Looking in the Wrong Places

Looking in the Wrong Places

Sabine Hossenfelder [4.30.18]

We should be very careful in thinking about whether we’re working on the right problems. If we don’t, that ties into the problem that we don’t have experimental evidence that could move us forward. We're trying to develop theories that we use to find out which are good experiments to make, and these are the experiments that we build.  

We build particle detectors and try to find dark matter; we build larger colliders in the hope of producing new particles; we shoot satellites into orbit and try to look back into the early universe, and we do that because we hope there’s something new to find there. We think there is because we have some idea from the theories that we’ve been working on that this would be something good to probe.

If we are working with the wrong theories, we are making the wrong extrapolations, we have the wrong expectations, we make the wrong experiments, and then we don’t get any new data. We have no guidance to develop these theories. So, it’s a chicken and egg problem. We have to break the cycle. I don’t have a miracle cure to these problems. These are hard problems. It’s not clear what a good theory is to develop. I’m not any wiser than all the other 20,000 people in the field.

SABINE HOSSENFELDER is a research fellow at the Frankfurt Institute for Advanced Studies, an independent, multidisciplinary think tank dedicated to theoretical physics and adjacent fields. She is also a singer-songwriter whose music videos appear on her website sabinehossenfelder.com (see video below). Sabine Hossenfelder's Edge Bio Page

LOOKING IN THE WRONG PLACES

I’m still asking myself the same question that I asked myself ten years ago: "What is going on in my community?" I work in the foundations of physics, and I see a lot of strange things happening there. When I look at the papers that are being published, many of them seem to be produced simply because papers have to be produced. They don’t move us forward in any significant way. I get the impression that people are working on them not so much because it’s what they’re interested in but because they have to produce outcomes in a short amount of time. They sit on short-term positions and have short-term contracts, and papers must be produced.

If that is the case, then you work on what’s easy to do and what can quickly be finished. Of course, that is not a new story. I believe it explains a lot of what I see happening in my field and in related fields. The ideas that survive are the ideas that are fruitful in the sense of quickly producing a lot of publications, and that’s not necessarily correlated with these ideas being important to advancing science.

The field that I mostly work in is the foundations of physics, which is, roughly speaking, composed of cosmology, the foundations of quantum mechanics, high-energy particle physics, and quantum gravity. It’s a peculiar field because there hasn’t been new data for almost four decades, since we established the Standard Model of particle physics. There has been, of course, the Higgs particle that was discovered at the LHC in 2012, and there have been some additions to the Standard Model, but there has not been a great new paradigm change, as Kuhn would have put it. We’re still using the same techniques, and we’re still working with the same theories as we did in the 1970s.

That makes this field of science rather peculiar and probably explains why there hasn’t been much progress. But it’s not like we don’t have any questions that need to be answered. There are a lot of questions that have been around for decades. For example, what is dark energy? What is dark matter? What are the masses of the Standard Model particles? And what’s up with the foundation of quantum mechanics? Is a theory that's fundamentally not deterministic, where we cannot predict outcomes, the last word that we have, or is there something more to it? Is there maybe another underlying structure to reality?

Why do people continue to work on it if it doesn’t look like anything has been happening? It’s a good question. The reason is that we are all pretty sure that there is more, but we haven't reached the fundamental level. Maybe we will never reach it. Certainly, the theories that we have right now are not all there is. The question is, of course, if we don’t have any guidance by experiment, how do we make progress? And are we doing the right thing?

Very plausibly, the main reason why we haven’t made progress is that we’re not doing the right thing. We’re looking in the wrong places. We are letting ourselves be guided by the wrong principles. It’s about time that we rethink this because, clearly, it’s not working. One of the things that I’ve spent a lot of time thinking about is what would be good principles to look at. Interestingly, in high-energy particle physics and also in cosmology, people pay a lot of attention to aesthetic criteria that they use to select theories they think are promising. And we know that paying attention to beauty is not very scientific. It’s certainly a human desire, but it’s questionable whether it will bring us anywhere.

Scientists often justify their use of these criteria by claiming it’s based on experience. Experience moves us forward until it doesn’t. We’ve reached this point where we have to carefully rethink if the criteria that we’re using to select our theories are promising at all. If one looks at the history of this field in the foundations of physics, progress has usually been made by looking at questions that, at least in hindsight, were well posed, where there was an actual mathematical contradiction.

For example, special relativity is incompatible with Newtonian gravity. If you try to resolve this incompatibility, you get general relativity. It’s a similar problem with the incompatibility between non-relativistic quantum mechanics and special relativity that led to the development of quantum field theory. There are various similar examples where such breakthroughs have happened because there was a real problem. There was an inconsistency and people had to resolve it. It had nothing to do with beauty. Maybe beauty was, in some cases, the personal motivation of the people to work on it. There’s certainly some truth to this, but I don’t think it’s good to turn this story around and say that if we only pay attention to this motivation that comes from ideals of beauty it will lead to progress.

