A new era of science

[img source: changingcourse.com]

Here in basic research we all preach the gospel of serendipity. Breakthroughs cannot be planned, insights not be forced, geniuses not be bred. We tell ourselves – and everybody willing to listen – that predicting the outcome of a research project is more difficult than doing the research in the first place. And half of all discoveries are made while tinkering with something else anyway. Now please join me for the chorus, and let us repeat once again that the World Wide Web was invented at CERN – while studying elementary particles.

But in theoretical physics the age of serendipitous discovery is nearing its end. You don’t tinker with a 27 km collider and don’t coincidentally detect gravitational waves while looking for a better way to toast bread. Modern experiments succeed by careful planning over the course of decades. They rely on collaborations of thousands of people and cost billions of dollars. While we always try to include multipurpose detectors hoping to catch unexpected signals, there is no doubt that our machines are built for very specific purposes.

And the selection is harsh. For every detector that gets funding, three others don’t. For every satellite mission that goes into orbit, five others never get off the ground. Modern physics isn’t about serendipitous discoveries – it’s about risk/benefit analyses and impact assessments. It’s about enhanced design, horizontal integration, and progressive growth strategies. Breakthroughs cannot be planned, but you sure can call in a committee meeting to evaluate their ROI and disruptive potential.

There is no doubt that scientific research takes up resources. It requires both time and money, which is really just a proxy for energy. And as our knowledge increases, new discoveries have become more difficult, requiring us too pool funding and create large international collaborations.

This process is most pronounced in basic research in physics – cosmology and particle physics – because in this area we deal with the smallest and the most distant objects in the universe. Things that are hard to see, basically. But the trend towards Big Science can be witnessed also in other discipline’s billion-dollar investments like the Human Genome Project, the Human Brain Project, or the National Ecological Observatory Network. “It's analogous to our LHC, ” says Ash Ballantyne, a bioclimatologist at the University of Montana in Missoula, who has never heard of physics envy and doesn’t want to be reminded of it either.

These plus-sized projects will keep a whole generation of scientists busy - and the future will bring more of this, not less. This increasing cost of experiments in frontier research has slowly, but inevitably, changed the way we do science. And it is fundamentally redefining the role of theory development. Yes, we are entering a new era of science – whether we like that or not.

Again, this change is most apparent in basic research in physics. The community’s assessment of a theory’s promise must be drawn upon to justify investment in an experimental test of that theory. Hence the increased scrutiny that theory-assessment gets as of recently. In the end it comes down to the question where we should put our money.

We often act like knowledge discovery is a luxury. We act like it’s something societies can support optionally, to the extent that they feel like funding it. We act like it’s something that will continue, somehow, anyway. The situation, however, is much scarier than that.

At every level of knowledge we have the capability to exploit only a finite amount of resources. To unlock new resources, we have to invest the ones we have to discover new knowledge and develop new technologies. The newly unlocked resources can then be used for further exploration. And so on.

It has worked so far. But at any level in this game, we might fail. We might not succeed in using the resources we have smartly enough to upgrade to the next level. If we don’t invest sufficiently into knowledge discovery, or invest into the wrong things, we might get stuck – and might end up unable to proceed beyond a certain level of technology. Forever.

And so, when I look at the papers on hep-th and gr-qc, I don’t think about the next 3 years or 5 years, as my funding agency wants me to. I think about the next 3000 or 5000 years. Which of this research holds the promise of discovering knowledge necessary to get to the next level? The bigger and more costly experiments become, the larger the responsibility of theorists who claim that testing a theory will uncover worthwhile new insights. Do we live up to this responsibility?

I don’t think we do. Worse, I think we can’t because funding pressures force theoreticians to overemphasize the promise of their own research. The necessity of marketing is now a reality of science. Our assessment of research agendas is inevitably biased and non-objective. For most of the papers I see on hep-th and gr-qc, I think people work on these topics simply because they can. They can get this research published and they can get it funded. It tells you all about academia and very little about the promise of a theory.

While our colleagues in experiment have entered a new era of science, we theorists are still stuck in the 20st century. We still believe our task is being fighters for our own ideas, when we should instead be working together on identifying those experiments most likely to advance our societies. We still pretend that science is somehow self-correcting because a failed experiment will force us to discard a hypothesis – and we ignore the troubling fact that there are only so many experiments we can do, ever. We better place our bets very carefully because we won’t be able to bet arbitrarily often.

The reality of life is that nothing is infinite. Time, energy, manpower – all of this is limited. The bigger science projects become, the more carefully we have to direct our investments. Yes, it’s a new era of science. Are we ready?