When I asked an experimentalist who has been searching over three decades for weakly-interacting massive particles as the elusive dark matter and did not find them, “how long will you continue?”, he answered: “as long as I am funded.”
For me, this was not a satisfactory answer. We live for a short time and we better spend it wisely so that at the end of our life we would feel that we made a meaningful contribution to the world. Ruling out something that does not exist for an entire scientific career is not as rewarding as finding something new that actually exists.
This subject came up in a Q&A session that I had with a few tens of students in the Physics & Astronomy department at Tufts University after the in-person colloquium that I gave there yesterday. One of the students asked: “What would constitute a good strategy for choosing a research topic for a PhD?” My advice was to select a topic in which scientific knowledge evolves rapidly or has a potential to make progress soon. These characteristics flag a large unexplored territory, a “Road Not Taken” in the words of Robert Frost — where low-hanging fruit has not been picked up by predecessors.
The physicists engaged with quantum mechanics in its early phase a century ago, made fundamental discoveries. For example, in a 70 page PhD thesis written in 1924, Louis de Broglie made the fundamental discovery of the wave-particle duality in quantum physics and won the Nobel Prize for it in 1927.
It is highly unlikely that Louis de Broglie, Niels Bohr, Max Born, Werner Heisenberg, Wolfgang Pauli, Erwin Schrödinger and Paul Dirac were far more talented than the generations of physicists that followed their footsteps. But decades later, the remaining fruits of quantum knowledge were left high up on the tallest branches and difficult to reach.
The same is true with the history of particle accelerators. The cyclotron developed by E.O. Lawrence was first to produce, identify and investigate mesons in 1948, a study which led to major developments in our understanding of nuclear physics and the uncovering of the fundamental building blocks of quarks and gluons in quantum chromodynamics. Half a century later, the investment of ten billion dollars in the Large Hadron Collider was not as revolutionary and primarily confirmed the existence of the Higgs boson so far.
Some research areas remain unpopular until they are legitimized by a major experimental discovery. Examples include the search for exoplanets by radial velocity or transit techniques, which was suggested in a 2-page paper by Otto Struve 1952, but only became popular in 1995 after the first identification of a planet around a Sun-like star, 51 Pegasi, by Michel Mayor and his PhD student, Didier Queloz, for which they received the Physics Nobel Prize in 2019. The same holds true for gravitational wave astrophysics, which became a mainstream research area after the discovery of the first gravitational-wave source GW150914 by the LIGO collaboration in 2015, for which the Physics Nobel Prize was awarded in 2018.
Today, a brief research note in the spirit of Struve’s paper — indicating a new path for discovery, would have likely been blocked by the moderators of the arXiv and never posted there. The moderators’ argument would be that the note is not extensive enough to be of substance, as it follows trivial extrapolations from what is known in binary star systems.
In contrast, the most important lesson to be learned from the history of physics is to avoid areas where little progress was made in advancing our scientific knowledge about reality for many decades. This includes frontiers in theoretical physics which are founded on concepts that did not receive experimental confirmation for more than half a century. This “half a century” timescale is fundamental in this context, as it represents the typical active period of a physicist and reflects the risk of spending a full career on a research program that does not lead to the discovery of a new facet of reality.
The world of ideas is far grander than the real world in which a small minority of these possibilities are realized. The task of a mathematician is simpler than that of a physicist because mathematical ideas do not need to stand up to the scrutiny of experimental evidence on whether they describe reality.
The most consequential choices in life involve taking risks because the outcomes are uncertain until we explore them. And by the time we explore them, any wasted time cannot be spent on better options. So, what does a physicist do to have a meaningful career? Focus on frontiers with fresh unexplained and exciting data and take some risks in an attempt to advance them. Exploring the unknown makes life meaningful and fun.
Do I expect most of the students who attended the Q&A after my colloquium to follow this advice? No, I am not that naive. Most will follow popular trends that offer the best prospects for postdoctoral and faculty jobs later on. These favored research areas were carved out by senior mentors who rested their prestige on the beaten path, even if that path did not reveal low hanging fruit for decades. The safe bet for fledgling scientists is to impress peers by following fashion. This offers the comfort of a large community of colleagues who meet regularly in the corridors of academia and in conferences to discuss the latest constraints on things that are not proven to exist.
The same students will eventually become senior faculty and answer the question: “how long will you continue?” by the answer: “as long as I am funded.” And they will continue to be funded, as long as the funding committees are populated by like-minded colleagues. Humans know how to make life a self-fulfilling prophecy.
ABOUT THE AUTHOR
Avi Loeb is the head of the Galileo Project, founding director of Harvard University’s — Black Hole Initiative, director of the Institute for Theory and Computation at the Harvard-Smithsonian Center for Astrophysics, and the former chair of the astronomy department at Harvard University (2011–2020). He chairs the advisory board for the Breakthrough Starshot project, and is a former member of the President’s Council of Advisors on Science and Technology and a former chair of the Board on Physics and Astronomy of the National Academies. He is the bestselling author of “Extraterrestrial: The First Sign of Intelligent Life Beyond Earth” and a co-author of the textbook “Life in the Cosmos”, both published in 2021. His new book, titled “Interstellar”, is scheduled for publication in August 2023.
