a few), to study in detail the work of many others, from Chandrasekhar to Spitzer to Zel’dovich, and to interact with some of their former students and colleagues in these times. What alway struck me with these people, and greatly influenced my own (much more modest) trajectory, is that they were or are first and foremost theoretical physicists, who also happened to be interested in what our large and beautiful Universe has on display physics-wise (although we should again not forget that many great scientists in this period owed their positions to making better nuclear bombs, or to provide their institutions with a fancy civilian dressing to new physics developments in the military context). Their calculations, essentially done on pen and paper, have endured the test of time. They have given their name to what are now our classic textbooks, theories, key equations and formulae.

In the same period, following the development of electromagnetic communication tech during the war and, again, the development of the bomb, but also rockets in the conquest of space, observational and experimental facilities also expanded a lot. In particular, radioastronomy, space agencies and astronomical observation from space all became a big thing in that period. Then came the 80s and supercomputers, which allowed theoreticians to run the first truly physically informative numerical simulations of astrophysical phenomena (in my own direct area of expertise, astrophysical fluid dynamics, the first major three-dimensional simulation of magnetohydrodynamics happened in 1981). With that, the face of theoretical astrophysics research changed, as pen and paper approaches started to show some limitations, and simulations opened new hopes and horizons to study complex physical processes. At about the same time, observational astronomy started its own analog to digital tech revolution: recently invented charge-coupled devices made their way to telescopes and space probes in the next decades, opening completely new horizons for astrophysics done from space in particular. By the mid 90s, film technology was essentially obsolete in professional astronomy.

Since then, computer chips and electronic sensors have kept becoming cheaper, more powerful and smaller — the tech in a smartphone today is more powerful than that in the best observational astronomy and computational facilities in the world in the 1980s, CPU and imaging-wise! The digital age has transformed the way we do astronomy, turning fields like cosmology into a precision observational science, enabling the detection of faint exoplanets, making it possible to measure the positions and velocities of billions of stars in our Galaxy from space with incredible accuracy — all leading to major leaps in knowledge for humanity. The recent prowess of the detection of gravitational waves, and the JWST, are just the latest, and most accomplished installments of this technological saga. On the theory side, high-performance computing has also been a game-changer, and has become indispensable tech too. We now perform huge simulations run on hundreds of thousands of computing cores simultaneously to try to understand, albeit at a much more phenomenological than quantitative mathematical level than before, highly complex dynamical phenomena, such as large-scale structure formation, the evolution of the Universe on its largest scales, galaxy formation, black hole accretion, planet formation, the dance of inspiraling compact objects, and the structure and dynamics of stars.

This diptych of high-resolution digital observations, and high-resolution computer simulations has been a blessing for our community, but it has also in my view gradually morphed into a cornucopia for increasingly meaningless short-term black-box research projects, supported by the (rarely explicited, yet very pregnant in the community) belief and assessment that technology and software pipelines will solve it all for us. Better, deeper, more precise observations, more “realistic”, higher-resolution simulations, machine-learning techniques taking over standard data analysis techniques to mine huge datasets, CPU-intensive statistical bayesian analyses frameworks replacing basic statistical analyses tools, all providing in research proposals a fancy dressing and promises of endless progress and sophistication — and for many too, given the systemic incentives in place, promises of funding and employment. We need better observations to inform better simulations, which in turn will justify new observations with even higher-resolution, which will then motivate new, bigger simulations… Big-data, big-science reasoning of this kind is now exploited almost mindlessly as an inexhaustible source of justification for funding incremental, hyperspecialized research…and also as an easy circular justification to our very own existence as scientists, and that of our field.

Something important is largely missing in this short-termist, technophile strategic vision: a deep, foundational physics understanding, and more generally an embrace of the field itself as a broad human scientific playground for ingenuous, long-term, non-oriented mathematical physics research. Long gone are the days when fundamental physics and applied maths were at the core of our efforts to understand the Universe, and when many scientists would be equally at ease working in problems on stellar, galactic or extragalactic. physics. Now that we know — or think we know! — the few remaining big questions, have some seemingly relevant equations, models and basic theory (that of the last century), it would seem that we can just, like little minions, organize in big teams and consortia, and go all in on tech and data crunching to make progress in our super-narrow subfields. This, at least, is how the system is increasingly pushing us to work.