We should be very careful in thinking about whether we’re working on the right problems. If we don’t, that ties into the problem that we don’t have experimental evidence that could move us forward. We’re trying to develop theories that we use to find out which are good experiments to make, and these are the experiments that we build.  

We build particle detectors and try to find dark matter; we build larger colliders in the hope of producing new particles; we shoot satellites into orbit and try to look back into the early universe, and we do that because we hope there’s something new to find there. We think there is because we have some idea from the theories that we’ve been working on that this would be something good to probe.

If we are working with the wrong theories, we are making the wrong extrapolations, we have the wrong expectations, we make the wrong experiments, and then we don’t get any new data. We have no guidance to develop these theories. So, it’s a chicken and egg problem. We have to break the cycle. I don’t have a miracle cure to these problems. These are hard problems. It’s not clear what a good theory is to develop. I’m not any wiser than all the other 20,000 people in the field.

We certainly see why things are going wrong in my community and also in other communities. It’s not so different from other fields. Just this morning someone made a joke that we should have a Godwin’s Law for scientific discussions, which is that if the discussion goes on long enough, in the end it will always be about funding in academia. There’s certainly some truth to this because the funding that we get, and how we get it, and who gets it, and how long we have it, has a huge influence on what research we make and also what we believe in eventually. Once you work on something for some years, you start believing in it.

The way that research is funded in foundations of physics and in many other fields just puts a lot of things at a disadvantage that are not pursued anymore. Typically, everything that takes longer than three years to complete, no one will start it because they can’t afford it. They can literally not afford it.

On the other hand, all the questions that are fruitful and produce lots of papers in a short amount of time are things that people will work on. That’s exactly what you see happening in the cosmology of the early universe—models for the rapid expansion that went on there, which is called inflation. A lot of people believe that it must have happened. There are hundreds of models that people have proposed. They are basically indistinguishable by data. In high-energy particle physics, we likewise have hundreds, if not thousands, of different models that have absolutely no experimental evidence speaking for it.

We can try to find out what would be better criteria to develop theories, and that’s a good question that should be asked, but I’m not the right person to ask. It’s a question that the community should address. This will only happen if this problem with the pressure from the funding is no longer there so that the community can start to think about what else they should be doing.

Who makes the decisions about the funding? Superficially, people say that it's a funding agency, so it’s the university who get to hire people. But that puts the blame on the wrong party. In the end it’s the community itself who makes the decisions. What do the funding agencies do if they get a proposal? They send it to reviewers. And who are the reviewers? They're people from the same community. If you look at how hiring decisions are being made, there’s some committee and they are people from the same community. They have some advisory boards or something, which contains people from the same community.

Even if that wasn’t so, what the people in these committees would be doing is looking at easy measures for scientific success. Presently, the most popular of these measures are the number of publications and the number of citations. And maybe also whether the person has published in high-impact journals. So, these are the typical measures that are presently being used. But what do they measure? They primarily measure popularity. They indicate whether somebody’s research is well received by a lot of people in the same community. And that’s why once a research area grows beyond a certain critical mass, you have sufficiently many people who tell each other that what they’re doing is the good thing to do. They review each other’s papers and say that that’s great and it's what we should continue to do. It’s a problem in all communities that grow beyond a certain size.

There is a group of people who do frontier work, people who do great work that brings us forward. But then there are 95 percent of the people who are just there because they’re productive. You see this in high-energy physics phenomenology, in nuclear physics, in heavy ion physics, and you see this in various approaches to quantum gravity. I don't want to single out string theory. I’m quite fond of string theory. It’s the same with string theory as it is in loop quantum gravity. There’s a lot of stuff produced that seems to be produced just for the purpose of producing it, because people can live from it. It’s literally the reason why they do it, and that’s not good.

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I originally studied mathematics. I have a bachelor’s degree in mathematics. I didn’t stay in mathematics because everything in mathematics was great. I couldn’t decide what to do, and at some point, you have to pick a topic and specialize in it. It helped that I went to a seminar by a mathematical physicist, which was about the then developed new approach to quantum gravity. After that, I knew which area of mathematics I should specialize in—that part of mathematics that describes the world we see. That’s where my interest in the mathematical structure of reality comes from.

It’s not so surprising that I then ended up in the Department of Physics at the University of Frankfurt, in Germany. They didn't do anything there that was related to the foundations of physics, though. They did mostly heavy ion physics and nuclear physics. It was not the best place for me. I later came to the United States and then Canada, and that gave me the opportunity to learn a lot about quantum gravity. I also figured out that much of what goes on in quantum gravity is very detached from reality. It’s pretty much only mathematics. Yes, the mathematics is there, but I still don’t know if it’s the mathematics that describes reality.