Don’t get me wrong: there are definitely some areas of astronomy and science where it is obvious that technology (either observational or computational), sophisticated stats, and big data can and will be a game changer, and where organizing in big teams is the only viable option to make significant progress. But there are also many traditional areas where I would argue astro has lost its playful theoretical physics craftmanship roots, and is devolving into a cold, soulless tech-driven activity.

Of course, it is also possible that I am one of those missing the point: that astrophysics has indeed sufficiently matured scientifically and theoretically for most of the challenges left ahead to be of technological, rather than scientific nature. I doubt that, but maybe. Maybe too, it has always been like that and I am deluded about the past. I doubt that too, based on my twenty years of experience and human and scientific encounters during that time. Maybe too I am deluded about why astrophysics research still exists, and too much of an utopian. It is possible that the essential reasons the field still gathers political support (and funding) are not scientific, or the enlightment of humanity, but rather as a (quite) popular public entertainement and PR machine (judging by the number of press releases in the field), a prestigious geopolitical intellectual competition between wealthy countries (or groups of nations), and an instrument to justify and subsidize technology R&D in the industrial sector, most importantly, of course, the mighty space industry and military. Viewed from this perspective, some of the forementioned evolutions would at least make sense.

Whatever the reasons for this evolution, and whether or not my own convictions about the nature of astrophysics research still make sense in today’s world, I certainly do not recognize my own original ingenuous aspirations anymore in the current state of affairs. What I find most depressing about all this, in the end, is not just that fundamental physics and theory in astro has become subservient and secondary to the rest, but that this field, of all fields, now appears to be the mirror of how our wealthy societies “work”. It increasingly feels like we are like headless chickens hypnotized by the promises of tech, big data, big science, running towards a future that has no particular sense, except for producing and growing ever more: “to infinity and beyond !”. But for what exactly ? In the astro world these days, I feel waterboarded daily in a mash-up of technosolutionism, hype and mindless “olympic” competition between people, projects and institutions, that is many of the same evils that are already doing so much harm to the rest of humanity and our planet.

Witnessing my own idealistic childhood passion being increasingly contaminated by futility and superficiality, I feel nauseous and sad realizing that this field which, of all scientific fields, should have been at the core of much needed societal reflections on the long-term future of humanity, is shrinking into a soulless astro-industrial complex. And, having reached out to quite a few trusted colleagues over the last year to explain my intentions to change research fields, I also now know I am far from the only astrophysicist or astronomer with a generalistic scientific theoretical background who has to live with this kind of feelings and disillusions. As I discussed in a recent post, a recent French scientific prospective report has also recently triggered a broader alarm about the increasing loss of sense for many of us regarding our high-environmental impact scientific activities in Universe sciences in the face of the climate and environmental emergency. Overall, I would therefore not be surprised at all to see many more life boats launched out of the astrophysics liner in the upcoming decade.

A final addendum to this long post: if, after reading all of this, you think I am exaggerating the evanescence of non-oriented, foundational theoretical research within astro, or that I am just taking an easy pretentious stance as an old-school theoretician, you don’t have to take my word for it! I encourage you to read the latest (2020) US astro decadal survey , a reference prospective exercise done by the US astro community every ten years, which contains things such as

• Bolster theory underpinnings. Theoretical investigations, crucial as both a mechanism for driving new discoveries and a framework for interpreting essentially all signals received from space, are, like grants at NSF, lacking crucial funding at a level that can sustain the necessary projects.
• When addressing the question of balance, the Panel and the steering committee identified a few critical areas where evolution in the funding balances within NSF and NASA has drifted into unhealthy territory […] Previously identified under-investments in laboratory astrophysics and theory remain as critical needs.
• 4.2.2 The Importance of a Healthy Theory Foundation
  Theory is crucial in astrophysics, as both a mechanism for driving new discoveries and a framework for interpreting essentially all signals received from space. The focus of modern theoretical research has expanded from traditional pencil-and-paper calculations to complex computer simulations and sophisticated statistical analyses […]
  Low funding rates at both NASA and NSF have affected the ability to carry out theoretical investigations.
  When the longer [proposal schedule] cadence is coupled with low success rates, scientists have little realistic expectation that their research will be funded while it is most relevant, if it is ever to be funded.
  A strong foundation of theoretical research remains critical for interpreting astrophysical observations and planning new facilities, but past decadal survey recommendations for supporting theory have not been implemented.