Since there were already a lot of people working on the mathematical aspects, I dedicated my research to the question of how to find out which of these approaches describes nature. I mostly work on the question of how to find experimental evidence for the quantization of gravity, which is not as hopeless as some people think it is. There are various ways that one can approach the problem.

The reason that a lot of people think it’s probably impossible to ever find evidence for the quantization of gravity is that you want to directly produce the quantum of gravity—a particle called the graviton—you need to reach energies that are so high that we will never be able to reach them in a particle collider. So, it’s pretty much hopeless. But that’s not the only way that you can probe quantum gravity. There are various reasons for why we expect effects of quantum gravity to also be accessible at much lower energies: There could be relics from quantum gravitational effects in the early universe that are imprinted in the cosmic microwave background—that’s a very simple example. People are looking for it. They are not quite there yet, but they’re looking for it.

There are other reasons to be optimistic as well. For example, a lot of people think that a theory for the quantum structure of spacetime would violate certain symmetries that are valid in a special and general relativity. That would have observational consequences that are not hidden at high energies; they could also be visible at low energies.

Maybe most interesting is a fairly recent development, which is that we might be able to measure quantum super positions of gravitational fields. I have to admit that when I heard about it, it was surprising even to me. The reason is fairly simple. We’re often told that it’s hard to measure quantum gravitational effects because gravity is such a weak force, and the quantum effects of gravity are even weaker. But that’s not strictly speaking true because how strong gravitational effects are depends on the mass that gravitates. That’s the very reason why we don’t normally think of gravity as a weak force. It’s the only force that is left over on long distances, and the reason for this is that it adds up. It gets stronger the more mass you pile up. More precisely, we should say that the reason we find it so hard to measure quantum gravitational effects is that we either have a particle that has very pronounced quantum properties, like, say, a single electron or something like that, but then it’s so light that we cannot measure the gravitational field. Or we have some object that is so heavy that we can measure the gravitational field, but then it doesn’t have quantum properties. Okay, so that’s the actual problem.

It’s interesting that experimentalists have made a lot of progress in bringing heavier and heavier objects into quantum super positions. They are not yet quite at masses where we can measure the gravitational fields of these objects, but it’s not so far away. Usually when we speak about the difficulties of measuring quantum gravitational effects, we’re speaking of effects that are thirty or forty orders of magnitude beyond what we can measure. But with these experiments, we’re talking about three or four orders of magnitude. And it seems to me quite possibly that this is a gap that will be closed within the next ten or twenty years.

I frequently get asked if I have an approach to quantum gravity that is my favorite, to which the answer is no. Most of the approaches, at least the larger ones, have something speaking for them. They all have their benefits and shortcomings. For me the question is, can you go and test them? Do they make some predictions that you can go and look for? This experiment that I was talking about, where you might be able to measure the gravitational field of some heavy quantum object, it does not measure the strong field limit of gravity, which is where it would be the easiest to distinguish between different approaches to quantum gravity; it measures the weak field limit.

Some people are quite unexcited about this, which I find totally ridiculous. They’re like, "Oh, but this would only be the weak limit of quantum gravity." I can only respond by saying, "But it would be quantum gravity. It will be the first evidence for quantum gravity. It would make this field a real science if we could go and measure it."  It’s not uninteresting in contrast to what some people seem to believe, because in different approaches to quantum gravity this limit could look different, and we could go and measure it.

The problems that I see in my own community worry me a lot. Not so much because I’m so terribly worried about quantum gravity. On a certain level, even though it’s my personal interest, I realize that for most of the people on the planet making progress in quantum gravity is not that terribly important. It worries me because I have to question how well science itself is working.

The problems that I was speaking about in my own community—that people work on certain topics just because the money is there, because it’s something that is popular and that their colleagues appreciate—are problems that almost certainly exist in most scientific communities. My extrapolation from my own field would tell me that I should be very skeptical about whatever comes out of the scientific community. And that’s not good. Clearly that’s not good.

I’ve been thinking for a lot of time how we could go about and try to solve these problems. It’s hard, but it’s necessary. We need science to solve the problems on this planet, problems that we have caused ourselves. For this we need science to work properly. First of all, to get this done will require that we understand better how science works. I find it ironic that we have models for how political systems work. We have voting models. We have certain understanding for how these things go about.

We also have a variety of models for the economic system and for the interaction with the political system. But we pretty much know nothing about the dynamics of knowledge discovery. We don’t know how the academic system works, for how people develop their ideas, for how these ideas get selected, for how these ideas proliferate. We don’t have any good understanding of how that works. That will be necessary to solve these problems. We will also have to get this knowledge about how science works closer to the people who do the science. To work in this field, you need to have an education for how knowledge discovery works and what it takes to make it work properly. And that is currently missing.

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"Catching Light"
By Sabine Hossenfelder